Some time in 2023, Tom Kalil told me he thought it would be a good idea to carve out a chunk of time and get to work on some ARPA project histories. The ARPA model was proliferating, and Tom felt these pieces might find a ready audience of ARPA emulators and fans eager to make use of the actionable information. Tom, who was then at Schmidt Sciences and is now President of Renaissance Philanthropy, has good taste. When he suggests something, I’ve learned you should listen. So I trusted him and threw myself into the work.

If any of you have enjoyed this series and wondered how the sausage is made, “How does one figure out how a 60-year-old R&D project — with no book written about it — was managed?” The answer is often: oral histories. The documentation that enabled many of these histories came to be because, at some point, committed historians sat down with a set of DARPA Directors, officer directors, staff, program managers, and funded researchers to record interviews with them on the practical details of their work.

Usually, I’m just a consumer of these oral histories. In today’s piece, in a departure from my usual role, I get to deliver you all an oral history — one I think is ideally suited to FreakTakes readers. It’s an oral history with possibly the best guest I could have asked for: Ilan Gur. Ilan is the founding CEO of the UK’s new Advanced Research and Invention Agency (ARIA). And, better yet, he’s a huge metascience nerd! The two-hour interview, recorded in Berkeley, attempts to unpack the metascience experiment that is ARIA.

I can’t thank Asimov Press enough for funding the interview and facilitating its recording. The full audio, video, and transcript are here on FreakTakes. And I also worked with Asimov to write up a much snappier, abridged version of the interview. You can find that piece in Asimov Press today.

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If you prefer to listen to podcasts on Spotify, the Spotify version of this interview can be found here.

And since the text formatting for podcast transcripts on Substack can be annoying, I’ve also published the written transcript as its own piece, in addition to including it below.

Eric: Ilan, the CEO of the [UK] Advanced Research and Invention Agency. Thank you so much for being here and doing the Asimov interview today.

Ilan: Thanks for having me. I don’t think I have ever been interviewed by someone who geeks out about the same things I do as much as you.

Eric: Well that’s exhilarating, because this is my first interview. We’ll see how it goes! [Laughter]

First question. We’ll start with a fun one. As grandiose as it sounds, ARIA’s mandate is to aim big and try to create technologies as important as the ARPANET or spark new fields the way the Rockefeller Foundation did with molecular biology. Do you consciously think about that to yourself — that you have to be or find the next Warren Weaver or JCR Licklider? Does that keep you up at night?

Ilan: [Laughter] What keeps me and our team up at night is actually having a massive enough impact. Do we think about trying to be or find the next Weaver or Licklider? Probably not. I use an analogy often of being a catalyst or an enzyme. Whether it's me or our team, we're one thing you introduce into the system that hopefully mobilizes a bunch of other stuff to make an impact.

Eric: In that case, if you think about being a catalyst, what makes a reaction big enough?

Ilan: That’s a great question. You’ll appreciate this: when we have program directors that come into ARIA, some of the pre-reads we give them before they start are interviews with Bob Taylor or stories from DARPA or otherwise. And the main thing is to try and get in their heads, “What does a win look like?” For a lot of places if the research you fund leads to a new product that makes an impact, that's a big win. I often say, “That would be a loss for ARIA.” Because what we really need to do is catalyze something that is bigger than a product, bigger than a company. It should essentially be like a movement, an entirely new technology platform that didn't exist, an entirely new industry that didn't exist. And I think the way you catalyze that can be really different for different people. So if I think about our program directors, they're all different. They all have different superpowers. Just like if you think about Licklider...I mean you're a history geek, right? So just like if you think about Licklider and Bob Taylor, right, you could talk about them each as having catalyzed this massive transformation, but in very different ways.

Eric: Are there any reactions that have been catalyzed in the past 10 or 20 years or so where you look at them and you say “Wow that's the kind of thing we should be going for”? I’m definitely guilty of thinking too far in the past on some of these things, so I’d love to hear your examples.

Ilan: One of our advisors for ARIA is Aslem Turechi, one of the founders of BioNTech. And so you think about their story of having sort of worked so hard on mRNA-based vaccines and systems — initially for cancer. And then you think of Dan Wattendorf at DARPA who basically started the program thinking about vaccines for pandemics. All of that was in the mix, and then all of a sudden you had the pandemic event that actually turned it all into the world-changing impact. So I think that's such an easy one to go to. I also want us to be thinking differently at ARIA around how those transformations might take place.

Interestingly, for example, you think of ASML as a company. But it really is a company that manifests, in that one company, a massive transformation in the field, in terms of UV lithography. Especially with ARIA being something based in the UK...you can't be picky in terms of how you're gonna get that world changing of a transformation within an ecosystem that is bound like the UK. I mean, we’re working globally, but I think ASML is such a compelling example of, “Out of some fodder and set of reactants, back to the catalyst, something catalyzed this massively transformative company and then field shift.”

Eric: Do you have any program in the current cohort that you think, like, their way of scaling to impact might be in an ASML-shaped box?

Ilan: That’s a great question. I think it may be for...any of them. [Laughter] In the sense that, and we may talk about this more later on, one of the big things about ARIA that we're trying to build in...that maybe differentiates it from, say, ARPA agencies or DARPA (which started seventy years ago) is recognizing just how important entrepreneurship and startups are to cutting-edge research in today's world. Our bet with ARIA is that probably the biggest driving force for impact will be through entrepreneurs and entrepreneurship, in some way. Whether you end up catalyzing a whole ecosystem of entrepreneurs and different companies, or entrepreneurs that are focused on government, or whatever else. Or what emerges from that is one singularity of a company that changes the world, or like an “Ozempic moment.” Again, I don’t think we can be picky. I think you could imagine that happening in just about any of our spaces. For example, I think about neurotech, I think about programmable plants, and certainly in robotics. It's just a question of do we get lucky and nucleate that right thing at the right time.

Eric: On that point. So I read your House of Lords testimony and a lot of things of that sort…

[Laughter]

Eric: I’d love to parrot back to you how I understand ARIA, from those materials. You can tell me what’s right, what’s wrong, what I need to say differently, etc. Also, if you could use examples from some of the current programs, that would be great. I’m sure there are many listeners who may have seen a program announcement, but that’s all they know. So as I understand it: ARIA programs must be 1) “big if true” and 2) differentiated. You don't want to fund programs that somebody else in the ecosystem would fund otherwise. And while each project doesn't have to succeed — the vast majority won't in the traditional sense — they should all succeed in materially changing the conversation regarding what's possible in a given space. In terms of your mandate in the UK — in the long term, these programs are meant to help drive economic output, quality of life improvements, health benefits, etc. Is that more or less accurate, how you'd conceptualize it? If someone says, “Isn’t that what deep tech VCs do?” what would you say?

Ilan: First of all, is that right? I think that’s right. We're meant to take bold bets that kind of amplify different parts of the research system in new ways. I think about our programs as funding like a constellation of teams that can lead to massively transformative outcomes at the intersection of quality of life and economic growth — not just for the UK, but for the world. I think that ‘for the world’ is really about the scale of ambition that we are talking about.

You were asking, “How’s that different from a VC?”

Eric: If somebody says, “How’s that different from a VC? Or “...than if the NIH spins up a new study section?” Or something of that sort.

Ilan: I think those are two very different questions. Let’s talk about VCs. There are a lot of VCs who are just in it to make money...but in terms of the mindset and the motivations...a lot of VCs, I think, do see venture capital as a platform to change the trajectory of the future and world in positive ways. I think the big difference with VC is — when talking about the idea of ‘big-if-true’ — there’s a sense of scale, right? You have to think about the scale of “how big is ‘big’?” — and how speculative are you willing to get on the ‘if-true’?

In talking to venture capitalist friends about what I do and what we do at ARIA, sometimes you hear this metaphor around startups and VCs: “surfing a wave.”

That’s one way to think about this. What does a VC do? A VC is meant to be like a surfer in the water, to look out at the wave set that’s coming and ask themselves, “Oh, okay, is that wave forming? Is that going to be a really big one?” The size of the wave is, kind of, how big of a market they think might emerge. And the bet they’re trying to make is, “I bet that’s a big enough wave.” And then they’re trying to bet on the timing, like, “Okay, this is when I should grab a surfboard and start paddling.” And you can think of the surfboards as the companies they’re investing in.

I think the big difference [between ARIA and VC] is, that’s being very reactive to the system. You’re trying to find the trends you can hop on and surf, so that you can maximize the ROI of your investment in a very concrete, direct way.

I see our job as more of putting the energy in to create the wave. A venture capitalist can only fund into a thesis once there’s enough momentum where they can start reading, “I see the market forming, I think there are technologies that can work here.” And most importantly, “There are companies.” Like, most VCs are waiting for companies to come find money. So there need to be enough entrepreneurs and companies doing that.

If you look at the spaces that we’ve carved out [at ARIA], we’ve said, “Right now everyone looks out and just sees flat water, but we believe that by pushing a little bit here or there we can start to build a wave.” And if we can catalyze the formation of a wave that’s big enough in one of these spaces, then actually that’s going to catalyze all the VCs to want to jump on that wave and to want to invest in companies. Then you get a win-win and, ultimately, change the world. [Laughter]

Eric: And so…

Ilan: Was that helpful, that analogy? I probably went a little too much on that.

Eric: No no no, it was great! So I have some questions. Sometimes, in terms of creating the wave...I’m sure there are times where you put a certain amount of money in a space, and there's enough teams out there that already care about this and have the proper background and the right incentives to just throw themselves into it once the capital is there. And then there's probably other cases where more legwork is necessary. Because that's not quite what a university would do — or usually a startup would do X task, but this isn’t quite a VC-scale market. How do you approach those two different types of areas?

Ilan: There’s so much we can talk about here. I’m glad this is a long form interview, because we’ll have time to get into a bunch of this. Part of this has to do with how we organize what we focus on, and maybe we’ll come back to that. I think it’s worth just talking about an example here. What came to mind as we were talking about the wave and VCs, I was thinking about one of our program directors, Angie [Burnett]. This might be particularly interesting to this audience. Angie’s a plant physiologist by background, had worked in academia, a national lab, she worked for the UN for a little bit. She came into ARIA initially thinking about food security and what we could do in food security. Fast forward — where did she end up with her opportunity space, which is what we call our focus areas, and then the program that she launched? The opportunity space that she launched is called Programmable Plants.

We tend to think for all of these [opportunity spaces], there’s some insight there. For us, an opportunity space needs to be, like you said, big-if-true. And we need to be able to make an argument relative to the potential impact. So if it’s highly consequential for society and relative to that impact you can argue it’s underexplored...you know, not enough funding or not enough of the right type of ideas or bets being made in that space. And that for some reason, it’s ripe for transformation. That defines a very big [opportunity] space that we are now going to start working in — and basically buying options through the early research that we’re funding to learn more and see if we find something that could become one of those big waves.

Angie's insight on this space was that if you just think from first principles, when you look at some of the biggest problems and opportunities we have in the world, obviously, agriculture is one of them. You think about food security, you think about climate change. The tough part about these segments is that they're massive problems, right? You need to talk in terms of gigatons of CO2 or carbon, in either case. And her view is that, actually, you can think of plants as a technology platform, and plants are one of the few technology platforms we know of that, actually, we have a system that operates at that scale — of gigatons of carbon.

And what do I mean by technology platform? A plant is a piece of hardware. It has certain functionality. Interestingly, in many plants, like you go to the store and you buy a cob of corn, we have actually engineered the functionality of that plant over many years. And you have distribution channels and the ability to deliver these things at a massive global scale, commensurate with those problems — food security, climate, etc.

The problem is...it's like a really shitty technology platform, right? We're very limited in what functionality we can build in. Instead of 18 months for a new iPhone, you take 18 years to get a new crop that's actually viable. Interestingly, if you talk to most investors, they will say, “Well, in the ag space...you've got the top [incumbent] ag companies and [given the incumbents and structure] it's basically the hardest, most entrenched space to innovate in.” It's just not a great place to invest. Massive capital, massive entrenched interests, there’s regulations, etc.

The bet that we're making is that actually...on first principles, when you look at what’s happening in synthetic biology, when you look at the problems and the forcing functions that are coming, requiring a change to how we do agriculture...there’s a pretty strong argument to be made that, sometime in the next few decades, there will be a shift in how we approach global agriculture. You can think about it as something like, “There will be an ASML-type company that completely disrupts the big five ag companies in the world, and does things radically differently.”

Eric: And what's Angie's job over the course of five years? And I guess also tie in, what is a program director? And how important is it that they have a point of view? And does that come out as you're picking them? ...I asked you a lot of questions.

Ilan: No, that’s fine. Angie’s job was first — together with me and the cohort we had — beating up the question of, “How do you define a space that’s interesting and in line with this idea of ‘plants as a technology platform that’s underappreciated’?” Synthetic biology has been this massive vector of technology progress, which is not being leveraged for plants and ag to anywhere near the extent it’s being leveraged for human health. So now there’s like this arbitrage [opportunity]: “We’re making all this progress in synbio, we have this massive problem opportunity in ag.” But they’re not really connecting the dots.

Eric: And how many years behind do people perceive ag as, in terms of the cutting edge in synbio? I’ve heard 10 or 20 years, but you’d have a better...

Ilan: Well, let’s fast forward. So, what is Angie’s job? Her first job is to lay out that space. The next job was to say, “Okay, what’s a funding program we’re going to launch?”

She had a bunch of different ideas. Where she ended up is a program that we’ve now launched — and we’ve just announced the people and groups we’re funding. That program is called Synthetic Plants. [See this link for more information.]

And the idea was, if you look at the real frontier edge of synthetic biology, and we're talking about things like de novo genome synthesis, like actually thinking about synthetic organelles. You have, in the UK and other parts of the world, really amazing progress happening. But when you go and talk to those researchers working in those areas, and you say, “Well, we're thinking about doing a plant program,” the reaction Angie got from all of them was, “Why? There's so much to be done in mammalian systems, we're making all this progress...like, plants are hard! They have multiple copies of the genome, it's impossible to figure out how to transform them, it’s XYZ...”

And instead of getting discouraged by that, Angie got more excited by that. She said, “Well, wait a second, let me tell you a little bit about the potential impact we could make if you start working on plants.” Long story short, she held a workshop. And I got to be at this workshop, where she brought together a combination of top synbio people, top ag people in the UK and otherwise. There were probably 50 people in the room. One of the questions I asked was, “How many other people in the room did you know when you walked in?” And I had said [gesturing his hand upward], “Raise your hand if you only knew one person, raise your hand if you only knew X...”

And I think most people knew like five out of the 50...and none of the synbio people had talked to any of the plant people.

What we’ve found is, now, there are all these new collaborations. We have synbio folks who are basically saying, “I’m shifting my work to plants because I’m just convinced this is the most important thing I can do.”

Eric: And when you say ‘folks,’ how many are thinking of shifting their work to plants?

Ilan: Well, you’ll see how many synbio people we fund in this program when it gets announced. But I know of at least two specific cases Angie’s mentioned where, when she started the process, the person was so averse to the idea of doing anything in plants and thought it was a waste of time...who have built really meaningful collaborations and — whether they get our funding or not — are going to start working on that. So, it’s cool.

Eric: When is high variance [in reactions] among the adjacent experts exciting? When is it less exciting?

Ilan: Oh yeah. How do you know when people just say, “Oh, that's a horrible idea.” How do you know when it actually is a horrible idea? [Laughter]

Yeah, I mean this is an interesting thing. You talk about variance, right? Someone from DARPA once shared this with me, and it's a framework that I really love, which is...if you think about the role DARPA plays, more important than anything else, it is a mechanism to increase variance in the system.

It’s actually something I think a lot about for ARIA. The idea there is, more than anything else, ARIA was created to do things differently. The idea is: do things differently, and by doing things differently, by shifting the modality of research, you can get different outcomes. We can spend a lot of time coming back and talking about that.

But if you want to do things differently, first of all, you need people who see things differently. It’s one of the reasons the PD [program director] model is very helpful. But secondly, you have to break what is, I think, a pretty strong and homogeneous sort of truism of how we (largely governments) fund research. Which is something like, “We’re pretty good at funding the well-known disciplines. And we’re pretty good at funding the obvious problems or opportunities.” But that's all very linear, like, “More funding for biology, or synthetic biology, or semiconductors, because we see what's happening geopolitically.”

If you want to do something different, you need to find some way to cut and slice through that in a different way. Interestingly, the ARPA model says, “Okay, you find a program director, like Angie. You have them look across the system and say, ‘Well, what’s an actual thesis of something new that we could do, that’s not a single discipline? Maybe it is, but it cuts across TRLs [Technology Readiness Levels].” That’s the other thing. People sometimes ask, “Is this low TRL or high TRL?” It’s like, no. We’re mixing these modes in new ways.

Eric: You’re ambitious and applied...

Ilan: Yeah, and you have sort of a spectrum of portfolio. What that means is, what we end up funding on the backend of one of these theses we’ve developed, is going to be a very different set of people with a very different set of incentives — in terms of what they are going to do — than would otherwise get created.

And the variance is...if everyone thought it was a good idea, we would be introducing no variance into the system. If no one thought it was a good idea, we probably shouldn’t do it because it probably is not a good idea. But if you get spiky reactions to anything you’re doing, it’s the sort of thing where...okay, you have some minority that actually think this could work. But in a consensus panel, peer review, that minority voice would probably not win out or be there. So it would never happen otherwise. And, actually, I think the hardest job of a program director is to be able to actually face the criticism of so many people saying, “You don’t know what you’re talking about!”

Eric: You need to have courage to live with your bet, for years on end...

Ilan: You need to have courage to live with your bet, yeah.

Eric: And so some people...

Ilan: Wait, I’ve been talking a lot! I feel like it’ll be good for this audience...as we’ve been talking, what comes up for you as you think about some of the history that you’ve learned about for program managers at DARPA, variance, etc.?

Eric: So, I guess what I’ve been really impressed by, in working with the ARIA PDs, and ARIA in general, is when I read about early ARPA, 1960s and 1970s in particular, it seems like they really did trust the PMs to have an opinion. Or to say, “Here’s why this contractor’s best. You have to see it [the vision], and here’s why there’s only one group to do X thing.”

It seems like ARIA has given its PDs a long enough leash to have the point of view and follow it wherever it may lead. When I talk to folks at a place like DARPA, or something, I often get the sense that the PMs do have a strong point of view, but it’s an older organization. Like, it’s a 60 year old government agency. I think a part of the magic of DARPA is, so many government organizations only get more bureaucratic over time. They’ve [DARPA] been phenomenal at, like every five or ten years, finding ways to clear out a lot of the red tape, scar tissue, etc. But it does still build up a little bit.

So it’s been really cool. Something I try to impress upon people is that 2025 DARPA is not 1965 DARPA. You need to pursue different programs and do different things [today]. And when people ask me, “Well, do we have an early ARPA [today]?” Before ARIA, I guess I’d say, “Maybe OpenPhil.” OpenPhil lets people be free like this. But as ARIA has come into existence, it seems like you all live in the vein of early ARPA much more closely than anyone else. But, saying that, I also know you want to do something new...

Ilan: No, it’s interesting though, because I think this relates to the variance point. I’m trying to keep this dear to ARIA in the early days. It’s not about, “Did we find the right bet?” Because actually, given the variance point, in the early days, it’s not going to be obvious which is the right bet.

So it’s really about, “Are we being true to a commitment to increasing the variance of what gets funded?” And then, “Are we going to have the muscle to see the right bets emerge from that work?”

I actually had a [ARIA] board member recently say, “Isn’t one of our biggest risks right now that we created the wrong programs — like we’re funding the wrong programs?” And I said, “No, I don’t think that’s a risk at all, in part because we decided to create these opportunity spaces.” The whole idea behind an opportunity space for us, in these focus areas, is that our whole job is to take speculative bets. What that means is we can’t know upfront whether this is going to lead to impact. We can’t engineer that. The only way we get it wrong is if we take a speculative bet in an unproductive direction. So the point of an opportunity space is to say, “Let’s define what we think is a productive direction.”

An opportunity space is going to have certain beliefs that bound it. And the point is, if you can get yourself to believe these things...e.g. “Pressure on food security and climate is going to force us to do some things different in agriculture,” “Synthetic biology is moving...” Right? If you believe those things, you have to imagine there is the potential for enormous value — economic value and social impact — that can happen in this space. And now that we’ve bound that space and set that opportunity space, now we can take steps, big and small, and make bets in that area without having to worry, like, “Is synthetic plants the right program?” I’m not worried about it at all. Because we’re making a bet in a direction that’s productive.

The only thing we now have to worry about is that we don’t do what we were made to do. What makes ARIA unique — and what’s meant to make a place like DARPA unique, certainly in the early DARPA days — is that you make a bet, you take a step, and then you learn something, and you can pivot and say, “Oh! Actually it’s this 5% of what we’ve done so far that is starting to feel really valuable. Let’s minimize the rest and 10X that 5%.” That’s the thing that...I think that’ll be one of the big muscles we have to create for ARIA in this next phase.

Eric: So, you’ve moved to the UK, and ARIA is...

Ilan: I’m sorry, I have to stop! I’m like, I’m sitting here wondering if people watching this are excited about it. It’s just like — the idea that there’s now a community that’s excited to hear this conversation — that’s something I’ve been searching for for a while.

Eric: [Excited laughter] Okay, so, in that case...

Ilan: How many subscribers do you have?

Eric: Like 4,000. But there’s people like Matt Clancy who have like 15,000, or something like that. [Correction: Matt has over 18,000.]

Ilan: But those are high impact people.

Eric: Yes, I am continually wowed by the subscribers I have...and when I write something, the email outreach I get. It’s very much a dream for someone like me who...I wish I could be a great researcher [gestures at Ilan], but it was not in the cards for me.

Ilan: [Laughter] I wish I could be a great researcher too. Wasn’t in the cards for me. Definitely more of a Bob Taylor than a Licklider.

Eric: So you’ve been doing this for so much longer than many people. A lot of people have maybe gotten interested in this space in the past 5–6 years or something.

Ilan: Wait, what’s “this space”?

Eric: We’ll call it this “applied metascience” space. People who want to really consciously experiment with how you build R&D ecosystems differently, or research labs differently. In many ways, you’ve been doing this for possibly the majority of your professional career. Can you tell people about the different stops you’ve taken? Maybe different things you’ve learned along the way? Different gripes you’ve picked up? ... [I imagine] you only throw yourself into this if there’s stuff to be fixed and you have ideas.

Ilan: Yeah, I mean, I sometimes describe it as, like, I got thrown into this just because I felt like a misfit in all of the different environments to do research. And we can talk more about that. But I think that is a motivating factor, right? What motivates me, and probably what motivates most of the folks who would listen to a podcast like this, is just realizing that you can take the things we’re learning at the cutting edge of science and discovery, and turn them into stuff that’s useful, real, and awesome.

I mean I had — actually, you’ll probably appreciate this story — I was one of a rare set of people who was an undergraduate major in material science. Material science is kind of a weird field that most people, at least when I went to college, didn’t really know about.

Eric: They’d pick it up as a masters...

Ilan: Yeah, exactly. I think there were maybe like five people at Berkeley who came into the undergrad material science program. But the reason I got into material science...I grew up in Pittsburgh and went to a public school, which just happened to have a couple of phenomenal science teachers. And one of them encouraged me in 10th grade to put in an application for this program that CMU [Carnegie Mellon] did, where they would host high school students in a lab.

And I still remember, like, they gave you a questionnaire, and it was like, “What are your interests?” And I was in 10th grade, you know, I was not a polymath who was way ahead of their time. So my interests are like, ”I like physics [shrugs]...maybe chemistry?” You know, you just say pretty banal, normal stuff. Anyway, they paired me with a material science lab. And I remember showing up and saying, “Why did I get the oddball thing? Why couldn’t I just be paired with a normal lab?” And I didn’t think it was going to be cool or exciting.

The project — and this is the piece that I think you’ll appreciate — the project that I got paired with was a lab that worked in magnetics. What they wanted to do was come up with a new magnetic storage medium. At the time, you know, a hard drive was, what, 16 megabytes? You didn’t have flash drives, etc. And so the question was like, “How could you get much higher density?” So what they were doing is they were taking a material called MCM 41 — this is the part you’ll love — MCM 41 was one of a class of what are called molecular sieves. It’s a material that has a microporous structure, a lot of core space, sort of a zeolite material used as a molecular sieve/filter/etc. Basically it had like honeycomb pockets. The project was, through different means — chemically, sputtering, etc. — to fill these honeycomb pores with magnetic material, with some iron compound. And then the idea is that the ceramic honeycomb borders would be the separations between domains of a magnetic storage medium.

I still remember, at the time — you’d go around and say things like, “You could imagine putting a gigabyte on something the size of your hand!” But it was mind blowing! Just the whole idea that you have these nano honeycombs, and then you’d have a head that would sort of scan them.

Eric: Did you believe it? Or did you feel like that was crazy?

Ilan: No, I totally believed it! And the reason you’ll like the story is because MCM 41 stands for “Mobile Corporation Material #41.” So I’m still waiting for you to do a post — maybe you’ve done one and I’ve missed it — on all of the amazing discoveries, fundamental and otherwise, that came out of the oil and gas research labs. Mobile Corporation did all this incredible material science work. And, of course, they named all the compounds, like, “MCM 3, MCM 5.” So MCM 41 was, like, something everybody knows about...or at the time did!

Eric: That actually would be an interesting post too. Because I was just yelling [injecting historical stories into random conversations] at some people on Twitter the other day about the origins of TI [Texas Instruments], as just like, one of the early oil and gas firms that had a ton of early MIT ties. They just got very good at making their own instrumentation. And that’s a pretty high margin business. It’s a little less speculative. And they just like...I forget if it [TI] was a spinoff or if the firm [the original oil and gas firm] entirely pivoted. But yeah, maybe I should. If you have ideas!

Ilan: Oh yeah! Materials, lithium ion batteries, came out of an oil and gas lab. A bunch of solar cell work. I think there’s something cool there, but...

Videographer: Can we take a quick break?

[Camera Break]

Ilan: You were asking about the trajectory of ARIA?

Eric: Yeah, it would be good if we could discuss how...you were at ARPA-E. What in the world is Activate? All of these things, probably like, being dissatisfied in different ways. Or being happy with what you did, but dissatisfied drove you...?

Ilan: I think there’s a story of navigating, you know, continuing to basically try and do bigger and bigger metascience experiments, if you call it that. There’s a version of that which is, like, me being disillusioned by different institutional structures, or different silos, and how we do research. But maybe a more positive or interesting version is that, as I think over that time, is...I talked about being at CMU. When I did that research project at CMU, what flipped on for me was this idea of, “Holy shit, the wonder of the ways that we can take scientific discoveries and turn them into massive impact!” For me, the ultimate [thing] at the time — and this probably went all the way through my undergrad and into my PhD — the most valued currency for me in terms of changing the world with science was the ideas. And the instruments and the processes and the methods. I was so obsessed and in love with that, and I saw that as the big driver.

Interestingly, I had this experience 18 months into my PhD where we had written a Science paper. We were on the cover of Forbes for this new approach to creating solar cells much cheaper, you know, II-VI nanoparticles that we were going to print like newspaper. There was all this excitement. And I spent a couple of days with some business school folks with technical backgrounds, and realized it was all BS. We actually weren’t solving the right problems.

And I became...you could think about it as being disillusioned, but actually I think it’s more [that] I recognized that the world of ideas that I was in, where that was the currency, there was something missing there, in terms of how you drive impact.

And then I ended up in startups, VC-backed startups. My mindset moved from like, “Actually, ideas are pretty cheap, you know? Ideas are pretty easy to come across.” It’s more about, “How quickly can you iterate through them?”

But I also got obsessed with currency as the currency for driving impact. Because my job running a startup was, like, “Raise money.” And you could see that the more money you could raise, the more of an opportunity you had to drive and get to faster outcomes relative to competitors, or whatever else. So I really was in this mindset of money.

And having a chance to go to ARPA-E, one of the things I found very compelling was that it was a different mode from venture capitalists. I thought venture capital was sort of too narrow of an impact model for doing early-stage science, especially for industrial markets. But I also found compelling, like, “Oh wow. We’re going to be the biggest Skunk Works innovation funder in the US, for anything climate-related.” And I was attracted to this big money question. Money is like the driving force you have for reactions.

And now I think, through that time for me, at ARPA-E, my biggest recognition was that we had...

We had an incredible mission: to drive translational science into big impact in climate and energy. We had access to a lot of funding to do it, so we had the driving force. We had access to all these brilliant ideas, meaning every researcher who worked in any of these areas in the country would apply to our programs if we could just pick and choose the ideas. And the thing I realized was that, actually, none of those was actually the thing that mattered. What really mattered was people and institutions and incentives. And you can have all the money you want, and you can have all the ideas you want,  but if you don't have the right people in the right institutional environments with the right incentives to drive progress, you're pushing on a rope.

Eric: At ARPA-E, were you ever wowed by some set of people and institutions and incentives that you got to deal with?

Ilan: Well, in the end, I came back to...I left my startup feeling somehow like I had been misled. The idea of, “Venture Capital-backed startups are going to change the world.” We were working on batteries for EVs, industrial markets, very low margin business. Probably our timing was off. But I was like, I don’t see how we can develop the technology, get it to scale, and actually have it converge for someone like Vinod Khosla, who was like, “Either this needs to be a trillion dollar…” it was at the time billion dollar, now like, “...trillion dollar company, or it’s not worth doing.”

And so I kind of had a feeling when I went to ARPA-E, like, “Actually venture-backed startups are not the way to do this. And startups might not be the way to do this. Let’s figure out all the other institutional modes.” What I found in the end was that, to your question, of all the environments that I was funding research, the ones that felt most resonant and most productive were either the startups or the folks within academic labs that were already operating as though they were spinning out a company.

And what I realized was that the venture capital funding model has constraints, but if you don’t worry about the funding model for a second and you just think, “Well, what is a startup?” A startup is a vehicle for getting the right people into the right environment with the right incentives completely aligned with some translational research mission.

If you think about it, [for] everyone in an early-stage startup, the goal is to create value in a very concrete way. You’re probably doing something very speculative, if it’s science-based. Everyone who’s there in the early days has decided they’re going to commit the next chapter of their life to that pursuit. The incentive is clear. The alignment is clear. You often are getting people from different backgrounds, in interdisciplinary ways, to do it. So I think startups are massively valuable and important vehicles for R&D.

And the question becomes, and we can have a conversation about this, the question becomes, “How can we fund them? How can we fund them as R&D centers?” Venture capital is not a great way to do that. Some VCs actually do fund very applied R&D and take speculative bets. And I think those are companies that tend to change the world. But relative to the, like, $70 billion of US funding to applied and basic research — that number is probably dated right now — you don’t have anywhere near that going into super science-y startups.

Eric: To understand the problem...You love the shape of VC-funded startup groups — the people, environment, incentives they create — for the problems they want to attack. But there’s all sorts of problems that...

Ilan: They can do it if they see the wave coming and they’re just hopping on the wave. So when that happens, they work great. But why can’t you have the same aligned incentives, full-on commitment, before the wave even exists? And couldn’t that be a mechanism to create some of those waves?

Eric: And how do you think about making that happen…

Ilan: I have no idea.

Eric: ...at ARIA?

Ilan: Oh, at ARIA!

Eric: Yes. And of course all of my readers will know I’m biased. I’ve spent this huge amount of time writing about the best early ARPA contractors, like BBN or the CMU autonomous vehicle groups...groups that were very startup-related, but really embraced technical ambition over market size. Their constraint was that they need some amount of grants [or contracts] to fund it. But I’m sure you have all sorts of theories on how to make this work for you [ARIA] in spots where there are parts of the R&D ecosystem that could use a little bolstering — at least in terms of ARIA’s incentives.

Ilan: Yeah. So one of the things we’re doing at ARIA, which I think is probably different than DARPA, is being really open-minded and attuned to, “How do we try and fund not just the best people and ideas, but with resonance in terms of the environments and incentives where they are doing the work?”

What does that mean? That means a few things. One is that we are very comfortable with the idea that, using ARIA funding, a researcher might decide to go start a company. They might decide to go, leave their academic lab, and just do the research as an independent researcher, because that’s what they think is the right thing.

We have something interesting, which is we do these seed funding awards. I mentioned those opportunity spaces where we say, “This is just the direction that we think is fertile.” A program director will create a program, which is their thesis, and that’s where they’re going to focus a lot of energy and where we’ll focus a lot of funding initially. But then what we do is we say, “Well, we’re not the only smart people around. And it’s all about increasing variance. So why don’t we find other people and let them start seeding ideas that could lead to the massive breakthroughs...[unintelligible]”

And this is like, you know, give us a three-page application, tell us why you’re obsessed with this idea, and [why] no one else will fund it. And we’ll give you up to £500k. So just start running at it. And if you come back with something compelling, we can double down with you. [We can] either make it a bigger project or actually have it inspire a whole program.

Eric: So Jenny said something in one of her interviews. Jenny is the PD on the robotic dexterity program. She said at one , “I was almost disappointed that I didn’t get the chance to fund, like, some random person in their garage.” Because the funds are open to them. Can...

Ilan: Anything.

Eric: Can you explain what it would look like to be...like if I’m a random guy in Birmingham and I want to…?

Ilan: [Gestures at Eric] As opposed to a random guy in…

Eric: Yeah, in Chicago. [Laughter] And if I wanted to run it out of my garage, how much paperwork is involved? It seems to be a very fair [reasonable] amount.

Ilan: So this is really interesting. What we started with at ARIA is, we said, we wanted to make clear that we are completely agnostic. We wanted to fund the best people in the best environments. Apply. We don’t care if you’re at a university. Just tell us you’re obsessed with the idea, what the idea is, and show us that with our funds you can get access to the equipment you need to make it work. And we wanted to be really agnostic.

Now, there’s a piece of this, which is we have a brilliant, awesome, founding CFO for ARIA. Her name is Antonia [Jenkinson]. She and her team, I went to them and I said, “This is a little hard to do as a government agency. You got to do due diligence on these people. How are they using their money?” And they said, “Yeah, but this is what we’re built to do, so we’ll just figure out how to do it.”

Eric: And is it true that she walks around with the [ARIA] founding mandate in her pocket?

Ilan: [Laughter] She has been known to carry the ARIA Act around, which I love. So we started and said, “Yes, we can fund this [alternative applicants].” And seeds were a three-page application. We would tell you within three weeks whether you got the funding.

Eric: Three pages? Like...[makes a show of counting out three pages]

Ilan: Three pages, yeah. It was a three-page application, three weeks to funding decisions. And when we did it, we did have this. We had people apply. And then we had a few people who said...we had one person at a well-known university in the UK who said, “I’m really glad I’m getting this seed. To be honest, I don’t think I want to do this in my academic lab. For a number of reasons.” I think they were actually a postdoc. They were, sort of, earlier [career]. And they said, “What do you think about me, just like, finding and renting some space to do this work as an independent researcher?” The program director talked through it with them and said, “Actually, that makes sense. You’ll probably do a lot better. You’ll probably be more motivated.” Whatever it was. And so we just figured out how to give that person the award as an individual to do it in this way.

And we saw a few of those. Then we paused, and we said, “Well, wait a second. People are funded and excited to work on these projects.” And when we tell them we’re open to wherever you do it, they’re telling us, “Well, maybe I’ll do it some other way.” So the next time we did a seed call, as part of the questions we said, “What’s the institution you’re in now? If we award you the seed, where would you like to do the work? It doesn’t have to be the same place.” And the options were, “Will you do it in an academic environment?” You know, “my current university, another university, a company,” wherever else. And then we [included], “still undecided”.

First of all, I think we’re the only government funding agency in the world that gives that option. Secondly, the fact that there was an undecided bucket means, “We’re cool...like, we’ll talk through it.” I think we had like 23% of applicants in the next seed call say “Undecided.”

Which for me is such a big deal, because it suggests that being prompted with the question of like, “Eric, there’s a big project...it could be the most important thing you do in your life. Stop and think about, ‘What is the best environment for you to do this work and have it succeed and have a chance to change the world?’” And what we learned is like 23% of people [think], “Maybe it should be a startup, maybe this is my moment.” Or, “Maybe I should move to the UK and try to do this at a university in the UK,” which has happened now with ARIA grants. So, that was pretty cool.

Eric: Yeah…

Ilan: That felt like a...I warned you that if you get me excited about something, I’m just going to keep talking about it!

Eric: No, no, no! That was great! So I have a question [from my notes] lingering here, I don’t know where to put it. So I’ll just ask you now.

Ilan: Go ahead!

Eric: So this one comes from Tom Kalil. He said, “In what specific ways do you desire to transcend the DARPA model?” Because you’re not looking to set up some version of an American ARPA in the UK?

Ilan: I think that’s right.

Eric: There’s lessons you’re taking, but…

Ilan: Yeah, I mean look...I think DARPA is such incredible inspiration. You know what I mean. Like people argue about, “Is DARPA past its heyday?” “Is it doing good or bad?” But we have this beautiful gift, which is just the history and the reality and the myth of DARPA all wrapped in. And, honestly, if you can’t be inspired by that, like, forget you! Right? And I think that inspiration is so important and true.

We’ve touched on some of the things that I’m hoping with ARIA...ARPA, like you said, established 70 years ago in a very different time. It’s changed in many ways. I think for me, the most important things — one of them is one of the things we talked about earlier, which is having the intellectual humility to, and the eye on part of our job as just to increase variance and learn and pick up on threads that are valuable. That is really important to me.

One of the things I’ve noticed — and this is good and bad — but when our program directors...we pair them up with DARPA PMs, former and current, to give advice and whatever else. And oftentimes I will hear a DARPA PM say, “Wait, 37 performers for this program? You can’t do that. That’s not how we do things. That’s not the right way to do it.” What we’ve had the chance to do is kind of go to first principles on everything. And that’s a real case. I don’t think it’s 37. But davidad, who runs our Safeguarded AI program...for the first technical area of his program, he wants to, as quickly as possible, answer some theory questions and develop some frameworks which he thinks are best done as open source. And, actually, where that led him is we’re funding a lot of teams with small awards, to which normally people would say, “It’s not worth the management,” or “It’s not cohesive enough.” But the first principles suggest that, yeah, that’s the right thing to do there.

So, it’s kind of like having the intellectual humility to say, “Okay, I don’t know if this is exactly right. But it feels like it’s matching the first principles. And across what we’re doing, it gives us variance. We’ll learn more on the go.” I think that’s one thing that I’m hoping gets preserved at ARIA.

This other thing we’re talking about is probably the other most important one, which is...DARPA, rightfully, has a mantra of, “We don’t have our own labs. We don’t create institutions. We fund research projects.” And DARPA increasingly has done more with startups, which I think is great and one of the biggest impact vectors it has. But I think for us, for ARIA, being able to say from the beginning, “Actually, the people and the institutions matter. And there may be new institutions that we need to form — or that we catalyze forming. And we’re not going to be, sort of, scared about that,” is important.

Eric: Yeah. This is also something I think early DARPA was a bit friendlier to. They wouldn’t necessarily found an org, but they would write a pretty big check to an org that, like, didn’t seem to have an office yet or something like that.

Ilan: Was RAND DARPA?

Eric: Was RAND DARPA...

Ilan: I remember reading something that...

Eric: No, I think RAND would’ve been...I do think the USC ISI [Information Sciences Institute] was very clearly heavily early DARPA funded [from its earliest days, which helped create the organization of largely RAND alums]. They ran DARPA’s early MOSIS initiative, which was one of the first fabless [services]. That’s definitely a case of...those guys may have left RAND to form...I’d have to go double check some of my notes. But that’s a case of them [DARPA] writing [very early checks into an org] and making some promises, and it was an institution they needed.

Ilan: Yeah, it’s actually interesting! MOSIS came up recently at ARIA because, one of the programs that we’ve launched...we’re already starting to see that, within this...

[Camera Break]

Eric: You were talking about MOSIS and how it fits into one of your programs that you were talking about recently.

Ilan: Yeah, the opportunity space is Nature Computes Better. One of the theses there is that there have been lots of attempts to think about how you disrupt general computing. But it’s such an impossible thing to think about doing because of the massive supply chain and all the different forms of general compute. Suraj Bramhavar, one of our program directors, his insight was, “Actually, AI is very unique in the history of computing because you have a compute mode with a pretty narrow set of mathematical primitives, but potentially massive applicability, value, and impact. And that narrow mode of AI could be a new foothold to think about alternative types of computation — with alternative physics, alternative hardware, alternative substrates, etc.”

And the other piece of this is...when we think about, “Is there a program or opportunity space here,” one of the important questions to ask is, “What is the fundamental limit of performance that could happen in this space? And where are we now?” And one of the things we know about computation is,[even though] we’ve had Moore’s law for as long as we have, we are still orders of magnitude from the fundamental limits of computation. Whether it’s [the fundamental limit based on] Shannon’s information theory or what we see happening in nature. So the idea behind the space is, “Can we find new approaches inspired by physical systems, natural systems, other ideas that researchers have, etc. to use AI as a foothold for next gen compute?” The program that we’ve shaped aims to demonstrate that you can show, as a first step, AI training at a thousandth the cost and energy consumption than state of the art today.

And there are a bunch of really interesting systems questions around, like, “How do you even prove that in sort of a demo system?” We’ve now funded a set of teams across academia, startups, big companies, and a number of approaches that we think, in coordination, can get there. And from that work we’re already seeing, “Wow, there might be a next phase of this given some of the early excitement that we have.”

How would you take advantage of it? Maybe you need some MOSIS-like institution that is focused on this area. It’s still very early, but it’s cool because, like, you had your post on MOSIS and it actually is making a difference, being able to give us [ARIA] a catalyst of things to chew on.

Eric: And can you paint a picture of what this MOSIS would be doing? Like if a lot of these contractors are point solutions or different approaches, what would you need them [this MOSIS] to do?

Ilan: [Laughter] I don’t think I could paint a picture of that for Suraj’s program because he’s literally just in the early stages of thinking about it and I don’t think I could actually talk through it without disclosing things that he probably wouldn’t want me to. But I do think, you know, one of the things we talked about earlier was the question of, “Where are there new institutions, and how could they help ARIA?” We talked about our Creators. (DARPA talks about the people they fund as ‘performers.’) We thought that was a little odd. Actually, you might know the origin story of where ‘performers’ came from. Maybe it’s like: you want performance, so you have performers? Anyway, we call the people and institutions we fund ‘Creators.’ The idea being, the work we do at ARIA, I think you need equal doses of creativity and creation. This word ‘create’ is interesting because you can think about it in terms of creativity — which is like pie in the sky thinking — or you can think about it as like, “No! Go create something, like building!” And our view is you need both of those to come together.

Anyway, we talked about new institutions around Creators. We’ve also been thinking about new institutions to help ARIA do better. You might have seen our Activation Partners call.

Eric: Yes. Can you explain what that is?

Ilan: I can. [Laughter] This might be a divergence, but...

Eric: We can come back to it later if you prefer.

Ilan: No, let’s do it! When we think about the ARIA model as a whole, we talked about finding the opportunity spaces, being able to inject energy, catalyze these big waves — which are essentially new movements of technology...but then talent and capital that can transform the world in one of these spaces.

There is a question. We’re not DARPA. One of the things that allows DARPA to get things from early idea/technology into practical systems in the field is that they have this massive lever that is the Department of Defense budget. [Laughter]

Eric: Yeah, they have a built-in customer.

Ilan: Yeah, they have a built-in customer. And there is no bigger driving force than the procurement power of the Department of Defense, if wielded in the correct way. ARIA’s mandate is much broader. We’re not just defense, we’re actually not doing any defense right now — it’s quality of life and economic growth, broadly speaking. We don’t expect to have a built-in customer from government. There might actually be cases where government, like the NHS [National Health Service] could be an amazing partner and uptake vehicle for technologies we develop. But outside of having purchasing power as the driving force, our bet is that the biggest driving force that exists to get new ideas into the world at scale is going to be entrepreneurship.

It’s that whole idea of, “If you, as the researcher and a team of people are willing to commit their life for a stretch of time, yes, you could change the world.” We know it. We’ve seen that happen.

So, one of the questions we’re trying to grapple with is, we’ve created these opportunity spaces specifically to be places where the wave doesn’t yet exist. So, there probably aren’t a lot of startups in these spaces because venture capitalists aren’t super active in all these spaces. Maybe there are some. What can we do to increase the amount of reactants that are entrepreneurial in the opportunity spaces we have?

And we thought about a few things. When I was at ARPA-E, actually, we ran an experiment that I helped launch, which is called the technology to market program. We basically built, within a government funding agency, a business analysis/biz dev type function. The idea being, “Let’s figure out how to inject into our programs some thinking around how you translate the technologies.” DARPA does some of this.

Our view is actually, for ARIA, there are some things we can do internally...but to think about how technology’s transition to market, especially through startups and entrepreneurship, the best people in the world doing that are going to be people doing it in the field. And you might be able to attract one or two of them, here and there, into a government funding agency, but you’re not going to be the best in the world at doing that. So what we did was we put out a call, and we said, “Listen, we think there is going to be massive opportunities and value created in these spaces. It’s still early. If you are an organization that deals with venture talent creation, entrepreneurship, rapid prototyping...anything related to tech translation, transitions, and value creation...and you’re amazing at what you do, could you imagine focusing your energy on some of our spaces? And just do what you do really well, but inject more reactants into that system.”

My colleague Pippy [James], who’s our Chief Product Officer, was really the visionary behind driving this forward. Where we ended up was, we have a handful of organizations. Some of them are venture capital firms that are saying, “We will, for the first time, focus on the UK and look at opportunity creation in these spaces.” They’re doing things like running fellowship programs for scientists who want to be entrepreneurs.

Renaissance Philanthropy is another Activation Partner thinking about, “How do we create a two-sided marketplace between the technologies that start to emerge and philanthropic goals/philanthropic funding?”

Eric: A lot of people don’t think about it, philanthropic demand is demand all the same. They [philanthropists] often have particular technologies they want to bring into existence. But it’s often unclear how to solicit demand from philanthropic...the mass of philanthropies. It’s hard to understand what they want.

Ilan: Yeah, and in a lot of these spaces it’s not clear that when we’re done with our program, the commercial value is going to be right there. It may be that we’re still in a tragedy of the commons, market failure mode, and we need to band together with others to do more in those spaces. So I think that’s going to be important.

But one of the things that came to mind as we were talking earlier is one of the Activation Partners we have, I think you’ve spent time with them, is this company Amodo [Design].

Eric: Amodo, yeah! Love Tom [Milton]!

Ilan: Amodo is such an interesting story. They’re based in Sheffield. It’s a small team. It just reminds me of the things you write about! It’s a small team that, you know, they’ve been involved in a spin out of a university and they basically recognize that, like, “Man, universities don’t do a very good job of prototyping things, having a rapid iteration mindset, or understanding how to get things into a more commercial place. Why don’t we just set up a shop to do that as a service — for startups, academics, and otherwise?”

Eric: So you don’t have to shoehorn your experiments into off-the-shelf Thermo-Fisher equipment. Tom and them can make what you need.

Ilan: Exactly! “Let’s go solve it!” They’re like mechanical, electrical, prototyping fixers!

Eric: And they’re hiring!

Ilan: And they’re hiring! [Laughter] So, interestingly, they applied to be an Activation Partner, alongside...you know, our other Activation Partners are, like, Google DeepMind...but they applied. And first you look at it, and you’re like, “Oh you’re five people in a room in Sheffield?” And then when we talked to them and we saw what they were doing and the vision, it was like, “Actually, this is a massive asset for ARIA to be successful.”

And maybe it won’t just be Amodo over time, maybe we’ll find others. But already, through the arrangement that we’ve built, they’re actually doing this as a service for a bunch of Creators that we’re funding, who are saying like, “Oh my goodness, I thought it was going to take us six months to do this and I got a much better version of it in a week!” So I think that’s super cool.

Eric: And the PDs have seemed very impressed with them. Like when I was talking to some of the PDs [and other ARIA staff] about the BBN thing, the concept that I used was, “Oh, do you want an Amodo for your area?”

Ilan: And that’s one of the things we’re doing through Activation Partners, which, again, is sort of an experiment around this idea of, “The best people, in the right environment, with [the right] incentives.” We’re working with Convergent Research on what I think will be the first experiment of them saying, “Wide open to the spaces,” which will be our opportunity spaces. Instead of being a kind of two-sided marketplace and connector of talent with philanthropic or other funders for FROs (Focused Research Organizations), they’re basically saying, “If you’re someone talented who wants to commit your life to building a focused research organization in one of ARIA’s]opportunity spaces, apply! Then we’re going to find one, maybe even more, to go launch.” And it’s exactly what you said...

Eric: To people in the metascience space, I think Convergent is maybe one of the most exciting...

Ilan: Yeah.

Eric: ...kinds of Activation Partnerships. Because I think everybody [metascience nerds] was around when they first kicked up. And they also always knew [suspected] the vision was probably that Convergent might like to win NIH funds, or something like that, and set up more every single year. So to have an official [Activation] partnership was exciting, for somebody who’s just been a fan for a while.

Ilan: I think the biggest — we might agree on this — but I think probably the most important thing to accelerate progress in the research ecosystem is to increase the diversity of institutional types. Convergent is one of the few examples we have of a mode that is taking root, that’s saying, “Here’s a new institutional type. Let’s figure out how to scale it!” You talk to Adam [Marblestone] and he talks about...you know, he sees a thousand — I think he says either a hundred or a thousand — FRO-shaped things that need to be created in the world. I think it’s a thousand. I imagine there are a thousand. If he thinks it’s a hundred, I can probably debate it. [Laughter]

Eric: It was one of those two numbers. One more question, and then I’m going to do a little pivot. You seem to have a very good grasp of early/mid-20th Century R&D, the institutions, some of the stories, etc. Is there any organization or group from that period you find yourself thinking a lot about? Either because you want somebody to emulate it or you just think it’s cool?

Ilan: That’s a good question. I think the ones I think about are maybe, not surprisingly, the ones that feel like startups before their time. You wrote the piece about Edison.

Eric: Yeah.

Ilan: That was a story I was already obsessed with...but the whole idea of, like, Edison in the workshop. There’s an organ in the back, there are bunk beds, they’re sleeping there. They’re just all in, committed. You know, he’s raising money based on a dream. You think it’s bullshit, but then he makes it true by doing the work to close the loop.

Eric: The financiers come to visit and he looks crazy...

Ilan: That’s one piece. I love the story of Philo Farnsworth. I don’t know how much you know about that one?

Eric: I don’t know that one.

Ilan: 15-year-old farm boy who has a vision of making television. And basically through some serendipitous set of events, because he’s so passionate about it, ends up moving to San Francisco, getting funded by like an LA financier from Hollywood, and is competing with RCA in a race for the first television. And you just look at that, and look at the lab, and look at the talent times intrinsic motivation in the right place and the right time...

And I think Curie — this is more academic — but I think Marie Curie is another example of this. It doesn’t seem like it, but when you look at how she and Pierre Curie worked, it definitely feels like a startup.

Eric: What about it is very startup-y to you?

Ilan: Oh, the combination of the singular focus and the idea of, “We’re going to be open-minded and try to get to the goal through all means.” I always love the story of — I might have this wrong — but my impression is that Pierre Curie discovered piezoelectricity as part of trying to figure out how to very sensitively measure the radioactivity in the materials that he and Marie were looking at. So, basically, you have an academic pursuit to discover and understand this phenomenon of radium that no one understood, that leads to stumbling into discovering a whole other phenomenon, piezoelectricity — which has massive implications technologically. And it’s all because you had this intensity of spirit in one place.

[MIT’s] Rad Lab is probably another example of this. I don’t know if you’ve written a piece on Rad Lab.

Eric: I’ve never written a piece on the Rad Lab. There’s one book that’s continually over $100. And I check Amazon like once a month to see if the price will come down and I can finally get it. [Laughter]

Ilan: I’m going to buy you that book, whatever it is.

Eric: You don’t have to do that!

Ilan: If it means you’re going to write a piece about Rad Lab, then I think we all...we’ll do like a GoFundMe campaign to buy you the book!

Eric: [Laughter] I can promise to find a way to have it out in the next year, somehow! I have a few other Rad Lab oral histories sitting on my shelf that I’ve been letting pile up, so I do have to do this.

Ilan: Yeah, but the whole idea that because we got a group of physicists together to try and build radar systems, what fell out of that was, like, MRI...and the basic theoretical and practical things around that is just awesome!

Eric: Yeah, and also in terms of funding something for five years [as FROs tend to be], and then it's set off in a direction of its own...people at Rad Lab seem to have thought of some of Weiner’s early cybernetics writing, and things of that sort, as helping set the agenda for the RLE [Research Laboratory of Electronics, which the Rad Lab morphed into postwar] going into peacetime. It’s very clear that [the Rad Lab] was catalytic in extreme ways. The kind of thing that would be ARIA ‘returning the fund’ level [results].

Ilan: Yeah, it’s funny, one of the things that’s coming to mind here, as we think about FROs...one of the things I think a lot about is, for so many of these institutions, and I feel this way about ARIA right now. We’re two years in from starting everything from scratch. It feels like we have the environment where these amazing things can come out of it. When I think of our program directors, when I think about the Creators they’re starting to fund, the dynamic of the team, I’m like, “Wow. This has the energy and the characteristics you would want.”

The big fear is, I think, “Okay, this is founder mode.” [Laughter] These are early days! If you look at Rad Lab, it was this intensive thing, and MRI and these other things came out of it in the early days. And more came out of it later, but that question of, “How do you capture that founding period and not lose it?” I mean, what I love about FROs is the idea is, “Don’t even try.” Imagine that you’re going to have an intensive thing for five years. And then it turns into something else, like it metamorphizes. I think there’s something really important about that.

Eric: I remember hearing Adam muse at one point about the idea of, “Oh, it would be great if we had funders who could accept or were excited about the idea of maybe one FRO maybe leading into another FRO.” That is the outcome. You [ARIA] are playing a bit more of a repeated game. How do you think about that, one ARIA program leading to another ARIA program?

Ilan: Oh, 100%. I think most likely that is how we will make an impact, which is we’ll have a program that inspires the next program. And within that next program, we see something and we double down on it...and that’s the thing that happens, being adaptive in that way.

One of the interesting things that I’m noticing is...we haven’t talked much about how we recruit program directors. But the combination of our broad mandate and the fact that we are bringing in, as cohorts, program directors from such different backgrounds...we have these opportunity spaces that the program directors have shaped, and, yet, we’re now starting to see as we dig into them, these really interesting intersections between them. And I’m just wondering what’s going to happen. What are we going to do about that? Are we going to have programs that sit across two opportunity spaces? Are they going to merge into one? You know?

Eric: And can we talk about your new program directors? Who are they? Why did you choose to light up flares around these particular people and their expertise, or their point of view?

Ilan: Yeah. I think this recording is going to come out right after we have announced them. It’s probably worth first saying, we made a bet early on at ARIA. And my colleague Pippy had a really big role in this, which is we basically decided that one of the hardest parts for a research organization like this in the UK was going to be to find program directors or program managers, because, you know, it’s a weird thing to do. You’re on some amazing career trajectory and you decide to, like, step out of that for three to five years to do this other weird thing with a brand new agency that no one has ever heard of. Probably the listeners of this realize that one of the core parts of the DARPA model, which we’ve adopted at ARIA, is this idea of term limits. The people who are developing the theses are people that are coming in from the front lines of doing research in some way. They’ve got to sprint for three to five years to develop a thesis, fund a program, have an impulse function that hopefully catalyzes change, and then they go out and we refresh with some new program director. And part of that is to keep the ideas fresh, but actually, a big piece of it is to keep it incentive-aligned.

I’m never worried that a program director is going to make a decision on their program based on worrying about their career trajectory and what their boss at ARIA thinks, because they’re going to expire in three years. So they’re all just purely focused on, “How do I use this time to make something happen?”

One of the bets we made was, we knew it was going to be a challenge to find people. So we decided, rather than just hire people one-off, as we found them, let’s actually do what we believe is the most open call of its kind to find program directors. Let’s imagine that we can think of a set of characteristics that matter and that we think are going to make for a good program director. And that’s going to be more important than specifically their resume or what they’ve done before. And then we decided that we’ll bring them in as a cohort. So, part of the idea here was, if it’s going to be a risky thing for somebody to come join ARIA at the early stages, it becomes a lot less risky if, when they’re thinking about joining, they can look around and see five or six other people that they think are pretty awesome, who are also going to jump into that pursuit.

And I think that worked out really well. If you look at the first set of program directors, we’ve got someone like davidad who, I think he got his masters degree from MIT at age 15. I don’t think he ever finished his PhD. He ended up working at places like Twitter doing independent research. And he sits in our office next to Jenny Read, who is like a seasoned senior professor at the University of Newcastle — in different fields.

And you have all these other people, and they’re so spiritually aligned, and respect each other, and push each other. It’s really cool. [pause] We were talking about new program directors, but I didn’t get to it.

Eric: No, no, it’s okay!

Ilan: What would you want to see from ARIA’s next program directors?

Eric: [Laughter] What would I want to see?

Ilan: Trying to figure out how to...oh you’ve met some of our, you’ve met our existing program directors! If I were to say, like, “Okay, you have the chance to double the size of the group of program directors and make it an even stronger group. What would you try and sprinkle into the mix?”

Eric: So, that’s tough for me [laughter]...because I’m not a technical genius or a polymath in any way. I’ve been very intrigued by the energy of everybody involved [as an ARIA program director] and I’ve always left excited. But I guess, I don’t know. Engaging in this work as a non-technical person...

Ilan: Yeah.

Eric: ...I more just go in with the assumption of, “Somebody sees genius or a spark of something in this person. I’d love to help them any way I could!” I guess, reading the history... it’s unclear that it would be obvious to anybody, or me going into the past that, like, Frank Heart would be Frank Heart, or J.C.R. Licklider would be Licklider. So, I guess I don’t know...I attempt not to answer these questions or go down this line of thinking because I think I would be biased by random things, probably. For example, I go talk to [ARIA-related] people, and most of them are British. And it’s like, this is a new cultural context for me. Sometimes, with people in my personal work, I go based on spark or energy or something like that. But I don’t think that’s quite how a British scientist would do it. So I don’t really know. I won’t answer your question, essentially!

[Post-interview note: As I transcribe this interview, I wish I would have flagged that some social science program like a computational law program could be cool!]

Ilan: Yeah, interestingly, it goes to the intellectual humility point. You said something that resonated with me, which is like, “I imagine someone saw a spark of genius or brilliance in them.” So we designed our process to recruit program directors — I think we started, the first time we did it, we had seven qualities we were looking for. And they have names, like, obviously like ‘technical depth,’ but we have one called ‘vision to action,’ ‘adaptability,’ etc. We basically put all the applicants through the paces in different formats. We were probing them in different ways to test along those axes. And the idea is not to just have some aggregate score for someone who’s great, but the idea is to find the spikes. We talk a lot about how each of our program directors has a different set of spikes, meaning like superpowers that they’re going to leverage to do the job in their own ray, recognizing that a Licklider has very different strengths than a Bob Taylor, right?

And I think that’s worked out really well. We did the same thing with this new cohort of program directors. But we looked at our first set of program directors and what we learned from them, and we realized a few things. One was, there was something that they were showing in their behavior that we hadn’t tested against, which is something like ‘value recognition’ or ‘opportunity recognition.’ The ability to see the dots and find the constellation within them. So we added that to the mix. We also deliberately tried to recruit...our first set of program directors, roughly 2/3rds to 3/4s of them have more academic backgrounds. They tend to be sort of — I don’t want to offend anyone — misfits? They tend to have different mindsets than your typical academic, that’s why they’re attracted to this role. One thing we tried to do deliberately with the new program directors is say, “Let’s try and bias towards more people with industry or startup experience,” which is the case. So, what can I tell you about them?

Eric: Can you give us a couple examples of program directors who clearly have overlap with an opportunity space from the first cohort? And any examples of people who are, kind of, breaking new ground?

Ilan: Yeah, so a lot of them are breaking new ground. Actually, we’re already starting to see a bunch of different connectivity between them.

I’ll share one. One of our incoming program directors, Rico [Chandra], is Swiss. He studied at CERN, he’s a nuclear physicist. He then decided to go do a startup in the nuclear security space. He’s coming into ARIA, and the thing he’s become obsessed with is this question of...the fact that with all of our modern technology, flight and the ability to transport things in the air is still a big challenge, especially sustainably. And his view is that, “Actually, we know that there are plenty of birds, albatrosses and others, that can go vast distances, thousands of kilometers, without any source of power, in perpetual flight. Why is it that we can’t beat them with modern technology?”

So, you know, with our incoming program directors, we basically say, “Listen, just have a starting point, and then we’ll go from there.” We don’t know if it’ll turn into a program, if it might pivot or not.

Eric: It’s also interesting because more recent people in aeronautical engineering who we think of as geniuses, like Kelly Johnson, [often] thought in wind tunnels. But when you go back to the Wright brothers, they were obsessed with birds. Like there were all these stories of them on the beach where they were apparently — I forget if it was Wilbur or Orville or both — they were impeccable at imitating the motion of the birds’ wings.

Ilan: Oh I love that.

Eric: [gesturing to imitate the Wright brothers imitating the birds] As they were trying to figure it out. So it’s fun that...to find a really ambitious program, he’s also kind of gone back to the source.

Ilan: So one of the interesting things about Rico is he also happens to be, like, a world-record holding long distance hang glider. So he’s been thinking about this a lot. We don’t know whether it’s a program, but one of the things we realized...we have an opportunity space called Scoping Our Planet. And the thesis there is, “With climate change, the thing we really care about is the climate changing. We obviously care about and know that fossil fuels and greenhouse gas emissions are causing the climate to change. But there’s very little we know and very little energy has been put in by the innovation community to understand how we monitor the climate.”

And you can think about why that’s important. Everything from measurement and verification of things like carbon removal, which is sort of a big and unsolved market failure problem. But you can also think about weather prediction. You can think about understanding climate tipping points, which is what our program is focused on. Rico came in and we realized, “Oh, is this like a new aeronautics opportunity space?” And then we realized, “Well, maybe this is just the capability that can be very valuable in scoping our planet.” So now he’s talking to Sarah [Bohndiek] and Gemma [Bale] [the Scoping Our Planet program directors] and trying to understand, “Is this something that can be game-changing around how we have new sensors for parameterizing the earth and communication protocols?” So that’s kind of an interesting, surprising one [new program idea] that connects to something we’ve done.

Eric: So, it seems like you really do hire people first, and find the specific programs later. A lot of your first cohort of program directors are working on programs that, like, it’s maybe not what their academic lab focuses on. Are there any people you’ve hired in this new cohort where you think, “Oh, what they might end up working on is exceptionally broad.” You’ve hired them with a guess, but it’s hard to tell where precisely it will go.

Ilan: I think that’s true of a number of them. I was just chatting with one of our incoming program directors, Alex [Obadia]. Alex is really interesting. He’s a mathematician by training, who then got involved in cryptography. He’s been doing essentially crypto and blockchain stuff, but he’s really passionate about thinking about how the kernels of innovation in real cryptography, that’s being applied to financial systems and otherwise, are going to be consequential to the future of society.

He turned me on to — folks should look this up if they haven’t — this paper on programmable cryptography. The idea there is, right now you think of cryptography as, “Okay, I have a certain piece of data in a discreet way. It’s encrypted or it’s not. I can see it or not.” There’s a whole community of people, now, thinking about, “Could I have a whole program that’s encrypted? Could I have a computer program that goes and does programming on your data without actually seeing your data, because of the encryption?” Or even a computer program that is doing computation and getting answers based on data where no one actually knows what the program is. And you think, “Like, what are we talking about here?” But clearly, as we think about AI, and AI agents playing a bigger role in our lives, there is a question of, “How do we optimize the efficiency of what we can learn and the value we can create with AI, where one of the big barriers is privacy of data?”

So, you can imagine — and I’m not an expert here — but the sense I get is, you can imagine programmable cryptography allowing me to, say, have a set of preferences, my values, things that are very sensitive to me, where I can tell an AI agent that is going and engaging in some democratic process on my behalf. Or I can have an election process that runs a program where it queries, “What are my really sensitive personal preferences?” and has it feed into an answer of a program without ever seeing my data.

So I got very excited about this! And I said, “Alex, this is massive, this is definitely an opportunity space!” And his view was, “Yeah, but I think enough people are already working on this, it might happen anyway.” And we got in this big argument. So now he’s thinking about, “Actually, what’s the next stage beyond that?” We have this massive convergence that’s coming, where we’re going to be fusing humans with technology in new ways. You can think of neurotech. You can think of, you know, just the way we’re much closer to devices. What does preserving privacy and trust look like when your devices are not purely digital, purely physical, or purely biological, but somehow sit at the intersection? I don’t know whether there’s a ‘there’ there, but that’s what he’s starting to explore.

Eric: You seem to have a number of life sciences-adjacent folks in the new cohort.

Ilan: We do.

Eric: What’s the thinking behind that?

Ilan: It’s a good question. Again, it’s another indicator that we really were people-first. When we got the first cohort, we realized there were really only two program directors working on things related to life sciences and biology — Angie, on Programmable Plants, and then Jacques [Carolan], who has the Precision Neurotech program within the Scalable Neurotechnology space. But if you look at the UK, it has incredible strengths in biology. If you look at technology vectors that are progressing extremely quickly — synthetic biology, right? You have all these pieces. So, shouldn’t we have more?

We do have more program directors thinking about biology in the new cohort. Brian [Wang] is an organic chemist, but then moved into thinking about pandemic preparedness. And he still cares about that very deeply, and one of the questions he’s asking is, “Can we utilize new learnings about the innate immune system?” The innate immune system is the part of your body that reacts to pathogens and toxic in broad spectrum ways, right? So it’s not creating antibodies to specifically attack a specific vector, it’s just that initial response. It turns out, actually, the way plants deal with pathogens is entirely innate immune system. And his view is, “Well, maybe we can be inspired by that to figure out how to create therapeutics that can be effective against new pathogens, new bugs, that we haven’t seen before.” And there could be a number of implications to that work where, through that same inspiration, basically the question is, “How do you get ahead of things that are evolving?” You know, you think about the Covid experience. But cancer is the same way, right? How do you get out ahead of something that is a foreign...

Eric: So, when you’re selecting program directors, you’re in a room and you have some exceptional electrical engineer who wants to work on some project nobody has ever done before. You might have a biophysicist interested in some medical area. You might have somebody from a field that doesn’t even have a name. How do you go about...? You have to come out of there with eight people. What does that prioritization even look like? Is it painful, because there truly is no apples-to-apples comparison? How does it feel? What do you do?

Ilan: No, this is actually where the approach...Historically, I think I always felt like I had a pretty good instinct on talent. You know, you hear about this in research and otherwise. I mean, you’ve written about this, which is just, like, there’s a taste and there’s ability to spot talent. And that’s something I always try to be attuned to, and refine.

I think over time I’ve come to realize that one of the best ways to find talent is actually to just create a product that really talented people want, that doesn’t exist. If you think about the ‘product’ we have at ARIA, you have, in this very open way, an ability to take £50 million and figure out how to create a wave that changes the world. That’s really compelling if people believe you. So that’s one thing that I think has changed where you say, “Okay, that’s a great way to attract talent.”

The other thing is, and the big lesson for me around our program director recruitment, by trying to strip away to first principles around, like, “What do we really care [about] in terms of the characteristics of these people?”...and this is very much like a Kahneman-based approach of recruiting and selecting people, which is just like, “We’re going to have the criteria. We’re going to probe the system a bunch of ways. We’re going to see how they spike against the criteria.” And ideally where that ends up, to your point...when we went through that process based on paper applications, phone call screens, technical interviews, we ended up with this set of people — this year I think it was 16 — where we said, “Based on everything we’ve seen, any one of these 16 people could be a program director.” Because who are we to know? Like again, the intellectual humility. I could guess, but I’d probably be wrong.

So then we said, “Forget it. Rather than just trying to pick the right ones out of the 16, let’s actually bring the 16 people together.” One thing that’ll happen is...these are awesome people who will go drive impact in the world, and they’ll probably all do more if they’re connected to each other. But it’ll [also] give us one more way to look at how they show up, not just as individuals, but also how they sort of connect to each other.

Basically, at the end of the process, we’re just thinking about the portfolio. We’re thinking about the portfolio of people, portfolio of ideas, based on what we think they might do, what they might bring to the cohort. Just curating based on that.

Eric: If I can probe you with a bit of an edge case from history, I’d love to get your...

Ilan: Oh boy, I might not...

Eric: So, speaking of intellectual humility, I’m a big Warren Weaver fan.

Ilan: Yes!

Eric: And something that comes out all throughout his writing...he is an exceptionally...he’s a Midwesterner with a lot of humility. It comes out in all sorts of his [writing]. So when he first came to the Rockefeller Foundation, even though he had humility, he had one of the more extreme bets in philanthropic history. The [Rockefeller] Natural Sciences Division, which gave out on the order of what ARIA gives out per year, maybe a little less. It’s hard to do a one-to-one, because science was cheaper back then. But, essentially, they [Weaver’s predecessors] said, “Oh we fund electrical engineering, zoology, etc. And we fund the very best people who come in.” And when he came in, he said, “That’s fantastic. We’re not going to do that anymore.”

When he’d gone around and talked to people, he said, “There’s something right there in that area between biology and physics. So, yes, our budget is really big, but it’s very finite. We’re going to press on that.” And he essentially put 80% of his budget towards — it was 1932 — five years later, he would name it ‘molecular biology.’

Ilan: Out of curiosity, do you know how long he was in the foundation before he made that bet? You probably do.

Eric: I think he came in with the bet.

Ilan: Oh okay!

Eric: He took the interview with them to say, “I don’t think I’m your guy. I’m just an applied mathematician. But there’s this thing..."

Ilan: “Here’s the thing we would do!”

Eric: Yeah. He read very broadly, for sure. And he kept at it [funding molecular biology] for 20 years before moving on to something else. But if you all felt you had an ARPAnet or a molecular biology on your hands, how much is too much of your funds focused on that one area? There’s maybe a limit. 80% is a lot, for example.

Ilan: Yeah. This is interesting. This is something we talk about a lot. First of all, the question of, “We have these seven opportunity spaces. Why are we recruiting more program directors? You know, aren’t we doing enough? Like the goal isn’t just to boil the ocean.” And actually, we tend to think really deliberately about, “We need to get to this one outcome that is so massive. Do we think we’re touching enough surface area right now to fast forward ten years, and realize we got lucky and we just noticed that thing that was going to be so valuable?”

And when we looked at our budget, we looked at the size of the UK ecosystem, and we looked at what we were doing, we said, “Actually, no. We’re probably not touching enough surface area.” So we now have more program directors coming in. There will be some new opportunity spaces. We’ve also said, “There’s a limit.”

It’s likely that every other year ARIA will recruit a set of program directors. It’s a three to five year term. So that gets you into a steady state of 15–20 program directors. And that’ll be it. So we’ll have a first set of opportunity spaces. That’ll be the surface area that we touch. And really what success needs to look like is...out of that, we’ve found something that we not just want to double down on, but 10X on. And so if a big portion of ARIA’s budget does not end up in one of those areas over the others, there’s a problem.

Eric: Oh wow.

Ilan: That’s my take! You know, I’m on a term limit, too! I probably won’t be the CEO when they have to figure this out. But is that 80%? I could imagine it. We talk a lot about…

Eric: And could the person in charge of ARIA...

Ilan: Decide?

Eric: ...if they were a brave person, if they thought it was right, is that that? Are there some structural or institutional barriers that would make bravery even tougher, beyond the pure pressure of people looking at you like you’re a little crazy or something?

Ilan: One of the nice things about ARIA, it’s worth mentioning, the UK — like a number of people who were in UK government, civil servants, others, Parliament — they got this right. In the sense of, ARIA really does have the right mandate, freedom, flexibilities. There’s not political intervention, there’s not a lot of BS processes...they’re the right processes to make sure we’re responsible stewards of taxpayer funds. But one of those things is the CEO of ARIA makes programmatic decisions; that’s very much modeled after DARPA. I think that’s 100% true. And that’s good to have in place from a governance perspective. The question is, “Will the organization have a culture that leans towards the bold bet?

We’ve been talking about this a lot. So far in ARIA’s history, the things we’re most proud of are when we’ve gotten exposed to something and then we just said, “Ok, let’s do the bolder thing here.” And it happens in big and small ways. Sometimes it’s about a program director we decided to bring in. Sometimes it’s about a program that we launched. Sometimes it’s like, “Do we use Slack?” Because there are potentially any number of issues from having your Creator community on a Slack system. We just had this conversation and said, “We should bias towards doing the bold thing.” [Laughter]

And my hope is that we build into the agency that a leader in the future will be celebrated by pushing that bold bet.

Eric: I had a question written down, and I think maybe you just answered it. I was going to ask, “How do you deal with a program that you’re exceptionally excited about, but maybe the follow-on funder doesn’t get it? Like the VCs aren’t sure what to think about it five years in advance. Which is relevant, because with early autonomous vehicles, it’s not that the Army desperately wanted...they didn’t really know what to do with it. But it sounds like your answer is, maybe, “If it’s a bold enough bet, we can be the follow-on funder. For a while at least.”

Ilan: Yeah, that’s definitely our mindset. And we’ve even tried to build that in. Some ARPA agencies require cost share in their projects: “Oh, you have to show us that someone else has skin in the game by funding 20%.” We basically said, “We’re not doing that, because that actually could as easily could be a counter-indicator for us.” In the future, we think we’ll probably leverage other funders as follow-on partners, and everything else. But let’s make sure there’s nothing that prevents us from doing the bold thing.

That said, it can’t be as easy as, you know, in your scenario, “What’s going to get us to one day have 80% of our funding in one of these spaces?” It can’t just be someone walked in, looked around, and said, “Okay, yeah, let’s just do that.” We should be evidence-based. [Laughter]

We have a pretty good set of principles. A lot of this is, “What are the principles? And then what are the processes that allow us to make sure we’re holding true to those principles?” We have that for creating opportunity spaces. We have that for approving budget for programs. The next thing is to have that for portfolio allocations. Meaning, “We’ve run these opportunity spaces. Where do we think we are seeing the bigger bets emerging versus not?” So that we can say, “This opportunity space is going to get bigger or more focused, and this other one might go into hibernation because we don’t think the elements are there to create the wave.”

Eric: Yeah, no, that’s very interesting. I didn’t know a lot of that, so that was great to hear! So a bit of a question very relevant to...

Ilan: How many questions do you have?! [Laughter] It’s like an endless amount. Are you just making them up and the papers [Eric’s notes] are just like a...

Eric: Well I’ve skipped some [gestures at discarded paper pile], I’ve come up with some new ones [waves papers]. They’re not all off the page! They [Asimov Press] brought me in for a reason.

Ilan: {Laughter] He’s just got like blank pieces of paper just to make it look official.

Eric: I could show blanks! [shows the blank side of his stack of papers]

Do you spend a significant amount of your time thinking about setting up a portfolio to take advantage of AI? Obviously a lot of big breakthroughs in science history come from using the big thing from last year or 5 years ago to apply to some new area?

Ilan: Yeah, it’s a really hard one. I mean, the simple answer is, “Yes.” We are spending a lot of time thinking about how AI — the fact that we’re starting an agency like ARIA at this moment in time, given what’s happening in AI development. One of the easy inspirations for new programs at places like DARPA or ARPA-E is, “What are the technology vectors that are making incredible progress? What are the learning curves you can ride?”

So, I remember at ARPA-E, we had a number of projects we funded based on the fact that fiber optic lasers were getting much cheaper and more powerful year after year. So we had a project we funded on basically using that for geothermal — like drilling hard rock — and other things. AI is like that, just massively.

I think we’re trying to be a little bit deliberate before we figure out exactly what that means for ARIA. For instance, we haven’t jumped in and built, for ARIA, a major compute cluster. We’re starting to think about, “What does an AI program director look like?” You know, how to actually do a lot of the soundboarding that we do. Our program directors are actually using AI. It turns out AI is actually, like, an incredible tool as a program director. Because often you’re looking at things outside of your area of expertise. Oftentimes you’re like, “Oh, if only I had an expert that I could bounce this off of!” Having a thousand experts in all the areas at your fingertips makes a big difference.

I think the much more powerful part is, when we think about these opportunity spaces, one of the questions becomes, “Relative to the impact we think AI could have on this space, how much activity is there to start to deploy that?” And I think that’s going to be one of the important...especially for this new cohort, we’ll end up with some programs that really have AI at the center.

But I think for all of them, there will be this question of, “In this space, where are we in terms of the max benefit that AI is going to build by integrating with this discipline or set of fields, versus now?” And I think that will help dictate how much of an AI flavor we have in the space, and what we’re doing to be differentiated. I actually don’t know if I believe that answer that I just gave, but it sounded good.

Eric: Before we move on, is there any other technology you spend a lot of time thinking about? The world of science and engineering is broad. There might be something else that you think people don’t pay enough attention to.

Ilan: I mean, there are little examples. Like expansion microscopy, that’s such a cool thing! Most people don’t know! It’s popping up in different places.

Eric: For people who don’t know, the TLDR on expansion microscopy is, “What if you made the sample bigger!” And...

Ilan: By literally just putting it in a gel and expanding it. And it works! It’s unbelievable.

I don’t know. I think synbio comes up a lot. I think data, beyond just AI, data comes up a lot as an area where, when you look at some of these disciplines...this is something we’ve found in some of our climate work. You look at the best repositories and the most valuable repositories of data around climate and weather, and realize that none of them are engineered to be accessed in a way that’s compatible with modern data techniques. So there are just infrastructure gaps where you think, “Okay, there’s something cross-cutting around data that we can do.” Or a barrier that we need to get over.

Eric: All right. So I have a suite of metascience questions for you.

Ilan: Okay.

Eric: So, you can go rapid-fire responses, or spend time on them!

Ilan: [Laughter] Okay!

Eric: Do you consider now a great time to work on metascience?

Ilan: Yes. It’s probably the best time to work on metascience that has existed in my life.

Eric: You’ve done this for a few decades, depending on how you want to look at it. Were some periods a lot more frustrating than others?

Ilan: When I left ARPA-E, I wanted to go start...actually, I may have sent you the paper, I had a paper...

Eric: ‘ARPA Lab.’

Ilan: Yes, ARPA Lab. I wanted to create an ARPA Lab. And the point was, like, “ARPA-E is great as a funding agency. The problem is I don’t have resonant institutions to fund. So let’s imagine a lab that is ARPA-minded, that is very entrepreneurial.” And I sort of mapped it out. It was probably like a lab that would have been a compilation of FROs.

And I thought maybe we’d get philanthropy to fund it. And, you know, who was I? So maybe someone else could have done it. But like, crickets, you know, nobody! You know, philanthropy funding science, it sounds like it was a long time ago; it wasn’t that long ago. But the state of affairs, the default for philanthropy and science historically, probably for all time — you can tell me if I’m wrong — has been like, “Oh, I have a family member who got this disease, and I’m going to fund research on this disease.” Or, “I went to this university, so I’m going to give them money to do scientific research.” The idea that you’d have philanthropists making big bets like Convergent Research or Arc [Institute], in terms of new modalities for R&D, that is a new phenomenon and a really exciting one.

Eric: Speaking of something like Arc...

Ilan: This is meant to be rapid fire! [Laughter] You let me go on!

Eric: A lot of people conceptualize the new science orgs as experiments, in and of themselves, in how to do science differently. ARIA is also some version of this. Is it difficult to see what’s going on at a place like Arc, and, if there’s a useful learning, fold it into your operation? Am I not thinking about that right?

Ilan: I think you are thinking about it right. I think the biggest thing — as someone who grew out of venture capital, startups, and Silicon Valley — the thing I’ve realized is, the power of a vibrant ecosystem of startups is you create evolutionary pressure for institutional change. Meaning, nobody talked about OKRs until Google came around. And then everyone needed to do OKRs! And then Stripe came around, and I don’t know whether Stripe does OKRs, but they do things differently. And then all of a sudden it’s like, “Oh, that’s the way to do things.”

It drives you to say, “Oh there are competitors, or peer organizations, that are figuring out better ways to do things institutionally.” And that’s keeping the system super fresh. We don’t have that in research. The institutions are so stagnant for so long that you don’t have the evolutionary pressure to change.

For me, what metascience means is: go run those experiments and find ways to start diversifying and creating a more vibrant institutional ecosystem. Partially so you can get that institutional pressure! You need a critical mass of those things to get that institutional pressure.

So you asked, “What is ARIA learning from Arc?” I love Arc as an experiment, and I think it’s going to change the world. I initially was skeptical that Arc was going to be so close to Stanford as a university. And that they were going to hire people that were still in the academic incentive structure. I think, actually, it’s probably proving me wrong on that. And that’s a great learning. But it’s a very high level, like from a distance, learning.

The beauty would be if we had enough of these things where I could tell you that, “With a 90% certainty, that some one in ARIA’s team, in three years, will come from Arc.” Like if you look at startups in the Valley, right, like, “What are the chances that someone who was at Tesla will end up at another one of these companies?” Absolutely, right? That’s one of the things that drives that learning. It would be awesome if, within the R&D ecosystem, we had that kind of vibrancy and mobility, because I think then you really get the learning.

Eric: And if you personally had the funds, for whatever reason, to fund additional orgs to complement ARIA, like completely different metascience experiments, does anything come up in your head?

Ilan: [Laughter] Yeah, what came to mind, just thinking about your audience, was a conversation with Michael Nielsen when we started ARIA, who was basically giving me a hard time: “What you’re talking about doesn’t feel that differentiated. Where’s the gap? What about a research organization that gives 100-year grants?” The idea of, “We don’t have long term modes.” If you think of time constants as one of the axes of the portfolio, there’s not a lot of diversity on time constants, to like 100 years. Which I loved! I basically said, “Yeah, but if I look at ARIA’s mandate, actually, ARIA’s mandate is not to create new fields.” That’s important. It’s not like [to create] molecular biology. We are built to get something to a new technology platform or industry base. And I don’t think the hundred year timescale is going to work for that.

But I think long duration...basically modes of getting talent focused on either creative research or creation research for long periods, I think there are far too few modes for that, and fewer than there used to be.

Eric: So, that’s obviously ambitious. It’s also expensive. ARIA is pretty expensive, Arc is expensive. Do you think you need a minimum amount of funds to do a good metascience experiment? Do you have low-cost ideas?

Ilan: Well, I don’t know if the long-term thing is expensive. I mean, look, what is expensive? It’s all relative to the potential impact. You have to normalize it, right? So, one of the things I’d love to see someone do is...I think a lot about, “How do we train scientists?” Translational scientists in particular...there aren’t great training environments anymore for translational scientists. One thing I’d love to see someone do is basically say, especially with AI, the training is going to be less and less about the knowledge, and more and more about the taste, the tacit knowledge. and the instincts. So apprenticeship is really important. Why don’t we take kids that are high potential — and when I say kids, I don’t know whether I mean age 15 or 22, who knows? But take high potential people and basically say, “We are going to engineer for you a program where the next 15 years of your life you are constantly being taught how to do research, translational research, through a series of apprenticeships with incredible people.”

And maybe that’s in conjunction with a university, maybe it’s not. To pay for that, you can basically say, “We’ll give you fellowships,” or “You’ll work part of it.” That sounds very expensive, but my instinct is that if you did something like that, you could create the super researchers of the next generation that change the world. So probably not that expensive. [Laughter]

Eric: I’d love to poke on that...

Ilan: Maybe that’s too expensive.

Eric: ...but I’m going rapid-fire.

Ilan: Let me give you one more!

Eric: Yeah, for sure!

Ilan: Very cheap metascience experiment, probably the cheapest one I can think of. I noticed in my PhD, and actually when I hired for my startup, I found myself hiring people...a mode that I would hire was someone, who went into their PhD, they totally butt heads with their advisor, and they walked out. They ended up having to change advisors, or even complete disciplines, and then they thrived. And they come out with this like, “Oh, that was a horrible experience. But it made me change and I’m in a good place.”

Anyway, I keep thinking, I found an amazing PhD advisor that was really resonant. I didn’t waste my time. I felt like I hit the ground running. And I had this incredible experience. So a simple idea: a matchmaking app for PhDs and their advisors, when they come in. If you could increase and improve the compatibility of a PhD student and their advisor, on whatever axes, I think that ends up being a big deal. And it’s basically free.

Eric: Okay, great. That’s fantastic. Thinking of ARIA as a kind of experiment in and of itself, what’s a current bottleneck you all have that you’re very eager to find a way around or work on? There’s always small things in working on an organization.

Ilan: I’ll tell you what comes to mind. It’s kind of a hard one, but I think we’ll probably have to solve for it. We want to move fast in our programs. The view is, “You’re doing something speculative, so time to the next learning cycle is really important and valuable.” And we want to be funding people with diverse skillsets in diverse institutional types. Some institutions...the kinetics of the institution are very slow. And yet, we still want to fund people in those institutions. So one of the questions becomes, “If the kinetics of the institution, just in terms of how fast they can get stuff done, are generally very slow, but you have a Creator in that institution who wants to move fast, how can we help them move faster?”

And I actually think the only answer is we need, like, a fixer. We need an organization whose job it is to de-bottleneck activities within other institutions.

So my imagination is, Eric, you start the Research Speed Fixing Company, and we contract you, and you know, Jenny has found this great performer, but things are moving too slow in this institution. And Jenny gives them a phone number, that’s like a magic phone number. And they call it and you say, “Eric’s Fixing Services! We’ll send someone over right away!” And someone shows up in that institution, and they're running around the admin, just like putting pressure on things and getting people to move faster!

Eric: There are actually things like this in DARPA history.

Ilan: Are there? Amazing!

Eric: I can’t think of one from a performer, but I can think of one from central office. So, for example, when you read through all the oral histories, there’s this guy from early IPTO — which is computing office — Al Blue. And his name just keeps coming up as the guy who makes any bid you want to put out legal, workable, straightforward. I don’t know if he was an engineer or scientist or anything like that. He might have been one of the military guys who finds a way in and has to make his way in the office.

But that kind of stuff makes a big difference! Like in the same breath where they’ll be like, “Oh Licklider was a god,” they’ll also be like, “Al Blue made X thing happen. You need to talk to him.”

Ilan: Yeah! Well, we’re trying to build it into the culture! Right? Like the program directors know...it’s my [Ilan’s] job to have some pressure around, like, learning cycles, it’s their job to do the same. Hopefully we’ll create a Creator community...picking people that are intrinsically motivated, so they want to be pushing the kinetics of what they’re doing. And, yet, it would be really nice if you had more help on that.

Videographer: Time for a battery swap.

[Camera Break]

Eric: Alright, next in the rapid-fire questions…

Ilan: Can we, can we just pause for a bit. I love that we’re doing this long form thing, but people have to realize that this camera right here — there’s a camera with like a bag of ice on top of it because we’re going so long that it’s overheating. Which is great!

Eric: We’re making it work, though. I think the camera looks great, you know? It’s like when you go in the locker room at the end of the game and everybody’s got ice on their knees.

Ilan: Yeah, totally.

Eric: Both teams played hard.

Ilan: We’ll feel like we played hard today. [Laughter]

Eric: Is there anything you personally think people who write about metascience spend too little or too much time on? Like is there some hypothetical Substack where, as the CEO of ARIA, you would hoover up if somebody wanted to spend the time on it? I already have homework where I have to write a Rad Lab piece.

Ilan: That’s right! You do have to write a Rad Lab piece. Multiple! There’s like a series there. Oh, you also need to write a piece about how, actually, DARPA ended up emerging in part because of the UK’s radar effort. Which is important for me because it brings things full-circle to ARIA.

Metascience...honestly, what I would love is a blog that just chronicles metascience experiments and their learnings, and just keeps tabs on them. And that that grows and grows.

Eric: And what are variables that you think should be...some of would be qualitative, you meet them where they are...but would there be any underlying variables you’d want if somebody was writing about Convergent or Arc or ARIA, to constantly revisit?

Ilan: Incentives.

Eric: Incentives?

Ilan: Incentives. I think that is the only theme that matters. [Laughter]

Eric: Yeah, I think that makes sense. Do you have any call to action for any groups involved in metascience, or who would want to be involved in metascience, that you think would be useful to put out there? That can be researchers, engineers, ops people, policy people, whatever it is I am.

Ilan: I’m going to say something controversial, which has been on my mind a lot, which is...I think metascience is, at the same time, one of the most important movements, in terms of driving more progress out of research, and also in some ways one of its most dangerous movements.

The reason I say that is, when I was at ARPA-E, I was really interested in the question of, “How does ARPA-E understand its impact, map its impact, and measure it?” And I tried to dig into how we could do that. And both from my explorations of the community of people thinking about that and from the many activities we had to go through at ARPA-E to try and show and prove our impact, how things work...the amount that was “useful” was probably 10%, and the amount that was, “Actually, you’re trying to map something that doesn’t make any sense onto what we’re doing. You don’t really understand the context of how we work, and you’re trying to measure it. And you have a number of theories, but even when I tell you they don’t map on here, you don’t believe me,” actually led to a lot of inefficiency.

So I think what I would say is, if you’re in metascience, recognize that first of all, if you can do something experimental which pushes that evolutionary pressure on the system, great! If you can show there are better ways to do things by doing them and then having results, amazing! If you’re working more on the theoretical side or the evaluation side, just recognize you have a big responsibility, which is to make sure that when you add up all the hours of people who are engaged with that — from agencies doing the work, startups doing the work, or whatever else — that you have high conviction it’s going to be net benefit as opposed to net cost. Is that...?

Eric: No, that’s perfect!

Ilan: I feel like I’ve said that to people, and I think I’ve offended them in some ways, but I think it’s a really important thing to be thinking through.

Eric: No, that's perfect. We’ll end the official questions there. That’s Ilan Gur! Thank you so much for doing this and how long you were willing to spend with me today.

Some time in 2023, Tom Kalil told me he thought it would be a good idea to carve out a chunk of time and get to work on some ARPA project histories. The ARPA model was proliferating, and Tom felt these pieces might find a ready audience of ARPA emulators and fans eager to make use of the actionable information. Tom, who was then at Schmidt Sciences and is now President of Renaissance Philanthropy, has good taste. When he suggests something, I’ve learned you should listen. So I trusted him and threw myself into the work.

If any of you have enjoyed this series and wondered how the sausage is made, “How does one figure out how a 60-year-old R&D project — with no book written about it — was managed?” The answer is often: oral histories. The documentation that enabled many of these histories came to be because, at some point, committed historians sat down with a set of DARPA Directors, officer directors, staff, program managers, and funded researchers to record interviews with them on the practical details of their work.

Usually, I’m just a consumer of these oral histories. In today’s piece, in a departure from my usual role, I get to deliver you all an oral history — one I think is ideally suited to FreakTakes readers. It’s an oral history with possibly the best guest I could have asked for: Ilan Gur. Ilan is the founding CEO of the UK’s new Advanced Research and Invention Agency (ARIA). And, better yet, he’s a huge metascience nerd! The two-hour interview, recorded in Berkeley, attempts to unpack the metascience experiment that is ARIA.

I can’t thank Asimov Press enough for funding the interview and facilitating its recording. The full audio, video, and transcript are here on FreakTakes. And I also worked with Asimov to write up a much snappier, abridged version of the interview. You can find that piece in Asimov Press today.

Enjoy!

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For those who’d like to listen along while they read, I’ve embedded the Spotify version of the podcast. Full transcript below. Special thanks to my girlfriend Katherine for helping me edit the full transcript:)

Eric: Ilan, the CEO of the [UK] Advanced Research and Invention Agency. Thank you so much for being here and doing the Asimov interview today.

Ilan: Thanks for having me. I don’t think I have ever been interviewed by someone who geeks out about the same things I do as much as you.

Eric: Well that’s exhilarating, because this is my first interview. We’ll see how it goes! [Laughter]

First question. We’ll start with a fun one. As grandiose as it sounds, ARIA’s mandate is to aim big and try to create technologies as important as the ARPANET or spark new fields the way the Rockefeller Foundation did with molecular biology. Do you consciously think about that to yourself — that you have to be or find the next Warren Weaver or JCR Licklider? Does that keep you up at night?

Ilan: [Laughter] What keeps me and our team up at night is actually having a massive enough impact. Do we think about trying to be or find the next Weaver or Licklider? Probably not. I use an analogy often of being a catalyst or an enzyme. Whether it's me or our team, we're one thing you introduce into the system that hopefully mobilizes a bunch of other stuff to make an impact.

Eric: In that case, if you think about being a catalyst, what makes a reaction big enough?

Ilan: That’s a great question. You’ll appreciate this: when we have program directors that come into ARIA, some of the pre-reads we give them before they start are interviews with Bob Taylor or stories from DARPA or otherwise. And the main thing is to try and get in their heads, “What does a win look like?” For a lot of places if the research you fund leads to a new product that makes an impact, that's a big win. I often say, “That would be a loss for ARIA.” Because what we really need to do is catalyze something that is bigger than a product, bigger than a company. It should essentially be like a movement, an entirely new technology platform that didn't exist, an entirely new industry that didn't exist. And I think the way you catalyze that can be really different for different people. So if I think about our program directors, they're all different. They all have different superpowers. Just like if you think about Licklider...I mean you're a history geek, right? So just like if you think about Licklider and Bob Taylor, right, you could talk about them each as having catalyzed this massive transformation, but in very different ways.

Eric: Are there any reactions that have been catalyzed in the past 10 or 20 years or so where you look at them and you say “Wow that's the kind of thing we should be going for”? I’m definitely guilty of thinking too far in the past on some of these things, so I’d love to hear your examples.

Ilan: One of our advisors for ARIA is Aslem Turechi, one of the founders of BioNTech. And so you think about their story of having sort of worked so hard on mRNA-based vaccines and systems — initially for cancer. And then you think of Dan Wattendorf at DARPA who basically started the program thinking about vaccines for pandemics. All of that was in the mix, and then all of a sudden you had the pandemic event that actually turned it all into the world-changing impact. So I think that's such an easy one to go to. I also want us to be thinking differently at ARIA around how those transformations might take place.

Interestingly, for example, you think of ASML as a company. But it really is a company that manifests, in that one company, a massive transformation in the field, in terms of UV lithography. Especially with ARIA being something based in the UK...you can't be picky in terms of how you're gonna get that world changing of a transformation within an ecosystem that is bound like the UK. I mean, we’re working globally, but I think ASML is such a compelling example of, “Out of some fodder and set of reactants, back to the catalyst, something catalyzed this massively transformative company and then field shift.”

Eric: Do you have any program in the current cohort that you think, like, their way of scaling to impact might be in an ASML-shaped box?

Ilan: That’s a great question. I think it may be for...any of them. [Laughter] In the sense that, and we may talk about this more later on, one of the big things about ARIA that we're trying to build in...that maybe differentiates it from, say, ARPA agencies or DARPA (which started seventy years ago) is recognizing just how important entrepreneurship and startups are to cutting-edge research in today's world. Our bet with ARIA is that probably the biggest driving force for impact will be through entrepreneurs and entrepreneurship, in some way. Whether you end up catalyzing a whole ecosystem of entrepreneurs and different companies, or entrepreneurs that are focused on government, or whatever else. Or what emerges from that is one singularity of a company that changes the world, or like an “Ozempic moment.” Again, I don’t think we can be picky. I think you could imagine that happening in just about any of our spaces. For example, I think about neurotech, I think about programmable plants, and certainly in robotics. It's just a question of do we get lucky and nucleate that right thing at the right time.

Eric: On that point. So I read your House of Lords testimony and a lot of things of that sort…

[Laughter]

Eric: I’d love to parrot back to you how I understand ARIA, from those materials. You can tell me what’s right, what’s wrong, what I need to say differently, etc. Also, if you could use examples from some of the current programs, that would be great. I’m sure there are many listeners who may have seen a program announcement, but that’s all they know. So as I understand it: ARIA programs must be 1) “big if true” and 2) differentiated. You don't want to fund programs that somebody else in the ecosystem would fund otherwise. And while each project doesn't have to succeed — the vast majority won't in the traditional sense — they should all succeed in materially changing the conversation regarding what's possible in a given space. In terms of your mandate in the UK — in the long term, these programs are meant to help drive economic output, quality of life improvements, health benefits, etc. Is that more or less accurate, how you'd conceptualize it? If someone says, “Isn’t that what deep tech VCs do?” what would you say?

Ilan: First of all, is that right? I think that’s right. We're meant to take bold bets that kind of amplify different parts of the research system in new ways. I think about our programs as funding like a constellation of teams that can lead to massively transformative outcomes at the intersection of quality of life and economic growth — not just for the UK, but for the world. I think that ‘for the world’ is really about the scale of ambition that we are talking about.

You were asking, “How’s that different from a VC?”

Eric: If somebody says, “How’s that different from a VC? Or “...than if the NIH spins up a new study section?” Or something of that sort.

Ilan: I think those are two very different questions. Let’s talk about VCs. There are a lot of VCs who are just in it to make money...but in terms of the mindset and the motivations...a lot of VCs, I think, do see venture capital as a platform to change the trajectory of the future and world in positive ways. I think the big difference with VC is — when talking about the idea of ‘big-if-true’ — there’s a sense of scale, right? You have to think about the scale of “how big is ‘big’?” — and how speculative are you willing to get on the ‘if-true’?

In talking to venture capitalist friends about what I do and what we do at ARIA, sometimes you hear this metaphor around startups and VCs: “surfing a wave.”

That’s one way to think about this. What does a VC do? A VC is meant to be like a surfer in the water, to look out at the wave set that’s coming and ask themselves, “Oh, okay, is that wave forming? Is that going to be a really big one?” The size of the wave is, kind of, how big of a market they think might emerge. And the bet they’re trying to make is, “I bet that’s a big enough wave.” And then they’re trying to bet on the timing, like, “Okay, this is when I should grab a surfboard and start paddling.” And you can think of the surfboards as the companies they’re investing in.

I think the big difference [between ARIA and VC] is, that’s being very reactive to the system. You’re trying to find the trends you can hop on and surf, so that you can maximize the ROI of your investment in a very concrete, direct way.

I see our job as more of putting the energy in to create the wave. A venture capitalist can only fund into a thesis once there’s enough momentum where they can start reading, “I see the market forming, I think there are technologies that can work here.” And most importantly, “There are companies.” Like, most VCs are waiting for companies to come find money. So there need to be enough entrepreneurs and companies doing that.

If you look at the spaces that we’ve carved out [at ARIA], we’ve said, “Right now everyone looks out and just sees flat water, but we believe that by pushing a little bit here or there we can start to build a wave.” And if we can catalyze the formation of a wave that’s big enough in one of these spaces, then actually that’s going to catalyze all the VCs to want to jump on that wave and to want to invest in companies. Then you get a win-win and, ultimately, change the world. [Laughter]

Eric: And so…

Ilan: Was that helpful, that analogy? I probably went a little too much on that.

Eric: No no no, it was great! So I have some questions. Sometimes, in terms of creating the wave...I’m sure there are times where you put a certain amount of money in a space, and there's enough teams out there that already care about this and have the proper background and the right incentives to just throw themselves into it once the capital is there. And then there's probably other cases where more legwork is necessary. Because that's not quite what a university would do — or usually a startup would do X task, but this isn’t quite a VC-scale market. How do you approach those two different types of areas?

Ilan: There’s so much we can talk about here. I’m glad this is a long form interview, because we’ll have time to get into a bunch of this. Part of this has to do with how we organize what we focus on, and maybe we’ll come back to that. I think it’s worth just talking about an example here. What came to mind as we were talking about the wave and VCs, I was thinking about one of our program directors, Angie [Burnett]. This might be particularly interesting to this audience. Angie’s a plant physiologist by background, had worked in academia, a national lab, she worked for the UN for a little bit. She came into ARIA initially thinking about food security and what we could do in food security. Fast forward — where did she end up with her opportunity space, which is what we call our focus areas, and then the program that she launched? The opportunity space that she launched is called Programmable Plants.

We tend to think for all of these [opportunity spaces], there’s some insight there. For us, an opportunity space needs to be, like you said, big-if-true. And we need to be able to make an argument relative to the potential impact. So if it’s highly consequential for society and relative to that impact you can argue it’s underexplored...you know, not enough funding or not enough of the right type of ideas or bets being made in that space. And that for some reason, it’s ripe for transformation. That defines a very big [opportunity] space that we are now going to start working in — and basically buying options through the early research that we’re funding to learn more and see if we find something that could become one of those big waves.

Angie's insight on this space was that if you just think from first principles, when you look at some of the biggest problems and opportunities we have in the world, obviously, agriculture is one of them. You think about food security, you think about climate change. The tough part about these segments is that they're massive problems, right? You need to talk in terms of gigatons of CO2 or carbon, in either case. And her view is that, actually, you can think of plants as a technology platform, and plants are one of the few technology platforms we know of that, actually, we have a system that operates at that scale — of gigatons of carbon.

And what do I mean by technology platform? A plant is a piece of hardware. It has certain functionality. Interestingly, in many plants, like you go to the store and you buy a cob of corn, we have actually engineered the functionality of that plant over many years. And you have distribution channels and the ability to deliver these things at a massive global scale, commensurate with those problems — food security, climate, etc.

The problem is...it's like a really shitty technology platform, right? We're very limited in what functionality we can build in. Instead of 18 months for a new iPhone, you take 18 years to get a new crop that's actually viable. Interestingly, if you talk to most investors, they will say, “Well, in the ag space...you've got the top [incumbent] ag companies and [given the incumbents and structure] it's basically the hardest, most entrenched space to innovate in.” It's just not a great place to invest. Massive capital, massive entrenched interests, there’s regulations, etc.

The bet that we're making is that actually...on first principles, when you look at what’s happening in synthetic biology, when you look at the problems and the forcing functions that are coming, requiring a change to how we do agriculture...there’s a pretty strong argument to be made that, sometime in the next few decades, there will be a shift in how we approach global agriculture. You can think about it as something like, “There will be an ASML-type company that completely disrupts the big five ag companies in the world, and does things radically differently.”

Eric: And what's Angie's job over the course of five years? And I guess also tie in, what is a program director? And how important is it that they have a point of view? And does that come out as you're picking them? ...I asked you a lot of questions.

Ilan: No, that’s fine. Angie’s job was first — together with me and the cohort we had — beating up the question of, “How do you define a space that’s interesting and in line with this idea of ‘plants as a technology platform that’s underappreciated’?” Synthetic biology has been this massive vector of technology progress, which is not being leveraged for plants and ag to anywhere near the extent it’s being leveraged for human health. So now there’s like this arbitrage [opportunity]: “We’re making all this progress in synbio, we have this massive problem opportunity in ag.” But they’re not really connecting the dots.

Eric: And how many years behind do people perceive ag as, in terms of the cutting edge in synbio? I’ve heard 10 or 20 years, but you’d have a better...

Ilan: Well, let’s fast forward. So, what is Angie’s job? Her first job is to lay out that space. The next job was to say, “Okay, what’s a funding program we’re going to launch?”

She had a bunch of different ideas. Where she ended up is a program that we’ve now launched — and we’ve just announced the people and groups we’re funding. That program is called Synthetic Plants. [See this link for more information.]

And the idea was, if you look at the real frontier edge of synthetic biology, and we're talking about things like de novo genome synthesis, like actually thinking about synthetic organelles. You have, in the UK and other parts of the world, really amazing progress happening. But when you go and talk to those researchers working in those areas, and you say, “Well, we're thinking about doing a plant program,” the reaction Angie got from all of them was, “Why? There's so much to be done in mammalian systems, we're making all this progress...like, plants are hard! They have multiple copies of the genome, it's impossible to figure out how to transform them, it’s XYZ...”

And instead of getting discouraged by that, Angie got more excited by that. She said, “Well, wait a second, let me tell you a little bit about the potential impact we could make if you start working on plants.” Long story short, she held a workshop. And I got to be at this workshop, where she brought together a combination of top synbio people, top ag people in the UK and otherwise. There were probably 50 people in the room. One of the questions I asked was, “How many other people in the room did you know when you walked in?” And I had said [gesturing his hand upward], “Raise your hand if you only knew one person, raise your hand if you only knew X...”

And I think most people knew like five out of the 50...and none of the synbio people had talked to any of the plant people.

What we’ve found is, now, there are all these new collaborations. We have synbio folks who are basically saying, “I’m shifting my work to plants because I’m just convinced this is the most important thing I can do.”

Eric: And when you say ‘folks,’ how many are thinking of shifting their work to plants?

Ilan: Well, you’ll see how many synbio people we fund in this program when it gets announced. But I know of at least two specific cases Angie’s mentioned where, when she started the process, the person was so averse to the idea of doing anything in plants and thought it was a waste of time...who have built really meaningful collaborations and — whether they get our funding or not — are going to start working on that. So, it’s cool.

Eric: When is high variance [in reactions] among the adjacent experts exciting? When is it less exciting?

Ilan: Oh yeah. How do you know when people just say, “Oh, that's a horrible idea.” How do you know when it actually is a horrible idea? [Laughter]

Yeah, I mean this is an interesting thing. You talk about variance, right? Someone from DARPA once shared this with me, and it's a framework that I really love, which is...if you think about the role DARPA plays, more important than anything else, it is a mechanism to increase variance in the system.

It’s actually something I think a lot about for ARIA. The idea there is, more than anything else, ARIA was created to do things differently. The idea is: do things differently, and by doing things differently, by shifting the modality of research, you can get different outcomes. We can spend a lot of time coming back and talking about that.

But if you want to do things differently, first of all, you need people who see things differently. It’s one of the reasons the PD [program director] model is very helpful. But secondly, you have to break what is, I think, a pretty strong and homogeneous sort of truism of how we (largely governments) fund research. Which is something like, “We’re pretty good at funding the well-known disciplines. And we’re pretty good at funding the obvious problems or opportunities.” But that's all very linear, like, “More funding for biology, or synthetic biology, or semiconductors, because we see what's happening geopolitically.”

If you want to do something different, you need to find some way to cut and slice through that in a different way. Interestingly, the ARPA model says, “Okay, you find a program director, like Angie. You have them look across the system and say, ‘Well, what’s an actual thesis of something new that we could do, that’s not a single discipline? Maybe it is, but it cuts across TRLs [Technology Readiness Levels].” That’s the other thing. People sometimes ask, “Is this low TRL or high TRL?” It’s like, no. We’re mixing these modes in new ways.

Eric: You’re ambitious and applied...

Ilan: Yeah, and you have sort of a spectrum of portfolio. What that means is, what we end up funding on the backend of one of these theses we’ve developed, is going to be a very different set of people with a very different set of incentives — in terms of what they are going to do — than would otherwise get created.

And the variance is...if everyone thought it was a good idea, we would be introducing no variance into the system. If no one thought it was a good idea, we probably shouldn’t do it because it probably is not a good idea. But if you get spiky reactions to anything you’re doing, it’s the sort of thing where...okay, you have some minority that actually think this could work. But in a consensus panel, peer review, that minority voice would probably not win out or be there. So it would never happen otherwise. And, actually, I think the hardest job of a program director is to be able to actually face the criticism of so many people saying, “You don’t know what you’re talking about!”

Eric: You need to have courage to live with your bet, for years on end...

Ilan: You need to have courage to live with your bet, yeah.

Eric: And so some people...

Ilan: Wait, I’ve been talking a lot! I feel like it’ll be good for this audience...as we’ve been talking, what comes up for you as you think about some of the history that you’ve learned about for program managers at DARPA, variance, etc.?

Eric: So, I guess what I’ve been really impressed by, in working with the ARIA PDs, and ARIA in general, is when I read about early ARPA, 1960s and 1970s in particular, it seems like they really did trust the PMs to have an opinion. Or to say, “Here’s why this contractor’s best. You have to see it [the vision], and here’s why there’s only one group to do X thing.”

It seems like ARIA has given its PDs a long enough leash to have the point of view and follow it wherever it may lead. When I talk to folks at a place like DARPA, or something, I often get the sense that the PMs do have a strong point of view, but it’s an older organization. Like, it’s a 60 year old government agency. I think a part of the magic of DARPA is, so many government organizations only get more bureaucratic over time. They’ve [DARPA] been phenomenal at, like every five or ten years, finding ways to clear out a lot of the red tape, scar tissue, etc. But it does still build up a little bit.

So it’s been really cool. Something I try to impress upon people is that 2025 DARPA is not 1965 DARPA. You need to pursue different programs and do different things [today]. And when people ask me, “Well, do we have an early ARPA [today]?” Before ARIA, I guess I’d say, “Maybe OpenPhil.” OpenPhil lets people be free like this. But as ARIA has come into existence, it seems like you all live in the vein of early ARPA much more closely than anyone else. But, saying that, I also know you want to do something new...

Ilan: No, it’s interesting though, because I think this relates to the variance point. I’m trying to keep this dear to ARIA in the early days. It’s not about, “Did we find the right bet?” Because actually, given the variance point, in the early days, it’s not going to be obvious which is the right bet.

So it’s really about, “Are we being true to a commitment to increasing the variance of what gets funded?” And then, “Are we going to have the muscle to see the right bets emerge from that work?”

I actually had a [ARIA] board member recently say, “Isn’t one of our biggest risks right now that we created the wrong programs — like we’re funding the wrong programs?” And I said, “No, I don’t think that’s a risk at all, in part because we decided to create these opportunity spaces.” The whole idea behind an opportunity space for us, in these focus areas, is that our whole job is to take speculative bets. What that means is we can’t know upfront whether this is going to lead to impact. We can’t engineer that. The only way we get it wrong is if we take a speculative bet in an unproductive direction. So the point of an opportunity space is to say, “Let’s define what we think is a productive direction.”

An opportunity space is going to have certain beliefs that bound it. And the point is, if you can get yourself to believe these things...e.g. “Pressure on food security and climate is going to force us to do some things different in agriculture,” “Synthetic biology is moving...” Right? If you believe those things, you have to imagine there is the potential for enormous value — economic value and social impact — that can happen in this space. And now that we’ve bound that space and set that opportunity space, now we can take steps, big and small, and make bets in that area without having to worry, like, “Is synthetic plants the right program?” I’m not worried about it at all. Because we’re making a bet in a direction that’s productive.

The only thing we now have to worry about is that we don’t do what we were made to do. What makes ARIA unique — and what’s meant to make a place like DARPA unique, certainly in the early DARPA days — is that you make a bet, you take a step, and then you learn something, and you can pivot and say, “Oh! Actually it’s this 5% of what we’ve done so far that is starting to feel really valuable. Let’s minimize the rest and 10X that 5%.” That’s the thing that...I think that’ll be one of the big muscles we have to create for ARIA in this next phase.

Eric: So, you’ve moved to the UK, and ARIA is...

Ilan: I’m sorry, I have to stop! I’m like, I’m sitting here wondering if people watching this are excited about it. It’s just like — the idea that there’s now a community that’s excited to hear this conversation — that’s something I’ve been searching for for a while.

Eric: [Excited laughter] Okay, so, in that case...

Ilan: How many subscribers do you have?

Eric: Like 4,000. But there’s people like Matt Clancy who have like 15,000, or something like that. [Correction: Matt has over 18,000.]

Ilan: But those are high impact people.

Eric: Yes, I am continually wowed by the subscribers I have...and when I write something, the email outreach I get. It’s very much a dream for someone like me who...I wish I could be a great researcher [gestures at Ilan], but it was not in the cards for me.

Ilan: [Laughter] I wish I could be a great researcher too. Wasn’t in the cards for me. Definitely more of a Bob Taylor than a Licklider.

Eric: So you’ve been doing this for so much longer than many people. A lot of people have maybe gotten interested in this space in the past 5–6 years or something.

Ilan: Wait, what’s “this space”?

Eric: We’ll call it this “applied metascience” space. People who want to really consciously experiment with how you build R&D ecosystems differently, or research labs differently. In many ways, you’ve been doing this for possibly the majority of your professional career. Can you tell people about the different stops you’ve taken? Maybe different things you’ve learned along the way? Different gripes you’ve picked up? ... [I imagine] you only throw yourself into this if there’s stuff to be fixed and you have ideas.

Ilan: Yeah, I mean, I sometimes describe it as, like, I got thrown into this just because I felt like a misfit in all of the different environments to do research. And we can talk more about that. But I think that is a motivating factor, right? What motivates me, and probably what motivates most of the folks who would listen to a podcast like this, is just realizing that you can take the things we’re learning at the cutting edge of science and discovery, and turn them into stuff that’s useful, real, and awesome.

I mean I had — actually, you’ll probably appreciate this story — I was one of a rare set of people who was an undergraduate major in material science. Material science is kind of a weird field that most people, at least when I went to college, didn’t really know about.

Eric: They’d pick it up as a masters...

Ilan: Yeah, exactly. I think there were maybe like five people at Berkeley who came into the undergrad material science program. But the reason I got into material science...I grew up in Pittsburgh and went to a public school, which just happened to have a couple of phenomenal science teachers. And one of them encouraged me in 10th grade to put in an application for this program that CMU [Carnegie Mellon] did, where they would host high school students in a lab.

And I still remember, like, they gave you a questionnaire, and it was like, “What are your interests?” And I was in 10th grade, you know, I was not a polymath who was way ahead of their time. So my interests are like, ”I like physics [shrugs]...maybe chemistry?” You know, you just say pretty banal, normal stuff. Anyway, they paired me with a material science lab. And I remember showing up and saying, “Why did I get the oddball thing? Why couldn’t I just be paired with a normal lab?” And I didn’t think it was going to be cool or exciting.

The project — and this is the piece that I think you’ll appreciate — the project that I got paired with was a lab that worked in magnetics. What they wanted to do was come up with a new magnetic storage medium. At the time, you know, a hard drive was, what, 16 megabytes? You didn’t have flash drives, etc. And so the question was like, “How could you get much higher density?” So what they were doing is they were taking a material called MCM 41 — this is the part you’ll love — MCM 41 was one of a class of what are called molecular sieves. It’s a material that has a microporous structure, a lot of core space, sort of a zeolite material used as a molecular sieve/filter/etc. Basically it had like honeycomb pockets. The project was, through different means — chemically, sputtering, etc. — to fill these honeycomb pores with magnetic material, with some iron compound. And then the idea is that the ceramic honeycomb borders would be the separations between domains of a magnetic storage medium.

I still remember, at the time — you’d go around and say things like, “You could imagine putting a gigabyte on something the size of your hand!” But it was mind blowing! Just the whole idea that you have these nano honeycombs, and then you’d have a head that would sort of scan them.

Eric: Did you believe it? Or did you feel like that was crazy?

Ilan: No, I totally believed it! And the reason you’ll like the story is because MCM 41 stands for “Mobile Corporation Material #41.” So I’m still waiting for you to do a post — maybe you’ve done one and I’ve missed it — on all of the amazing discoveries, fundamental and otherwise, that came out of the oil and gas research labs. Mobile Corporation did all this incredible material science work. And, of course, they named all the compounds, like, “MCM 3, MCM 5.” So MCM 41 was, like, something everybody knows about...or at the time did!

Eric: That actually would be an interesting post too. Because I was just yelling [injecting historical stories into random conversations] at some people on Twitter the other day about the origins of TI [Texas Instruments], as just like, one of the early oil and gas firms that had a ton of early MIT ties. They just got very good at making their own instrumentation. And that’s a pretty high margin business. It’s a little less speculative. And they just like...I forget if it [TI] was a spinoff or if the firm [the original oil and gas firm] entirely pivoted. But yeah, maybe I should. If you have ideas!

Ilan: Oh yeah! Materials, lithium ion batteries, came out of an oil and gas lab. A bunch of solar cell work. I think there’s something cool there, but...

Videographer: Can we take a quick break?

[Camera Break]

Ilan: You were asking about the trajectory of ARIA?

Eric: Yeah, it would be good if we could discuss how...you were at ARPA-E. What in the world is Activate? All of these things, probably like, being dissatisfied in different ways. Or being happy with what you did, but dissatisfied drove you...?

Ilan: I think there’s a story of navigating, you know, continuing to basically try and do bigger and bigger metascience experiments, if you call it that. There’s a version of that which is, like, me being disillusioned by different institutional structures, or different silos, and how we do research. But maybe a more positive or interesting version is that, as I think over that time, is...I talked about being at CMU. When I did that research project at CMU, what flipped on for me was this idea of, “Holy shit, the wonder of the ways that we can take scientific discoveries and turn them into massive impact!” For me, the ultimate [thing] at the time — and this probably went all the way through my undergrad and into my PhD — the most valued currency for me in terms of changing the world with science was the ideas. And the instruments and the processes and the methods. I was so obsessed and in love with that, and I saw that as the big driver.

Interestingly, I had this experience 18 months into my PhD where we had written a Science paper. We were on the cover of Forbes for this new approach to creating solar cells much cheaper, you know, II-VI nanoparticles that we were going to print like newspaper. There was all this excitement. And I spent a couple of days with some business school folks with technical backgrounds, and realized it was all BS. We actually weren’t solving the right problems.

And I became...you could think about it as being disillusioned, but actually I think it’s more [that] I recognized that the world of ideas that I was in, where that was the currency, there was something missing there, in terms of how you drive impact.

And then I ended up in startups, VC-backed startups. My mindset moved from like, “Actually, ideas are pretty cheap, you know? Ideas are pretty easy to come across.” It’s more about, “How quickly can you iterate through them?”

But I also got obsessed with currency as the currency for driving impact. Because my job running a startup was, like, “Raise money.” And you could see that the more money you could raise, the more of an opportunity you had to drive and get to faster outcomes relative to competitors, or whatever else. So I really was in this mindset of money.

And having a chance to go to ARPA-E, one of the things I found very compelling was that it was a different mode from venture capitalists. I thought venture capital was sort of too narrow of an impact model for doing early-stage science, especially for industrial markets. But I also found compelling, like, “Oh wow. We’re going to be the biggest Skunk Works innovation funder in the US, for anything climate-related.” And I was attracted to this big money question. Money is like the driving force you have for reactions.

And now I think, through that time for me, at ARPA-E, my biggest recognition was that we had...

We had an incredible mission: to drive translational science into big impact in climate and energy. We had access to a lot of funding to do it, so we had the driving force. We had access to all these brilliant ideas, meaning every researcher who worked in any of these areas in the country would apply to our programs if we could just pick and choose the ideas. And the thing I realized was that, actually, none of those was actually the thing that mattered. What really mattered was people and institutions and incentives. And you can have all the money you want, and you can have all the ideas you want,  but if you don't have the right people in the right institutional environments with the right incentives to drive progress, you're pushing on a rope.

Eric: At ARPA-E, were you ever wowed by some set of people and institutions and incentives that you got to deal with?

Ilan: Well, in the end, I came back to...I left my startup feeling somehow like I had been misled. The idea of, “Venture Capital-backed startups are going to change the world.” We were working on batteries for EVs, industrial markets, very low margin business. Probably our timing was off. But I was like, I don’t see how we can develop the technology, get it to scale, and actually have it converge for someone like Vinod Khosla, who was like, “Either this needs to be a trillion dollar…” it was at the time billion dollar, now like, “...trillion dollar company, or it’s not worth doing.”

And so I kind of had a feeling when I went to ARPA-E, like, “Actually venture-backed startups are not the way to do this. And startups might not be the way to do this. Let’s figure out all the other institutional modes.” What I found in the end was that, to your question, of all the environments that I was funding research, the ones that felt most resonant and most productive were either the startups or the folks within academic labs that were already operating as though they were spinning out a company.

And what I realized was that the venture capital funding model has constraints, but if you don’t worry about the funding model for a second and you just think, “Well, what is a startup?” A startup is a vehicle for getting the right people into the right environment with the right incentives completely aligned with some translational research mission.

If you think about it, [for] everyone in an early-stage startup, the goal is to create value in a very concrete way. You’re probably doing something very speculative, if it’s science-based. Everyone who’s there in the early days has decided they’re going to commit the next chapter of their life to that pursuit. The incentive is clear. The alignment is clear. You often are getting people from different backgrounds, in interdisciplinary ways, to do it. So I think startups are massively valuable and important vehicles for R&D.

And the question becomes, and we can have a conversation about this, the question becomes, “How can we fund them? How can we fund them as R&D centers?” Venture capital is not a great way to do that. Some VCs actually do fund very applied R&D and take speculative bets. And I think those are companies that tend to change the world. But relative to the, like, $70 billion of US funding to applied and basic research — that number is probably dated right now — you don’t have anywhere near that going into super science-y startups.

Eric: To understand the problem...You love the shape of VC-funded startup groups — the people, environment, incentives they create — for the problems they want to attack. But there’s all sorts of problems that...

Ilan: They can do it if they see the wave coming and they’re just hopping on the wave. So when that happens, they work great. But why can’t you have the same aligned incentives, full-on commitment, before the wave even exists? And couldn’t that be a mechanism to create some of those waves?

Eric: And how do you think about making that happen...…

Ilan: I have no idea.

Eric: ...at ARIA?

Ilan: Oh, at ARIA!

Eric: Yes. And of course all of my readers will know I’m biased. I’ve spent this huge amount of time writing about the best early ARPA contractors, like BBN or the CMU autonomous vehicle groups...groups that were very startup-related, but really embraced technical ambition over market size. Their constraint was that they need some amount of grants [or contracts] to fund it. But I’m sure you have all sorts of theories on how to make this work for you [ARIA] in spots where there are parts of the R&D ecosystem that could use a little bolstering — at least in terms of ARIA’s incentives.

Ilan: Yeah. So one of the things we’re doing at ARIA, which I think is probably different than DARPA, is being really open-minded and attuned to, “How do we try and fund not just the best people and ideas, but with resonance in terms of the environments and incentives where they are doing the work?”

What does that mean? That means a few things. One is that we are very comfortable with the idea that, using ARIA funding, a researcher might decide to go start a company. They might decide to go, leave their academic lab, and just do the research as an independent researcher, because that’s what they think is the right thing.

We have something interesting, which is we do these seed funding awards. I mentioned those opportunity spaces where we say, “This is just the direction that we think is fertile.” A program director will create a program, which is their thesis, and that’s where they’re going to focus a lot of energy and where we’ll focus a lot of funding initially. But then what we do is we say, “Well, we’re not the only smart people around. And it’s all about increasing variance. So why don’t we find other people and let them start seeding ideas that could lead to the massive breakthroughs...[unintelligible]”

And this is like, you know, give us a three-page application, tell us why you’re obsessed with this idea, and [why] no one else will fund it. And we’ll give you up to £500k. So just start running at it. And if you come back with something compelling, we can double down with you. [We can] either make it a bigger project or actually have it inspire a whole program.

Eric: So Jenny said something in one of her interviews. — Jenny is the PD on the robotic dexterity program. She said at one , “I was almost disappointed that I didn’t get the chance to fund, like, some random person in their garage.” Because the funds are open to them. Can...

Ilan: Anything.

Eric: Can you explain what it would look like to be...like if I’m a random guy in Birmingham and I want to…?

Ilan: [Gestures at Eric] As opposed to a random guy in…

Eric: Yeah, in Chicago. [Laughter] And if I wanted to run it out of my garage, how much paperwork is involved? It seems to be a very fair [reasonable] amount.

Ilan: So this is really interesting. What we started with at ARIA is, we said, we wanted to make clear that we are completely agnostic. We wanted to fund the best people in the best environments. Apply. We don’t care if you’re at a university. Just tell us you’re obsessed with the idea, what the idea is, and show us that with our funds you can get access to the equipment you need to make it work. And we wanted to be really agnostic.

Now, there’s a piece of this, which is we have a brilliant, awesome, founding CFO for ARIA. Her name is Antonia [Jenkinson]. She and her team, I went to them and I said, “This is a little hard to do as a government agency. You got to do due diligence on these people. How are they using their money?” And they said, “Yeah, but this is what we’re built to do, so we’ll just figure out how to do it.”

Eric: And is it true that she walks around with the [ARIA] founding mandate in her pocket?

Ilan: [Laughter] She has been known to carry the ARIA Act around, which I love. So we started and said, “Yes, we can fund this [alternative applicants].” And seeds were a three-page application. We would tell you within three weeks whether you got the funding.

Eric: Three pages? Like...[makes a show of counting out three pages]

Ilan: Three pages, yeah. It was a three-page application, three weeks to funding decisions. And when we did it, we did have this. We had people apply. And then we had a few people who said...we had one person at a well-known university in the UK who said, “I’m really glad I’m getting this seed. To be honest, I don’t think I want to do this in my academic lab. For a number of reasons.” I think they were actually a postdoc. They were, sort of, earlier [career]. And they said, “What do you think about me, just like, finding and renting some space to do this work as an independent researcher?” The program director talked through it with them and said, “Actually, that makes sense. You’ll probably do a lot better. You’ll probably be more motivated.” Whatever it was. And so we just figured out how to give that person the award as an individual to do it in this way.

And we saw a few of those. Then we paused, and we said, “Well, wait a second. People are funded and excited to work on these projects.” And when we tell them we’re open to wherever you do it, they’re telling us, “Well, maybe I’ll do it some other way.” So the next time we did a seed call, as part of the questions we said, “What’s the institution you’re in now? If we award you the seed, where would you like to do the work? It doesn’t have to be the same place.” And the options were, “Will you do it in an academic environment?” You know, “my current university, another university, a company,” wherever else. And then we [included], “sStill undecided”.

First of all, I think we’re the only government funding agency in the world that gives that option. Secondly, the fact that there was an undecided bucket means, “We’re cool...like, we’ll talk through it.” I think we had like 23% of applicants in the next seed call say ‘“Undecided.”’

Which for me is such a big deal, because it suggests that being prompted with the question of like, “Eric, there’s a big project...it could be the most important thing you do in your life. Stop and think about, ‘What is the best environment for you to do this work and have it succeed and have a chance to change the world?’” And what we learned is like 23% of people [think], “Maybe it should be a startup, maybe this is my moment.” Or, “Maybe I should move to the UK and try to do this at a university in the UK,” which has happened now with ARIA grants. So, that was pretty cool.

Eric: Yeah…

Ilan: That felt like a...I warned you that if you get me excited about something, I’m just going to keep talking about it!

Eric: No, no, no! That was great! So I have a question [from my notes] lingering here, I don’t know where to put it. So I’ll just ask you now.

Ilan: Go ahead!

Eric: So this one comes from Tom Kalil. He said, “In what specific ways do you desire to transcend the DARPA model?” Because you’re not looking to set up some version of an American ARPA in the UK?

Ilan: I think that’s right.

Eric: There’s lessons you’re taking, but…

Ilan: Yeah, I mean look...I think DARPA is such incredible inspiration. You know what I mean. Like people argue about, “Is DARPA past its heyday?” “Is it doing good or bad?” But we have this beautiful gift, which is just the history and the reality and the myth of DARPA all wrapped in. And, honestly, if you can’t be inspired by that, like, forget you! Right? And I think that inspiration is so important and true.

We’ve touched on some of the things that I’m hoping with ARIA...ARPA, like you said, established 70 years ago in a very different time. It’s changed in many ways. I think for me, the most important things — one of them is one of the things we talked about earlier, which is having the intellectual humility to, and the eye on part of our job as just to increase variance and learn and pick up on threads that are valuable. That is really important to me.

One of the things I’ve noticed — and this is good and bad — but when our program directors...we pair them up with DARPA PMs, former and current, to give advice and whatever else. And oftentimes I will hear a DARPA PM say, “Wait, 37 performers for this program? You can’t do that. That’s not how we do things. That’s not the right way to do it.” What we’ve had the chance to do is kind of go to first principles on everything. And that’s a real case. I don’t think it’s 37. But davidad, who runs our Safeguarded AI program...for the first technical area of his program, he wants to, as quickly as possible, answer some theory questions and develop some frameworks which he thinks are best done as open source. And, actually, where that led him is we’re funding a lot of teams with small awards, to which normally people would say, “It’s not worth the management,” or “It’s not cohesive enough.” But the first principles suggest that, yeah, that’s the right thing to do there.

So, it’s kind of like having the intellectual humility to say, “Okay, I don’t know if this is exactly right. But it feels like it’s matching the first principles. And across what we’re doing, it gives us variance. We’ll learn more on the go.” I think that’s one thing that I’m hoping gets preserved at ARIA.

This other thing we’re talking about is probably the other most important one, which is...DARPA, rightfully, has a mantra of, “We don’t have our own labs. We don’t create institutions. We fund research projects.” And DARPA increasingly has done more with startups, which I think is great and one of the biggest impact vectors it has. But I think for us, for ARIA, being able to say from the beginning, “Actually, the people and the institutions matter. And there may be new institutions that we need to form — or that we catalyze forming. And we’re not going to be, sort of, scared about that,” is important.

Eric: Yeah. This is also something I think early DARPA was a bit friendlier to. They wouldn’t necessarily found an org, but they would write a pretty big check to an org that, like, didn’t seem to have an office yet or something like that.

Ilan: Was RAND DARPA?

Eric: Was RAND DARPA...

Ilan: I remember reading something that...

Eric: No, I think RAND would’ve been...I do think the USC ISI [Information Sciences Institute] was very clearly heavily early DARPA funded [from its earliest days, which helped create the organization of largely RAND alums]. They ran DARPA’s early MOSIS initiative, which was one of the first fabless [services]. That’s definitely a case of...those guys may have left RAND to form...I’d have to go double check some of my notes. But that’s a case of them [DARPA] writing [very early checks into an org] and making some promises, and it was an institution they needed.

Ilan: Yeah, it’s actually interesting! MOSIS came up recently at ARIA because, one of the programs that we’ve launched...we’re already starting to see that, within this...

[Camera Break]

Eric: You were talking about MOSIS and how it fits into one of your programs that you were talking about recently.

Ilan: Yeah, the opportunity space is Nature Computes Better. One of the theses there is that there have been lots of attempts to think about how you disrupt general computing. But it’s such an impossible thing to think about doing because of the massive supply chain and all the different forms of general compute. Suraj Bramhavar, one of our program directors, his insight was, “Actually, AI is very unique in the history of computing because you have a compute mode with a pretty narrow set of mathematical primitives, but potentially massive applicability, value, and impact. And that narrow mode of AI could be a new foothold to think about alternative types of computation — with alternative physics, alternative hardware, alternative substrates, etc.”

And the other piece of this is...when we think about, “Is there a program or opportunity space here,” one of the important questions to ask is, “What is the fundamental limit of performance that could happen in this space? And where are we now?” And one of the things we know about computation is,[even though] we’ve had Moore’s law for as long as we have, we are still orders of magnitude from the fundamental limits of computation. Whether it’s [the fundamental limit based on] Shannon’s information theory or what we see happening in nature. So the idea behind the space is, “Can we find new approaches inspired by physical systems, natural systems, other ideas that researchers have, etc. to use AI as a foothold for next gen compute?” The program that we’ve shaped aims to demonstrate that you can show, as a first step, AI training at a thousandth the cost and energy consumption than state of the art today.

And there are a bunch of really interesting systems questions around, like, “How do you even prove that in sort of a demo system?” We’ve now funded a set of teams across academia, startups, big companies, and a number of approaches that we think, in coordination, can get there. And from that work we’re already seeing, “Wow, there might be a next phase of this given some of the early excitement that we have.”

How would you take advantage of it? Maybe you need some MOSIS-like institution that is focused on this area. It’s still very early, but it’s cool because, like, you had your post on MOSIS and it actually is making a difference, being able to give us [ARIA] a catalyst of things to chew on.

Eric: And can you paint a picture of what this MOSIS would be doing? Like if a lot of these contractors are point solutions or different approaches, what would you need them [this MOSIS] to do?

Ilan: [Laughter] I don’t think I could paint a picture of that for Suraj’s program because he’s literally just in the early stages of thinking about it and I don’t think I could actually talk through it without disclosing things that he probably wouldn’t want me to. But I do think, you know, one of the things we talked about earlier was the question of, “Where are there new institutions, and how could they help ARIA?” We talked about our Creators. (DARPA talks about the people they fund as ‘performers.’) We thought that was a little odd. Actually, you might know the origin story of where ‘performers’ came from. Maybe it’s like: you want performance, so you have performers? Anyway, we call the people and institutions we fund ‘Creators.’ The idea being, the work we do at ARIA, I think you need equal doses of creativity and creation. This word ‘create’ is interesting because you can think about it in terms of creativity — which is like pie in the sky thinking — or you can think about it as like, “No! Go create something, like building!” And our view is you need both of those to come together.

Anyway, we talked about new institutions around Creators. We’ve also been thinking about new institutions to help ARIA do better. You might have seen our Activation Partners call.

Eric: Yes. Can you explain what that is?

Ilan: I can. [Laughter] This might be a divergence, but...

Eric: We can come back to it later if you prefer.

Ilan: No, let’s do it! When we think about the ARIA model as a whole, we talked about finding the opportunity spaces, being able to inject energy, catalyze these big waves — which are essentially new movements of technology...but then talent and capital that can transform the world in one of these spaces.

There is a question. We’re not DARPA. One of the things that allows DARPA to get things from early idea/technology into practical systems in the field is that they have this massive lever that is the Department of Defense budget. [Laughter]

Eric: Yeah, they have a built-in customer.

Ilan: Yeah, they have a built-in customer. And there is no bigger driving force than the procurement power of the Department of Defense, if wielded in the correct way. ARIA’s mandate is much broader. We’re not just defense, we’re actually not doing any defense right now — it’s quality of life and economic growth, broadly speaking. We don’t expect to have a built-in customer from government. There might actually be cases where government, like the NHS [National Health Service] could be an amazing partner and uptake vehicle for technologies we develop. But outside of having purchasing power as the driving force, our bet is that the biggest driving force that exists to get new ideas into the world at scale is going to be entrepreneurship.

It’s that whole idea of, “If you, as the researcher and a team of people are willing to commit their life for a stretch of time, yes, you could change the world.” We know it. We’ve seen that happen.

So, one of the questions we’re trying to grapple with is, we’ve created these opportunity spaces specifically to be places where the wave doesn’t yet exist. So, there probably aren’t a lot of startups in these spaces because venture capitalists aren’t super active in all these spaces. Maybe there are some. What can we do to increase the amount of reactants that are entrepreneurial in the opportunity spaces we have?

And we thought about a few things. When I was at ARPA-E, actually, we ran an experiment that I helped launch, which is called the technology to market program. We basically built, within a government funding agency, a business analysis/biz dev type function. The idea being, “Let’s figure out how to inject into our programs some thinking around how you translate the technologies.” DARPA does some of this.

Our view is actually, for ARIA, there are some things we can do internally...but to think about how technology’s transition to market, especially through startups and entrepreneurship, the best people in the world doing that are going to be people doing it in the field. And you might be able to attract one or two of them, here and there, into a government funding agency, but you’re not going to be the best in the world at doing that. So what we did was we put out a call, and we said, “Listen, we think there is going to be massive opportunities and value created in these spaces. It’s still early. If you are an organization that deals with venture talent creation, entrepreneurship, rapid prototyping...anything related to tech translation, transitions, and value creation...and you’re amazing at what you do, could you imagine focusing your energy on some of our spaces? And just do what you do really well, but inject more reactants into that system.”

My colleague Pippy [James], who’s our Chief Product Officer, was really the visionary behind driving this forward. Where we ended up was, we have a handful of organizations. Some of them are venture capital firms that are saying, “We will, for the first time, focus on the UK and look at opportunity creation in these spaces.” They’re doing things like running fellowship programs for scientists who want to be entrepreneurs.

Renaissance Philanthropy is another Activation Partner thinking about, “How do we create a two-sided marketplace between the technologies that start to emerge and philanthropic goals/philanthropic funding?”

Eric: A lot of people don’t think about it, philanthropic demand is demand all the same. They [philanthropists] often have particular technologies they want to bring into existence. But it’s often unclear how to solicit demand from philanthropic...the mass of philanthropies. It’s hard to understand what they want.

Ilan: Yeah, and in a lot of these spaces it’s not clear that when we’re done with our program, the commercial value is going to be right there. It may be that we’re still in a tragedy of the commons, market failure mode, and we need to band together with others to do more in those spaces. So I think that’s going to be important.

But one of the things that came to mind as we were talking earlier is one of the Activation Partners we have, I think you’ve spent time with them, is this company Amodo [Design].

Eric: Amodo, yeah! Love Tom [Milton]!

Ilan: Amodo is such an interesting story. They’re based in Sheffield. It’s a small team. It just reminds me of the things you write about! It’s a small team that, you know, they’ve been involved in a spin out of a university and they basically recognize that, like, “Man, universities don’t do a very good job of prototyping things, having a rapid iteration mindset, or understanding how to get things into a more commercial place. Why don’t we just set up a shop to do that as a service — for startups, academics, and otherwise?”

Eric: So you don’t have to shoehorn your experiments into off-the-shelf Thermo-Fisher equipment. Tom and them can make what you need.

Ilan: Exactly! “Let’s go solve it!” They’re like mechanical, electrical, prototyping fixers!

Eric: And they’re hiring!

Ilan: And they’re hiring! [Laughter] So, interestingly, they applied to be an Activation Partner, alongside...you know, our other Activation Partners are, like, Google DeepMind...but they applied. And first you look at it, and you’re like, “Oh you’re five people in a room in Sheffield?” And then when we talked to them and we saw what they were doing and the vision, it was like, “Actually, this is a massive asset for ARIA to be successful.”

And maybe it won’t just be Amodo over time, maybe we’ll find others. But already, through the arrangement that we’ve built, they’re actually doing this as a service for a bunch of Creators that we’re funding, who are saying like, “Oh my goodness, I thought it was going to take us six months to do this and I got a much better version of it in a week!” So I think that’s super cool.

Eric: And the PDs have seemed very impressed with them. Like when I was talking to some of the PDs [and other ARIA staff] about the BBN thing, the concept that I used was, “Oh, do you want an Amodo for your area?”

Ilan: And that’s one of the things we’re doing through Activation Partners, which, again, is sort of an experiment around this idea of, “The best people, in the right environment, with [the right] incentives.” We’re working with Convergent Research on what I think will be the first experiment of them saying, “Wide open to the spaces,” which will be our opportunity spaces. Instead of being a kind of two-sided marketplace and connector of talent with philanthropic or other funders for FROs (Focused Research Organizations), they’re basically saying, “If you’re someone talented who wants to commit your life to building a focused research organization in one of ARIA’s]opportunity spaces, apply! Then we’re going to find one, maybe even more, to go launch.” And it’s exactly what you said...

Eric: To people in the metascience space, I think Convergent is maybe one of the most exciting...

Ilan: Yeah.

Eric: ...kinds of Activation Partnerships. Because I think everybody [metascience nerds] was around when they first kicked up. And they also always knew [suspected] the vision was probably that Convergent might like to win NIH funds, or something like that, and set up more every single year. So to have an official [Activation] partnership was exciting, for somebody who’s just been a fan for a while.

Ilan: I think the biggest — we might agree on this — but I think probably the most important thing to accelerate progress in the research ecosystem is to increase the diversity of institutional types. Convergent is one of the few examples we have of a mode that is taking root, that’s saying, “Here’s a new institutional type. Let’s figure out how to scale it!” You talk to Adam [Marblestone] and he talks about...you know, he sees a thousand — I think he says either a hundred or a thousand — FRO-shaped things that need to be created in the world. I think it’s a thousand. I imagine there are a thousand. If he thinks it’s a hundred, I can probably debate it. [Laughter]

Eric: It was one of those two numbers. One more question, and then I’m going to do a little pivot. You seem to have a very good grasp of early/mid-20th Century R&D, the institutions, some of the stories, etc. Is there any organization or group from that period you find yourself thinking a lot about? Either because you want somebody to emulate it or you just think it’s cool?

Ilan: That’s a good question. I think the ones I think about are maybe, not surprisingly, the ones that feel like startups before their time. You wrote the piece about Edison.

Eric: Yeah.

Ilan: That was a story I was already obsessed with...but the whole idea of, like, Edison in the workshop. There’s an organ in the back, there are bunk beds, they’re sleeping there. They’re just all in, committed. You know, he’s raising money based on a dream. You think it’s bullshit, but then he makes it true by doing the work to close the loop.

Eric: The financiers come to visit and he looks crazy...

Ilan: That’s one piece. I love the story of Philo Farnsworth. I don’t know how much you know about that one?

Eric: I don’t know that one.

Ilan: 15-year-old farm boy who has a vision of making television. And basically through some serendipitous set of events, because he’s so passionate about it, ends up moving to San Francisco, getting funded by like an LA financier from Hollywood, and is competing with RCA in a race for the first television. And you just look at that, and look at the lab, and look at the talent times intrinsic motivation in the right place and the right time...

And I think Curie — this is more academic — but I think Marie Curie is another example of this. It doesn’t seem like it, but when you look at how she and Pierre Curie worked, it definitely feels like a startup.

Eric: What about it is very startup-y to you?

Ilan: Oh, the combination of the singular focus and the idea of, “We’re going to be open-minded and try to get to the goal through all means.” I always love the story of — I might have this wrong — but my impression is that Pierre Curie discovered piezoelectricity as part of trying to figure out how to very sensitively measure the radioactivity in the materials that he and Marie were looking at. So, basically, you have an academic pursuit to discover and understand this phenomenon of radium that no one understood, that leads to stumbling into discovering a whole other phenomenon, piezoelectricity — which has massive implications technologically. And it’s all because you had this intensity of spirit in one place.

[MIT’s] Rad Lab is probably another example of this. I don’t know if you’ve written a piece on Rad Lab.

Eric: I’ve never written a piece on the Rad Lab. There’s one book that’s continually over $100. And I check Amazon like once a month to see if the price will come down and I can finally get it. [Laughter]

Ilan: I’m going to buy you that book, whatever it is.

Eric: You don’t have to do that!

Ilan: If it means you’re going to write a piece about Rad Lab, then I think we all...we’ll do like a GoFundMe campaign to buy you the book!

Eric: [Laughter] I can promise to find a way to have it out in the next year, somehow! I have a few other Rad Lab oral histories sitting on my shelf that I’ve been letting pile up, so I do have to do this.

Ilan: Yeah, but the whole idea that because we got a group of physicists together to try and build radar systems, what fell out of that was, like, MRI...and the basic theoretical and practical things around that is just awesome!

Eric: Yeah, and also in terms of funding something for five years [as FROs tend to be], and then it's set off in a direction of its own...people at Rad Lab seem to have thought of some of Weiner’s early cybernetics writing, and things of that sort, as helping set the agenda for the RLE [Research Laboratory of Electronics, which the Rad Lab morphed into postwar] going into peacetime. It’s very clear that [the Rad Lab] was catalytic in extreme ways. The kind of thing that would be ARIA ‘returning the fund’ level [results].

Ilan: Yeah, it’s funny, one of the things that’s coming to mind here, as we think about FROs...one of the things I think a lot about is, for so many of these institutions, and I feel this way about ARIA right now. We’re two years in from starting everything from scratch. It feels like we have the environment where these amazing things can come out of it. When I think of our program directors, when I think about the Creators they’re starting to fund, the dynamic of the team, I’m like, “Wow. This has the energy and the characteristics you would want.”

The big fear is, I think, “Okay, this is founder mode.” [Laughter] These are early days! If you look at Rad Lab, it was this intensive thing, and MRI and these other things came out of it in the early days. And more came out of it later, but that question of, “How do you capture that founding period and not lose it?” I mean, what I love about FROs is the idea is, “Don’t even try.” Imagine that you’re going to have an intensive thing for five years. And then it turns into something else, like it metamorphizes. I think there’s something really important about that.

Eric: I remember hearing Adam muse at one point about the idea of, “Oh, it would be great if we had funders who could accept or were excited about the idea of maybe one FRO maybe leading into another FRO.” That is the outcome. You [ARIA] are playing a bit more of a repeated game. How do you think about that, one ARIA program leading to another ARIA program?

Ilan: Oh, 100%. I think most likely that is how we will make an impact, which is we’ll have a program that inspires the next program. And within that next program, we see something and we double down on it...and that’s the thing that happens, being adaptive in that way.

One of the interesting things that I’m noticing is...we haven’t talked much about how we recruit program directors. But the combination of our broad mandate and the fact that we are bringing in, as cohorts, program directors from such different backgrounds...we have these opportunity spaces that the program directors have shaped, and, yet, we’re now starting to see as we dig into them, these really interesting intersections between them. And I’m just wondering what’s going to happen. What are we going to do about that? Are we going to have programs that sit across two opportunity spaces? Are they going to merge into one? You know?

Eric: And can we talk about your new program directors? Who are they? Why did you choose to light up flares around these particular people and their expertise, or their point of view?

Ilan: Yeah. I think this recording is going to come out right after we have announced them. It’s probably worth first saying, we made a bet early on at ARIA. And my colleague Pippy had a really big role in this, which is we basically decided that one of the hardest parts for a research organization like this in the UK was going to be to find program directors or program managers, because, you know, it’s a weird thing to do. You’re on some amazing career trajectory and you decide to, like, step out of that for three to five years to do this other weird thing with a brand new agency that no one has ever heard of. Probably the listeners of this realize that one of the core parts of the DARPA model, which we’ve adopted at ARIA, is this idea of term limits. The people who are developing the theses are people that are coming in from the front lines of doing research in some way. They’ve got to sprint for three to five years to develop a thesis, fund a program, have an impulse function that hopefully catalyzes change, and then they go out and we refresh with some new program director. And part of that is to keep the ideas fresh, but actually, a big piece of it is to keep it incentive-aligned.

I’m never worried that a program director is going to make a decision on their program based on worrying about their career trajectory and what their boss at ARIA thinks, because they’re going to expire in three years. So they’re all just purely focused on, “How do I use this time to make something happen?”

One of the bets we made was, we knew it was going to be a challenge to find people. So we decided, rather than just hire people one-off, as we found them, let’s actually do what we believe is the most open call of its kind to find program directors. Let’s imagine that we can think of a set of characteristics that matter and that we think are going to make for a good program director. And that’s going to be more important than specifically their resume or what they’ve done before. And then we decided that we’ll bring them in as a cohort. So, part of the idea here was, if it’s going to be a risky thing for somebody to come join ARIA at the early stages, it becomes a lot less risky if, when they’re thinking about joining, they can look around and see five or six other people that they think are pretty awesome, who are also going to jump into that pursuit.

And I think that worked out really well. If you look at the first set of program directors, we’ve got someone like davidad who, I think he got his masters degree from MIT at age 15. I don’t think he ever finished his PhD. He ended up working at places like Twitter doing independent research. And he sits in our office next to Jenny Read, who is like a seasoned senior professor at the University of Newcastle — in different fields.

And you have all these other people, and they’re so spiritually aligned, and respect each other, and push each other. It’s really cool. [pause] We were talking about new program directors, but I didn’t get to it.

Eric: No, no, it’s okay!

Ilan: What would you want to see from ARIA’s next program directors?

Eric: [Laughter] What would I want to see?

Ilan: Trying to figure out how to...oh you’ve met some of our, you’ve met our existing program directors! If I were to say, like, “Okay, you have the chance to double the size of the group of program directors and make it an even stronger group. What would you try and sprinkle into the mix?”

Eric: So, that’s tough for me [laughter]...because I’m not a technical genius or a polymath in any way. I’ve been very intrigued by the energy of everybody involved [as an ARIA program director] and I’ve always left excited. But I guess, I don’t know. Engaging in this work as a non-technical person...

Ilan: Yeah.

Eric: ...I more just go in with the assumption of, “Somebody sees genius or a spark of something in this person. I’d love to help them any way I could!” I guess, reading the history... it’s unclear that it would be obvious to anybody, or me going into the past that, like, Frank Heart would be Frank Heart, or J.C.R. Licklider would be Licklider. So, I guess I don’t know...I attempt not to answer these questions or go down this line of thinking because I think I would be biased by random things, probably. For example, I go talk to [ARIA-related] people, and most of them are British. And it’s like, this is a new cultural context for me. Sometimes, with people in my personal work, I go based on spark or energy or something like that. But I don’t think that’s quite how a British scientist would do it. So I don’t really know. I won’t answer your question, essentially!

[Post-interview note: As I transcribe this interview, I wish I would have flagged that some social science program like a computational law program could be cool!]

Ilan: Yeah, interestingly, it goes to the intellectual humility point. You said something that resonated with me, which is like, “I imagine someone saw a spark of genius or brilliance in them.” So we designed our process to recruit program directors — I think we started, the first time we did it, we had seven qualities we were looking for. And they have names, like, obviously like ‘technical depth,’ but we have one called ‘vision to action,’ ‘adaptability,’ etc. We basically put all the applicants through the paces in different formats. We were probing them in different ways to test along those axes. And the idea is not to just have some aggregate score for someone who’s great, but the idea is to find the spikes. We talk a lot about how each of our program directors has a different set of spikes, meaning like superpowers that they’re going to leverage to do the job in their own ray, recognizing that a Licklider has very different strengths than a Bob Taylor, right?

And I think that’s worked out really well. We did the same thing with this new cohort of program directors. But we looked at our first set of program directors and what we learned from them, and we realized a few things. One was, there was something that they were showing in their behavior that we hadn’t tested against, which is something like ‘value recognition’ or ‘opportunity recognition.’ The ability to see the dots and find the constellation within them. So we added that to the mix. We also deliberately tried to recruit...our first set of program directors, roughly 2/3rds to 3/4s of them have more academic backgrounds. They tend to be sort of — I don’t want to offend anyone — misfits? They tend to have different mindsets than your typical academic, that’s why they’re attracted to this role. One thing we tried to do deliberately with the new program directors is say, “Let’s try and bias towards more people with industry or startup experience,” which is the case. So, what can I tell you about them?

Eric: Can you give us a couple examples of program directors who clearly have overlap with an opportunity space from the first cohort? And any examples of people who are, kind of, breaking new ground?

Ilan: Yeah, so a lot of them are breaking new ground. Actually, we’re already starting to see a bunch of different connectivity between them.

I’ll share one. One of our incoming program directors, Rico [Chandra], is Swiss. He studied at CERN, he’s a nuclear physicist. He then decided to go do a startup in the nuclear security space. He’s coming into ARIA, and the thing he’s become obsessed with is this question of...the fact that with all of our modern technology, flight and the ability to transport things in the air is still a big challenge, especially sustainably. And his view is that, “Actually, we know that there are plenty of birds, albatrosses and others, that can go vast distances, thousands of kilometers, without any source of power, in perpetual flight. Why is it that we can’t beat them with modern technology?”

So, you know, with our incoming program directors, we basically say, “Listen, just have a starting point, and then we’ll go from there.” We don’t know if it’ll turn into a program, if it might pivot or not.

Eric: It’s also interesting because more recent people in aeronautical engineering who we think of as geniuses, like Kelly Johnson, [often] thought in wind tunnels. But when you go back to the Wright brothers, they were obsessed with birds. Like there were all these stories of them on the beach where they were apparently — I forget if it was Wilbur or Orville or both — they were impeccable at imitating the motion of the birds’ wings.

Ilan: Oh I love that.

Eric: [gesturing to imitate the Wright brothers imitating the birds] As they were trying to figure it out. So it’s fun that...to find a really ambitious program, he’s also kind of gone back to the source.

Ilan: So one of the interesting things about Rico is he also happens to be, like, a world-record holding long distance hang glider. So he’s been thinking about this a lot. We don’t know whether it’s a program, but one of the things we realized...we have an opportunity space called Scoping Our Planet. And the thesis there is, “With climate change, the thing we really care about is the climate changing. We obviously care about and know that fossil fuels and greenhouse gas emissions are causing the climate to change. But there’s very little we know and very little energy has been put in by the innovation community to understand how we monitor the climate.”

And you can think about why that’s important. Everything from measurement and verification of things like carbon removal, which is sort of a big and unsolved market failure problem. But you can also think about weather prediction. You can think about understanding climate tipping points, which is what our program is focused on. Rico came in and we realized, “Oh, is this like a new aeronautics opportunity space?” And then we realized, “Well, maybe this is just the capability that can be very valuable in scoping our planet.” So now he’s talking to Sarah [Bohndiek] and Gemma [Bale] [the Scoping Our Planet program directors] and trying to understand, “Is this something that can be game-changing around how we have new sensors for parameterizing the earth and communication protocols?” So that’s kind of an interesting, surprising one [new program idea] that connects to something we’ve done.

Eric: So, it seems like you really do hire people first, and find the specific programs later. A lot of your first cohort of program directors are working on programs that, like, it’s maybe not what their academic lab focuses on. Are there any people you’ve hired in this new cohort where you think, “Oh, what they might end up working on is exceptionally broad.” You’ve hired them with a guess, but it’s hard to tell where precisely it will go.

Ilan: I think that’s true of a number of them. I was just chatting with one of our incoming program directors, Alex [Obadia]. Alex is really interesting. He’s a mathematician by training, who then got involved in cryptography. He’s been doing essentially crypto and blockchain stuff, but he’s really passionate about thinking about how the kernels of innovation in real cryptography, that’s being applied to financial systems and otherwise, are going to be consequential to the future of society.

He turned me on to — folks should look this up if they haven’t — this paper on programmable cryptography. The idea there is, right now you think of cryptography as, “Okay, I have a certain piece of data in a discreet way. It’s encrypted or it’s not. I can see it or not.” There’s a whole community of people, now, thinking about, “Could I have a whole program that’s encrypted? Could I have a computer program that goes and does programming on your data without actually seeing your data, because of the encryption?” Or even a computer program that is doing computation and getting answers based on data where no one actually knows what the program is. And you think, “Like, what are we talking about here?” But clearly, as we think about AI, and AI agents playing a bigger role in our lives, there is a question of, “How do we optimize the efficiency of what we can learn and the value we can create with AI, where one of the big barriers is privacy of data?”

So, you can imagine — and I’m not an expert here — but the sense I get is, you can imagine programmable cryptography allowing me to, say, have a set of preferences, my values, things that are very sensitive to me, where I can tell an AI agent that is going and engaging in some democratic process on my behalf. Or I can have an election process that runs a program where it queries, “What are my really sensitive personal preferences?” and has it feed into an answer of a program without ever seeing my data.

So I got very excited about this! And I said, “Alex, this is massive, this is definitely an opportunity space!” And his view was, “Yeah, but I think enough people are already working on this, it might happen anyway.” And we got in this big argument. So now he’s thinking about, “Actually, what’s the next stage beyond that?” We have this massive convergence that’s coming, where we’re going to be fusing humans with technology in new ways. You can think of neurotech. You can think of, you know, just the way we’re much closer to devices. What does preserving privacy and trust look like when your devices are not purely digital, purely physical, or purely biological, but somehow sit at the intersection? I don’t know whether there’s a ‘there’ there, but that’s what he’s starting to explore.

Eric: You seem to have a number of life sciences-adjacent folks in the new cohort.

Ilan: We do.

Eric: What’s the thinking behind that?

Ilan: It’s a good question. Again, it’s another indicator that we really were people-first. When we got the first cohort, we realized there were really only two program directors working on things related to life sciences and biology — Angie, on Programmable Plants, and then Jacques [Carolan], who has the Precision Neurotech program within the Scalable Neurotechnology space. But if you look at the UK, it has incredible strengths in biology. If you look at technology vectors that are progressing extremely quickly — synthetic biology, right? You have all these pieces. So, shouldn’t we have more?

We do have more program directors thinking about biology in the new cohort. Brian [Wang] is an organic chemist, but then moved into thinking about pandemic preparedness. And he still cares about that very deeply, and one of the questions he’s asking is, “Can we utilize new learnings about the innate immune system?” The innate immune system is the part of your body that reacts to pathogens and toxic in broad spectrum ways, right? So it’s not creating antibodies to specifically attack a specific vector, it’s just that initial response. It turns out, actually, the way plants deal with pathogens is entirely innate immune system. And his view is, “Well, maybe we can be inspired by that to figure out how to create therapeutics that can be effective against new pathogens, new bugs, that we haven’t seen before.” And there could be a number of implications to that work where, through that same inspiration, basically the question is, “How do you get ahead of things that are evolving?” You know, you think about the Covid experience. But cancer is the same way, right? How do you get out ahead of something that is a foreign...

Eric: So, when you’re selecting program directors, you’re in a room and you have some exceptional electrical engineer who wants to work on some project nobody has ever done before. You might have a biophysicist interested in some medical area. You might have somebody from a field that doesn’t even have a name. How do you go about...? You have to come out of there with eight people. What does that prioritization even look like? Is it painful, because there truly is no apples-to-apples comparison? How does it feel? What do you do?

Ilan: No, this is actually where the approach...Historically, I think I always felt like I had a pretty good instinct on talent. You know, you hear about this in research and otherwise. I mean, you’ve written about this, which is just, like, there’s a taste and there’s ability to spot talent. And that’s something I always try to be attuned to, and refine.

I think over time I’ve come to realize that one of the best ways to find talent is actually to just create a product that really talented people want, that doesn’t exist. If you think about the ‘product’ we have at ARIA, you have, in this very open way, an ability to take £50 million and figure out how to create a wave that changes the world. That’s really compelling if people believe you. So that’s one thing that I think has changed where you say, “Okay, that’s a great way to attract talent.”

The other thing is, and the big lesson for me around our program director recruitment, by trying to strip away to first principles around, like, “What do we really care [about] in terms of the characteristics of these people?”...and this is very much like a Kahneman-based approach of recruiting and selecting people, which is just like, “We’re going to have the criteria. We’re going to probe the system a bunch of ways. We’re going to see how they spike against the criteria.” And ideally where that ends up, to your point...when we went through that process based on paper applications, phone call screens, technical interviews, we ended up with this set of people — this year I think it was 16 — where we said, “Based on everything we’ve seen, any one of these 16 people could be a program director.” Because who are we to know? Like again, the intellectual humility. I could guess, but I’d probably be wrong.

So then we said, “Forget it. Rather than just trying to pick the right ones out of the 16, let’s actually bring the 16 people together.” One thing that’ll happen is...these are awesome people who will go drive impact in the world, and they’ll probably all do more if they’re connected to each other. But it’ll [also] give us one more way to look at how they show up, not just as individuals, but also how they sort of connect to each other.

Basically, at the end of the process, we’re just thinking about the portfolio. We’re thinking about the portfolio of people, portfolio of ideas, based on what we think they might do, what they might bring to the cohort. Just curating based on that.

Eric: If I can probe you with a bit of an edge case from history, I’d love to get your...

Ilan: Oh boy, I might not...

Eric: So, speaking of intellectual humility, I’m a big Warren Weaver fan.

Ilan: Yes!

Eric: And something that comes out all throughout his writing...he is an exceptionally...he’s a Midwesterner with a lot of humility. It comes out in all sorts of his [writing]. So when he first came to the Rockefeller Foundation, even though he had humility, he had one of the more extreme bets in philanthropic history. The [Rockefeller] Natural Sciences Division, which gave out on the order of what ARIA gives out per year, maybe a little less. It’s hard to do a one-to-one, because science was cheaper back then. But, essentially, they [Weaver’s predecessors] said, “Oh we fund electrical engineering, zoology, etc. And we fund the very best people who come in.” And when he came in, he said, “That’s fantastic. We’re not going to do that anymore.”

When he’d gone around and talked to people, he said, “There’s something right there in that area between biology and physics. So, yes, our budget is really big, but it’s very finite. We’re going to press on that.” And he essentially put 80% of his budget towards — it was 1932 — five years later, he would name it ‘molecular biology.’

Ilan: Out of curiosity, do you know how long he was in the foundation before he made that bet? You probably do.

Eric: I think he came in with the bet.

Ilan: Oh okay!

Eric: He took the interview with them to say, “I don’t think I’m your guy. I’m just an applied mathematician. But there’s this thing..."

Ilan: “Here’s the thing we would do!”

Eric: Yeah. He read very broadly, for sure. And he kept at it [funding molecular biology] for 20 years before moving on to something else. But if you all felt you had an ARPAnet or a molecular biology on your hands, how much is too much of your funds focused on that one area? There’s maybe a limit. 80% is a lot, for example.

Ilan: Yeah. This is interesting. This is something we talk about a lot. First of all, the question of, “We have these seven opportunity spaces. Why are we recruiting more program directors? You know, aren’t we doing enough? Like the goal isn’t just to boil the ocean.” And actually, we tend to think really deliberately about, “We need to get to this one outcome that is so massive. Do we think we’re touching enough surface area right now to fast forward ten years, and realize we got lucky and we just noticed that thing that was going to be so valuable?”

And when we looked at our budget, we looked at the size of the UK ecosystem, and we looked at what we were doing, we said, “Actually, no. We’re probably not touching enough surface area.” So we now have more program directors coming in. There will be some new opportunity spaces. We’ve also said, “There’s a limit.”

It’s likely that every other year ARIA will recruit a set of program directors. It’s a three to five year term. So that gets you into a steady state of 15–20 program directors. And that’ll be it. So we’ll have a first set of opportunity spaces. That’ll be the surface area that we touch. And really what success needs to look like is...out of that, we’ve found something that we not just want to double down on, but 10X on. And so if a big portion of ARIA’s budget does not end up in one of those areas over the others, there’s a problem.

Eric: Oh wow.

Ilan: That’s my take! You know, I’m on a term limit, too! I probably won’t be the CEO when they have to figure this out. But is that 80%? I could imagine it. We talk a lot about…

Eric: And could the person in charge of ARIA...

Ilan: Decide?

Eric: ...if they were a brave person, if they thought it was right, is that that? Are there some structural or institutional barriers that would make bravery even tougher, beyond the pure pressure of people looking at you like you’re a little crazy or something?

Ilan: One of the nice things about ARIA, it’s worth mentioning, the UK — like a number of people who were in UK government, civil servants, others, Parliament — they got this right. In the sense of, ARIA really does have the right mandate, freedom, flexibilities. There’s not political intervention, there’s not a lot of BS processes...they’re the right processes to make sure we’re responsible stewards of taxpayer funds. But one of those things is the CEO of ARIA makes programmatic decisions; that’s very much modeled after DARPA. I think that’s 100% true. And that’s good to have in place from a governance perspective. The question is, “Will the organization have a culture that leans towards the bold bet?

We’ve been talking about this a lot. So far in ARIA’s history, the things we’re most proud of are when we’ve gotten exposed to something and then we just said, “Ok, let’s do the bolder thing here.” And it happens in big and small ways. Sometimes it’s about a program director we decided to bring in. Sometimes it’s about a program that we launched. Sometimes it’s like, “Do we use Slack?” Because there are potentially any number of issues from having your Creator community on a Slack system. We just had this conversation and said, “We should bias towards doing the bold thing.” [Laughter]

And my hope is that we build into the agency that a leader in the future will be celebrated by pushing that bold bet.

Eric: I had a question written down, and I think maybe you just answered it. I was going to ask, “How do you deal with a program that you’re exceptionally excited about, but maybe the follow-on funder doesn’t get it? Like the VCs aren’t sure what to think about it five years in advance. Which is relevant, because with early autonomous vehicles, it’s not that the Army desperately wanted...they didn’t really know what to do with it. But it sounds like your answer is, maybe, “If it’s a bold enough bet, we can be the follow-on funder. For a while at least.”

Ilan: Yeah, that’s definitely our mindset. And we’ve even tried to build that in. Some ARPA agencies require cost share in their projects: “Oh, you have to show us that someone else has skin in the game by funding 20%.” We basically said, “We’re not doing that, because that actually could as easily could be a counter-indicator for us.” In the future, we think we’ll probably leverage other funders as follow-on partners, and everything else. But let’s make sure there’s nothing that prevents us from doing the bold thing.

That said, it can’t be as easy as, you know, in your scenario, “What’s going to get us to one day have 80% of our funding in one of these spaces?” It can’t just be someone walked in, looked around, and said, “Okay, yeah, let’s just do that.” We should be evidence-based. [Laughter]

We have a pretty good set of principles. A lot of this is, “What are the principles? And then what are the processes that allow us to make sure we’re holding true to those principles?” We have that for creating opportunity spaces. We have that for approving budget for programs. The next thing is to have that for portfolio allocations. Meaning, “We’ve run these opportunity spaces. Where do we think we are seeing the bigger bets emerging versus not?” So that we can say, “This opportunity space is going to get bigger or more focused, and this other one might go into hibernation because we don’t think the elements are there to create the wave.”

Eric: Yeah, no, that’s very interesting. I didn’t know a lot of that, so that was great to hear! So a bit of a question very relevant to...

Ilan: How many questions do you have?! [Laughter] It’s like an endless amount. Are you just making them up and the papers [Eric’s notes] are just like a...

Eric: Well I’ve skipped some [gestures at discarded paper pile], I’ve come up with some new ones [waves papers]. They’re not all off the page! They [Asimov Press] brought me in for a reason.

Ilan: {Laughter] He’s just got like blank pieces of paper just to make it look official.

Eric: I could show blanks! [shows the blank side of his stack of papers]

Do you spend a significant amount of your time thinking about setting up a portfolio to take advantage of AI? Obviously a lot of big breakthroughs in science history come from using the big thing from last year or 5 years ago to apply to some new area?

Ilan: Yeah, it’s a really hard one. I mean, the simple answer is, “Yes.” We are spending a lot of time thinking about how AI — the fact that we’re starting an agency like ARIA at this moment in time, given what’s happening in AI development. One of the easy inspirations for new programs at places like DARPA or ARPA-E is, “What are the technology vectors that are making incredible progress? What are the learning curves you can ride?”

So, I remember at ARPA-E, we had a number of projects we funded based on the fact that fiber optic lasers were getting much cheaper and more powerful year after year. So we had a project we funded on basically using that for geothermal — like drilling hard rock — and other things. AI is like that, just massively.

I think we’re trying to be a little bit deliberate before we figure out exactly what that means for ARIA. For instance, we haven’t jumped in and built, for ARIA, a major compute cluster. We’re starting to think about, “What does an AI program director look like?” You know, how to actually do a lot of the soundboarding that we do. Our program directors are actually using AI. It turns out AI is actually, like, an incredible tool as a program director. Because often you’re looking at things outside of your area of expertise. Oftentimes you’re like, “Oh, if only I had an expert that I could bounce this off of!” Having a thousand experts in all the areas at your fingertips makes a big difference.

I think the much more powerful part is, when we think about these opportunity spaces, one of the questions becomes, “Relative to the impact we think AI could have on this space, how much activity is there to start to deploy that?” And I think that’s going to be one of the important...especially for this new cohort, we’ll end up with some programs that really have AI at the center.

But I think for all of them, there will be this question of, “In this space, where are we in terms of the max benefit that AI is going to build by integrating with this discipline or set of fields, versus now?” And I think that will help dictate how much of an AI flavor we have in the space, and what we’re doing to be differentiated. I actually don’t know if I believe that answer that I just gave, but it sounded good.

Eric: Before we move on, is there any other technology you spend a lot of time thinking about? The world of science and engineering is broad. There might be something else that you think people don’t pay enough attention to.

Ilan: I mean, there are little examples. Like expansion microscopy, that’s such a cool thing! Most people don’t know! It’s popping up in different places.

Eric: For people who don’t know, the TLDR on expansion microscopy is, “What if you made the sample bigger!” And...

Ilan: By literally just putting it in a gel and expanding it. And it works! It’s unbelievable.

I don’t know. I think synbio comes up a lot. I think data, beyond just AI, data comes up a lot as an area where, when you look at some of these disciplines...this is something we’ve found in some of our climate work. You look at the best repositories and the most valuable repositories of data around climate and weather, and realize that none of them are engineered to be accessed in a way that’s compatible with modern data techniques. So there are just infrastructure gaps where you think, “Okay, there’s something cross-cutting around data that we can do.” Or a barrier that we need to get over.

Eric: All right. So I have a suite of metascience questions for you.

Ilan: Okay.

Eric: So, you can go rapid-fire responses, or spend time on them!

Ilan: [Laughter] Okay!

Eric: Do you consider now a great time to work on metascience?

Ilan: Yes. It’s probably the best time to work on metascience that has existed in my life.

Eric: You’ve done this for a few decades, depending on how you want to look at it. Were some periods a lot more frustrating than others?

Ilan: When I left ARPA-E, I wanted to go start...actually, I may have sent you the paper, I had a paper...

Eric: ‘ARPA Lab.’

Ilan: Yes, ARPA Lab. I wanted to create an ARPA Lab. And the point was, like, “ARPA-E is great as a funding agency. The problem is I don’t have resonant institutions to fund. So let’s imagine a lab that is ARPA-minded, that is very entrepreneurial.” And I sort of mapped it out. It was probably like a lab that would have been a compilation of FROs.

And I thought maybe we’d get philanthropy to fund it. And, you know, who was I? So maybe someone else could have done it. But like, crickets, you know, nobody! You know, philanthropy funding science, it sounds like it was a long time ago; it wasn’t that long ago. But the state of affairs, the default for philanthropy and science historically, probably for all time — you can tell me if I’m wrong — has been like, “Oh, I have a family member who got this disease, and I’m going to fund research on this disease.” Or, “I went to this university, so I’m going to give them money to do scientific research.” The idea that you’d have philanthropists making big bets like Convergent Research or Arc [Institute], in terms of new modalities for R&D, that is a new phenomenon and a really exciting one.

Eric: Speaking of something like Arc...

Ilan: This is meant to be rapid fire! [Laughter] You let me go on!

Eric: A lot of people conceptualize the new science orgs as experiments, in and of themselves, in how to do science differently. ARIA is also some version of this. Is it difficult to see what’s going on at a place like Arc, and, if there’s a useful learning, fold it into your operation? Am I not thinking about that right?

Ilan: I think you are thinking about it right. I think the biggest thing — as someone who grew out of venture capital, startups, and Silicon Valley — the thing I’ve realized is, the power of a vibrant ecosystem of startups is you create evolutionary pressure for institutional change. Meaning, nobody talked about OKRs until Google came around. And then everyone needed to do OKRs! And then Stripe came around, and I don’t know whether Stripe does OKRs, but they do things differently. And then all of a sudden it’s like, “Oh, that’s the way to do things.”

It drives you to say, “Oh there are competitors, or peer organizations, that are figuring out better ways to do things institutionally.” And that’s keeping the system super fresh. We don’t have that in research. The institutions are so stagnant for so long that you don’t have the evolutionary pressure to change.

For me, what metascience means is: go run those experiments and find ways to start diversifying and creating a more vibrant institutional ecosystem. Partially so you can get that institutional pressure! You need a critical mass of those things to get that institutional pressure.

So you asked, “What is ARIA learning from Arc?” I love Arc as an experiment, and I think it’s going to change the world. I initially was skeptical that Arc was going to be so close to Stanford as a university. And that they were going to hire people that were still in the academic incentive structure. I think, actually, it’s probably proving me wrong on that. And that’s a great learning. But it’s a very high level, like from a distance, learning.

The beauty would be if we had enough of these things where I could tell you that, “With a 90% certainty, that some one in ARIA’s team, in three years, will come from Arc.” Like if you look at startups in the Valley, right, like, “What are the chances that someone who was at Tesla will end up at another one of these companies?” Absolutely, right? That’s one of the things that drives that learning. It would be awesome if, within the R&D ecosystem, we had that kind of vibrancy and mobility, because I think then you really get the learning.

Eric: And if you personally had the funds, for whatever reason, to fund additional orgs to complement ARIA, like completely different metascience experiments, does anything come up in your head?

Ilan: [Laughter] Yeah, what came to mind, just thinking about your audience, was a conversation with Michael Nielsen when we started ARIA, who was basically giving me a hard time: “What you’re talking about doesn’t feel that differentiated. Where’s the gap? What about a research organization that gives 100-year grants?” The idea of, “We don’t have long term modes.” If you think of time constants as one of the axes of the portfolio, there’s not a lot of diversity on time constants, to like 100 years. Which I loved! I basically said, “Yeah, but if I look at ARIA’s mandate, actually, ARIA’s mandate is not to create new fields.” That’s important. It’s not like [to create] molecular biology. We are built to get something to a new technology platform or industry base. And I don’t think the hundred year timescale is going to work for that.

But I think long duration...basically modes of getting talent focused on either creative research or creation research for long periods, I think there are far too few modes for that, and fewer than there used to be.

Eric: So, that’s obviously ambitious. It’s also expensive. ARIA is pretty expensive, Arc is expensive. Do you think you need a minimum amount of funds to do a good metascience experiment? Do you have low-cost ideas?

Ilan: Well, I don’t know if the long-term thing is expensive. I mean, look, what is expensive? It’s all relative to the potential impact. You have to normalize it, right? So, one of the things I’d love to see someone do is...I think a lot about, “How do we train scientists?” Translational scientists in particular...there aren’t great training environments anymore for translational scientists. One thing I’d love to see someone do is basically say, especially with AI, the training is going to be less and less about the knowledge, and more and more about the taste, the tacit knowledge. and the instincts. So apprenticeship is really important. Why don’t we take kids that are high potential — and when I say kids, I don’t know whether I mean age 15 or 22, who knows? But take high potential people and basically say, “We are going to engineer for you a program where the next 15 years of your life you are constantly being taught how to do research, translational research, through a series of apprenticeships with incredible people.”

And maybe that’s in conjunction with a university, maybe it’s not. To pay for that, you can basically say, “We’ll give you fellowships,” or “You’ll work part of it.” That sounds very expensive, but my instinct is that if you did something like that, you could create the super researchers of the next generation that change the world. So probably not that expensive. [Laughter]

Eric: I’d love to poke on that...

Ilan: Maybe that’s too expensive.

Eric: ...but I’m going rapid-fire.

Ilan: Let me give you one more!

Eric: Yeah, for sure!

Ilan: Very cheap metascience experiment, probably the cheapest one I can think of. I noticed in my PhD, and actually when I hired for my startup, I found myself hiring people...a mode that I would hire was someone, who went into their PhD, they totally butt heads with their advisor, and they walked out. They ended up having to change advisors, or even complete disciplines, and then they thrived. And they come out with this like, “Oh, that was a horrible experience. But it made me change and I’m in a good place.”

Anyway, I keep thinking, I found an amazing PhD advisor that was really resonant. I didn’t waste my time. I felt like I hit the ground running. And I had this incredible experience. So a simple idea: a matchmaking app for PhDs and their advisors, when they come in. If you could increase and improve the compatibility of a PhD student and their advisor, on whatever axes, I think that ends up being a big deal. And it’s basically free.

Eric: Okay, great. That’s fantastic. Thinking of ARIA as a kind of experiment in and of itself, what’s a current bottleneck you all have that you’re very eager to find a way around or work on? There’s always small things in working on an organization.

Ilan: I’ll tell you what comes to mind. It’s kind of a hard one, but I think we’ll probably have to solve for it. We want to move fast in our programs. The view is, “You’re doing something speculative, so time to the next learning cycle is really important and valuable.” And we want to be funding people with diverse skillsets in diverse institutional types. Some institutions...the kinetics of the institution are very slow. And yet, we still want to fund people in those institutions. So one of the questions becomes, “If the kinetics of the institution, just in terms of how fast they can get stuff done, are generally very slow, but you have a Creator in that institution who wants to move fast, how can we help them move faster?”

And I actually think the only answer is we need, like, a fixer. We need an organization whose job it is to de-bottleneck activities within other institutions.

So my imagination is, Eric, you start the Research Speed Fixing Company, and we contract you, and you know, Jenny has found this great performer, but things are moving too slow in this institution. And Jenny gives them a phone number, that’s like a magic phone number. And they call it and you say, “Eric’s Fixing Services! We’ll send someone over right away!” And someone shows up in that institution, and they're running around the admin, just like putting pressure on things and getting people to move faster!

Eric: There are actually things like this in DARPA history.

Ilan: Are there? Amazing!

Eric: I can’t think of one from a performer, but I can think of one from central office. So, for example, when you read through all the oral histories, there’s this guy from early IPTO — which is computing office — Al Blue. And his name just keeps coming up as the guy who makes any bid you want to put out legal, workable, straightforward. I don’t know if he was an engineer or scientist or anything like that. He might have been one of the military guys who finds a way in and has to make his way in the office.

But that kind of stuff makes a big difference! Like in the same breath where they’ll be like, “Oh Licklider was a god,” they’ll also be like, “Al Blue made X thing happen. You need to talk to him.”

Ilan: Yeah! Well, we’re trying to build it into the culture! Right? Like the program directors know...it’s my [Ilan’s] job to have some pressure around, like, learning cycles, it’s their job to do the same. Hopefully we’ll create a Creator community...picking people that are intrinsically motivated, so they want to be pushing the kinetics of what they’re doing. And, yet, it would be really nice if you had more help on that.

Videographer: Time for a battery swap.

[Camera Break]

Eric: Alright, next in the rapid-fire questions…

Ilan: Can we, can we just pause for a bit. I love that we’re doing this long form thing, but people have to realize that this camera right here — there’s a camera with like a bag of ice on top of it because we’re going so long that it’s overheating. Which is great!

Eric: We’re making it work, though. I think the camera looks great, you know? It’s like when you go in the locker room at the end of the game and everybody’s got ice on their knees.

Ilan: Yeah, totally.

Eric: Both teams played hard.

Ilan: We’ll feel like we played hard today. [Laughter]

Eric: Is there anything you personally think people who write about metascience spend too little or too much time on? Like is there some hypothetical Substack where, as the CEO of ARIA, you would hoover up if somebody wanted to spend the time on it? I already have homework where I have to write a Rad Lab piece.

Ilan: That’s right! You do have to write a Rad Lab piece. Multiple! There’s like a series there. Oh, you also need to write a piece about how, actually, DARPA ended up emerging in part because of the UK’s radar effort. Which is important for me because it brings things full-circle to ARIA.

Metascience...honestly, what I would love is a blog that just chronicles metascience experiments and their learnings, and just keeps tabs on them. And that that grows and grows.

Eric: And what are variables that you think should be...some of would be qualitative, you meet them where they are...but would there be any underlying variables you’d want if somebody was writing about Convergent or Arc or ARIA, to constantly revisit?

Ilan: Incentives.

Eric: Incentives?

Ilan: Incentives. I think that is the only theme that matters. [Laughter]

Eric: Yeah, I think that makes sense. Do you have any call to action for any groups involved in metascience, or who would want to be involved in metascience, that you think would be useful to put out there? That can be researchers, engineers, ops people, policy people, whatever it is I am.

Ilan: I’m going to say something controversial, which has been on my mind a lot, which is...I think metascience is, at the same time, one of the most important movements, in terms of driving more progress out of research, and also in some ways one of its most dangerous movements.

The reason I say that is, when I was at ARPA-E, I was really interested in the question of, “How does ARPA-E understand its impact, map its impact, and measure it?” And I tried to dig into how we could do that. And both from my explorations of the community of people thinking about that and from the many activities we had to go through at ARPA-E to try and show and prove our impact, how things work...the amount that was “useful” was probably 10%, and the amount that was, “Actually, you’re trying to map something that doesn’t make any sense onto what we’re doing. You don’t really understand the context of how we work, and you’re trying to measure it. And you have a number of theories, but even when I tell you they don’t map on here, you don’t believe me,” actually led to a lot of inefficiency.

So I think what I would say is, if you’re in metascience, recognize that first of all, if you can do something experimental which pushes that evolutionary pressure on the system, great! If you can show there are better ways to do things by doing them and then having results, amazing! If you’re working more on the theoretical side or the evaluation side, just recognize you have a big responsibility, which is to make sure that when you add up all the hours of people who are engaged with that — from agencies doing the work, startups doing the work, or whatever else — that you have high conviction it’s going to be net benefit as opposed to net cost. Is that...?

Eric: No, that’s perfect!

Ilan: I feel like I’ve said that to people, and I think I’ve offended them in some ways, but I think it’s a really important thing to be thinking through.

Eric: No, that's perfect. We’ll end the official questions there. That’s Ilan Gur! Thank you so much for doing this and how long you were willing to spend with me today.

In the episode, I discuss:

• FreakTakes as an applied research shop, and how I choose what to work on

• The role Bell Labs-style systems engineers can play at new science orgs

• How I might give away $100M, inspired by Warren Weaver and the Rockefeller Foundation

• BBNs at early ARPA, the upside of building more BBNs today, and why I joined RenPhil to work on this challenge

• The effect of events like Watergate and Vietnam on scientific bureaucracies

• What Gerald Holton and certain scientists’ oral histories have to say on the ‘burden of knowledge’ as a human systems problem

• Tons of R&D history anecdotes, including:

  • The complicated takeaways of Claude Shannon’s time at Bell Labs

  • Wilbur Wright’s taste

  • Irving Langmuir at GE Research

  • Praise for early MIT and the role of market signals in shaping their research agenda

As always, just email me (gilliam@renphil.org) to discuss any ideas discussed in the episode! I’m particularly eager to spend time with those who are curious about founding for funding BBNs.

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Introduction

Many experts believe we are living in a post-Moore’s law world. NVIDIA’s Jensen Huang and computing legends like John Hennessy and David Patterson count themselves among them. But that does not mean these predictions spell doom for the computing field. Their predictions simply acknowledge that we are approaching the end of the “there’s plenty of room at the bottom” era of general-purpose computing — and moving on to another.

As Hennessy and Patterson point out, this shift hearkens the semiconductor ecosystem back to a style of work that was common before the 1980s — an era FreakTakes has covered extensively. In this piece, I’ll detail how the best teams from that period operated and why it’s necessary to bring those operating models back to thrive in this new era of semiconductor design.

The piece is broken up into three sections.

• In the first section, I briefly cover the history of the “there’s plenty of room at the bottom” era.

• In the next section, I explain what experts believe a “there’s plenty of room at the top” era could look like. Current researchers and veterans like Hennessy, Patterson, and Leiserson et al. believe the shift to looking for progress at the top of the computing stack will involve the vertical integration of research teams and a focus on domain-specialized hardware.

• In many ways, this is a shift back to how computing research groups used to operate before the 1980s. So, in the third section, I will summarize key management decisions that characterized some of the best old school computing organizations — such as BBN and the CMU autonomous vehicle groups.

With that, let’s get into it.

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This piece heavily draws on two prior FreakTakes pieces on the BBN and CMU teams:

• “The Third University of Cambridge”: BBN and the Development of the ARPAnet

• An Interview with Chuck Thorpe on CMU: Operating an autonomous vehicle research powerhouse

Readers familiar with the basics of semiconductor history may skip the first section. Readers familiar with Leiserson et al.’s “There’s plenty of room at the Top” paper may skip all but the final three paragraphs of the second section.

There was plenty of room at the bottom

The optimism that drove the early Moore’s Law era of general-purpose computing is well-characterized by Richard Feynman’s “There’s Plenty of Room at the Bottom,” speech to the American Physical Society in 1959. In his speech, Feynman implored scientists and engineers to focus their efforts on the exciting opportunity of engineering biological, electrical, and physical systems on exceedingly small scales. He believed we were nowhere near the limitations of physics when it came to engineering systems on these scales. So, he asserted that the area was ripe for talented engineers and scientists to pile in and build a world of systems whose possibilities were orders of magnitude beyond the status quo in 1959.

For decades, the semiconductor field did just that, doubling performance every 18-24 months until the early 2000s. It still continues to excel at a remarkable rate, simply with more tradeoffs than we have become accustomed to seeing. The practical foresight of individuals like Gordon Moore in his 1965 Moore’s Law paper, Robert Dennard et al. in the more technically-detailed 1974 Dennard Scaling paper, and Gordon Moore again in his 1975 paper — summarizing of the field’s progress and providing updated predictions for the coming decades — largely held true until the early 2000s.

As the early 2000s approached, it was becoming clear to many in the industry that the general approaches outlined in the Dennard Scaling paper were not going to continue to provide the same improvements. The aptly named 1999 Paul Packan paper, Pushing the Limits, outlined several physical limits the field was approaching with the current approaches — including thermal limit challenges. Many of the specific challenges Packan outlined in the paper had no known path of attack that did not entail major trade-offs. Industry attempted to take alternative paths of attack to continue to scale computing power — such as the increased emphasis on multi-core processors — but the limitations researchers like Packan outlined have proven to be quite difficult. Since the mid-2000s progress in the field has continued, but it has not been Moore’s Law-level progress.

So, if there is not much cost-efficient room to be found at the bottom, where should the field look? Well, many researchers believe the natural place to look is: the top.

There’s plenty of room at the top, but…

In Leiserson et al.’s 2020 paper, There’s plenty of room at the Top, a group of researchers from MIT outlines a vision for the potential gains in computing power by focusing on the top of the computing stack — software, algorithms, and hardware architecture. They are quick to point out that this approach will require divorcing one's thinking from the “rising tide lifts all boats” approach which many became accustomed to under Moore’s Law. The authors write:

Unlike the historical gains at the Bottom…gains at the Top will be opportunistic, uneven, and sporadic…they will be subject to diminishing returns as specific computations become better explored.

The authors paint a broad picture of what this integrated approach will look like, writing:

Architectures are likely to become increasingly heterogeneous, incorporating both general-purpose and special-purpose circuitry. To improve performance, programs will need to expose more parallelism and locality for the hardware to exploit. In addition, software performance engineers will need to collaborate with hardware architects so that new processors present simple and compelling abstractions that make it as easy as possible to exploit the hardware.

The authors then go on to demonstrate a toy example in the area of software performance engineering. They use a simple baseline problem as an example, multiplying two 4096-by-4096 matrices. To start, they implement this in the Python code that minimizes programmer time spent. They then proceed to do performance engineering until the same function eventually runs 60,000 times faster — first by changing to more efficient coding languages, then introducing parallelization, and beyond.

At the end of the performance engineering section, they reflect on what it will take for teams of researchers and engineers to effectively take advantage of opportunities analogous to this one in the future:

Because of the accumulated bloat created by years of reductionist design during the Moore era, there are great opportunities to make programs run faster. Unfortunately, directly solving [some arbitrary, domain-specific] problem A using specialized software requires expertise both in the domain of A and in performance engineering, which makes the process more costly and risky than simply using reductions. The resulting specialized software to solve A is often more complex than the software that reduces A to B. For example, the fully optimized code in Table 1 (version 7) is more than 20 times longer than the source code for the original Python version (version 1).

The authors’s next section explores a few major successes in the history of algorithmically-driven computing performance. They use the history of algorithms for matrix multiplication as a key example to note that while the history of algorithm improvements has been a bit uneven in terms of rate of discovery, in certain cases it has rivaled Moore’s Law-level progress.

The authors highlight algorithms as another area that, while only semi-reliable, holds extreme promise for continuing to push computing progress forward. Among other reasons, they think there might be promise in this approach because many commonly used algorithms were originally designed to utilize random access memory on the serial/sequential processors of the early 1960s and 1970s.1 They believe many algorithms that take this approach use modern hardware inefficiently because they under-utilize the parallel cores and vector units in modern machines.

But, at the end of the algorithms section, the authors once again note that there is a clear difficulty in pursuing problems of this form in the modern, rather modularized research ecosystem. They write:

These approaches actually make algorithm design harder, because the designer cannot easily understand the ramifications of a design choice. In the post-Moore era, it will be essential for algorithm designers and hardware architects to work together to find simple abstractions that designers can understand and that architects can implement efficiently.

In the final section, on hardware, the authors outline the general characteristics of computing areas which they believe can continue to experience extreme performance improvements — and which will curtail. Areas that benefit from parallelism and streamlining are notable examples with a lot of potential for progress to continue. The authors use the following graphic to highlight the continued progress in SPECint rate performance — a processing performance metric which increasingly benefits from parallelism as more cores are used — as an archetypal example of a metric that they expect to continue improving at a high rate.

As designers increasingly embrace parallelism, Leiserson et al. believe “the main question will be how to streamline processors to exploit application parallelism.” In tackling this challenge, they expect two strategies to dominate. The first is that they expect designers to increasingly use simpler cores that require fewer transistors in chip designs. These simpler cores will be specifically chosen to efficiently accomplish the task at hand. For this to be worthwhile, designers must find ways to ensure two simplified cores incorporated in a specialized design can accomplish more than a single complex core.

On the second approach to tackling the challenge of streamlining processors, the authors write:

Domain specialization may be even more important than simplification. Hardware that is customized for an application domain can be much more streamlined and use many fewer transistors, enabling applications to run tens to hundreds of times faster. Perhaps the best example today is the graphics-processing unit (GPU), which contains many parallel “lanes” with streamlined processors specialized to computer graphics. GPUs deliver much more performance on graphics computations, even though their clocks are slower, because they can exploit much more parallelism. GPU logic integrated into laptop microprocessors grew from 15 to 25% of chip area in 2010 to more than 40% by 2017…Hennessy and Patterson foresee a move from general-purpose toward domain-specific architectures that run small compute-intensive kernels of larger systems for tasks such as object recognition or speech understanding.

While many interpret the belief that we have seen the end of Moore’s law as lacking in technological optimism, that does not have to be so. Hennessy and Patterson’s 2017 Turing Award Lecture on this topic was titled, “A New Golden Age for Computer Architecture.” There’s no reason this shift in approach must result in disappointment.

The following excerpt from a version of the Turing Lecture Hennessy gave at Stanford in 2019 briefly characterizes their thoughts on what the near future of semiconductor design will look like.

I think Dave [Patterson] and I both believe that the only path forward is to go to domain-specific architectures that dramatically improve the environment and the application for that particular environment in the performance that’s achievable as well as the energy consumption. Just do a few tasks, but do them extremely well. And then, of course, combination — putting together languages which help specify applications for these particular architectures and combining it with the particular architectures.

Hennessy concludes the talk by specifically emphasizing the implications of the new domain-specific design approaches on scientific team structures, saying:

This creates a new Renaissance-like opportunity — because now unlike what’s happened for many years in the computer industry. Now people who write applications need to work with people who write compiler technology and languages; they need to work with people who design hardware. So, we’re re-verticalizing the computer industry as it was before the 1980s. And it provides an opportunity for a kind of interdisciplinary work in the industry that I find really exciting. It’s sort of like this great quote, “Everything old is new again.” It’s back to the future. And I think this will provide interesting opportunities for new researchers as well as deliver incredible advances for people who use our technology.

What did the old models look like?

Hennessy has as much of a right as anybody to be excited about the re-verticalization of hardware design and the re-introduction of the old models. This “old” era is one that Hennessy understands well; it is the era in which he came up. In the following excerpt from his oral history, Hennessy describes the integrated nature of his PhD thesis — which he called “a combination of language design and compiler technology” — on a domain-specific problem at Stony Brook:

My thesis work was on real time programming…[I worked with] a guy who was a researcher at Brookhaven National Lab [that] came along with an interesting problem. He was trying to build a device that would do bone density measurements to check for long term, low level radiation exposure among people who were working at Brookhaven. What he wanted to do was build a very finely controlled x-ray scanning device that would scan an x-ray across an arm or so and get a bone density measurement. The problem is you had to control it pretty accurately because, of course, you don’t want to increase the radiation exposure to people. And micro processors at that time were extremely primitive so the real question is could we build a…programming language that could do this kind of real time control in which you could express the real time constraints. You could then use compiler technology to ensure that they were satisfied.

After joining the Stanford department in the late 1970s, Hennessy continued to partake in projects that were structured something like the one above — such as Jim Clark’s Geometry Engine project. As Hennessy mentioned, it was normal in that era. Several historically-great computing research groups that utilized this general operating structure have already been covered on FreakTakes. Early BBN and the early CMU autonomous vehicle teams are two great examples of the dynamism of this approach at work.

While BBN was a private research firm and the CMU Robotics Institute was technically an academic group, when it came to operations and incentives, the two had more in common with each other than they did with many fellow companies or academic researchers. Both were:

• Novelty-seeking

• Committed to building useful prototypes and technology for users, not doing mere “paper studies”

• Utilized firm-like management structures

These traits led each to great success in their respective fields. The following two subsections will briefly summarize the relevant operational strategies each used in their work that the new-era semiconductor ecosystem can learn from.

Early BBN

BBN had an exceptional talent for finding ways to generate revenue through contract research and research grants that allowed the firm to build academic ideas into real technologies. In many areas — such as real-time computing in the late 1960s — BBN was the go to group for projects that required both academic research toolkits and the kind of cutting-edge engineering which academic departments are rarely structured to pursue. J.C.R. Licklider’s Libraries of the Future project, BBN’s work as the prime systems integrator and IMP designer on the ARPAnet contract, and BBN building a time-sharing computer for the Massachusetts General Hospital in the early 1960s are just a few examples. BBN’s projects often simultaneously required bleeding-edge knowledge of computing, performed a practical service for a paying customer, and could result in technology that pushed the technical frontier forward.

BBN often did all of this with relatively small, vertically integrated teams of talented people. The firm was able to recruit many of MIT’s best researchers because of its unique model of both seeking novel technical problems and commitment to building practical technology. At the time, researchers who did “paper studies” and built basic prototypes at places like Lincoln Labs often grew disenchanted; they felt their work might not be built into industry products for a decade or more. But these disenchanted individuals still felt they would be wasted and bored if they joined a company like Honeywell. But BBN presented an exciting third option. With BBN, there were no such fears. The firm earned nicknames from MIT affiliates like “the third great university of Cambridge,” “the cognac of the research business,” and the true “middle ground between academia and the commercial world.”

With this reputation and the ability to recruit top talent that came with it, small teams at BBN could do big things. The BBN team primarily responsible for building the first ARPAnet IMPs and managing the first year of the project was only about eight people. Small is how ARPAnet team leader Frank Heart preferred it. As he saw it, that small, vertically integrated team of elite talent in the relevant areas was all BBN needed. In his oral history, he described the project’s management style, saying:

I mostly I tend to believe important things get done by small groups of people who all know all about the whole project. That is, in those days all the software people knew something about hardware, and all the hardware people programmed. It wasn't a group of unconnected people. It was a set of people who all knew a lot about the whole project. I consider that pretty important in anything very big. So I suppose if you call it a management style, that would be something I'd state. I think also that they were a very, very unusually talented group. I think things tend to get done best by small groups of very, very good people — if you can possibly manage that. You can't always manage it. So if you again want to call it a management style, it is to get the very, very best people and in small numbers, so they can all know what they're all doing.

The approach Frank Heart describes is not complex, but it’s also not how most universities handle similar projects. The more vertically integrated semiconductor design becomes, the more common it will become for BBN-model groups to be the ideal team structure for research projects. If veterans like John Hennessy are right and the computing industry is re-integrating and re-verticalizing, semiconductor research funders should ensure that groups with this uncommon structure can win funding to work on the research areas to which they are ideally suited.

CMU’s Early Autonomous Vehicle Teams

There are successful historical examples of universities operating in a very BBN-like fashion, as well. For example, much of MIT’s early history as an institute of technology dedicated to serving industry above all else demonstrates this point. In the early 1900s, the Institute placed such a heavy emphasis on contract research that, at one point, its applied chemistry laboratory was over 80% industry-funded. However, a much more recent example of this mode of operating is CMU’s 1980s autonomous vehicle research groups. CMU succeeded in maintaining a vertically integrated, applications-focused ethos in a period when most universities were taking a step back from this approach.

CMU’s autonomous vehicle vision research teams — and many other computing teams at the university — had a talent for operating in a way that could only be described as “firm-like.” Many grad students who worked on projects like the 1980s NavLab project were as much project employees as they were graduate students. They generated theses they could be sole authors on, but their work often had to be a part of a team effort on a single piece of integrated technology. Also, many staff were solely incentivized to build great technology, not rack up citations and build useful technology when they could find the spare time. In his FreakTakes interview, Chuck Thorpe recalled the following conversation he had with Raj Reddy about his incentive structure as he was being hired to manage the autonomous vehicle project:

Raj took me aside. He said, “I don't care how many papers you write. I don't care how many awards you win. That vehicle has to move down the road. If you do that, you're good. I'll defend you. I'll support you, I'll promote you.”

Aligning the incentives of key staff and organizing grad students in a way that enables the group to build the most ambitious, useful system it can makes sense. But this is also not how university’s tend to manage applied projects. Few universities succeed in doing things like creating tenured research tracks that are truly equal to traditional professorships. The best staff scientists and engineers I meet from places like MIT feel there is an obvious ceiling on how high they can rise. By getting many of these key incentive alignment, strategy, and team structure questions right, CMU built up a powerhouse research team that, in the 1980s, laid the base for the autonomous vehicle revolution.

The CMU team’s status as a sort of middle ground between academia and the commercial world proved to be a clear comparative advantage for them in the early days of DARPA’s first autonomous vehicle project, the Autonomous Land Vehicle (ALV) — detailed in a prior FreakTakes piece. At the end of the project’s first stage, DARPA had to fire the prime contractor, Martin Marietta — the “Martin” in Lockheed Martin. Martin had continually pressured DARPA to give them concrete, intermediate benchmarks to hit. When DARPA did just that, Martin found ways to hit the benchmarks without incorporating the best tech from DARPA’s basic vision researchers. The basic researchers also fell short of DARPA’s expectations. Many of DARPA’s SCVision researchers seemed more interested in collecting data from the machines’ cameras and sensors to plug into their academic projects. Oftentimes, their models would not work well when plugged into real-world machines. The academics knew this not because Martin was diligently testing each of their ideas, but because the CMU research team had pushed DARPA for modest funds to build their own vehicles. Using these vehicles, they tested and iterated upon cutting-edge vision models in a practical setting. Unlike most academic departments that did not want the massive systems integration and logistical headaches that came with this engineering-heavy task, CMU wanted to do it. DARPA was impressed by the productivity of the scrappy CMU team and continued to fund them even after the ALV project ended.

To the modern eye, the most striking early success from the CMU group might be the group’s neural net-based wheel-turning system. In my introduction to the Chuck Thorpe interview, I summarized the breakthrough:

In 1988, then-CMU grad student Dean Pomerleau successfully integrated the first neural net-based steering system into a vehicle — his ALVINN system. In 1995, Dean and fellow grad student Todd Jochem drove the successor to Dean’s ALVINN — the more complex RALPH — across the country on their “No Hands Across America” tour. The RALPH system employed neural nets but also put much more effort into model building and sensor processing. Holding Dean and Todd, the upgraded NavLab was able to autonomously drive 98.5% of the way on its successful cross-country journey.

According to Chuck Thorpe, there was something specific about Dean that enabled him to make this breakthrough with such limited compute. The trait Thorpe pointed out is one very relevant to this piece. According to Thorpe, what made Dean special was that he closely worked with the hardware developers at CMU and was one of the only people who understood how to get the most out of the group’s systolic array machine. Thorpe described Pomerleau’s extreme effectiveness in getting the most out of the Warp machine:

One of the supercomputers [DARPA] built was at Carnegie, and it was a thing called the Warp machine. The Warp machine had ten pipelined units, each of which could do ten million adds and multiplies at once.

H. T. Kung was working on systolic computing, where things just sort of chunk through the pipeline. And we said, “Here's this big box. Because we're sponsored by Strategic Computing, we'll put it on the NavLab. Can anybody figure out what to do with it?” “Well, it's a really complicated thing and really hard to process.” But Dean could figure out what to do with it. Partly because Dean is a really, really smart guy.

Partly because the inner structure of a neural net is, “Multiply, add, multiply, add.” You take these inputs, you multiply them by a weight, you add them together, you sum it up, run it through your sigmoid function. So, Dean was, as far as I know, the only person…well, that's maybe a bit of an exaggeration. Some of the speech people were able to use the Warp also, because they were doing similar kinds of things…But Dean got the full hundred megaflops of processing out of the Warp machine! And then he put it onto the NavLab and we got the whole thing to work.

It was not random that CMU was working on a systolic array computer. DARPA had contracted CMU to build the systolic array machines with computer vision as an early use case in mind. DARPA hoped that the two CMU projects would prove to be complementary. While the Warp team and the autonomous vehicle teams were not working together as one at this point, Pomerleau’s hard work ensured that they complemented each other to world-changing effect.

As Hennessy pointed out in his Turing Lecture at Stanford, Google’s now-famous TPUs with systolic array processors — optimized for machine learning applications — are a key example of the coming trend in domain-specialized hardware. Research groups that operate like BBNs ARPAnet team or CMU’s early autonomous vehicle teams seem ideally suited to help build this future.2

Everything old is new again

I am not qualified to make predictions on the future of Moore’s Law or what percentage of R&D budgets should be allocated to domain-specific semiconductor design teams. But if what people like Hennessy, Patterson, and Leiserson et al. are saying is even partially true, more research organizations set up like the best ones from the past are needed. The early operating structures of BBN and the CMU Robotics Institute, two underrated giants of the old computing community, are ideal groups to use as models.

As I understand it, Groq’s approach is rather similar to what I’ve described. And it’s phenomenal to see the progress they’ve made! But the vast majority of potential use cases for this org structure might be in market areas that are too small to raise VC rounds or for ideas considered too speculative. These are ideal areas in which to deploy CHIPS Act funding to seed BBN-like organizations and research groups. Whether it be seeding groups do practical work on the most speculative ideas coming out of academic labs or building in areas that are more important to the US than they are to VCs, BBN-model orgs have to chance to connect many pieces of the CHIPS contractor ecosystem that currently do not fit together well — just as DARPA’s contractors on the Autonomous Land Vehicle project did not fit together without CMU.

With the ramp-up in government CHIPS Act funding — endowing groups like the NSTC with up to $11 billion that has not been spent yet — now is the time to ensure groups are built up that can utilize this money as effectively as possible. One straightforward way to do this is for:

• Groups like the NSTC and the DOD Microelectronics Commons to decide and make it known that they are willing to wholly fund Day 0 orgs of 5-20 talented engineers, researchers, and systems engineers organized in BBN-model project teams as contractors.

• Alternative approaches that are similar in spirit but with key logistical differences are also possible. For example:

  • Attaching similar groups to pre-existing government contractors or universities.

  • Having NSTC program managers scout a domain area and assemble these teams to best fill acute needs in their portfolios.

  • Etc.

If any relevant parties are reading this, please reach out and I’d be happy to discuss alternative approaches and bureaucratic details. What is important is that research groups like the ones I’ve described find a way to get funding somehow.

On the university end, it would be great if institutions could quickly find ways to establish homes for research groups like this, with incentivizes and team structures that align with the task at hand. But given the difficulty of making decisions within universities that upset the natural order of things, this can often be slow and requires tough “consensus building.” So it’s maybe not worth holding our breath on that.

In the post-war period, it was common for government R&D funders to be the first — and sometimes only — major funding into new organizations of talented individuals. If they felt the team could do work that was good for the country, they took the risk. This was a common path to starting technical firms for grad students and professors. The market sizes were often modest and the teams often didn’t raise VC money. But the best of MIT, CMU, or the University of Illinois could simply set up shop as a firm and solve whatever problems the government needed them to at a fair market rate. With this recent, strong push to make things happen in the American semiconductor ecosystem, talented groups might have the chance to do something like that again.

Thanks for reading:)

Also, while doing background research for this piece and trying to make sense of the technical and management trends in different eras, I found the writing of Hassan Khan exceptionally helpful. I encourage any FreakTakes readers to check out his blog here.

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If you would like to read more, check out some of the following FreakTakes pieces on related topics:

• “The Third University of Cambridge”: BBN and the Development of the ARPAnet

• An Interview with Chuck Thorpe on CMU: Operating an autonomous vehicle research powerhouse

• ILLIAC IV and the Connection Machine

• MOSIS: The 1980s DARPA 'Silicon Broker'

• Managing Lockheed’s Skunk Works

One Last Announcement: Interested readers should check out this policy opportunity FAS sent over. “The Federation of American Scientists is looking for federal policy ideas to tackle critical science and technology issues. Areas of interest include R&D and Innovation, Emerging Technologies, Artificial Intelligence, Energy and Environment, Federal Capacity, Global Security, and more. Learn more and submit an idea here by July 15.”

Many in Silicon Valley think of Y Combinator (YC) as the sum of its services. The services are, in short: cash, a network, and guidance for early-stage (mostly software) founders. The YC model and its effectiveness have become widely known and understood in Silicon Valley. The organization has become a staple of the software VC community, applying many principles that have made software VC a success to founders and companies at the earliest stages of company formation. Many of YC’s bets are made so early that the org has been known to make bets on attractive founding teams with no workable company idea yet. 

But Tony Kulesa’s Substack piece provided enough perspective to see the YC model in a different light than it is usually seen in: YC as a sum of its goals. Tony writes the following on what early YC was gearing itself to do:

One could summarize YC’s structure: 

• Invest in young, smart, energetic, and determined hackers

• Give them enough money to pay for living expenses, but not much more

• Give them a few months to build something, launch it, and see some evidence of growth

And, since finding good ideas is hard, get statistics on your side by batch processing – run as many of these experiments as you can in parallel.

The specific resources that YC chose to provide were those that allowed for fast experimentation and proof-of-growth. Considering the 'YC model' as a set of goals — rather than a set of resources —  has interesting implications for one notable area in which modern VC approaches have generally not worked well: deep tech. Satisfying YC's original goals in the realm of deep tech, for most market sizes and technology areas, has proven significantly more challenging than in the realm of software entrepreneurship. Some areas, such as biotech, have found some level of success — although not on the level of software VC. But, in general, VCs have had limited success in the realm of deep tech in comparison to their software efforts.

Tony’s piece helps the reader understand exactly how the early goals of YC and the principles on which the org was founded subsequently led to the org growing into the basket of services and resources it is today. YC’s initial goals paired with the specific market and specific technologies that surround software businesses led to the YC in its current form. But, it should be remembered, had the nature of the markets and technologies that surround software businesses looked different, then the YC model could have turned out completely differently. It is this framing that I’d like the reader to keep in mind as they read today’s piece.

Today’s piece proposes a new model of deep tech VC that seems to satisfy the same goals YC had at its inception, but looks completely different from the current, largely software VC-inspired models of deep tech VC. The specific structure I propose is inspired by some of the research organizations that helped drive the effective deep tech research and commercialization pipeline of the mid-20th C. United States.

The model I propose seeks to pair the practical problem selection and cost-efficient problem solving of entities like the early GE Research Lab, Bell Labs, and MIT’s 1920s Technology Plan with a modern understanding of risk capital. In the natural course of operation in each of those three labs — and many like them in the era — each ended up with technologies that could have been ripe for spinoff as their own independent companies. In many cases, the course of research en route to one of these potential spinoffs was a cash-flow-generating activity in and of itself. In this era, while America did have refined systems of deep tech problem discovery and technological development that are jealousy-inducing by most modern standards, it often did not have financiers willing to give money to businesses with moderate chances of failure the way modern venture capitalists are quite comfortable doing.

The model I propose builds on the formulas of these three research organizations and seeks to facilitate the creation of companies that originate with non-zero customer bases and few technical risks. I am calling the model the William Walker model of deep tech VC. Walker was a key leader of MIT’s Technology Plan and  a pioneer in the field of chemical engineering practice. In both an applied scientific and an administrative capacity, Walker’s career makes him an ideal namesake. 

The William Walker model is not dependent on a few bets “returning the fund” as is often the case in software VC. Instead, it depends on starting good, moderately sized businesses and ensuring that as much of the R&D process as possible can generate its own cash-flow. 

The rough order of the piece will go as follows:

• I’ll introduce the problem further.

• I’ll (briefly) outline some market dynamics that separate deep tech companies from software companies.

• I’ll explore some of the history of the three research organizations I mentioned — and 20th C. deep tech in general — that inform this model.

• Lastly, I’ll outline how the William Walker model for incubating deep tech companies can satisfy YC’s original goals given the more constrained financial fundamentals of deep tech companies. 

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If any of Tony’s readers are visiting FreakTakes for the first time today, great to have you! If you’re a regular FreakTakes reader who hasn’t read Tony’s work before, check out his Substack!

This piece, as always, is done in partnership with the Good Science Project.

Back to the action.

It's no secret that the deep tech VC industry is still looking for a model that sticks. Their 21st C. efforts, largely inspired by software VC approaches, have not generally achieved the desirable returns or societal impacts they were looking for. One possible reason for this might be that software VC-type approaches were just not built to service the vast majority of deep tech companies. The structure of many deep tech VCs — when considering Tony’s piece — may be more in line with a formula that mirrors YC's current offerings than a formula put together to accomplish YC’s original goals for deep tech founders.

But I don’t think this means we can’t hope to start deep tech companies in bulk the way we’ve learned to do with software companies. It just seems that the model has to look different. In finding a model of deep tech VC that seeks to satisfy the spirit of YC's initial goals for deep tech founders, the approach of the William Walker model is very different from software-focused VC. But that should not be surprising. Achieving similar goals in two very different problem areas can often require two very different solutions.

Proposing this model does not mean it can or should be a replacement for all current models of deep tech VC. For certain (specific) problem areas, modern deep tech VC approaches work well. But, as Tony pointed out in his piece, the status quo in most areas of engineering and science is many thousands of PhDs entering into job markets with few opportunities to use their expertise and energy to start companies. 

My solution is one aimed at putting as many of them to work profitably solving problems for American industry as possible.

Tony’s Framing of YC’s Goals

The two major things early YC hoped to provide its founders shelter to pursue were: 

1. Fast experimentation

2. Proof-of-growth

In the case of YC and software startups in general, it turns out that a modest financial package and access to a network of ongoing advisory relationships are more than enough to facilitate both of these. In fact, they work so well that, to many in the Valley, a pile of money and advice is what has become synonymous with the ‘YC model.’ 

And, while that is what YC is doing now, thinking only of these specific resources as the formula to achieve YC’s two goals is probably overfit to the special case of software startups.

The Different Market Dynamics of Deep Tech

When we take a step back, it’s maybe a bit strange to assume that some variant of the financing model that proved optimal for software startups would prove optimal in the general case. The (simplified) examples of products that can be scaled with the most negligible costs that one finds in Econ textbooks are software and certain chemicals/drugs. Additionally, most software companies have the added benefit of negligible technical risks when compared to startups in the hard sciences. Frankly, most scientists would be insulted if you compared the technical risks involved in constructing something like Uber’s early product to what they were working on. 

It’s wonderful that a lever as straightforward as a modest amount of capital can facilitate new company formation in an area like software entrepreneurship — as long as the potential market is large enough. But the dual factors of negligible technical risk (when compared to the hard sciences) and (relative) ease of scaling make software a relatively easy industry to enable via venture capital. Much of the modern software VC industry has structured itself with these dynamics in mind. In fact, as I understand it, the closer the fundamentals of a would-be biotech company are to that of a VC-attractive software startup (in terms of market size and ease of scaling), the more likely it is to get funding. And that makes sense. These dynamics make for fantastic VC investments! When markets have these dynamics, the current VC model works great.

Even a deep tech company like Varda is heavily leaning on these dynamics in its monetization strategy. Varda, the space bio-manufacturing company which Not Boring Capital announced an investment in last month, aspires to be a generalized space manufacturing company. In general, companies in the defense/space spaces are already more VC-investable because something like a $60 million Air Force contract can offset much of your early-stage R&D costs — if you can clear the bureaucratic hurdles to winning a government contract. Even with that contract in place, the initial product that Varda is looking to manufacture that makes their future balance sheet more ‘venture-scale’ is drugs. Drugs have the extremely high margins (and low weight) needed to make this a solid VC investment. And, with all that and a great team in place, Varda does seem to be an extremely compelling investment for deep tech VCs.

But that is also a lot of pieces that needed to come into place. The markets Varda is serving in the short and long run are all very special cases. The joint vertical of  “space drug manufacturer that wins defense contracts to offset R&D costs” is an unbelievably specific category that was seemingly made in a lab to be a VC-investable bet. (It should probably be unsurprising that Delian Asparouhova, Varda’s co-founder, was a VC before starting Varda.)

The number of potential deep tech companies that can meet the financial criteria that venture-scale software companies are able to meet is absolutely minuscule. This group of possible venture-scale deep tech companies is absolutely dwarfed in size by the number of hypothetical companies out there that technical researchers are suited to pursue. The following chart from a 2018 MIT report will not shock you. Certain kinds of companies in certain fields are flourishing. But it is a special set of companies that utilize a specific sliver of MIT’s talented alumni.

As you can see, there is a very large (and growing) pool of ambitious, talented scientists and engineers that have few opportunities to use their degrees to start companies. More/slightly different structures on current VC models is one solution that could certainly solve a portion of the problem — which is what often gets talked about. One such example of a small modification to current models would be earlier/more frequent engagement with applied professors at land grant universities who frequently work on applied research contracts for industrial customers, but are not otherwise involved with the VC ecosystem. However, for most would-be founders and companies, deep tech VCs — in their current form —  are just not offering the right set of resources to start a company in their field.

‘Jet fuel’ is not right for every problem in the short run. But YC’s initial principles, which led them to the specific resources they currently offer software founders, may lead us to the right bundle of resources for a larger pool of would-be deep tech founders.

A Model Inspired by MIT’s Technology Plan & 20th C. Industrial R&D Labs

An effective model to support these technical founders and their ventures does not necessarily need to be as profitable as software VC in as short of a time horizon, but it should aspire to be profitable. Additionally, the model should make use of both the learnings from the last five decades of development in the VC industry as well as the well-functioning deep tech pipeline of the early/mid-20th C. United States. After all, before the boom in software/EE/biotech startups, deep tech was not even a phrase. For the most part, all tech was deep tech.

As Tony framed it, YC’s goals were to provide founders with the right resources for fast experimentation as well as proof of growth. For the case of deep tech research, we can maybe fiddle with these to instead be labeled 1) many rounds of experimentation and 2) product-market fit.

In most areas of science, of course, rounds of experimentation are both longer and more expensive than in software. In most cases, it’s not profitable for a venture capital firm to rain experimentation money on a researcher and see what happens. Additionally, many PhDs are not schooled enough on the business side of technical ventures to know how/where to shepherd their resources and efforts. This is noteworthy because false starts and wide pivots are far more expensive learning experiences in deep tech than in software.

Interestingly, labs in the early/mid-1900s US dealt with these issues quite well. These labs possessed great systems for exposing top researchers to all sorts of nitty-gritty problems and profitably carrying out numerous rounds of experimentation on those problem areas.  These systems — while they did go away for various reasons unrelated to their profitability — were generally seen to be effective and profitable. The two most notable examples are large industrial R&D labs and the portions of universities (particularly land grant universities) dedicated to applied research. Entities I’ve covered on FreakTakes such as the early GE Research Laboratory, Bell Labs, and early MIT’s Technology Plan typify the models to which I refer.

I encourage you to check out each of the pieces to understand the approach of each lab in depth. But, in short:

• Bell Labs had a fantastic system of exposing its researchers to problems all across Bell’s operations — including the day-to-today problems of its manufacturing entities, implementation staff, and elsewhere. Researchers’ regular interactions with people and problems from all parts of the enterprise were not serendipitous, but an intentional outcome of Bell Labs’ management. Researchers at Labs had it instilled in them that it was “a matter of individual responsibility” to find problems that paid off for Labs. Bell also did not rely on researchers to find just the right problem by themselves. Bell maintained a corps of “systems engineers”  to ensure that its researchers were shepherded towards the profitable/useful problems that researchers found interesting (and not just any random problem they found interesting). Bell’s engineers and metallurgists being systematically exposed to ideal research problems — such as the fact that a billion maintenance dollars a year were being spent on fixing a specific kind of wire that degraded in certain climates — was no accident. Bell’s leaders knew their systems of problem exposure and selection were the secret sauce that allowed them to effectively deploy their research talent.

• The GE Research Laboratory, similar to Bell Labs, had excellent methods of problem identification. Like many applied research groups at the time, they were also excellent at brute force experimenting their way to the solutions to the right problems. But the lab also had a fantastic system of managing its basic researchers — such as Irving Langmuir — by granting them what I call a “long leash within a narrow fence.” Langmuir was allowed to work on any basic research project he wanted…so long as it was directly related to a project already underway on the applied side of the lab. His arbitrary selection of bulb vacuums — even though he could care less about the practicality of the project — led him to findings that would not only win him a Nobel Prize in what would come to be known as surface chemistry, but also cut the energy usage of GE’s bulbs in half while tripling their shelf life. 

• MIT, while short on cash in the 1920s, implemented a program called the Technology Plan. MIT’s Technology Plan carried out industry research contracts and consulting work in order to subsidize the Institute’s other research activities. The work was not ‘consulting’ in the style of today’s ‘management consulting,’ but, rather, more in the style of early-1900s engineering or research consulting projects. Companies came to the departments with concrete technical needs, and MIT researchers would often deploy their experimental skills and scientific knowledge to find a solution to the problem. The program was enormously profitable. At one point, 6/7ths of MIT’s Applied Chemistry department’s funds were coming from Technology Plan contracts. Many researchers even preferred this work. Industry’s problems were often interesting. And MIT staff got to use their brains to figure things out for actual businesses with pressing problems that were so important that the businesses were willing to pay a premium to have them solved. 

The (very) general ingredients that these programs had in common were: 

1. They had a pool of talented researchers excited to work on interesting, applied problems.

2. They each had a system of exposing their researchers to profitable, interesting problems.

3. They effectively paired researchers to short-term problems they were well-tooled to solve.

The labs deployed the day-to-day efforts of their researchers on near-term problems that were profitable to some business. The researchers were shepherded to these problems and, over time, learned to identify good problems for themselves in their industry. Each lab encouraged its researchers to do additional exploratory research related to potential customer problems. Each lab also had technically competent, business-savvy individuals who sourced customers, contracts, and problems for the researchers.

While working on problems in this ecosystem, the researchers learned the ins and outs of their industry and how their work could profitably fit into it. Many times, when attempting to solve a smaller-market problem for a customer, researchers would stumble onto a course of research that solved a much larger-market problem. Often, this also happened when researchers used excess funds to pursue problems of their own interest. Those same individuals who sourced problems/consulting work often sourced initial customers for new discoveries that came from the labs’ exploratory research.

Of course, none of these research organizations were explicitly aimed at creating startups. The industrial R&D labs were dedicated to servicing the research needs of the large organizations to which they were attached. MIT’s Technology Plan carried out industry research contracts and consulting work in order to subsidize the Institute’s other research activities. But the scaffolding and organizational structures these labs erected provide a clear template for a modern organizational structure that could meet both of the goals of the original YC model in the deep tech space. 

By pursuing continuous research consulting style contracts, an organization could offer hopeful technical founders the chance to continuously experiment in areas that many businesses objectively need help in and are willing to pay for. One-off problems that require research consulting that are brought to the org could provide industry experience and experimentation resources to the pool of researchers — who would all be aspiring deep tech founders. And any solution that members of the org develop that has a more general use can be taken by interested lab members and spun off into its own company. The goal of the contracts would be as a ‘break-even search function,’ not a profit generator in and of itself. Contracts should be viewed as ways to learn an industry or provide excess funds for experimentation. The endless ‘selling work’ that management consultants do should not be incentivized. Uninteresting and needless projects are unlikely to lead to new company formation.

The 20th C. models I have outlined went away, but they were financially sound and made sense. William Walker, who headed the MIT department that coordinated research contracts and brought in customers, once said, “There could be no more legitimate way for a great scientific school to seek support than by being paid for the service it can render in supplying special knowledge where it is needed.” This was not Walker paying lip service to some concept he didn’t wholly believe in. He would go down as a pioneer in many areas of the young field of chemical engineering practice largely because of his applied contracting work with industry. 

Emphasis on the Technology Plan program faded over the years because, to many in the MIT administration, it came to be seen as a program of necessity. MIT was going broke, but a time came when they no longer needed the money. Most modern universities would not be well-suited to attempt to bring this model back. As Corin Wagen — who received his PhD in Chemistry at Harvard — noted in a blog post last year, nowadays it is common that “policies like [Harvard's] prevent companies from hiring research labs on a purely transactional basis, forcing academics to decouple their incentives from those of industry…research groups cannot simply remake their interests to suit whichever employer they want to attract.”

Universities are not pursuing goals that are anti-industry. But, at many top universities, it has become much much harder, over the decades, to explicitly align one’s research goals to be directly in service to industry — as the entire institution of MIT once proudly did.

But an entity like the model of deep tech VC I describe could be ideally suited for such a task. 

Modern Risk Capital Could Take This Model to Another Level

These early-1900s orgs clearly had effective scaffolding for sourcing problems and profitably coming to solutions in markets that did not have software-style fundamentals. But what their researchers absolutely did not have was access to risk capital that is anything close to what we have today. A 1997 BankBoston report on the status of MIT-related startups demonstrates the extreme extent to which, even in the later-1900s,  technical founders usually had to bootstrap their companies through immediate cash-flow positivity or their own savings.

If a researcher wanted to leave MIT or some company’s R&D department to start a company related to their work, financial institutions were not much help. This was often true even if the IP on which the business was based had been technically de-risked and warm relationships with potential customers were in place. (Also, on the point of IP, to leave Bell Labs to spin off a piece of technology was no small thing either. On one’s first day at Bell Labs, employees signed an IP agreement signing over all IP created over to Labs for $1…)

70 years ago, it was extremely difficult to spin off many great and (mostly) technically de-risked ideas because the state of capital financing was not where it is today. Today, we have a different set of problems. Our corporate R&D labs in most industries have taken a step back in how “basic” their research is. Meanwhile, what universities call ‘applied’ research has become much less applied than it used to be. This ‘middle’ of the deep tech pipeline has been hollowed out.

The mere availability of $2 million VC checks is not enough to bring most could-be companies into existence. Practical entrepreneurial knowledge gaps aside, most technical ideas are not meant for “jet fuel.” In the BankBoston dataset of MIT companies, 7/8ths of them remained under 100 employees 15 years into their existence. Many were planning expansions in various ways, but in a modest sense. With friendlier capital markets, some surely would choose to expand more aggressively. But most probably wouldn’t. Most markets are only so big. This doesn’t mean technical ventures with modest initial market caps can’t grow massive, they just might do so on a different time horizon. As the report pointed out, “Of the 17 largest firms [with 10,00+ employees in the dataset], all but 5 were founded by students who left MIT more than 50 years ago and none were founded by those graduating in the last 30 years.”

This was the traditional route to mega-unicorn status. Companies learned to effectively serve some target market for 5-10 years and gradually expanded as the decades wore on — some until they were as massive as Koch Industries. Modern risk capital can surely speed up this process, but it is a process that surely will take longer than the 10 to 15-year time horizon of many current VC funds.

Also, most likely, the base rate of unicorns in deep tech will be smaller than in software. But there seems to be a way to mitigate that issue from a financial standpoint. Even if the base rate of unicorns and mega-unicorns in deep tech is smaller, it’s very possible that the mid-20th C. inspired model could lead to a much higher base rate of break-even and moderately profitable companies than is seen in software VC. Looking at the 2018 MIT report (with data on MIT-related companies from 1940 onward), it seems only a minority of these MIT businesses failed in the first 5-10 years (possibly as little as 20% of businesses after 5 years and 30% after 10). While the data are possibly crude and no specific number should be trusted too closely, a failure rate this low may not be so surprising given that so many of the companies were being started by those who knew an industry well and began the companies’ life cycle with immediate cash-flow positivity. 

In summary, while the base rate of unicorns in deep tech is likely lower and it will likely still take at least 20 years for most potential unicorns to become unicorns with modern risk capital, there are ways to drastically reduce the number of investments that go to zero — with the median case being a moderately profitable company. That limited downside, combined with the upside being companies like Koch Industries, could make this model workable.

The Median Case

Most portfolio companies would never grow as large as Koch Industries, and that should be ok because the median case in this model is still extremely compelling. The median case is far more ambitious and interesting than the mere $300,000 yearly profit after expenses and salaries on its balance sheet would have you believe. A model like this has the potential to create many small, profitable technical companies that could effectively utilize the skills of otherwise underemployed PhDs and engineers. The model could help rebuild the chasm between many areas of STEM research and American industry that has formed over the past 50 years. These companies could be bastions of profitable engineering and scientific excellence, leveraging Bell-style problem finders and effective sales operations. 

If they grow big, great! But if all most of the portfolio companies end up doing is collectively solving as many problems as possible and their researchers make a good living doing it…the right kind of investors might find that exciting! For that mission, they might be willing to have their money held for a longer term or be open to a different style of returns than in software VC. After all, few investors partake in deep tech VC because it is the fastest or surest way to get rich. Many, frankly, want to do their part to help America recover its status as a powerhouse of great industrial research in all technical areas.

A (brief) look at the financials

(The basic models and discussion that went into this section were worked on jointly with Aakash Pattabi, who understood better than I what kinds of simplified models would be productive for this brief exploration.)

The return profile of a VC model like the one I describe, as you’d expect, looks very different from traditional software VC. The following graphic shows a simplified model of what has come to be normal in something like Series A software VC. In this style, as many know, the hits make the portfolio. Investors are happy to write off 85+% of their checks as most likely going to zero. This is ok because the big hits make or break the fund's success. In the following case, a 5% home run rate — in this case over a ten-year time horizon for a fund that writes 100 $1 million checks — can help the fund return $510 million after ten years.

That case, of course, is a case of things going extremely well. Most funds do not achieve anything close to that kind of success on average. If a VC does not find those few companies that “return the fund,” things can look much more bleak. 

In the William Walker model, one can “return the fund” over a ten-year time horizon with quite modest assumptions. The returns in this basic model are much less sensitive to ‘home run’ performance than in the software model because, not unreasonably, I assume that a deep tech home run in the William Walker model might be a company 10Xing its initial valuation in the first ten years — rather than 100Xing. What performance for a William Walker model fund is much more sensitive to, on the other hand,  is the growth rate of more standard companies in the portfolio. But these standard companies need not be extremely large companies. In this case, I imagine:

• 50% of companies achieve the goal of 50% total growth (over the first ten years) from their modest initial valuations

• 15% of companies achieve moderately ambitious growth goals, 3Xing their initial valuations

• 5% achieve 10X valuations

• And 30% of companies crash and burn

With these assumptions, we observe a return profile that is almost comparable to buying and holding index funds.

The assumptions and outcomes in this hypothetical scenario are only to give the reader an idea of the thought process and goals that one would have if they were looking at this model as an investor who wanted to match stock market returns. Of course, one would need to deploy this “experiment” in the real world to observe what truly realistic assumptions actually are.

It could go wildly well. The following is a version of the model that  would justify scaling the model with reckless abandon if proven true. These (still not crazy) assumptions imagine the following over a ten-year time horizon:

• Home runs were 1/5th the growth rate of software companies rather than 1/10th

• Moderately ambitious growth multiples are 5X rather than 3X

• And the base growth rate was a company 2Xing in 10 years rather than 1.5Xing

With that, the ten-year return on the fund is $275 million on a $100 million investment.

Things could go even better than this model. For example, the Fraunhofer-Gesellschaft — Germany’s system of applied research institutes that serve a similar function to what the Max Planck institutes are for German basic research — report a survival rate of 90% after five years for their spinoff companies. A crash and burn rate far below the 30% number I used in the model could make the financial outcomes even more compelling.

Of course, there exists a world where this could also go very poorly from an ROI perspective. As you’d expect, the worst possible scenario is one in which the companies have a crash and burn rate similar to the hit-or-miss world of software VC — where companies are encouraged to swing big by design.  The following graphic shows a version of this going badly, with half of investor money disappearing. With the same return multiples that netted a $170 million total fund return on $100 million invested, the following assumptions yield a very different financial outcome:

• There are no home runs

• 5% of companies grow moderately ambitiously (rather than 15%)

• 25% of companies grow by 50%

• 70% of companies fail

If one picks investments that go to zero too often, then this is not viable. But if one picks businesses that — as the old MIT-style companies were — are almost immediately cash-flow positive and launch with customer bases and warm leads, then the model is extremely compelling. This is why the pivotal first step in making this a profitable investment class is a style of labs and consulting contracts similar to MIT’s Technology plan, Bell Labs, or early GE Research. These environments produced engineers and scientists whose ideas and ventures could be considered ‘safe bets.’

There would naturally be many small differences in the operation of this model that differ from software VC. One would imagine that — as in the early era of Silicon Valley when VCs were funding more chip/hardware companies — William Walker funds might take a higher percentage of the companies they invest in than is normal in software and, if need be, write fewer checks to ensure companies have the resources they need from the start. This is a reasonable approach when one assumes that far more of its companies will survive the early years than in software VC. Additionally, dilution of one’s equity is a much more negligible factor in this style of VC. Lastly, the styles of businesses being launched would be much more capable of issuing things like yearly dividends to investors. So, even if exits to financial actors like search funds of low-to-mid-market PE firms take a while to materialize, some liquid returns can be seen in the interim.

There is a chance that the William Walker model turns out to be attractive in its own right from the POV of a self-interested investor. But this “experimental” fund idea should be extremely compelling, in particular, to the affluent groups that have, to this point, been losing money in an effort to fund technological growth. Many of these individuals have either been directly funding research through philanthropic giving or been contributing large amounts to ambitious deep tech VC projects knowing the investments are not as profitable as alternative investments.

Investing in this model has the potential to: 

1. At the minimum, bring into existence a new style of org where under-employed, top minds can start companies that solve the problems of American industry even if they are only modestly profitable.

2. Possibly prove out an extremely profitable model of VC. And, even if it doesn't, the organization would have an extremely high chance of breaking even as an experiment — as opposed to many experiments that have no chance of returning the donor’s money back to them under any circumstance.

Maybe this is an experiment that launches a new area of venture, or maybe it just turns out to be a new and clever way to enable top research minds to generate industry solutions — but doesn’t work as a for-profit company. Regardless, it is an experiment worth running.

An ‘Old New Model’ for Deep Tech Venture

This alternative approach to deep tech VC has the potential to marry the best of the old and new. On the day-to-day, doing consulting project work like that of MIT’s Technology Plan projects or Bell Labs-style assignments could bring in money and experience. This provides would-be deep tech founders runway to experiment and on-the-job industry know-how. In general, the goal of the org should be to produce profitable new companies in the long run while (at least) breaking even in the short run on its contracts. When they spin off, the companies would ideally be further along than many deep tech investments currently are — originating with a non-zero customer base and fewer technical risks.

In that case, providing risk capital to the spinoff for 25% of its equity could be (very roughly) one-third as likely to go to zero as the standard deep tech check currently. Each of these successful, break-even companies is one less hole in your balance sheet and one more chance at a company that, in the longer run, can grow into a mega-unicorn like Koch, Gillette, or (even) Campbell’s Soup did in the MIT data.

Not all university labs, of course, have forgotten how to do this style of work. Certain PIs and their labs do large amounts of applied research and continuously graduate grad students who spin off work that originated in the lab. And that’s great! Individuals just like that are the ones who should help guide an initiative like the one I’m describing. 

But what those labs are doing is not the default in academia. Incentives often lead researchers elsewhere. Lab heads like these are proving that it’s doable. But we could do with a hundred more of them across many fields.  The other week I spoke with a Big Ten Mechanical Engineering Professor who brings in industry contracts and whose students have gone on to collectively raise significant amounts in VC rounds. He felt that he had a much better sense of industry needs and how VCs thought than most of his departmental colleagues. I asked him if there were colleagues in his department whose labs he believed he could take over and get to the point that they were raising as much as his lab from VCs. He replied, “Several.”

I’ve also spoken to several professors at land grant schools who took over academic labs after having worked in industrial research for a portion of their careers. Even after transitioning into academia, the industry from which they came continued to lean on their research and hiring the grad students they trained. In various ways, they’ve all (politely) said that most researchers in academia just don’t really understand how to make themselves and their work genuinely useful to industry while working at a university. Their incentives and training seem to lead them elsewhere. 

All of these stories point to an opportunity! The William Walker model can take advantage of top research minds to solve very different problems in a very different organizational structure that is built to train future founders, preserve investor capital, and serve industry as its main goal. 

The right combination of older researcher/advisors and (the right) big-name financial backers could surely provide sufficient ‘signal’ so that some early customers with interesting projects would be willing to come on board. After all, the brands of people like Eric Schmidt have come to extend beyond the borders of Silicon Valley. And there is also a subset of applied-minded professors already known to produce novel, profitable research within their own industries. This William Walker model of deep tech VC, in its early years, could leverage both of these reputational signals to bring in early projects and get the experiment off the ground. (Of course, the young entrepreneur/researchers would do the lion’s share of the actual work on the projects, but an initial stream of projects would be vital to get the experiment off the ground.)

It would be ideal to set up a full William Walker-inspired org, from the start, that was equipped with full-time research heads to lead contracts, a small research facility,  a pool of capital to invest in spinoffs, and full-time research staff who aspire to be entrepreneurs. However, if it were more workable, there are more measured approaches to help the org “ramp up” to full capacity. At the minimum, the org should start with:

1. Salaries and facilities for the full-time research staff (who are hopeful entrepreneurs). The number of research staff could be small — around three to five people — if the org decided to focus on one specific area of research consulting and spinoffs.

2. (At least) part-time research heads — who would often be university PIs — who have experience working with industry contracts and could bring in initial contracts on which the full-time research staff could get started working.

3. Access to some form of capital that is excited about the experiment and willing to invest in the spinoffs of the research staff. If the William Walker org does not have a fund itself, it should establish some form of relationship to friendly capital pools that lead the org to believe investments in deserving spinoffs should materialize. However, since outside capital may be timid, it would be best if the org could initially raise at least a small fund to ensure it has enough money to invest in the first couple of spinoffs.

Other variations of this could work, but as much as is possible, no half-measures should be taken when it comes to the research staff. The potential entrepreneurs should be spending all of their time on this — it shouldn’t be some side-show to other work they are doing.

One could try to change academia to better correspond with these goals so professors and labs strive towards them more often — rather than tenure or filling amorphous ‘holes in the literature.’ One could also try to restructure large companies to more effectively pursue exploratory research and, when appropriate, cleanly spin the work off with a friendly deal and minimal IP annoyances.

But an entirely new organization dedicated to the task is probably best. Specifically, an org that is:

• Inspired by early YC’s goals

• Deploys the structures of early/mid-1900s applied research orgs

• And leverages the learnings of modern risk capital

If Tony’s article is correct, it seems that YC’s original thesis was about how to “solve the money problem” for hackers, not building huge companies. Talented engineers, instead of working for some pointy-haired boss on uninspired engineering work, could take a risk and earn themselves a chance to work on cool problems with a level of financial security. That was the idea.

The same history that leads me to propose this specific structure also leads me to believe this can be done profitably. Will it be as profitable as software VC, index funds, or real estate? I’m not sure. But, as it stands, current deep tech VCs cannot promise anything like that either. This approach offers a fresh perspective, but a perspective that is based on a historically profitable approach.

As it stands, for many LPs who invest in deep tech, it is about more than just money. Many hold the staunch belief that this country is meant to be a place that feverishly produces technical innovations across all scientific and engineering areas — not just two or three! And I think so too. For the most part, it was our consistently fantastic feats of applied science throughout the 20th C. that lead us to this mindset in the first place. That’s why, to me, when attempting to structure an organization that can enable the creation of technical business ventures across all industries, America’s 20th C. systems of applied science are the first place one should turn to for inspiration.

That history, combined with our expanded systems of risk capital, lead me to this model — which I’m calling the William Walker model of deep tech VC.

It might not be as profitable as YC. But it does allow technical individuals to work on hard, useful problems. And it can give them a level of financial security in doing so. It’s a very legitimate way to satisfy the spirit of both of YC’s original goals. 

So, it’s an idea worth entertaining.

Thanks for reading:)

But one last thing!

If anybody is interested in helping bring this org into existence…

I absolutely believe an organization like this should exist and would happily work with individuals excited to make it happen. I’m starting an offline list of potential markets in which researchers in the William Walker model could potentially be profitably deployed. So, if any folks do think this is interesting but don’t know exactly what specific markets the organization could start in, I’m already working on that and would love to share what I’ve come up with.

On that note, if anybody reading this works in some area like low-to-mid market industrial PE, I’d love to pick your brain on some things. In my market exploration so far, I’ve found individuals in these sorts of roles useful starting points. (My Twitter can be found here)

Lastly, since most of today’s piece was aimed at describing a new model of scientific organization, I’ve included an additional End Notes section with a couple of tamer takeaways that might be useful to existing deep tech VCs who do not intend to wholly change their model, but are compelled by the historical details contained in today’s piece.

End Notes/Tamer Takeaways

Of course, there are also ways to more easily fold the learnings from this piece into a modern deep tech VC to achieve at least some of the effect — with significantly less effort. But I wanted the chance to pitch the most extreme version of the idea first. But, of course, the learnings that inform this atypical idea can have more standard VC applications as well.

Working more closely with land grant professors who work on applied contracts

My first piece of advice is this: Deep tech VCs should establish much closer relationships with researchers who work more on applied contracts at land grant universities. Many of these professors continuously generate profitable and commercializable IP that plugs into the industrial process, but they are not necessarily plugged into the deep tech VC community.

I recently spoke to one Big Ten Material Science professor who said that when they hosted an ‘industry day,’ many companies who eventually became customers of the department’s services attended. But he couldn’t recall a single VC as having attended. Maybe one was there, but this professor couldn’t recall any. Maybe these professors’ work was not venture-scale, but I got the sense that many of their projects had never even come to the attention of a deep tech VC.

These labs are often sitting on know-how/skillsets that industries find usable and continually work with them to solve problems, but they are generally not plugged into the deep tech VC community. Relying on them to find a VC to share their learnings with/pitch ideas to is not a reliable approach.

Given how many VCs spend the majority of their time sourcing deals, having discussions with people in industries that they know have a low probability of leading to a deal, etc., it seems like these individuals should be actively sought out. If I worked at a deep tech VC fund as an analyst, I would spend a large amount of my time sourcing deals through this alternative channel if I could.

On that note…

Working more closely to help tailor projects the VC is not currently funding to be more VC-investable in the future

Many of these researchers are working on potentially commercializable problems on somebody else’s dime…use that! A VC can shape a project for many years before they are the one funding it.

I could imagine a world where a deep tech VC does something like ingratiate itself with the MIT master’s cohort. Many of those students, in a perfect world, would love to be deep tech founders. In a hypothetical world, a VC could attempt to shape the master’s thesis projects in the cohort — which the university is not as protective of as it is of its PhDs — as their projects are underway. For the (many) interested students, a VC could attempt to shape their research projects to be more VC-investable at the end of the two-year program. I could imagine this generating at least one or two noticeably de-risked investments for a VC firm. After all, as things stand, many of these students do not have much knowledge or direction in choosing initial project areas or choosing the ‘right’ next steps as the project goes on to make the project a commercial success.

These students seem to be one of the purest examples I can think of as having extreme talent and energy, but limited industry knowledge. Servicing them and their projects seems to be extremely aligned with the initial goals of YC — but for the deep tech space — as anything I can think of.

Of course, in the role of a VC, I would also attempt to informally do this with as many interested professors and their research directions as I could — years before I was even considering writing a check. Many professors are ‘over’ academia and would be happy to shape their research directions (on the NIH/NSF dime), over the course of a handful of years, to be more about solving the technical risks of a hypothetical company than upping their h-index. If I were a VC, I’d spend a massive amount of time working with them. If the issue many deep tech VCs have is that the deals coming across their table have too many technical risks than the VC is able to profitably fund experimentation to mitigate, this seems like a way to clearly be proactive about improving the quality of deals that cross your desk — if the VC takes a sufficiently long-term view. 

These are just a few of the tamer learnings that come to mind that could be folded into interested VC operations right now

Thanks for reading:)

As always, I would love to speak with any readers interested in applying any of these learnings to their own organization.

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Citation:

• Gilliam, Eric. “An Alternative Approach to Deep Tech VC.” FreakTakes Substack. 2023.

But as I’ve continued to explore the history of early-to-mid 1900s science — which largely occurred in a period pre-dating the best micro-level data we see in the economics of innovation literature — I’ve become much more skeptical.

I’m not saying that as more and more things are known in a field, it doesn’t take longer to learn each of them. That is, of course, true. It takes longer to learn more things than it does fewer things. But what I am saying is that the accumulation of additional knowledge as the primary driver of our slowing rate of scientific progress is flimsy as a hypothesis. There are other theories that can fit the trends in the data just as well; one of these theories was put forward by scientists living through the mid-1900s who felt they were observing the onset of new branches of science becoming harder and harder to create.

Accounts I’ve come across of WW2-era physicists complaining about academia becoming a worse place to do creative or interdisciplinary work do not point to the growing size of the literature as the reason. Interestingly, their complaints had nothing to do with the growing size of hypothetical ‘idea space’ at all; their complaints often blamed administrative changes. They point to things like growing conference sizes or scientific meetings being held for narrower and narrower sub-branches of work rather than broad areas — human organization problems.

Today’s piece will put forward an alternative hypothesis as the primary driver of the scientific slowdown: the human systems hypothesis.

To inform different aspects of the hypothesis, I’ll examine:

• What the existing evidence from the economics literature does and does not say about the burden of knowledge

• Why many great mid-1900s scientists blamed human organization problems for the growing difficulty in asking new, big questions

• Why the exact nature of math and physics’ ‘divorce’ supports the human systems hypothesis

• And how the field of poetry — whose rate of progress is likely not vulnerable to burden of knowledge issues — suffered a similar fate to that of science when institutions like those in late-1900s science were introduced

Let’s get into it.

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• For those who listened to the Edison podcast, please feel free to comment or DM me topics that you’d like to see covered on the podcast!

• For the sake of this piece, ‘interdisciplinary work’ should be defined as work that draws from and/or is relevant to multiple disciplines.

• This piece, as always, is done in concert with the Good Science Project

I should state upfront that I don’t expect this hypothesis to win over a majority of the economists. The reason is that there is not exactly a single, clean ‘identification strategy’ to verify the theory. Most imaginable ‘natural experiments’ in the modern context would not approach any kind of clean answer. An unwieldy number of changes occurred in the culture, organization, and incentives of science that affected an entire generation of researchers and have continued to affect each generation afterward. Any single accidental change to one component would still leave most others intact.

So, instead, I employ a style of argument more familiar to later-1900s political science literature in which I attempt to fold in all available data into the theory, but am very willing to let relevant qualitative information inform pieces of the hypothesis when it makes sense to do so. This style of work was often used in areas such as later-1900s comparative economic development work. In a case like this, they had before them:

• A very specific and biased set of countries that had achieved 'developed country' status

• Some high-level data on most countries

• Some more granular data on some — mostly developed ones

• Detailed qualitative histories from many countries going back centuries

• But no data that was nearly specific enough or numerous enough to begin answering the question in a purely quantitative way

But the stakes were large and the questions were worth answering as best they could, so those studying economic development tried and used all the information at their disposal. For those readers familiar with the subject, works by people like Mancur Olson exemplify this tradition and are examples of this style done at the highest level.

With that explanation out of the way, let’s explore the argument.

A brief overview of the existing economics of innovation evidence

To start, I should briefly go over what has been confirmed by data in the existing economics of innovation literature and what has not on the question of the burden of knowledge.

Are ideas getting harder to find?

Whether ideas are getting harder to find or not is very much an open question — or at least has some notable caveats. What researchers like Bloom et al. have confirmed is that our research productivity across the board very likely seems to have been decreasing since about 1970 — give or take. As we’ve spent more money and more researchers than ever have poured into fields, we are getting less and less productive.

The following graphics from Bloom et al.’s famous paper demonstrates this disappointing trend on the micro-level, within fields. Some of the y-axes variables are more convincing than others — i.e. many would believe that transistor count is more robust than counting the number of clinical trials — but the general trends the paper observes seem quite robust and clear: we’ve been getting steadily less impressive outcomes compared to what we’ve been putting in since about 1970.

Now, all of this micro-level data only goes back to around 1970-ish — a little before in a few cases. A portion of the introduction of their paper paper — which introduces the topic using very macro, national trends — goes back as early as 1930. However, many question the ability of economy-wide metrics like TFP growth on one axis and total US expenditure in R&D on the other to be useful in understanding these questions since the metrics capture so many other trends that one can’t control for — particularly in a mid-1900s American science landscape where how research was used and invested in was rapidly transforming. The authors were aware of this, which is why they dove into the micro-level data shown above. The result was a fantastic and robust paper identifying a massive problem in American science from about 1970 onward.

As those micro-level charts show, in almost all research areas explored in the literature, we seem to be getting as little research productivity per dollar as ever. Of course, these fields do not cover everything. But they were selected because they were generally measurable. And I think that approach makes a lot of sense. From those graphs, it seems very likely that we’re not as productive as we used to be. That is hard to argue with — I wouldn’t argue it.

The natural next question is, “Is this our fault?”

Are ideas getting harder to find by some almost natural force? Or have we gotten worse at doing science somehow?

The ‘natural force’ supporters often believe that ideas just get harder to find because previous generations have somehow picked all the lower-hanging fruit. This implies that the lack of research productivity is not humanity’s fault, it’s just that we’re increasingly fighting an uphill battle.

Does the economics of innovation literature disentangle this question at all?

The Burden of Knowledge and the ‘Death of the Renaissance Man’

In short, not exactly.

When you trace ‘burden of knowledge’ up the citation tree in the economics literature, all roads lead you to Ben Jones at Northwestern. His big initial paper on the topic, for which this section is named, and a later paper called Age dynamics in scientific creativity confirm some things about the burden of knowledge, to be sure, but they don’t do anything to pin down the burden of knowledge as the primary factor in the slowdown of scientific ideas.

The first paper is not causal. It is a structural modeling paper with a portion dedicated to the analysis of some patent data from a high level. The paper, in a nutshell, posits what a good model of burden of knowledge-like dynamics would be if the dynamics existed. The data don’t confirm strong causality, simply that the theory put forward more or less can mesh with a reality in which the trends in the data exist. The data that the author used to fit his theory to was basic patent data noting things like team size and age of invention.

Even with this basic data, the theory hardly fit cleanly. The biggest reason I say this is that, even though he acknowledged some patent areas were more complex than others, he noted that:

Innovators in the same cohort choose the same amount of education across different areas of application. What is particularly surprising is that this result holds even though some areas may feature a greater difficulty in reaching the frontier of knowledge.

He attempts to fit this observation into the theory with a hypothetical explanation of how innovators could allocate themselves in a way that could make this consistent with the theory.

You get the idea. The paper surely empirically shows certain relationships — and I do genuinely love the paper — but it’s far from a ‘nail in the coffin’ for competing theories.

However, Jones did extend the idea further. He, along with Bruce Weinberg, wrote a fascinating follow-up paper using all of the physics, chemistry, and medicine Nobel Prize-winning discoveries from 1900-2008 as their dataset. Some relevant trends the authors observe are:

• The proportion of Nobel-winners who make their Nobel-winning discovery by the age of 30 or 40 is going down drastically.

• Theoretical contributions are associated with younger researchers.

• Physics Nobel winners showed a substantial burst in youthful productivity after quantum mechanics burst onto the scene in their field.

The following graph displays this youth boom in physics. The lower line is the percentage of Nobels given out to researchers who made their winning discovery by the age of 30, and the upper line by the age of 40. The quantum era seems to have initiated a steadily rising level of outstanding discoveries from young researchers, peaking in the 1930s.

I’ll re-examine more specific evidence from this paper later in the piece — once I’ve further fleshed out the historical argument for the human systems hypothesis. For now, I’d like to bring attention to a key caveat that the authors noted in explaining how this new branch of physics affected the trend of Nobel-prize winners getting increasingly older:

Age dynamics might be associated with changes in a field’s foundational knowledge, which may typically expand with time but also may contract in cases where new knowledge devalues old knowledge. Heisenberg [who won his Nobel for work done at 23 and 25], for example, nearly failed his PhD examinations at age 21, because he knew little of classical electromagnetism; his contributions in the subsequent 4 years suggest that training in classical physics may have become less salient.

This is a fantastic observation from the authors and one that often gets lost in discussions of the burden of knowledge. The concept of the burden of knowledge and its relationship with scientific productivity is one that cannot be disentangled from the concept of scientific branch-creation. The older the branch, the more the 'burdensome' of the burden of knowledge is; the younger the branch, the more negligible it becomes.

This observation, along with the oddity that fields of varying complexity have similar training times in Jones’ first paper, will fit very cleanly into the human systems hypothesis.

The historical perspective leads one to the human systems hypothesis

The reasons fields seem to grow apart, when one reads the historical sources, are quite interesting. The growing apart process often seems much more abrupt than the rate of change in the scientific fields themselves.

The opinions of many of the researchers themselves are the first point that lead me to this observation. The growing apart of fields in the years leading up to 1970 did not go unnoticed by researchers at the time. Researchers who lived through great eras of their fields in the early-1900s and continued to research through the 1970s point the finger at things like conference sizes and not the size of the literature as responsible for it becoming harder to do truly exploratory research. This group is interesting because many of them started out in fields that were smaller but explosively growing in terms of ideas and continued to research into the era in which the number of publications exploded but the rate of big ideas in their fields did not seem to be exploding.

To be clear, the growth in the size of the literature was surely noticed…

It’s material that great minds who thought critically about their fields chose not to complain about this growth in the size of the literature as much as things like conference sizes and incentives. Just because the early-1900s was an era in which one could try to keep up with all the literature in related fields just by reading it, that doesn't mean that's what researchers usually did. The accounts in this section paint a picture of researchers who largely kept up with science by keeping up with people.

The second point that leads me to this observation relates to the importance of how fields grow apart. The exact nature of how fields come together and grow apart often has more to do with people and incentives than ideas themselves. A supporter of the burden of knowledge hypothesis would likely expect that fields that were formerly very interrelated would grow apart somewhat gradually as keeping all the ideas in one's head became more and more untenable. Fields separating, usually, should not be for some interpersonal reason or internal politics. But this abrupt separation is often exactly what one finds.

I’ll use the accounts of mid-1900s physicists to explore both of these points.

Mid-1900s physicists point the finger at systems changes

Many World War II-era physicists were not only practicing researchers in the small and bustling field of early-1900s physics, but continued on as researchers well into the 1970s. As there was an explosion of publications in their field, the researcher accounts I’ve come across do contain complaints from the old-guard researchers. Several prominent examples note the feeling that academia was increasingly becoming a worse place to do creative or interdisciplinary work, but the complaints don’t pertain to the number of publications themselves — although they did grumble at the changing state of publications and how smaller findings were published more often.

In practice, they more so blamed the human organization problems — essentially administrative issues — that they saw all around them. The growing conference sizes made it much more difficult to keep up with adjacent fields and scientific meetings. Seminars began to cater to narrower and narrower sub-branches of work rather than broad ones.

These were the places that many researchers leveraged to actually keep up to date on new work and problems in their fields as well as others. But, as money began to funnel into their field in the post-War era, there were more and more researchers and logistical decisions had to be made on how to do things like run conferences and decide who sits in what seminars.

The following Richard Feynman excerpt — taken from a 1973 oral history interview, which was one of a series of interviews between Charles Weiner and Feynman — goes into why, in the early 1970s, Feynman felt physics conferences had begun to grow far less useful than they were during the initial interviews for the series — where Feynman had told positive stories about the state of conferences as recently as 1956:

Weiner: How are they [conferences] going from what you’ve seen over the years? Is this the same kind of continuing tradition of the same kinds of people coming together? Because in the early period — we talked about the meeting where you got up and said: “Mr. Block has an idea that I would like to tell you about,” and you talked at the following meeting on that, and these were very exciting things. Has it continued in that same tradition?

Feynman: No, they’ve gotten too big. For example, they have parallel sessions which they never had before. Parallel sessions means that more than one thing is going on at a time, in fact, usually three, sometimes four. And when I went to the meeting in Chicago, I was only there two days before I broke my kneecap, but I had a great deal of trouble making up my mind which of the parallel sessions I was going to miss. Sometimes I’d miss them both, but sometimes there were two things I would be interested in at the same time. These guys who organize this imagine that each guy is a specialist and only interested in one lousy corner of the field. It’s impossible really to go — so it’s just as if you went to half the meeting. Therefore half is not much better than nothing. You might as well stay home and read the reports.

This is no small thing. Feynman, who never religiously kept up with the literature, was one of many who used these conferences as a primary way of keeping up with the changing state of things.

We find a similar account in Warren Weaver’s autobiography.

In Weaver’s book, once again, we hear a 1970-ish account of a researcher who lived through and was active during the golden era of physics complaining about growing conference sizes, not the growing number of publications, making it more difficult to keep up with related scientific areas. Not only were conferences growing in size, but, in response, they separated various disciplines into their own conferences to make conference logistics more manageable.

Many economists tend to believe that it is the sheer size of the literature causing the problem. But both Weaver’s and Feynman’s accounts seem to more directly blame the highly statistically correlated, but fundamentally different, change in conference dynamics and logistics that came with more and more researchers flooding into the community.

Weaver wrote of the early AAAS, which he was once the President of:

This vast organization, with the largest membership of any general scientific society in the world, embraces all fields of pure and applied science. In the earlier days each branch of science conducted intensive sessions at which its own specialized research reports were given, and there was also some mild attempt to organize interdisciplinary sessions of general interest. Then the meetings got so large that they almost collapsed under their own weight. One group after another, first the chemists, then the physicists, the mathematicians, the biologists found it necessary to hold other and separate meetings. Attendance fell and the function of serving as a communication center between the various branches of science became less effective.

At a time when publications had roughly 10x’d, both Feynman and Weaver chose to talk about the masses of people flooding their conferences (and then conferences being held separately) rather than papers flooding their journals.

While the two were not active in the research community throughout the entirety of the decades-long explosion in journal articles — a scientific career is only so long — they were around for enough of the explosion for their accounts to be quite telling. If you take seriously the ability of individuals like Feynman and (especially) Weaver to diagnose issues in their fields — Weaver ‘saw the whole board’ well enough that he was the primary driver in jumpstarting the field of molecular biology as a grant funder — these accounts are surely not evidence to be disregarded.

How fields grow apart matters

Fields that used to be largely integrated can grow apart for a variety of reasons. On one end of the spectrum, fields can grow slowly grow apart. On the other end, they can rather abruptly divorce. As with a real divorce, divorce does not mean that the two fields do not at all interact anymore, but the frequency and amicability of the interactions do change drastically and abruptly.

The nature of how two fields that frequently produced interdisciplinary research come to separate is very relevant to how much faith we should have in the burden of knowledge hypothesis. If the sheer number of publications is the driving force behind the drop in research that combines disciplines, then a strict burden of knowledge hypothesis supporter would probably expect the amount of interdisciplinary research work to drop (more or less) in lockstep with the number of papers in those fields. However, that is often not what we see.

Let’s continue with the case of math and physics in the mid-1900s. These two once-married fields did grow apart, but it had little to do with the size of the literature.

Robert Dijkgraaf — a mathematical physicist, current Dutch Minister of Education, and former Director of the Princeton Institute for Advanced Study — recently published a book chapter in a volume about the late Freeman Dyson. The chapter talks about the ever-exploratory Dyson’s presence at the Institute and several areas of change during his tenure that he decried. One noteworthy change the mathematician-turned-physicist fought against was the divorce of the two fields within the Institute.

Dyson, a dear friend and mentee of Feynman, said this of the growing propensity of mathematicians and physicists to contribute to each other’s field in the 1972 Gibbs Lecture to the American Mathematical Society. The lecture was titled “Missed Opportunities”:

I happen to be a physicist who started life as a mathematician. As a working physicist, I am acutely aware of the fact that the marriage between mathematics and physics, which was so enormously fruitful in past centuries, has recently ended in divorce.

Dyson was the mathematician who proved the equivalence of Feynman diagrams and the operator method of Schwinger and Tomonaga. His style of work, answering physics questions that required the deep toolkit and experience of a solid mathematician, was not uncommon in his early years. One could view the work of von Neumann or Dirac in a similar vein.

Robert Dijkgraff elaborated on the events leading up to the divorce as follows:

As physics became messy and muddy, mathematics turned austere and rigid. After the war, mathematicians started to reconsider the foundations of their discipline and turned inside, driven by a great need for rigor and abstraction. The more intuitive and approachable style of the “old-school” mathematicians like von Neumann and Weyl, who eagerly embraced new developments in physics like general relativity and quantum mechanics, was replaced by the much more austere approach of the next generation. This movement towards axiomatization and generalization was largely driven by the French Bourbaki school, started by a group of young mathematicians in Paris in the 1930s. They had set themselves the task of rebuilding the shabby house of mathematics from its very foundations, under the motto “structures are the weapons of the mathematician.”

This arbitrary shift in taste — surely fueled, in part, by a post-war glut in American funding for research much more basic than before — encouraged young mathematicians to pursue problems in those areas rather than working on physics-related problems. The relationship between mathematicians and theoretical physicists began to change in noticeable ways. Dyson described how this affected his own life at the Institute in an interview with Natalie Walchover:

We had a unified school of mathematics which included natural sciences; it included Einstein; it included Pauli and other physicists. So, the mathematicians and physicists in the first 20 years of the Institute worked together. But at that time when I became a professor it just coincided with the time when Oppenheimer became director and there was a divorce largely occasioned by the fact that Oppenheimer had no use for pure mathematics, and the pure mathematicians had no use for bombs. So, there was a temperamental incompatibility. For one year, after I became a professor, we still had meetings of the whole faculty, but after that they were separate. We had meetings of the physicists and meetings of the mathematicians, no longer speaking to each other. So, that was sort of a local manifestation of the divorce.

Things were changing.

For a while, Dyson was exempt from exclusion on either side — he was a ‘real’ mathematician who simply had success plying his craft in particle physics, just as von Neumann once won fame for plying his mathematical craft in various non-math fields. But, eventually, this new wave of mathematicians did not want him either. He recalled in an interview with his son and science writer, George Dyson:

But I had the advantage, of course, that I was also a mathematician And the mathematicians knew that I had done some useful stuff in pure mathematics. And so, when I appeared here as a professor, I was actually invited to the faculty meetings in mathematics. And for several years [in the mid-1950s] I used to go to the mathematicians’ faculty meetings. And they were quite friendly. They considered me as one of them…So, for the first two years or so I functioned as a mathematician. But at some point, I was, I don’t remember how this happened, but I was dropped, and it was made clear that they didn’t want me at their meetings. So, they regarded me, at first, as being on their side, but then afterwards they found I wasn’t.

In this Dyson description, we see strong hints of academia beginning its march toward the siloed beast we know it as today.

In general, a divorce like this is not symptomatic of a ‘burden of knowledge,’ but, rather, a changing set of incentives and systems taking hold. One could say ‘maybe the fields would have grown apart (at some point) anyway if it weren’t for this systems-related divorce’ just as they could say ‘maybe Weaver and Feynman would have eventually started complaining about the size of the literature as it went from 10x to 30x the original size’ — even though they didn’t complain about it 10x’ing. If one wants to play counterfactual history in that fashion, they can. But we should take the events as they actually happened much more seriously.

With the American boom in post-war basic research funding, obligations for American researchers to have specific, short-term applications in mind for their work became lighter than ever. So, if a field was made up of individuals whose propensity leaned towards mathematical elegance and rigor over real-world applications, they now had more leeway to do that kind of thing. In fact, it might even be encouraged.

This style of thinking can quickly lead to intra-disciplinary work — and the creation of inward-looking sub-branches of science — rather than work that connects fields of separate departments or builds towards concrete applications. American academia was becoming a different world: more people, more funding, more bureaucracy, more silos.

A different world

Gerald Holton, writing at the end of a boom period in several scientific subjects in the mid-1900s, felt that ideas were getting easier to find. He was not the only researcher to think this. It seemed that whenever scientists found a new idea, in line with certain combinatorial theories of innovation, they now had a new hammer to use on existing nails. Alternatively, they could re-combine the idea with other existing ideas to see what happened. Doing this was speculative and prone to more misses than hits, but, to the researchers, the positive expected value of the work was obvious and many were excited to do the work. More importantly, they felt free to do so.

The era recounted in Dyson’s stories of the IAS corresponds with the onset of the modern, increasingly discipline-oriented organization of science. This is an era in which many feel publishing in multiple areas and extreme novelty are disincentivized in various ways due to current journal, grant, and tenure processes.

All of this has happened, coincidentally, as we’ve eased into a world in which it feels like ideas are getting harder to find rather than easier to find. My previous piece, When do ideas get easier to find?, documents Gerald Holton’s mid-1900s work on what seemed to be driving the productivity of early-to-mid-1900s physics. His model of the contemporary ‘physics production function’ placed an extremely high valuation on the importance of incentivizing the workflow of an individual like John von Neumann or the branch-creating inventions of a researcher like I.I. Rabi — whose work many subsequent Nobel prizes depended upon.

Theirs were results worth failing towards.

Holton documented — both anecdotally and with a graph documenting the productivity of research on particle accelerators — that the productivity of fields he was familiar with seemed to be almost entirely driven by the consistent creation of new branches of research. Holton, who was a physicist before he became something of a progress studies researcher, was telling the story of his own field.

As the following graphic shows, exponential growth (logged y-axis) in accelerator energies over several decades was achieved almost entirely by the consistent creation of new technologies and approaches to attack the same problem. The rate of progress for any individual branch of technology usually curtailed quite rapidly after its first 5 years or so, but new branches took its place.

He noted that the creation and extension of these new branches tended to be the domain of the young. Beating a long-tenured professor in an area of knowledge in which they have been building up minute knowledge for several decades is quite difficult. Knowing only 80% as much as the elder statesman doesn’t count for much on older branches of science. But understanding the old ideas, in a nutshell, is plenty when looking to apply the learnings of an old branch to another area of knowledge. When doing that sort of work, enthusiasm and willingness to take some risks count for much more. Most importantly, the young researchers tended to be the most tolerant of this failure-prone and open-ended exploration. They were often excited by it. It was a great way to make a name for yourself!

Holton did not choose this accelerator example because he felt the underlying dynamics driving its growth were any different from those that people believed to be present in the rest of the field. Similar to the choices made in the Bloom paper, it was just the most readily measurable example.

Building on his point, Holton noted that, at the time of writing in around 1962, work by M.M. Kessler had recently found that 50% of the references cited in the Physical Review — the top physics journal at the time — were less than three years old. And only 20% were more than seven years old. Decades on from the paradigm-changing discoveries of relativity and quantum mechanics, physics researchers had still been rapidly leapfrogging each other in the race for human progress, constantly citing young papers and letters. Science was moving so fast that a non-negligible number of citations in the journals were citing personal correspondence and conversations with other physicists as opposed to published papers.

I don’t believe Holton’s theory contradicts the evidence in the Jones and Weinberg paper, either. Even though the authors only examined the quantum revolution by name, there was a second, generally similar burst in theoretical knowledge that their data captured that they did not discuss — the birth of the field of molecular biology. I’m not sure why they omitted this, but it might be that the emergence of molecular biology and the magnitude of its importance is generally paid less attention to than quantum mechanics.

This young branch is one that I covered at length in a previous piece on this Substack. The piece details the dynamics of the burst in branch-creating science in the field of molecular biology between around 1933 and 1953. As the following graph shows, the chemistry Nobel Prize also experienced a resurgence in youth around this time.

The bump would probably look even starker if molecular biology didn’t split its Nobel Prizes between the chemistry and medicine categories.

Looking at the author’s Nobel in Medicine charts, things are less stark. But that should not be surprising. Medicine is a very broad field, handing out Nobel prizes to things like molecular biology discoveries that add to our theoretical understanding of medicine as well as applied findings such as “discoveries concerning heart catheterization and pathological changes in the circulatory system.” So, while the aggregate age trends in medicine don’t exhibit a similar bump (as I show below), the growth in the frequency of theoretical findings responsible for Nobel prizes in this period did experience a noticeable bump. And, as the authors pointed out, in the data theoretical findings were very strongly associated with youth. But, in general, making sense of the mixed bag of research projects that qualify for Nobels in medicine as a single statistical category is maybe not worth looking into too deeply.

Next, we look further into the figures to assess the validity of Holton’s observation that, decades after the start of the quantum revolution, the research being cited in the Physical Review was still extremely young. The larger citation dataset in the appendix of the Jones and Weinberg paper does nothing to make us doubt Holton’s observation. While the smaller, Nobel-prize-only data in the main paper observed shows steady increases in the age of citations, a different trend entirely comes to light in the more robust datasets used in the appendix — which include the 100 most cited papers per year in each field rather than just the Nobel-winning discoveries. In physics and chemistry, it seems that there is more or less a plateau — or extremely marginal decrease — in average citation age from around 1900 to 1970. Then, somewhat abruptly, there begins a significant and steady climb in citation age. One could interpret this, simplistically, as knowledge beginning to progress more slowly.

Interestingly, this late-1960s/early-1970s period is also when a lot of the data in papers like Bloom et al’s tends to begin. This is also about the time when Weaver and Feynman’s statements — pointing to a noticeable problem forming in science’s systems — take place. The historical perspective, when examining a question like this, is imperative.

Holton’s model — along with Feynman and Weaver’s statements — came right at the end of a bit of a golden era. Holton’s model describes a different world, but one that is very relevant to the question of how to re-ignite scientific productivity.

Reflecting on how there were a growing number of problem areas where headway could be made by individuals from as many as five fields, Holton asserted that:

It is becoming more and more evident that departmental barriers are going to be difficult to defend.

He believed that we might see the end of departmental barriers and a system that evolved to incentivize all-important, branch-creating science. Young branches were where the most productive science was done. Young branches are where the burden of knowledge isn’t so burdensome. He believed we would build institutions and systems focused on creating new branches above all else because that’s what was driving our productivity.

We built the exact opposite.

What ‘Poetry and Ambition’ can teach us

As you know, we cannot re-run recent scientific history, changing individual parameters as we wish. What if institutions and incentives hadn’t changed 50+ years ago? What if we could set the ‘burden of knowledge coefficient’ to zero and re-run the simulation with the same institutional changes? This inability is one that haunts social scientists every day.

But, luckily, we do have a case study available to us that provides a lot of perspective — and lends a lot of credibility to the human systems hypothesis. There is a non-STEM field where institutions and incentives similar to those introduced to American STEM research in the late-1900s were introduced. The field, to most people’s eyes, is subject to rather negligible burden of knowledge issues. And when similar institutions were introduced into the field, similar changes occurred.

It is an imperfect analogy, but one that comes close to setting the burden of knowledge coefficient to zero and re-running the simulation with similar institutional changes to observe how much of the slowdown persists.

The field: poetry.

Many within the field of poetry and creative writing in general, apparently, believe they are living through an extreme slowdown in work of the highest quality as well. This is something I was unaware of until recently when an unusually broad-ranging mathematician friend of mine, Chen Lu, began telling me about it and shared the piece on which this section is based. The piece is called Poetry and Ambition. It is a long, part essay/part poem published by Donald Hall who was a practicing poet from 1950 through the early-200s.

In Poetry and Ambition, Hall highlights the changing state of the field over his career in terms of goals, outcomes, incentives, and overall ambition. In many of the sections, if one replaces words like ‘writer’ and ‘poem’ with ‘researcher’ and ‘finding’, the excerpt sounds eerily similar to complaints from those in the progress community railing against science’s stagnation.

For example, Hall writes the following on the changing ambitions of the poet:

5. True ambition in a poet seeks fame in the old sense, to make words that live forever. If even to entertain such ambition reveals monstrous egotism, let me argue that the common alternative is petty egotism that spends itself in small competitiveness, that measures its success by quantity of publication, by blurbs on jackets, by small achievement: to be the best poet in the workshop, to be published by Knopf, to win the Pulitzer or the Nobel. . . . The grander goal is to be as good as Dante.

Let me hypothesize the developmental stages of the poet.

At twelve, say, the American poet-to-be is afflicted with generalized ambition. (Robert Frost wanted to be a baseball pitcher and a United States senator; Oliver Wendell Holmes said that nothing was so commonplace as the desire to appear remarkable; the desire may be common but it is at least essential.) At sixteen the poet reads [Walt] Whitman and Homer and wants to be immortal. Alas, at twenty-four the same poet wants to be in The New Yorker. . . .

To be clear, Hall is not some rogue in his beliefs. Mark McGurl wrote the following in his book, The Program Era, on postwar fiction and its effects on the field of creative writing:

While the existence of degree-granting entities like the Iowa Writers’ Workshop was the result, in part, of a new hospitality to self-expressive creativity on the part of the progressive-minded universities willing to expand the boundaries of what could count as legitimate academic work, the founders and promoters of these programs more than met the institution halfway, rationalizing their presence in a scholarly environment by asserting their own disciplinary rigor.

Halls words simply attempt to (eloquently) describe a wider trend.

Hall goes on to refer to the type of poem that the exploding poetry and MFA programs have geared themselves to train poets to produce as the ‘McPoem.’ “To produce the McPoem, institutions must enforce patterns, institutions within institutions.” These misguided forms of quality controls, in Hall’s eyes, were how most large American organizations had adapted themselves to meet the needs of larger and larger audiences who wanted to buy what they were selling. Similarly, this is how MFA programs had structured themselves to meet the increasing need of young people seeking out the degree programs. To him, the approach was far more suited to mass-market goods than his craft.

Hall continues, diving into what the work of the ‘poetic heroes of the American present’ often looked like:

When Robert Lowell was young, he wrote slowly and painfully and very well. On his wonderful Library of Congress LP, before he recites his early poem about “Falling Asleep over the Aeneid,” he tells how the poem began when he tried translating Virgil but produced only eighty lines in six months, which he found disheartening. Five years elapsed between his Pulitzer book Lord Weary’s Castle, which was the announcement of his genius, and its underrated successor The Mills of the Kavanaughs. Then, there were eight more years before the abrupt innovation of Life Studies. For the Union Dead was spotty, Near the Ocean spottier, and then the rot set in.

Now, no man should be hanged for losing his gift, most especially a man who suffered as Lowell did. But one can, I think, feel annoyed when quality plunges as quantity multiplies: Lowell published six bad books of poems in those disastrous last eight years of his life.

He continues:

9. Horace, when he wrote the Ars Poetica, recommended that poets keep their poems home for ten years; don’t let them go, don’t publish them until you have kept them around for ten years: by that time, they ought to stop moving on you; by that time, you ought to have them right. Sensible advice, I think — but difficult to follow. When [Alexander] Pope wrote “An Essay on Criticism” seventeen hundred years after Horace, he cut the waiting time in half, suggesting that poets keep their poems for five years before publication. Henry Adams said something about acceleration, mounting his complaint in 1912; some would say that acceleration has accelerated in the seventy years since. By this time, I would be grateful—and published poetry would be better—if people kept their poems home for eighteen months.

Poems have become as instant as coffee or onion soup mix. One of our eminent critics compared Lowell’s last book to the work of Horace, although some of its poems were dated the year of publication.

…

If Robert Lowell, John Berryman, and Robert Penn Warren publish without allowing for revision or self-criticism, how can we expect a twenty-four-year-old in Manhattan to wait five years—or eighteen months? With these famous men as models, how should we blame the young poet who boasts in a brochure of over four hundred poems published in the last five years? Or the publisher, advertising a book, who brags that his poet has published twelve books in ten years? Or the workshop teacher who meets a colleague on a crosswalk and buffs the backs of his fingernails against his tweed as he proclaims that, over the last two years, he has averaged “placing” two poems a week?

Hall then goes on to describe the MFA and how it has specifically, in his eyes, tainted the process of great poetry. Looking at the passage, one could imagine an eerily similar statement coming from a scientist who practiced from the mid into the late 1900s, talking about how the research process had become much more about detailed methods and learning to conduct a research pipeline slightly more rigorously and less about taking proper time and intellectual effort to do true exploration to find properly new ideas. Hall continues, furiously:

10. Abolish the MFA! What a ringing slogan for a new Cato: Iowa delenda est! [Iowa must be destroyed!] (Iowa possesses the most prominent MFA program.)

The workshop schools us to produce the McPoem, which is “a mold in plaster, / Made with no loss of time,” with no waste of effort, with no strenuous questioning as to merit. If we attend a workshop we must bring something to class or we do not contribute. What kind of workshop could Horace have contributed to, if he kept his poems to himself for ten years? No, we will not admit Horace and Pope to our workshops, for they will just sit there, holding back their own work, claiming it is not ready, acting superior, a bunch of elitists. . . .

When we use a metaphor, it is useful to make inquiries of it. I have already compared the workshop to a fast-food franchise, to a Ford assembly line. […] Or should we compare Creative Writing 401 to a sweatshop where women sew shirts at an illegally low wage? Probably the metaphor refers to none of the above, because the workshop is rarely a place for starting and finishing poems; it is a place for repairing them. The poetry workshop resembles a garage to which we bring incomplete or malfunctioning homemade machines for diagnosis and repair. Here is the homemade airplane for which the crazed inventor forgot to provide wings; here is the internal combustion engine all finished except that it lacks a carburetor; here is the rowboat without oarlocks, the ladder without rungs, the motorcycle without wheels. We advance our nonfunctional machine into a circle of other apprentice inventors and one or two senior Edisons. “Very good,” they say; “it almost flies. . . . How about, uh . . . how about wings?” Or, “Let me just show you how to build a carburetor. . . .”

Whatever we bring to this place, we bring it too soon. The weekly meetings of the workshop serve the haste of our culture. When we bring a new poem to the workshop, anxious for praise, others’ voices enter the poem’s metabolism before it is mature, distorting its possible growth and change.

He later moves on to examine the ill effects of the overt bureaucratization of the poetry profession — where, increasingly often, the university’s creative writing department or adjacent grant funders provided the best chance for poets to earn a steady income practicing some version of their craft. The effects could easily be seen. One only needed look at the industry’s newsletters:

14. A product of the creative writing industry is the writerly newsletter which concerns itself with publications, grants, and jobs—and with nothing serious. If poets meeting each other in 1941 discussed how much they were paid a line, now they trade information about grants; left wing and right united; to be Establishment is to have received a National Endowment for the Arts grant; to be anti-Establishment is to denounce the N.E.A. as a conspiracy.

…

Associated Writing Programs publishes A.W.P. Newsletter, which includes one article each issue—often a talk addressed to an A.W.P. meeting—and adds helpful business aids: The December 1982, issue includes advice on “The ‘Well Written’ Letter of Application,” lists of magazines requesting material (“The editors state they are looking for ‘straightforward but not inartistic work’”), lists of grants and awards (“The annual HARRY SMITH BOOK AWARD is given by COSMEP to…”), and notices of A.W.P. competitions and conventions. . . .

Really, these newsletters provide illusion; for jobs and grants go to the eminent people. As we all know, eminence is arithmetical: it derives from the number of units published times the prestige of the places of publication. People hiring or granting do not judge quality—it’s so subjective!—but anyone can multiply units by the prestige index and come off with the product. Eminence also brings readings. Can we go uncorrupted by such knowledge? I am asked to introduce a young poet’s volume; the publisher will pay the going rate; but I did not know that there was a going rate. . . . Even blurbs on jackets are commodities. They are exchanged for pamphlets, for readings; reciprocal blurbs are only the most obvious exchanges. . . .

I may need to add ‘Donald Hall’ to my list of ‘people who did progress studies before progress studies existed’…

Academics and the system they operated within used to understand that they were in a hit-making game. John Nash, with an h-index of 7, was employed by the profession for decades because they felt he, at any point, had the potential to produce a massive hit. Richard Feynman left new discoveries in his desk constantly. He felt they wouldn’t change much in the field, so they weren’t worth the hassle of publishing. He had more ambition than that. When he did publish interesting and ambitious papers, journals would not reject them because pieces of them were shaky. This Substack covered a case of Feynman publishing a finding, that turned out to be right, in spite of Bohr and Dirac openly saying beforehand they thought it was completely wrong. It was an amicable disagreement — most were. The journals were the best place to debate that sort of thing, so it was published!

Hall’s final paragraph, in a way, touches on all of this:

16. There is no audit we can perform on ourselves, to assure that we work with proper ambition. Obviously, it helps to be careful; to revise, to take time, to put the poem away; to pursue distance in the hope of objective measure. We know that the poem, to satisfy ambition’s goals, must not express mere personal feeling or opinion—as the moment’s McPoem does. It must by its language make art’s new object. We must try to hold ourselves to the mark; we must not write to publish or to prevail. Repeated scrutiny is the only method general enough for recommending. . . .

And of course repeated scrutiny is not foolproof; and we will fool ourselves. Nor can the hours we work provide an index of ambition or seriousness. Although Henry Moore laughs at artists who work only an hour or two a day, he acknowledges that sculptors can carve sixteen hours at a stretch for years on end—tap-tap-tap on stone—and remain lazy. We can revise our poems five hundred times; we can lock poems in their rooms for ten years—and remain modest in our endeavor. On the other hand, anyone casting a glance over biography or literary history must acknowledge: Some great poems have come without noticeable labor.

But, as I speak, I confuse realms. Ambition is not a quality of the poem but of the poet. Failure and achievement belong to the poet, and if our goal remains unattainable, then failure must be standard. To pursue the unattainable for eighty-five years, like Henry Moore, may imply a certain temperament. […] If there is no method of work that we can rely on, maybe at least we can encourage in ourselves a temperament that is not easily satisfied. Sometime when we are discouraged with our own work, we may notice that even the great poems, the sources and the standards, seem inadequate: “Ode to a Nightingale” feels too limited in scope, “Out of the Cradle Endlessly Rocking” too sloppy, “To His Coy Mistress” too neat, and “Among Schoolchildren” padded. . . .

Maybe ambition is appropriately unattainable when we acknowledge: No poem is so great as we demand that poetry be.

Ambition is not something to be metered and rewarded accordingly — it’s not possible. But everything possible should be done to, at the very least, not disincentivize it.

Poetry is only so similar to science. But it does seem that — even though in the American tradition writers and scientists do not co-habit the same areas of the intelligentsia as they do in Russia — many in both groups that lived through similar systems changes come together in the belief that the new institutions and incentives tainted their fields.

It’s not so silly to think that what happened to the field of poetry could inform how we think about counterfactual scientific history. As much as there are great scientists who learn by reading, the number of stories of great science as a predominantly learning-by-doing exercise abound. It’s not so silly to give serious consideration to the case of writers and the state of their field. Writers, after all, also spend substantial amounts of time formulating new ideas, perusing the works of peers, and attempting to deploy both new methods and ideas into their own work.

Surely, the burden of knowledge is more burdensome in science than in writing. But, it should not be forgotten, that many of the great scientists I’ve covered on this Substack didn’t place nearly as high a priority on ‘keeping up with the literature’ as modern researchers.

Edison spent time on it, but he spent far more time at the lab bench learning things for himself. He both kept up with and was extremely skeptical of the literature.

And if the reader feels that Edison’s era of electrical science was somehow primitive and is not representative, Willis Whitney — a former academic — eventually instituted a rule at the GE Research Lab where you’d get in trouble for going to the library too frequently. He learned, through early failures in relying too heavily on the literature, that it had limited effectiveness in solving problems — compared to experimentation and working with colleagues.

Not to belabor the point, but Feynman was also notorious for not exactly keeping up with the literature. He kept up to some extent, but often worked things out for himself, later checking the literature to see if he was the first one to have done that. He felt that was the best way — both to understand things and also to practice the process of figuring things out.

A different world — with different systems — yielded a different kind of researcher.

If true, how does the human systems hypothesis change things?

To me, the idea that the slowdown in scientific ideas might be driven far more by changes in human systems and incentives than some force of nature related to growing ‘idea space’ is great news. While solutions can likely be found to mitigate issues associated with the more standard burden of knowledge hypothesis, we’re still working against constraints of nature. In the world where it’s a human systems issue, we’re mostly working against people!

Working against people isn’t easy, but it’s doable. We’re already making great first steps. Progress studies funders have been very forward-thinking in funding new, experimental science orgs such as Arc Institute, Arcadia, and Convergent Research (with more to come) that provide invaluable learning opportunities on a small scale. Any learnings that prove successful on that small scale can grow into medium-term efforts — possibly even whole research institutes — which can scale, continue to experiment, and (hopefully) find even more success. In the longer run, the federal government — an effective copycat of ideas that have been de-risked and aren’t too politicized — could fold these learnings into their existing NIH and NSF policies. Or, as is often the case in government scientific history, they may start a new department to take advantage of the new learnings.

The pressing question then is: what are the best things these new science orgs can do?

The most general and boring answer is twofold:

1. Make sure you’re trying something truly different from existing efforts. We need novelty.

2. Document as much as possible about your novel attempt so we can learn from it!

My more prescriptive (and interesting) answer is also twofold:

1. Do more truly applied research! This was largely America’s biggest comparative advantage in research throughout the early-1900s. We found ways to let this process drive great basic research and vice-versa. I’ve written up detailed accounts of many different ways to do this that proved successful on this Substack:

   1. How did places like Bell Labs know how to ask the right questions?

   2. Irving Langmuir, the General Electric Research Laboratory, and when applications lead to theory

   3. A Progress Studies History of Early MIT— Part 2: An Industrial Research Powerhouse

   4. Tales of Edison's Lab & Thomas Edison, Technical Entrepreneur

2. If you’re doing basic research, focus on creating new scientific branches at the expense of all other things! It’s a right-tailed game, and it’s extremely worth it. As the pieces listed above detail, these new branches can often result from applied research projects if managed the right way — with researchers given certain problems and certain freedoms. The following pieces document processes that yielded branch-creation in a more (traditional) basic research setting:

   1. A Report on Scientific Branch-Creation: How the Rockefeller Foundation helped bootstrap the field of molecular biology

   2. John von Neumann: A Strange Kind of Bird

   3. When do ideas get easier to find?

To conclude, I implore the reader to remember something that Weaver, Feynman, Dyson, and Holton would agree upon: the way science is done is indelibly impacted by the way scientists are organized and incentivized. If you spoil their excitement and ambition, the whole enterprise becomes entirely different. The magnitude of change that can result should not be underestimated.

Thanks for reading:)

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In the near future, I would love to document — one by one — the historical details of why fields that used to work together closely grew apart. That kind of brute force project would go a long way in further addressing the question in today’s piece. If you’d like to help on that project, please reach out — it will take more people than just me!

Also, Chen Lu — the mathematician I mentioned — is finishing his Ph.D. in applied math at MIT and is looking for a job. Something like ML roles where he can use his math and coding toolkit would be ideal. You can check out his LinkedIn here and some of his publications here. If you’d like an intro, DM me on Twitter!

Appendix

When showing this paper around, one economist of innovation asked how I felt about Agarwal et al.’s paper on the growing size of publishing teams in mathematics in the aftermath of the Iron Curtain falling. I thought this was a very fair point and worth including, but one that would break up the flow of the main piece as it is a bit of an aside.

Before speaking briefly on the Agarwal paper, I should first start by explaining the previous and more well-known Borjas and Doran paper whose data Agarwal et al. used in their analysis. Borjas and Doran put together a dataset on the publications, citations, university affiliations, and more of both Soviet mathematicians as well as American mathematicians before and after the Iron Curtain falling. They pay special attention to the different effects the shock had on American mathematicians who were publishing in fields that the Soviet’s were particularly strong in vs. those where they were comparatively weak.

As the authors note, in spite of the fact that there were around 2.4x as many American mathematicians and Americans published 3x as many papers overall, there were areas in which the Soviets were far stronger, publishing 1.4x as many papers as Americans and having the undeniable world leaders in the space. There were also areas where the Soviet Union was essentially a non-factor, publishing around .05x as much as Americans. The following graphic gives you an idea of just how wide the difference was across fields — the bar measures the ratio of Soviet papers to American papers in a topic area.

Paying close attention to the labor market effects in the aftermath of the shock, the authors find (among other things):

• The overall number of papers written by professors at American universities was more or less unchanged after the Iron Curtain fell.

• The number of papers written per American mathematician and by American mathematicians overall went down, but this was counteracted by the effective increase in total Soviet-descendant professors publishing.

• American professors who published in the weakest Soviet disciplines were more or less unaffected, whereas those who published in Soviet areas of strength ended up publishing less, received fewer citations, were more likely to end up unemployed or at a worse university, etc.

  • However, if an American professor in an area of Soviet strength co-authored with a Soviet professor, it seems this was correlated with being unaffected.

• Around 1/8th of new professorships were being given to Soviet mathematicians immediately after the Iron Curtain fell, and these immigrants were particularly strong.

In general, I believe the Borjas and Doran observations in all of these areas are quite strong. As a dataset informing the labor market effects of the Soviet influence in American math academia from around 1975-2010 — which is what the paper claims to be — the methods and takeaways seem interesting and robust.

In the author’s own words, they summarize their results as follows:

Soviet mathematics developed in an insular fashion and along different specializations than American mathematics After the collapse of the Soviet Union, over 1,000 Soviet mathematicians (nearly a tenth of the pre-existing workforce) migrated to other countries, with about 30 percent settling in the United States. As a result, some fields in the American mathematics community experienced a flood of new mathematicians, theorems, and ideas, while other fields received few Soviet mathematicians and gained few potential insights.

Our empirical analysis unambiguously documents that the typical American mathematician whose research agenda most overlapped with that of the Soviets suffered a reduction in productivity after the collapse of the Soviet Union. Based solely on the pre-1992 age-output profile of American mathematicians, we find that the actual post-1992 output of mathematicians whose work most overlapped with that of the Soviets and hence could have benefited more from the influx of Soviet ideas is far below what would have been expected. The data also reveal that these American mathematicians became much more likely to switch institutions; that the switch entailed a move to a lower quality institution; that many of these American mathematicians ceased publishing relatively early in their career; and that they became much less likely to publish a “home run” after the arrival of the Soviet émigrés. Although total output declined for the pre-existing group of American mathematicians, the gap was “filled in” by the contribution of Soviet émigrés

I think that is a great paper and I value the results a lot.

Agarwal et al., four years later, use mostly the same data and attempt to tell a burden of knowledge hypothesis story with it. I don’t think it would be an unfair interpretation to say that their work surely approximates — to some extent — something of an upper-bound on the ‘burden of knowledge coefficient,’ but I believe it would be a stretch to say it establishes any kind of well-identified lower-bound. I’ll begin to tell you why in the next paragraph. But, before I do, it is probably worth pointing out that — in spite of Ben Jone’s paper on the burden of knowledge having been published several years before the Borjas and Doran paper — Borjas and Doran did not choose to make claims about their data as demonstrating proof of the burden of knowledge in their paper.

Agarwal et al., however, do attempt to make this claim using largely the same data. I don’t think it’s unreasonable for the journal to have published the paper, but I do think the results are not nearly as robust as Borjas and Doran’s and should be used with caution. Agarwal et al. attempt to exploit the difference in team size trends between the three sub-fields in which the Soviets were strongest and the three sub-fields in which the Soviets were the weakest. The trend they’re looking at is visualized below — with the orange line representing American team size in Soviet-rich areas and the blue the team size of areas of Soviet weakness.

As is common, the starting point of the data is in 1970. From 1970 to 1991, there is a slow and steady rise in both lines, then — and around the fall of the Iron Curtain — the author count in Soviet-rich sub-fields begins to climb at a higher rate. The authors wrote, “For the treated subfields (Soviet-rich), the mean team size for the 20-year period before 1990 was 1.34 compared to 1.78 for the 20-year period after. By comparison, for the control subfields (Soviet-poor), the mean team size was 1.26 before compared to 1.55 after.” That increase in .29 authors per paper in the ‘control’ group vs. .44 in the ‘treatment’ group is observational and not to be disputed. In relation to how this affects the human systems hypothesis, the grains of salt I take their solutions with — as they do/don’t apply to the hypothesis — have to do with 1) what the authors could not control for that also change around this period and 2) the time period of American academia in which the shock occurred.

The first grain of salt I take this chart in with is that all of the changes resulting from this shock are happening in a post-1970 American system which I’ve never disputed has certain norms and systems for accounting for new ideas that would make things like team size grow. That is my biggest issue, but it is also unsurprising, I’m sure.

The second grain of salt I take the results in with is that the effects of a knowledge shock that result from an entire country’s ideas — that have been built of over decades — reaching the world are probably not the same as when individuals or small teams produce an idea. One major difference being: if it’s just one researcher’s big and new idea, there is only one of them to go around. In the Iron Curtain case, there were 12,000+ other researchers who had been familiar with many of the ideas for a while. 1,000+ of the most talented ones abruptly left to research abroad in other country’s. When combined with the first grain of salt, this could impact the trends we see in the data in a way that is not representative of the standard case of idea creation.

The third grain of salt I take the paper with is that it does not control for the labor market influx of Soviet researchers to the US.1 And the influx was non-negligible. In fact, the labor market shock itself was what Borjas and Doran exploited in their paper. Borjas and Doran noted that around 1/8th of new professorships in the post-Iron Curtain falling years were going to Soviets — and quite inordinately talented Soviets. In an attempt to show that their results were robust to this, Agarwal et al. show a chart of Japan because Japan had almost no Soviet mathematics immigrants. They ran other regressions as well, but, first, I’ll address the Japan chart — the only other country’s chart they chose to show.2

Looking at the chart, I found it strange that the Soviet-poor fields had such steady team size numbers pre-fall of the Iron Curtain but then began a noticeable and steady climb after the Iron Curtain fell. Agarwal et al. did not mention this which I found strange, because whatever happened there is significantly larger than the effect noted by the distance between the orange and blue lines. This distance between the two lines is what the authors’ regressions concern themselves with. I asked an economics of innovation-related researcher who works with the Japanese government if anything happened in the early 1990s as well. He laughed and said that the years around 1995 marked extremely important changes. This period saw substantial increases in government input, funding, and planning for many types of scientific grants.

I asked some questions about how these worked, and it seems like the new policies were often very NIH-like — large government employee oversight, sizable panels, proposal processes, etc. So, I don’t personally take that Japan chart very seriously — unless you are very compelled by the first three pairs of dots post-Iron Curtain falling, in which they noisily grow apart and back together again before the onset of the government changes. If I did take the chart seriously, accounting for the change in human systems, it very well could tell a story that points the finger more towards the human systems hypothesis as driving the overall changes more so than the burden of knowledge hypothesis.

The regressions the authors ran on other countries — which they did not visualize — are essentially tracking the same thing — the statistical significance of the growth in the gap between those two lines before and after the iron curtain fell. (Half of these countries’ regression coefficients did not come out as significant at the 95% confidence interval.) As with the Japanese chart, the paper does not seem to pay attention to the fact that there could be much more significant changes happening elsewhere in the system that the methods (and authors) are unaware of and don’t account for. I don’t blame them because it is extremely burdensome — on the order of months — to figure out exactly what happened in even a handful of countries' scientific grant-funding ecosystems over that timeline. But, what matters for our interpretation is that they didn’t. Here is a 1995 Nature article titled Japan opens a new era in university funding very publicly exploring some of these changes.

(Also, see Figure 2-10 at this link, Trends in Budget for Grants-in-Aid for Scientific Research, showing related funding changes impacting trends as early as 1991.)

Speaking frankly, anything could have been happening around 1991 in any number of those countries that the authors do not know about. In the best case, the method only identifies the existence of a burden of knowledge and does nothing to identify the burden of knowledge effects as anything more than existing and being statistically significant — saying nothing about its presence as a primary driver of stagnation. And, once again, that is if you buy into the premise of their natural experiment as a natural experiment at all.

I read this paper as doing an okay job (at best) of isolating the presence of a burden of knowledge-type effect in the US ecosystem conditional on the shock being introduced to the post-1970 US ecosystem. I believe the coefficient estimates themselves are very likely overestimated. It is highly likely that they capture the effects of things that the authors did not/could not control for, such as: the new system itself interacted with the math field type, the full effects of new Soviet colleagues on their American colleagues, and the effects of the “knowledge” coming from 12,000 people all at once rather than a handful.

Natural experiment papers can only be as strong as the natural experiment itself. And there’s just a lot of moving parts here. Throughout this piece, I’ve used many papers whose results maybe get over-interpreted by others, but that I think are great and well-done papers that are very thorough. This paper — unlike the Borjas and Doran paper written using the same event as a shock — is one that I think should be used more carefully.

We have a word for people like him now: technical entrepreneur And he was the best ever.

• He took tech that barely worked and made it useful

• He took products to market at prices people were willing to pay

• He made things that could be manufactured at scale

• He set outrageous deadlines AND hit them

• He built systems with others' inventions that the original inventors didn't dream of

So no, he was not an inventor. He was something even better

Also, tragically, I don't think the modern US could make use of someone of Edison's talents. Check out the piece to learn how Edison did what he did and why a modern-day Edison might be wasted on today's US.

Check it out here!!

Also…

For those interested, check out the podcast I put together exploring what it was like to work in Edison’s lab:

I have another piece coming out Thursday diving into why the historical evidence leads me to believe there is a better hypothesis than the ‘burden of knowledge’ hypothesis to address the question, ‘What is the primary driver of the scientific slowdown?’ Stay tuned for that!

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Some research projects feel like they are squarely in one bucket or the other, but it’s not always that clear. Applied research is meant to be research with immediate applications in mind. But, of course, applied research could stumble upon something that leads to a fundamental insight. Basic research is meant to be curiosity-driven research without immediate applications in mind. But, of course, it could quickly lead to a killer application.

In the universe of possible courses of research, there exist many questions that, in the end, will satisfy the spirit of both applied and basic research.

The natural follow-up question is: is finding this subset of golden problems really feasible?

One’s knee-jerk reaction might be that it is not replicable in any kind of systematic way; it is a matter of unreliable personal taste. The history tells a different story. The mid-20th century’s great American R&D labs show us that selecting profitable courses of research that satisfy the spirit of basic research has been done at a high level within large research organizations over the course of several decades.

In this piece, I dive into exactly how Bell Labs ensured that their researchers were working on the right problems. This piece will be the first in a series examining what modern applied research orgs can learn from the great dragons of industrial R&D — places like Bell Labs, GE Research Laboratory, and DuPont’s research department.

Institutions like these not only had Nobel prizes to their names, but each — even though they’ve diminished for various reasons — was quite profitable too. They had their differences, but they all stumbled upon many aspects of managing their research operations that were rather similar. The managers of these organizations — and other researchers at the time — often felt the management decisions they made were common sense rather than some great discovery.

However, these common-sense decisions are things we often don’t do today – but almost certainly should.

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Sorry for the delay since my last post. I was 1) working on some projects for some applied science orgs and 2) wrote a piece for the coming issue of Works in Progress that is coming out soon!

You will be getting much more frequent releases from me in the coming couple of months, I promise. As always, if you’d like to discuss how to implement any of the ideas in the piece in your own operation, feel free to reach out on Twitter!

The initial inspiration for much of this piece comes from Jon Gertner’s book, Idea Factory, on the history of Bell Labs. In places, I quote Gertner’s descriptions of events where his words did a better job than mine could.

This piece is done in partnership with the Good Science Project.

Back to the action..

Bell Labs has become legendary in many tech circles. It’s no secret why. Famous ideas and technology like information theory, communications satellites, solar batteries, transistors, and countless other communications-related innovations trace their origins back to Bell Labs in one way or another.

Idolizing Bell Labs for its outcomes is very fair because its outcomes were extraordinary. Many, in recent years, have also begun to idolize Bell Labs’ for its processes. And there’s nothing conceptually wrong with that. If a place has consistently fantastic outcomes and seems to have some secret sauce that is super-additive to the productivity of its researchers, why would we not seek to replicate it?

We should. The issue is that many who idolize Bell’s processes seem to fundamentally misunderstand how the operation worked. The most notable misconception is that many put Bell forward as the poster child of how idle curiosity and the purest kind of basic research can have a role in industry. Looking at the historical sources, that’s not exactly an accurate takeaway.

Bell did a lot of astonishing basic research. But its research, while “basic” for an applied R&D lab, was not nearly as free as many imagine — or, rather, it embodied a different kind of freedom. Equating the freedom of a Fine Hall mathematician at the Princeton Institute for Advanced Study and a physicist at Bell Labs in the 1950s is not an accurate way of looking at it.

Bell was an industrial R&D lab. To an industrial R&D lab, the mission is everything. Frank Jewett, the founding Director of Bell Labs, once said that his new industrial R&D lab was to be:

An instrument capable of avoiding many of the mistakes of a blind cut-and-try experimentation. It is likewise an instrument which can bring to bear an aggregate of creative force on any particular problem which is infinitely greater than any force which can be conceived of as residing in the intellectual capacity of an individual.

This focus on applications leading the research is not one that faded over the course of Bell Labs’ lifetime.

John Pierce — whose 35-year career (1936-1971) at Bell Labs as researcher and manager encompassed most of Bell Labs’ existence — said this of what made Bell Labs a success:

Someone depended on them for something, and was anxious to get it. They were really needed, and they rose to the need.

The people who see Bell Labs as a bastion of freedom in private sector research are not entirely mistaken. Bell was pretty damn free for a private-sector lab. It’s just that there was a balancing act.

Jim Fisk was one of the “Young Turks” at Bell Labs — along with Pierce — who helped shepherd in its famous balance of deep research with careful problem selection. He said the following of Bell’s philosophy on problem selection when he was managing Bell Labs:

Our fundamental belief is that there is no difference between good science and good science relevant to our business. Among a thousand scientific problems, a hundred or so will be interesting, but only one or two will be truly rewarding — both to the world of science and to us. What we try to provide is the atmosphere that will make selecting the one or two in a thousand a matter of individual responsibility and essentially automatic.

This is not Fisk saying that the only relevant problems in electrical communication were those that served Bell’s business interests. But it was him saying that:

• Many scientific problems are kind of a bore or derivative. He ballparked it arbitrarily at 90%.

• Some minority of problems are interesting. He ballparked it arbitrarily at 10%.

• 1%-2% of the interesting problems — that is .1%-.2% of the total problems — would turn out to be worthwhile and relevant to Bell’s work.

The picture this paints of Bell’s preferences for its basic researchers is twofold:

1. The universe of possible problems is very large. Bell would like its more fundamental researchers to feel free to work on interesting ones.

2. Among those interesting problems, Bell Labs management would implement systems to make sure researchers identified problems that had a high probability of turning into profitable answers for the Bell Telephone system.

Over the years, Bell Labs management developed a small but coherent set of constraints and rules of thumb to ensure that its researchers internalized that, as Jim Fisk put it, it was “a matter of individual responsibility” to choose the right problems and that Bell Lab’s success in doing this at scale, across thousands of individuals, was “essentially automatic.”

Bell Labs research problem selection: rules of thumb, systems, and constraints

The majority of Bell Labs was made up of applied researchers, development engineers, and other staff — not basic researchers. And these groups usually had a normal boss and projects assigned to them – while Bell’s basic researchers did not. Nevertheless, even though the basic researchers did not have bosses in the traditional sense, they were still nudged to Bell-relevant problems in various ways.

The three key ways Bell Labs nudged its basic researchers toward the right problems were:

1. Granting researchers what I’ll call a “long leash, but a narrow fence” in which to conduct their explorations.

2. Facilitating very regular interactions between the basic researchers and Bell’s fundamental development researchers, engineers, manufacturing facilities, and implementation staff.

3. To top it off, Bell had a corps of what they called systems engineers who ensured that the integration of its best researchers and most pressing problems was not left to chance.

Let’s explore each of these, in turn.

1) Long leash, narrow fence

Bell didn’t exactly tell its basic researchers what they could and could not work on. Not usually at least. A basic researcher’s boss was more of a mentor or advisor than an actual boss.

(Note: the basic researchers made up anywhere from 7% to 18% of Bell Lab's headcount depending on the year and which Young Turk you quote.)

These individuals were guided toward the right problems in other ways. Firstly, it was made clear that the projects should have some obvious bearing on the Bell system and future business. And one was allowed to roam around, so to speak, for a bit before working out exactly what they would be spending their time on, but they should be looking to spend their time on something quite relevant to the business.

The following excerpt fromJohn Pierce’s oral history briefly describes his reflection on his time immediately after joining Bell. He had a particularly high level of freedom in feeling his way around for work, but still found his way into the Bell Labs groove all the same:

Pierce: I was told to do research on vacuum tubes. People sort of just left me alone. They did suggest that I go and see Philo Farnsworth, who was working on electron multipliers and television pick-up tubes, but I was left pretty much to myself. This was very, very confusing to me. I didn’t know what to do.

Interviewer: Were you doing it alone?

Pierce: Yes

Interviewer: Did they say, “So-and-so has been doing this and this is where he left off”?

Pierce: No. I was just supposed to plan something to do and do it. I think that is close to cruel and unusual punishment.

Pierce, who was giving this interview after his retirement from Bell Labs while he was at CalTech, then continues his reflection:

Pierce: Too much freedom is horrible. It’s like telling a young child, “Do whatever you want to.” You’ve heard this story. There are various outcomes. One is, “Do I have to do what I want to?” Complete freedom is not very helpful to a person who is inexperienced in the world. It’s certainly bad to be directed to do things very, very narrowly and with no freedom. It’s my guess that for every person who needs more freedom, there are ten people who need more help in finding their way.

Interviewer: So, did they tell you why they wanted the vacuum tubes, when you started off?

Pierce: Not really. I found out some way, inadvertently. Some people were working on electron multipliers, and I made some improvements on them. It became clear that people needed better vacuum tubes for building negative feedback amplifiers, and I worked on that. I don’t think I was told this formally; I just found out by talking to people. Then, as the war approached and we got into war, it became apparent that microwave radar was very, very important, and I worked on tubes for radar. It was a process of osmosis rather than direction that led me into these things, as I remember it.

This Pierce story is an example of things working exactly as they should. An extremely talented young researcher with a background obviously relevant to Bell — multiple electrical engineering degrees from CalTech — came to understand exactly what development work was ongoing at Labs, what it looked like for a basic researcher to be useful to that work, and came up with a course of work to suit those needs.

Morry Tannenbaum, a long-time Bell Labs chemist, famously described this patented level of freedom as “circumscribed freedom.”

Pierce’s story leads us into the second way in which Bell Labs nudged its basic researchers toward the right problems.

2) Frequent interactions with Bell’s development researchers, engineers, manufacturing facilities, and implementation staff

Relationships with the folks who might eventually deploy your research – from those who modified cutting-edge engineering equipment to those that worked in Bell’s factories – ensured researchers were hyper-aware of the problems happening throughout Bell’s massive operation.

The one hard and fast rule Labs did seem to have was that you could not say no to any request for help from any of the applied folks — or other researchers for that matter. Your day-to-day tasks often pertained to your own courses of research, but one’s role as in-house expertise was equally important. These consultations, unsurprisingly, led to all sorts of new ideas for basic research projects.

Another excerpt in Pierce’s oral history is just one of many data points that speaks to the importance of this relationship:

I remember that during the war we saw a good deal of people from Western Electric [Bell’s manufacturing arm], who were going to manufacture the things that we devised. Because all of these people were engaged in telephony, or during the war because they were all engaged in radar and other military things, you got to talk to people who were engaged in the operation of things, who were engaged in the manufacture of things, and you got a picture of the rest of the world which certainly influenced what research you did.

He continues, diving into how this type of interaction was a natural partner to great basic researchers:

I can understand a university, which does teaching and research. But the idea of a research institute without ties to either teaching or to manufacturing or operational organization seems a terribly sterile idea. You see that in the Soviet Union; there’s a lot of good activity that never results in anything. When they want to build automobiles, they hire Fiat to build an automobile plant, instead of relying on what they have learned.

(Note: Pierce also believed the university model of research to be an inferior model — for him at least — for reasons I’ll discuss later.)

And, since Bell, as a business and research operation, was far too vast and complex to rely on serendipity to match researchers and problems, it had an entire class of engineers dedicated to ensuring problems and solutions found each other.

3) Bell systems engineers tied this whole process together

Systems engineers – 10% of Bell Labs’ total headcount – were usually technically-trained individuals who spent all of their time, as Jon Gertner put it, keeping:

One eye on the reservoir of new knowledge and another on the existing phone system and analyzed how to integrate the two. In other words, the systems engineers considered whether new applications were possible, plausible, necessary, and economical.

The existence of systems engineers was Bell acknowledging that a culture of openness and helpfulness was just not sufficient when it came to finding the best problems possible. Of course, implementation/manufacturing/applied research staff often can identify which of their problems are ripe for the research team’s eyes, but a lot of the time they can’t. And yeah, sometimes researchers can come up with great research questions in their area that are ripe for helping a specific group’s work, but a lot of the time they don’t do a great job.

Even if a basic researcher does find a good applied problem, who’s to say that the problem is the best use of their time? There is almost surely a better problem out there. That’s life. The question is, can someone reliably find it?

If a systems engineer does their job well, they can.

Mervin Kelly, long-time Bell Labs manager, described the background of his systems engineers as follows:

[Systems Engineering] staff members must supply a proper blending of competence and background in each of the three areas that it contacts: research and fundamental development, specific systems and facilities development, and operations. It is, therefore, largely made up of men drawn from these areas who have exhibited unusual talents in analysis and the objectivity so essential to their appraisal responsibility.

Of course, there is a tradeoff here. Instead of using a systems engineer’s skills for normal scientific research or engineering tasks, these individuals were doing other kinds of work. That’s not a small tradeoff. At points, Bell’s systems engineering team was about the same size as, maybe larger than, Bell’s basic research group. But, in a large and complex organization like Bell, this tradeoff was well worth it.

The systems engineers made it their business to be extremely aware of the happenings of the research portions of Bell Labs as well as the minutiae of the industrial portions of Bell Telephone. This included details like:

• Manufacturing processes to produce electrical parts

• Which materials or parts tended to degrade and needed to be replaced in the telephone system

• The cost and time of various repairs and maintenance

• What portions of Bell’s service were currently bottlenecked by specific technical problems

Of course, no individual systems engineer could know everything and everyone at Bell. But the department as a whole attempted to account for everything, ensuring as little as possible fell through the cracks. And this process worked both ways. These systems engineers, in addition to bringing problems to researchers, also found ways to deploy researchers’ findings in ways that could solve problems in the field or improve Bell’s products and processes.

Mundane systems engineering problem spotting happens when a systems engineer identifies that Bell is spending the equivalent of $1 billion yearly on telephone wire maintenance in certain climates. This engineer can then notify the metallurgy researchers that this problem exists and is begging to be solved.

One Bell Labs executive, a former chemist, loved to point out that a synthetic plastic created by Bell chemists to replace the existing telephone cable sheathing saved Bell “more than the total research budget of Bell Labs for the decade in which the innovation was worked out.” This was an operationally boring problem that could have been hidden in some maintenance budget, away from the eyes of normal researchers. A system engineer exists to identify opportunities just like that.

The ROI of an applied research operation can obviously go up if researchers have problems like this regularly brought to them. And, it should be remembered, these problems were being brought to researchers not just as a veritable gold mine, but with many research-relevant constraints worked out from the beginning. It was the job of the systems researchers to work out as much of this as possible beforehand.

Mervin Kelly believed that the Bell’s continuity was what made it special. If the first two rules of thumb established the continuity, the systems engineers were what ensured it. Kelly spoke about the importance everything connecting the two endpoints of manufacture and basic research in a speech to the Royal Society, saying:

There has been so much emphasis on industrial research and mass-production methods in my country, that even our well-informed public is not sufficiently aware of the necessary and most important chain of events that lies between the initial step of basic research and the terminal operation of manufacture. In order to stress the continuity of procedures from research to engineering of product into manufacture and to emphasize their real unity, I speak of them as the single entity ‘organized creative technology.’

(Please see the bonus piece to learn more about this speech.)

Systems engineers did not technically do anything that you wouldn’t hope would happen with a culture of collaboration, but they were the people that made finding the “one or two in a thousand” problems relevant to Bell and converting them into successful business applications “essentially automatic.”

Freedom comes in many forms

These rules of thumb are contrary to what many believe of Bell Labs’s culture, but most accounts I’ve read from key Labs members point to these methods as a secret sauce that made Bell Labs effective.

The famous stories of Claude Shannon frittering away his days at Bell Labs is a special case. While most researchers did not have the kinds of freedoms Shannon — or many university professors at the time — had, they were usually happy with the tradeoffs. In other ways, many felt life at Bell Labs had a different kind of freedom.

Claude Shannon’s frittering

Stories of Claude Shannon frittering away his time playing games in the Bell lunchroom have become legendary. And I get why. The stories of Shannon building chess machines, juggling, and riding around on unicycles or pogo sticks are great stories. But these stories were not the norm at Bell Labs.

The bulk of these Shannon stories, at least the most “fritter-y” ones, come from after he became a celebrity in the communications world with his discovery — or “invention” depending on your philosophical view of mathematics — of information theory.

On the heels of that discovery, instead of some big financial reward for Shannon, Bell Labs management seems to have paid Shannon with a kind of emeritus status in which they gave the genius the freedom to do whatever he wished. This came with freedom to do unique things like unicycle down hallways or work with the door to his office closed.

Prior to this emeritus lifestyle, Shannon had lived a much more applied, standard life at Labs in which he was often roped into advising the applied folks on their issues and undertook more pressing courses of basic research — fire control and cryptography for the war effort, the mathematics of carrying calls along wires more efficiently, etc.

(Also, it’s worth noting, he used this emeritus-style freedom to accomplish little-to-nothing either for Bell Labs or his personal research agenda in comparison to his earlier life when he was a normal Bell Labs employee or a graduate student on Vannevar Bush’s differential analyzer project.)

In deciding to eventually leave Bell Labs for MIT in 1956, Shannon wrote the following in a letter to his supervisor, Hendrik Bode, on how he was spending his time at Labs:

It always seemed to me that the freedom I took [at the Labs] was something of a special favor.

He knew that the way he was spending his time at Bell Labs was not in line with its culture. At a university, he felt the freedom he took in terms of focus and hours of work would be less unusual.

Did the university-trained researchers yearn for the freedom of the university?

The lifestyle of a researcher at Bell Labs, on the face of it, does not seem to have the level of personal freedom university professors had.

Some researchers, like Shannon, did leave to work at universities. Their research often became smaller-scale in terms of resources, but they were more free to do as they wished. A Bell researcher leaving to join a university often viewed it as a lateral move. Shannon wrote in his letter to Bode:

With regard to personnel, I feel Bell Labs is at least equal in caliber to the general level in academic circles. In some of their specialties Bell Labs is certainly stronger.

University life surely had freedoms that Bell didn’t, but most Bell researchers seemed rather content with the tradeoffs.

Jon Gertner’s book has a great excerpt that recounts what John Pierce thought of the freedoms of his post-Bell home, CalTech, compared to his life at Bell. The excerpt helps one see how, in its own way, the circumscribed freedom of a researcher at Bell was much freer than a professor’s — even in a less bureaucratic era of university life. Gertner writes:

Pierce went back home to Caltech. For six years he had been doing research and advising graduate students, but he was finding the adjustment difficult. At Bell Labs he had spent his days doing whatever suited him. The brunt of his management work there had consisted of dropping in, unannounced, on colleagues in their labs to ask how work was progressing. But at Caltech he had to give lectures at a prearranged time and then had to spend hours explaining complex ideas to grad students. At Bell Labs, as he recalled it, the same conversation with his colleagues would usually take minutes. (Whether his colleagues actually understood his explanations, or whether he simply walked away before he could field their questions, was a matter for debate.) “I didn’t adapt well to Cal Tech,” he later admitted. “Not that there was anything wrong. For years and years I’d had it too easy. There were very few times when it mattered where I was. I had very few obligations to be at a particular place at a particular time to do a particular thing at Bell Labs.” Pierce obviously seemed to favor the Bell Labs arrangement. As he saw it, the work at the Labs was vital; it was required to improve the network. “People cared about everything,” he said of colleagues there. On the contrary, he noted, in the university “no one can tell a professor what to do, on the one hand. But in any deep sense, nobody cares what he’s doing, either.”

To Pierce, being genuinely needed was its own kind of freedom.

Karl Compton, who would eventually become President of MIT, wrote a Science article in 1927 dedicated to all the things a university physics department could learn from how industry R&D labs worked at the time. Some of his reasons for supporting this directly address Pierce’s “nobody ever actually depends on you for anything” conundrum. Compton writes:

Much can…be done to promote cooperation and coordination through actual methods of organization. This has been strikingly demonstrated in some of the big industrial research laboratories, from which the output has greatly exceeded the individual capacities of the research workers and has been achieved only by coordination of effort.

To Compton, the project coordination of places like Bell Labs or GE Research with a clear and limited set of goals — the narrow fence we speak of — was super-additive. The minds and hands, in this setting, added up to far more than they would’ve in a university setting.

It should also be noted that when Compton did eventually take over as the head of a physics department — at Princeton — he was not able to implement any of these lessons. I’m not even sure he tried. Then, as now, changing the structure of an old university was probably a non-starter.

Luckily, newer science organizations like the ones being started today are not so tradition-laden.

The mobile phone system: a case study in phenomenal systems engineering

Before concluding, I’d like to paint a picture of what fantastic systems engineering work can look like.

To some, the concept of systems engineers keeping one eye on the reservoir of new knowledge and the other on the details of the phone system does not leave a lot of room for personal glory. Those who feel this way might liken systems engineers to “system quarterbacks” — a mostly derisive word for American football quarterbacks who simply try to facilitate the careful running of the offense instead of attempting to make any big plays themselves.

I don’t think that’s accurate. Great systems engineering work, like great scientific research, has an element of glamor to it. The story of how a trio of Bell systems engineers helped make the mobile phone system a reality should help you see why.

In January 1966, there were rumors that the FCC was thinking about granting Bell Labs access to a larger portion of the limited radio spectrum — a finite resource that the US government decides how to allocate. The range of spectrum being allocated — which twenty years earlier had been allocated to television broadcasters — could be used to make the dream of widespread telephony a reality…probably…somehow.

There were many open questions, but Bell had a kernel of an idea on how to do this. The writeup of the idea was submitted to the FCC by Bell engineers two decades prior. Dick Frenkiel and Phil Porter now found themselves in charge of making the idea a reality. Frenkiel and Porter were both systems engineers at Bell’s rural Holmdel outpost — Frenkiel a mechanical engineer by training and Porter an electrical engineer with a master's in physics.

This was far more exciting work than their previous assignments — at least for Frenkiel who was previously working on machines that could read off pre-recorded messages such as the day’s date. The duo excitedly took to the work.

To start, the major question was, “What would a major course of development even look like for this primitive technology?”

Luckily, they were not starting from scratch. The first step was to dust off Doug Ring and Rae Young’s short 1947 memo to the FCC — two decades before — in which they proposed a non-obvious, very efficient (albeit hypothetical) system in which Bell could use the radio spectrum. Instead of providing coverage to some large circle of users with a cell antenna at the center of it, Ring and Young proposed Bell lay out the system as a honeycomb of hexagons with small antennas at the point of each hexagon and neighboring hexagons could use different frequencies. This would make the limited spectrum allocated to Bell go much further than it otherwise could.

To give the reader an idea, the following images were pulled from Ring and Young’s initial 1947 report. These images show what the layout would look like if the FCC granted Bell either three or four frequencies.

I was not able to figure out if Ring and Young were systems engineers or simply engineers doing systems engineering style work. Regardless, it was fantastic work and a great start to the project. But the most impressive aspects of the project, in my opinion, were almost entirely ahead of this point. After all, the concept of a hexagonal honeycomb is not unfamiliar to many engineers as an efficient way to cover 100% of a space with a circle-like shape that still has vertices.

The honeycomb idea was still a great idea, it just wasn’t going to win anybody any awards on its own. It was the fantastic planning, troubleshooting, and engineering development work of Bell, all started by these two systems engineers, that would turn this idea from a document of eight short pages plus an appendix into a mass-scale engineering reality.

Gertner writes on the (varied) early work of Frenkiel and Porter on this project:

Neither Frenkiel nor Porter knew precisely how this would be achieved. “It was just two of us,” Frenkiel says. “Nothing important.”

They spent most of 1966 working on the problem — or rather, the problems. The two men covered the walls of their offices with maps and climbed on ladders in various parts of the country to count hills. There were thousands of questions they would need to answer eventually. Many of these were extremely technical, regarding reception and transmission. They talked about signal strength and interference and channel width. They knew every cell would need to be served by what they called “base station” antennas. These antennas would (1) transmit and receive the signals from the mobile phones and (2) feed those signals, by cable, into a switching center that was connected to the nationwide Bell System. Still, several big conceptual problems stood out.

The first was, How large should a hexagonal cell be? Base station antennas would be expensive. How few could they install and still have a high-functioning system?

The second was, How could you “split” a cell? The system would almost certainly start with just a few users—meaning big cells. But as the number of users grew, those cells would subdivide to accommodate the traffic. And more, smaller cells would require more base stations. What was the best and cheapest way?

The third was, How would you “hand off” a call from one cell to another? It had never been done. But it would be the system’s essential characteristic. As a mobile telephone user moved around, how could you switch the call from one antenna to another — from cell to cell, in other words — without causing great distraction to the caller?

Question by question, they persisted.

A year or so after this work began a third systems engineer, Joel Engel joined the project. Engel — who had a Ph.D. in electrical engineering — was currently assigned to a project on the Bell Boy — a kind of beeper — and was excited to use his spare time on this project because the beeper was largely uninteresting to him. He noted that to get ahead at Bell Labs, “you were supposed to work on more than you were asked to work on.” Still a bit of a newcomer to Bell Labs, he was right on this point. Mervin Kelly used to often tell new hires at Labs, “You get paid for the seven and a half hours a day you put in here, but you get your raises and promotions on what you do in the other sixteen and a half hours.” 

So, Engel joined the duo. The now-trio would huddle into conference rooms to draw hexagons on the blackboard and figure out how the technical pieces of this thing could work.

They were neither true engineers nor business visionaries. The three would surely admit to this second point. They might be more reluctant on the first point — but the proper development engineers would sometimes mention this offhand. The three did not see the true scope of what their project could become. Engel once noted:

We were not visionaries,” Engel says of the early cellular meetings. “We were techies. If there was a vision it was primarily as a business service. Real estate agents. Doctors who made house calls.

Even as a specialized service for particular businesses, the economics worked. They’d done the math. They’d worked that out along with approximate answers to hundreds of technical questions that needed to be thought through before significant engineering time and resources should be invested in developing the project.

The trio was young and unafraid to work hard, diving into the open-ended, behemoth of a project. The trio’s in-depth planning leveraged:

1. Heavy fieldwork — to understand issues involving the terrain and weather

2. The more conceptual side of their degrees — to understand and extend the initial hexagonal idea

3. (Most of all) Their knowledge of recent developments in various engineering fields — to facilitate the storage and passing of signals

Working out a high-level, implementable, profitable system that could locate a user moving through a honeycomb cell, monitor the strength of the call, and pass the call between channels and towers was the job of the systems engineers. The task required deep scientific, engineering, and operational knowledge of Bell’s installation capacities.

In the end, the trio successfully navigated all of these difficulties. By any measurement, their individual effects on the massive field of mobile telephony are giant — even if their names are not.

Of course, the trio had their limitations. The win was a team win and required the skills of far more than just those three.

While the project did not require any brand-new, Nobel-level academic accomplishments, it did require hundreds of engineering innovations and improvements in the understanding of many pieces of technology. That is where the great development engineers at Bell came in — people like Bill Jakes and Gerry DiPiazza. These were some of “the guys who made cellular real,” as Frenkiel once said.

Jakes was the lead engineer on the fundamental development end of things — this group often carried out less open-ended research projects on things like engineering equipment. Jakes was known to lead crews of engineers out, piling into vans with recording equipment and headphones, to study the effects of forces like obstructions and distances on transmission and reception. They drove thousands of miles, over many months, working through problem after problem related to things like why some particular wave or piece of equipment behaved a certain way in a certain kind of terrain.

As was always the case, the systems engineers were there every step of the way helping coordinate this development work. This was exceedingly necessary as it was not only people like Jakes carrying out this sort of work. It grew into a very large operation — as projects like this always do — across many Bell Labs research locations and teams.

(Check out the bonus piece if you’d like to know more about how this work was coordinated)

One of these research teams operating in parallel, as an example, was led by another great Bell development engineer, Gerry DiPiazza — who I’ve seen called an “engineer’s engineer” in several places. His group was carrying out similar work learning how to build better signal hardware in a stripped trailer home outside of Philadelphia.

DiPiazza reflected on his team and what they were working on when they took their midnight research road trips — when they could test signal strengths and tinker with hardware in a more “noiseless” environment:

You had to find out, what is the noise level in a suburban environment? How far would a signal go if the antenna was at ten feet, twenty feet, fifty feet? Would it go one mile, two miles, four miles? How many antennas do you need? How do you build an antenna? What are you going to put the antenna on?

There were a haunting number of problems like the ones DiPiazza describes, worked through by many Bell engineers over many months. And, of course, there’s never any substitute for great fundamental development and engineering work. But, thanks to the likes of Frenkiel, Porter, and Engel, one could be confident that all this money and effort was being spent on the right sub-problems. More importantly, one could be confident that no wicked, unsolvable problems seemed to be awaiting them.

The whole thing had been planned exceedingly diligently. The planners were engineers and Ph.D.s. They already had deep familiarity with the phone system and all its details. They’d brought all the relevant scientific questions to top research minds, consulted engineers who work with relevant tech every day, and coordinated with Bell field staff. This is what they did. When you’re allocating this much money and research time to something, the confidence that systems engineers can provide is invaluable.

They kept a research organization like Bell Labs working on the best problems possible and helped ensure that as few resources as possible were wasted on research that would not turn out to be usable.

Applied science orgs need a systems engineer

In applied scientific work, great systems engineering work can rival the importance of great research minds.

It was not only Bell that stumbled upon a position like systems engineer to help facilitate its operation. GE Research and Dupont’s research arm — also applied science orgs that left some room for idle curiosity — had similar positions in their own operations that went by other names.

Frankly, it just makes sense. Any new science org attempting to pair usable applied science with some kind of fundamental research should think long and hard before they decide that a full-time systems engineer is not for them.

I’m not saying that, like Bell, a young applied science org needs as many systems engineers as basic researchers. I imagine the ratio of systems engineers to basic researchers should grow as the complexity of either the research operation or the system in which discoveries are going to be applied grows. No new science org has a research operation as large and varied as the mature Bell Labs. So, naturally, the ratio should be smaller.

But many new science orgs do hope to plug into complex systems and operations. Several of the orgs I’ve spoken with have problem scopes that, more or less, pertain to the needs/problems/holes present in all of life sciences research.

Finding a problem in these systems is not so hard for those familiar with the systems. That’s why many researchers and engineers do not feel the need to bring in help. But finding a set of good problems is not finding the best problems. Finding the best problems is a profession in and of itself. A systems engineer is worth it when, under the right scrutiny, it might turn out that the best problem is 10X as financially valuable, does 50X the social good, or is 2X as likely to work as just some run-of-the-mill good problem.

This can be left to researchers. But it shouldn’t.

For every ten or so basic researchers in an applied science org, it feels safe to say there should be at least one systems engineer. Bell Labs had about a 1:1 ratio of basic researchers to systems engineers and a 9:1 ratio of total research, engineering, and facilities development staff to systems engineering staff.

Different orgs will have different needs. But zero is almost surely the wrong number. Even some fraction of one, say 1/4, feels like it’s playing it needlessly cavalierly with such an important piece of an applied research organization. One person who is spending a day or two a week but most of their time on other things feels like a half-measure.

Bell had a massive sample size of engineers, researchers, and problems on their side, and even they didn’t rely on pure probability — serendipity — to do their problem identification for them.

There’s a reason: great problem selection is too important to be left to chance.

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Thanks so much for reading! For those interested, I’ve put together a document breaking a speech from longtime Bell Labs leader, Mervin Kelly, on:

• How Bell Labs was structured

• What kinds of individuals were hired for each portion of Labs

• How different sections of Bell Labs were integrated

• And what day-to-day life looked like for the different roles.

It is great information for those who run their own research operations or are just hardcore hobbyists/massive Bell Labs nerds. Bonus: More detail on how Bell Labs operated

And if you have any interest in being a kind of Bell Labs systems engineer, check out the following post. I am currently working to build more BBNs. Many BBN founders either must act like Bell Labs systems engineers or need to hire someone who can.

Citation:

• Gilliam, Eric. “How did places like Bell Labs know how to ask the right questions?” FreakTakes Substack. 2023. https://freaktakes.substack.com/p/how-did-places-like-bell-labs-know

Since the explosion in physics knowledge of the early 1900s, driven largely by discoveries in quantum mechanics and relativity, many argue that only two scientific fields have been explosively productive. The first is computer science and electrical engineering — the history of which most readers of this Substack are familiar. The other is molecular biology.

The story of how (and why) molecular biology came to exist as a breakthrough field can, possibly more than anything, help us understand how we should be funding extremely young science. The story is largely centered around one organization, the Rockefeller Foundation, and to a significant extent, the vision of one man: Warren Weaver.

This piece details the story of how a second-rate physicist turned into (probably) the best scientific grant funder ever and is largely responsible for the creation of a field in spite of never producing a single paper in it or doing a tour of duty on one of its lab benches.

I will dive into the Rockefeller Foundation’s ridiculously anomalous results, how Warren Weaver’s thesis on scientific giving changed the foundation’s approach, evidence of this in Rockefeller’s annual budgets/reports, and first-hand accounts from what would later become the “molecular biologists” themselves speaking to just how important Weaver’s Natural Sciences Division was to the birth of the field.

This piece aims to help the reader under exactly how new branches can be created. There has been a previous Substack post by Samir Unni diving into how Rockefeller’s grant officers performed their most vital function, scouting young talent and projects. And I welcome you to check that out here if you’re interested. Overall, this piece focuses on what seems to me to be the primary factor that drove the Rockefeller Natural Sciences Division’s anomalous results: its commitment to scientific branch-creation at the expense of all other activities.

A quick note on “molecular biology” and “branch-creation”

I should quickly clarify a couple of terms: molecular biology and scientific branch-creation. Feel free to skip these sections if you’re already familiar. (Note: Scientific branch-creation was the subject of this blog’s most well-known piece, When do good ideas get easier to find?)

Molecular Biology

Crudely, molecular biology “seeks to understand the molecular basis of biological activity.” It can be described as the understanding of biological systems on an extremely small level — the kind of level that early 20th-century physicists and chemists were used to thinking on, but early 20th-century biologists were generally not. Watson and Crick’s discovery of the double-helical structure of DNA is considered an achievement in molecular biology, as is any scientific work having to do with their discovery that has followed. Modern tools like CRISPR and other heredity-based lab work can be broadly categorized as molecular biology.

Scientific Branch-Creation

In When do ideas get easier to find?, I outline Gerald Holton’s model of how scientific knowledge progresses — which was heavily dependent on branch-creation. This model was constructed based on what observed as a physicist throughout the early and mid-1900s.

A “branch” can be loosely understood as what happens when a new idea or tool — often combining several previously unrelated ideas or uncovering an extremely non-obvious insight — gets combined with existing tools/ideas to help researchers spawn a cluster of brand new ideas. An example of a very rich, extended branch that Holton used was spawned by I.I. Rabi’s work in developing the original molecular beam techniques — represented by the black box at the bottom of the following image which begins to branch upwards. This work by Rabi stimulated a group of wildly productive colleagues and students to explore these problems further, carving out a new sub-area of physics.

Holton strongly credited branch-creation, rather than branch continuation, with the majority of the gains in scientific knowledge. Holton uses a graph of early linear accelerators’ total energy gains to exemplify this point. The graph demonstrates that the exponential growth in total accelerator energy was driven by the explosive gains that came in the early years of new technologies (sub-branches), but the productivity of each technology slowed rapidly after its early years.

The slowing rate of progress for the individual curves did not matter much. While it was all too common for a single branch to rapidly curtail in research productivity, almost all new branches had explosive growth in their early stages. So, as long as new branches were being created frequently, scientific growth was explosive.

With that, let’s dive into it!

Rockefeller’s Anomalous Outcomes

Rockefeller’s results were, in a word, absurd.

In short:

• In 1933, the Natural Sciences Division began to fund what it called “quantitative biology” at the expense of all other scientific areas. Weaver would not coin the term “molecular biology” until 1938. To put this in perspective, 1938 was 15 years before Watson and Crick discovered the structure of DNA which ushered in the “classical era” of molecular biology.

  • Even scientists in the mid-1940s, transitioning from fields like physics and biochemistry to molecular biology, still considered the move a gamble.

• From 1954-1965, 18 Nobel Prizes were given out for molecular biology. 15 of them were beneficiaries of Rockefeller Foundation funding.

  • And, before you retort that “it’s easy to fund winners if they already have a track record,” the Foundation funded them, as Weaver noted, “on the average over nineteen years in advance” of winning the prize. In that era, people were often winning Nobel Prizes in their mid-to-late 40s…

• Most of the influential scientists of the early field either directly credit the Rockefeller Foundation itself or one of the entities that were largely Rockefeller-funded with bootstrapping the early growth of the field — such as the Cold Spring Harbor Laboratory and its summer research program, the Caltech molecular biology research programs, or Max Delbrück himself. I’ll dive into the importance of all three later.

• If you’re thinking, “anybody can get lucky once if there are enough organizations giving grants,”…Weaver would go on to do it again. In the early 1950s, just as the field of molecular biology was blooming with the discovery of DNA’s structure, Weaver began diverting much of his Division’s funding away from molecular biology and towards a young agricultural research program. This program would go on to be responsible for one of the greatest scientific discoveries of the 20th century in terms of human welfare gains: miracle rice.

If that’s a satisfactory rundown of the Rockefeller Natural Sciences Division’s accomplishments for you, you can skip ahead to the next section. The coming (long) quote from Weaver is fantastic, but not essential to understand the core of the piece.

For those who are interested, I felt I should also include Weaver’s own summary of why molecular biology is so important and why he thought his Division was largely responsible for its early growth, in his own words. He is a very humble man — as the rest of his autobiographical writing demonstrates — who did not have a tendency to aggrandize his accomplishments. However, when it came to some of his Natural Sciences Division’s successes, it was simply hard not to view his Division’s work as causal.

The following is an excerpt from Weaver’s autobiography, written in the late 1960s.

Although the new Rockefeller Foundation program in quantitative experimental biology was not started until I assumed, in February 1932, my duties as the Director of the Division of Natural Sciences, the record of grants indicated that we began rather promptly to find opportunities to finance promising research programs that were relevant to our program interests. In 1932, for example, we made the first of what turned out to be a long series of grants to the Biological Laboratory at Cold Spring Harbor, Long Island, New York. That institution began a series of summer symposia on quantitative biology, and these meetings played a critically important role in attracting to newer fields of biology a considerable number of brilliant young scientists, several of whom went on to furnish leadership in the new developments. This record is impressively set out in a volume published by the Cold Spring Harbor Laboratory.

Also in 1932 my division of the Rockefeller Foundation made the first of a considerable series of grants to the California Institute of Technology to help support the research program of Dr. Linus Pauling. The Foundation report for 1932, using language that might have seemed a little overoptimistic at the time, stated that Pauling’s “program in structural chemistry extends the technique of wave mechanics to the study of complex inorganic and organic molecules.”

But in 1951 Dr. Pauling magnificently substantiated that statement by publishing his famous theoretical deduction of the α-helix structure that occurs in proteins, a result which Sir W. Lawrence Bragg has called the “first example of a correct determination of atomic arrangement in biological substances.”

Soon after 1932 we began to support the researches of W.T. Astbury in England, a pioneer in the X-ray analysis of natural fibers, his early work being done on wool. And then we began making grants to a considerable number of physicists who were applying X-ray diffraction methods to the study of the structure of biologically important substances, particularly proteins.

I include a few details of the early grants made in the Rockefeller Foundation program for two reasons. First, I consider the emergence of the subject now regularly called molecular biology to be one of the greatest developments in the history of science. The triumphs to date of molecular biology have been largely in the field of genetics. But there is every reason to believe that molecular biology will now attack, and similarly conquer, other basic biological problems—those of immunology, of cellular growth and development (including cancer), and even some of the most basic aspects of the functioning of the central nervous system.

Second, I believe that the support which the Rockefeller Foundation poured into experimental biology over the quarter of a century following 1932 was vital in encouraging and accelerating and even in initiating the development of molecular biology. Indeed, I think that the most important thing I have ever been able to do was to reorient the Rockefeller Foundation science program in 1932 and direct the strategy of deployment of the large sums which that courageous and imaginative institution made available. It was indeed a large sum, for between 1932 and my retirement from the Rockefeller Foundation in 1959 the total of the grants made in the experimental biology program which I directed was roughly ninety million dollars. [Note: Somewhere between $900 million and $2 billion today depending on what he meant]

There is some purely factual basis to support the views of the preceding paragraphs. When I read Jim Watson’s exciting account of the discovery of the structure of DNA, and came, page after page, to the names of the individuals who had played leading roles, I was struck by the fact that all these names had been written down by me, time after time, in my Rockefeller Foundation diary, and indeed also in recommendations I had made to the Rockefeller Foundation Board of Trustees. As I read on in the Watson book, I jotted down the names of what seemed to be the most significant actors in the play. I wrote down thirteen names in a first and most important category, and fourteen others, who were somewhat less importantly involved. And of these two lists, every person in the former and more significant group had received assistance from the Rockefeller Foundation. All but three of the second group of fourteen had also received Rockefeller Foundation assistance.

Recently President George W. Beadle of the University of Chicago identified eighteen of the Nobel Laureates, over the period of 1954 to 1965, as having been involved in one or another aspect of molecular biology. The mere fact that fifteen of the eighteen had received assistance from the Rockefeller Foundation is not especially significant; for if they are such outstanding scientists it ought to be easy to identify them for aid. So it is much more noteworthy that the Rockefeller Foundation assisted every one of the fifteen before he received the Nobel Prize, and indeed on the average over nineteen years in advance.

Two powerful streams of thought have converged to form the present discipline of molecular biology — the flow of structure studies which recognize physical laws as basic and sufficient for the understanding of the form and function of parts of a living system, and the considerable flow of studies in the genetics of phage. The work in phage genetics was to a great extent developed under the leadership of Max Delbrück and his associates. Delbrück was originally trained as a physicist. Watson, one of the two architects of the structure of DNA, is a biologist originally trained in phage genetics.

To substantiate the claim of the Rockefeller Foundation’s influence upon the emergence and development of molecular biology, I have stated some facts about the record of grants to those scientists who led in this development. I can add to this some direct evidence from certain leading recipients of this aid.

Not long ago, I wrote a number of leading scientists who had been involved in the development of molecular biology, asking for their opinion as to the most satisfactory definition of the phrase “molecular biology,” and also raise some questions as to the ways in which this field came into being. In reply, Delbrück [likely the most influential early researcher in the field] wrote me: “I can only testify as far as I am concerned and here very strongly and unambiguously: without the encouragement of the Rockefeller Foundation received in 1937 and their continuing support through the mid-forties I believe I would hardly have been able to make my contributions to biology.”

As a part of this same exchange of correspondence about molecular biology, I received a letter from Sir W. Lawrence Bragg, the younger of the father-and-son team that received the Nobel Prize in 1915 for their determinations of crystal structure by X-ray diffraction techniques [and the head of the Cavendish Laboratory Watson and Crick would research in]. In this letter Sir Lawrence said, “concerning the part the Rockefeller Foundation played in helping the ‘Cambridge School.’ Your help came at a vital time just before the war when I was trying to find some way of supporting Perutz’s work [Max Perutz was the chairman of the Laboratory of Molecular Biology at Cambridge] and it was continued after it. This school was responsible for DNA, for the first protein structures, for the first understanding of virus structure, and for work on muscle. The extent to which the X-ray analysis of protein was pioneer work is shown by the fact that only now, twelve years after the trail was beaten at Cambridge and the Royal Institution, has any other research center succeeded in getting a protein ‘out.’ I am allowing myself to put this so strongly because I think that the Foundation’s help made an outstanding difference to these advances.” Perutz has also written me, “…the Cambridge work on the structure of large molecules would never have got off the ground but for the Foundation’s support.”

The Rockefeller Foundation has, I firmly believe, a solid and authoritative basis for taking satisfaction in the role it played in emphasizing, over a period of over a quarter of a century, the support of research in quantitative biology.

The Natural Sciences Division Before Weaver

To understand how things changed under Weaver, we first need to understand how the Rockefeller Natural Sciences Division operated prior to his arrival.

The Division used to be more…normal. “Normal” in that they more or less opened up their coffers to all comers, heard their pitches, and gave the money to whatever pitches they found most compelling or exciting. It was a generalist fund, for the most part, and, in the budgets, the money was earmarked for specific projects/labs/research areas — usually at universities. Even so, the funding was general enough by today’s standards that a Rockefeller grant was closer to what we’d know as funding a “person or department head, not a project.”

Rockefeller’s grants to individuals/departments tended to be for things like the exploration of some very general process with some specific-ish method. For example, the following is one of Caltech’s grants from the 1933 Rockefeller Foundation Annual Report:

The special need of the department at the present time is for additional personnel to undertake studies of the biological stages that are found between the genes in the fertilized egg and the finished characters of the organism. Between the initial stage, which is the province of cytology, and the final stage, which is the subject matter of genetics, lies a significant and unexplored region. The Foundation's grant will make possible investigations in this field.

This grant was made in Warren Weaver’s first year with proper control of the fund. And, while one can (maybe) make the argument that the scope of the grants was a little different under Weaver, it was largely the same in providing broad funding that trusted the scientists to deploy the money and change directions as they saw fit.

What did change? Well, Weaver came in with a thesis, a strong one. And, while many capital allocators have theses on future trends that make headlines all the time, few really put their money where their mouth is in the extreme fashion he did. Weaver was not just willing to increase funding in the area in which he had conviction in some moderate way. He was willing to divert funding from almost all other (very promising) areas of science to this one particular area of focus.

To some, this might make Weaver seem like a betting man. And if he was, he was a historically great gambler. But I’m not so sure Weaver would see it that way. He would not have characterized this allocation of capital as “going all in” on one area, but, rather, as the kind of responsible specialization that most people adopt in normal, private sector business. This was also the kind of specialization that Karl Compton, an intellectual leader of the research profession at the time, felt that research departments should put into practice to optimize results.

Over the next 20 years, exactly how Weaver went about this long-term commitment to funding, on the face of it, kind of weird science — with few ground-breaking public results in the field’s early years — is invaluable learning material. Not only did his strategy prove that an organization could reliably create scientific branches, but his work can also serve as a playbook for modern scientific grant funders looking to do the same.

Weaver’s Thesis: A wave not yet gathering its strength

In 1932, Weaver was very surprised when the Rockefeller Foundation invited him to come to New York City to interview for the job as the head of its Natural Sciences Division. The interview came about because of a recommendation from Max Mason, one of his undergraduate mentors who later became his collaborator. Mason became the Rockefeller Foundation President in 1929 after having run its Natural Sciences Division.

In the interview for the role — which Weaver felt very unqualified for but also believed was too interesting to pass up — Weaver spoke of how he was “convinced that the great wave of the future in science, a wave not yet gathering its strength, was to occur in the biological sciences. The startling visions that were just beginning to open up in genetics, in cellular physiology, in biochemistry, in developmental mechanics — these were due for tremendously significant advances.” Elaborating on his hypothesis at the time, he continues:

I strongly felt that the Rockefeller Foundation ought to undertake a large and long-range support of quantitative biology.

This was by no means a uniquely inspired conviction, for others had the same idea, notably the German physiologist and Nobel Laureate Otto Warburg, who had written: “…the most important problem in biology is to obtain an understanding in physiochemical terms of the processes — and the substances which take part in the processes — that occur in the normal living cell.”

The idea that the time was ripe for a great new change in biology was substantiated by the fact that the physical sciences had by then elaborated a whole battery of analytical and experimental procedures capable of probing into nature with a fineness and with a quantitative precision that would tremendously supplement the previous tools of biology — one can say “the previous tool” of biology, since the optical microscope had furnished so large a proportion of the detailed evidence.

Even at the time, more than 35 years ago [written around 1968], one could identify some of the procedures and the instruments that were ready to be applied more intensely to basic biological problems. Although a practical working instrument had not yet been built, it was known that a microscope using ultraviolet light could discriminate detail about ten times as fine as that analyzable by a microscope using ordinary light. Indeed the wave aspects of quantum theory indicated that an electron microscope — although working models were then some years off — could reveal details at least a thousand times finer. More indirect ways of analyzing structure — extensions of the ordinary processes of seeing — were soon to be available through the use of X-ray and electron diffraction studies.

In addition to new ways to see in greater and more revealing detail, there was a rich promise of new ways to separate out the constituents of complicated biological systems such as blood and the other fluids of the body. The supercentrifuge of the Swedish chemist Theodor Svedberg, for example, was already available.

When one today looks through the massive annual issue of Science which is devoted to equipment, he realizes the tremendous range and power of the instrumentation — much of it employing automatic electronic techniques — now available for quantitative experimentation in biology and medicine. This was of course not foreseeable in any detailed way during 1931-1932. But enough was discernible to convince one that biology was about to have the tools to enable it to enter upon a new era.

Although I was convinced that the Rockefeller Foundation ought to move in this direction, it seemed even clearer to me that I was not qualified to direct such a program. I told this emphatically to the top officers of the foundation. But I was enthusiastically convinced of the importance of moving in that direction, and because I did have the necessary background knowledge in physical sciences, they somewhat rashly, as it seemed to me, offered me the directorship of that division of the Rockefeller Foundation dealing with all aspects of sciences other than professionally medical.

While Weaver is being a bit modest about his foresight, his conviction is obviously strong and there is sound reasoning behind it. He was a very serviceable research physicist — although his degree was in mathematics — and had been paying close attention to related fields, as many of the curious researchers of the day did. He had seen how physics instrumentation and models had played a massive part in the development of the field of chemistry — to the point where the two fields became so intertwined that it was ambiguous whether certain Nobel Prizes should be awarded for physics or chemistry. He saw that the field of biology was similarly poised to build on the prior generation’s explosion in physics’ ideas and methods.

Weaver saw, or was pretty sure at least, that there was significant “complementarity” — Bohr’s word — between the two subjects that could be leveraged. However, this complementarity was much less obvious to see than it was for physics and chemistry. Even in the mid-1940s, over ten years after Weaver’s interview, many physicists who would make the transition to molecular biology were just beginning to consider the implications of their methods in the biological sciences after reading books like Schrödinger’s What is Life? — which did not really make any practical advancements but did excite many physicists into thinking about the field. Even in the mid-1940s, physicists felt like they were on the very early wave of a very new trend when dipping their toes into this field (more on that later). Nevertheless, in 1932, Weaver saw it. A few select individuals like Otto Warburg saw it. But this was not a common opinion.

Surprised he had even been offered the job, Weaver felt like he had nothing to lose in taking it. Weaver knew for a fact that he was not a “first-rate man” when it came to physics. In his own words:

I lacked that strange and wonderful creative spark that makes a good researcher.

How did he know that exactly? Well…because of Max Mason. Weaver and he were collaborators at the University of Wisconsin. And, while Weaver felt he was a solid contributing member of the duo, he believed that around 95% of the actual new ideas the duo generated sprung from Mason’s head. Weaver was helpful in that he could work longer hours to work things out and help keep Mason on a schedule — which Mason did not do on his own.

Weaver, however, did not have that “wonderful creative spark” he needed to be a great researcher, but he did have a spark of something. In New York, working at Rockefeller, it would truly flourish.

The Weaver Approach: True specialization in an extremely young field

A philanthropy’s annual budget can tell you far more than any vision statement what exactly they value. To get to the bottom of what differentiated Weaver’s approach, there is no better place to go than Rockefeller’s Annual Report — which includes its budget and detailed narration of the year’s decisions.

Rockefeller’s yearly reports are shockingly enjoyable to read. I read all of their annual reports — the Natural Sciences sections at least — from around 1929 to 1955 to really understand how the money ebbed and flowed under Weaver’s direction as well as before he got there. And, frankly, the budgets speak for themselves. The images of a single year’s budget, shown in the coming section, tell the story in a nutshell.

While, of course, there is a lot of nuance that you’d need to read at least five years worth of budgets to fully appreciate, the evidence from just one year’s budget should present a stark enough contrast to give you a pretty damn good idea of the “Weaver Approach.” On paper, the language of the thesis that Weaver shared with the Rockefeller Foundation doesn’t seem stronger than the “vision statements” you often hear philanthropic heads spout off. But what made him, and Rockefeller, so different was that he was willing to divert almost all his Division’s money away from other promising areas of the natural sciences budget to seed this young area with sufficient funding.

Rockefeller’s 1933 Natural Sciences Budget: New vs. Old Appropriations

Prior to Weaver’s arrival, the Rockefeller Foundation had given some money to molecular biology-related grants — like those to Linus Pauling and Caltech. But it would not be unfair to characterize their granting as “spread around” across many scientific areas.

This state of affairs should be unsurprising because 1) “spread around” is a typical state of affairs for scientific grant makers and 2) if Weaver was willing to bet his whole interview on supporting one new area of science, it is not surprising that the Foundation at least had a passing interest in the field if they were willing to hire the physicist with the oddly specific interview. But with Weaver there, the Natural Sciences Division began to give to “quantitative biology” at the expense of all other things. They had the conviction to deal with the tradeoffs.

Below is a snapshot of the Division’s “new appropriations” in 1933. New appropriations are the brand new donation areas that the Division chose to fund in that year. After, I’ll share a snapshot of the “former appropriations” from the 1933 Annual Report. Former appropriations are the appropriations that the Division was paying out because they were promised from prior years — before Weaver’s time.

Taking a look below, the new appropriations for 1933 are very focused. Around a quarter of the money went to research programs dedicated to quantitative biology (under “Programs of Specific Concentration”); around 3% was set aside for earth sciences research; 46% for broader goals such as institution building in China and supporting journals and certain pieces of European science; and the rest was spent helping boost national research council fellowships.

The modern equivalents of these dollar amounts are something like $4 million, $400,000, $7 million, and $4 million respectively. Of course, that was only one portion of Rockefeller’s science giving. The Rockefeller medical sciences total budget — which was a separate pot of money — was $23.4 million in that year’s new appropriations and $31 million in payments on appropriations from prior years.

An additional $28 million in Weaver’s budget was earmarked for funding promises made in prior years. Below, I show a snapshot of these prior funding commitments in that same year. You see shades of Weaver’s interests in there, with line items such as those for Caltech and Cold Spring Harbor Laboratory, but it is comparatively very scattered. One difference between this budget and the budget above is very obvious: they don’t even attempt to break it up into subsections. It’s just…one long list. It seems they knew there was a little bit of everything in there.

This “little of everything” approach was not uncommon then, just as it is not uncommon now. It’s very tempting to put some money into an account earmarked for donations and say, “The most interesting projects from the scientists that are most exciting to us in any area that seems cool can win this money. All should feel welcome to apply!”

But that didn’t make much sense to Weaver at all. He writes in the 1933 Annual Report on the change of strategy being implemented:

During the years immediately following 1929, when The Rockefeller Foundation's program in the natural sciences was first organized, there was recognized, in selecting projects for aid, some preferential emphasis upon certain fields of interest; but the primary emphasis was not upon field but rather upon the outstanding leadership of the chosen men or institutions. In recent years, however, interest in certain definite fields has played the dominant role in the selective process. The opportunities open to the Foundation in the field of the natural sciences are, in fact, not likely to be met by supporting undertakings merely because they are sound scientific projects, or even because they are outstandingly good scientific projects. A highly selective procedure is necessary if the available funds are not to lose significance through scattering. Within the fields of interest decided upon, selection naturally continues to be made of the leading men and institutions.

The Rockefeller Foundation may have had more money than God by contemporary philanthropic standards, but no organization was above specialization. The Natural Sciences Division would pass up on the most impressive people and projects applying for money if they were not applying to work in the “fields of interest decided upon.”

In practice, it seems Weaver felt that the effect of the Division’s money was being diluted by this “scattering” — or, differently framed, that concentrating the grants in one scientific area would be super-additive.

How did Weaver justify choosing this specific area of specialization to Rockefeller?

What many would call “using the money to its utmost effect by funding the best ideas,” Weaver saw as a missed opportunity to concentrate the money in a way that could generate exponential returns in scientific knowledge — creating new scientific branches. In this case, the branches he wanted to create were at the then-fuzzy intersection of physics and biology. He didn’t have a name for it because these branches didn’t exist yet; but he had a good reason to believe 1) why they should exist and 2) that it would be a big deal if they did.

In the 1933 Annual Report, already having explained that the Natural Sciences Division would begin to specialize, Weaver attempted to outline a general model to justify why he would be choosing the area of concentration he chose. In his autobiography, Weaver seems to indicate that, as often happens in situations like this, he may likely have first decided to focus on molecular biology and the formal model for the justification came afterward. That’s how these things often go. However, given that annual reports are annual reports, in the report the mental model comes first — it helps create the allure of deducing the course of action from first principles. Weaver’s mental model, typified by some fuzzy language characteristic of many annual reports, went as follows:

The choice of fields of interest is influenced by several considerations. The field must contribute in a basic and important way to the welfare of mankind. It must be sufficiently developed to merit support, but still so imperfectly developed as to need it. It should be a field in which the contributions of the Foundation can play a significant role in producing and stimulating development that otherwise would not take place within a reasonable time.

It is obvious that the welfare of mankind depends in a vital way upon man's understanding of himself and of his physical environment. The problems of physical and mental growth and development and of reproduction of kind are of central importance to all individuals. Not only the well-being of present society, but even to a greater extent the well-being of the society of the future, depends upon a deeper understanding of the nature of these problems. Science has made magnificent progress in the analysis and control of inanimate forces, but it has not made equal advances in the more delicate, difficult, and important problem of the analysis and control of animate forces. This indicates the desirability of increasing emphasis on what may be called the vital sciences, or sciences dealing with the processes of life. These include the biological sciences, psychology, and those special developments in mathematics, physics, and chemistry which are fundamental to biology and psychology.

He then continues with what is likely where he actually started his thought process: why branch-creation at the intersection of biology and physics was practically possible. Essentially, he believed that the tools and mental models developed for fundamental physics in the preceding decade, which had also been fruitfully used in the field of chemistry, could go a long way in answering certain fundamental questions in very micro-level biology, such as answering questions related to genetics and inheritance.

He then asks a bunch of motivating rhetorical questions about how far science can go — which, once again, are often fixtures of these yearly reports — and follows with:

The past fifty or one hundred years have seen a marvelous development of physics and chemistry, but hope for the future of mankind depends in a basic way on the development in the next fifty years of a new biology and a new psychology. In selecting projects for Foundation aid in the natural sciences the major emphasis at present is upon certain fields of modern analytical biology.

There was a general — not necessarily quantitatively worked out — sense that society had gotten some massive return (100X?) out of what it had invested into the fields of physics and chemistry in the preceding decades. And there seemed, to Weaver, to be an obvious chance that this opportunity in quantitative biology could have a similar payoff.

He goes on to explain why earth sciences will be getting some attention — as something of a side project — while then-extremely popular fields like atomic physics and astrophysics would be ignored. The excerpt — and the choice itself — gives a lot of insight on what Weaver felt about funding popular areas.

It has not been judged feasible for The Rockefeller Foundation to support an extensive program, in the varied disciplines which study all aspects of the physical stage on which the drama of life is played. The field of the earth sciences (covering, for example, meteorology, atmospheric electricity and magnetism, earth currents, geophysics, etc.) has, however, been chosen to form a modest complement to the principal program in vital processes. Certain aspects of research in this field, particularly meteorology, have practical applications of high importance. Work in this field has the whole world as its laboratory, and for certain programs, necessarily organized on an international scale, aid is naturally sought from such organizations as The Rockefeller Foundation.

Research in the earth sciences has received little attention, being somewhat pushed off the stage by the more spectacular researches in atomic physics and astrophysics. It has been popular to work on the atom and on the cosmos, but there has been, relatively speaking, very little study of the less spectacular but important problems that refer directly to the earth. The situation is in some respects like that which prevailed in astronomy before there was emphasis on the desirability of the study of the sun as the nearest star.

Funding earth sciences and this quantitative biology stuff over things like atomic physics and astrophysics ran contrary to the scientific community . In previous years, Rockefeller had given substantial amounts of money to things like telescopes and accelerators. Now, if Weaver did give to popular physics-related projects in an area like accelerators, it was specifically with the tool’s under-explored biological use cases in mind. And it’s not like the accelerator trend in physics was passing, or was even considered a fad at the time. Recall the following graph tracking accelerator speeds. The start of exponential growth in accelerator speeds tracked in the graph was just starting in 1933 – look at the X-axis.

Yet, in 1933, Weaver already felt that Rockefeller’s sights should be shifting to under-explored pastures. This move by Weaver is not dissimilar to doing something like halting grants to machine learning research in 2014. If you were doing it under the justification that, “That stuff is overrated and will never bear much fruit,” then you’d look silly. But if your thought process was, “Bigger, more risk-averse funders and most researchers are already seeing this as an exciting field to jump into. Why are my dollars needed there?”, then you might be onto something — if you had more nascent research areas you were passionate about.

Weaver did.

How much of Weaver’s budget was spent on molecular biology?

Weaver was set to double down — in a literal sense, much more than double — on molecular biology. Other things would get funding, but “quantitative experimental biology” was the star. Earth sciences and non-bio-related fellowship funding were also shrinking. Weaver writes:

During 1933 the Foundation's allocation for earth sciences was sharply reduced because of the even greater urgency of the biological program. On a diminished scale also, the Foundation continued to give such basic and general support to the natural sciences as is furnished by fellowships and by grants in aid of research.

In the coming years, molecular biology’s role in the Natural Sciences’ portfolio would continue to become even more concentrated as the Division steadily unburdened itself from prior years’ commitments. In that first year, only a quarter of the budget was allocated to molecular biology — a massive increase in size, but nothing close to what it would soon grow into. Over the next five years, as Weaver observed the progress of his early bets and more funds made themself available, he must have felt that there was a strong enough proof of concept to continue on with the strategy. By 1939, as we see in the Annual Report’s budget (below), he had increased funding in the area to account for around 79% of the Division’s yearly appropriations.

According to my calculation done using the 1939 budget and the Annual Reports narration of the line items, around 79% of the money was given to molecular bio that year. And that ballpark, 80% of appropriations going towards molecular biology, was no one-off occurrence. The total balance was at about that level for years. In the 1953 Annual Report, Weaver confirms this back-of-the-envelope math, reflecting:

For about twenty years modern experimental biology received main emphasis in the program of this division of The Rockefeller Foundation. In fact, about 80 percent of the financial support recommended over the period 1932-1952 was devoted to various aspects of modern biology.

Weaver was not all-in, but molecular biology was clearly Rockefeller’s scientific Priority A and B. The Natural Sciences Division was, in effect, a molecular biology fund plus side bets and pet projects.

The Early Culture of the Field

Even as late as 1947, fourteen years after Weaver began this grand funding experiment, the field of molecular biology felt young. After all, he did choose to fund the field because it was, in 1933, just an idea and wouldn’t have been desirable to other funders — in spite of its potential impacts. But just how nascent was this field at the time Weaver began to heavily invest in it?

Many researchers in related areas didn’t even begin hearing about molecular biology, let alone consider a transition to it, until over a decade after Rockefeller had begun its heavy commitment. Just how under-the-radar molecular biology went for the first (almost) two decades of its existence is well-captured by the autobiographical accounts of thirty top researchers in the book Phage and the Origins of Molecular Biology — published by Cold Spring Harbor Laboratory Press. Each chapter contains an account of one influential early molecular biology researcher, explaining how they came to the field or how some of their well-known experiments came to be. The unifying thread holding the book together is quite simple: Max Delbrück. In fact, the book was published in honor of Delbrück’s 60th birthday. The goal was to share the stories of researchers whose projects or research direction were influenced by Delbrück in some way — and he did a lot of influencing.

So, before I start sharing accounts from that book, I should briefly explain who Delbrück is.

Delbrück’s degree was originally in physics. As a theoretical physicist, his interest was first piqued in biology when he received a Rockefeller Fellowship to visit Niels Bohr in Copenhagen (a couple years before Weaver’s time at Rockefeller). It was Bohr who first interested Delbrück in approaching the field of biology with his “complementary” physics toolkit. For several years afterward, he would publish mostly physics-related work. But, in 1935, he co-authored a very interesting paper on the nature and structure of gene mutation. Weaver’s Division, 1) already having Delbrück on the payroll/being aware of him, 2) constantly being on the lookout for exciting opportunities in experimental biology, and 3) looking to help displaced European scientists, jumped at the opportunity to offer Delbrück a Fellowship. They found Delbrück a spot at Caltech — Caltech already had several projects underway in molecular biology which were largely Rockefeller-funded. This move to Caltech would have surely been considered a strange career move for the promising Delbrück: theoretical physicists were not a common feature of biology laboratories. Regardless, Delbrück went and made great use of his physicist’s toolkit, working in their experimental biology program. Pleased with his work, the Foundation extended his grant, and later, helped facilitate a full-time US position for Delbrück at Vanderbilt by fronting a portion of his salary there. He would publish a trio of papers in 1939-40 that were pivotal to the early growth of the field and, more importantly, be a fantastic teacher/mentor/recruiter to dozens of early scholars entering into the field. That’s why they were able to write an entire book solely containing prominent researchers’ accounts of Delbrück’s influence on them and their work — he was seemingly everywhere.

Now, back to the point: what the field of molecular biology was like up to the mid-to-late 1940s, inspired by accounts from Phage and the Origins of Molecular Biology.

The first account of how small the field was comes from Salvador Luria, a relative unknown at the time of his first Fellowship who, at the time, came loosely recommended by Enrico Fermi. He received his Rockefeller Fellowship to do research at Columbia in 1940. He would go on to be a close collaborator of Delbrück and later win a Nobel Prize.

Twenty-five years ago, when Delbrück and I first met, we were probably the only two people interested in phage from the point of view of “molecular biology.” Our correspondence between 1940 and 1943 dealt, more often than not, with the problem of attracting the interest of geneticists, biochemists, and cell physiologists to the dimly glimpsed green pastures of the promised land. The first phage meeting, in Nashville, Tennessee, March 1947, attracted eight people (M.H. Adams, T.F. Anderson, S.S. Cohen, Max Delbrück, A.H. Doermann, A.D. Hershey [also a Nobel winner], M. Zelle, and myself).

Even in 1947, 14 years after Weaver took over, the conference on phage in molecular biology was only eight people. As early as 1943, the total number of researchers in the area was two. Of course, there were far more than eight people studying molecular biology as a whole in 1947. But there were so many important open questions, and so few people in the field, that each particular area often had only a small cadre of individuals working on it.

Particularly in the earlier years of this branch-creating approach, it was the researchers particularly excited by taking a risk and carving out the true frontier of a field that found their way into the work — often powered by Rockefeller funds. Two researchers of this variety were George Beadle and Boris Ephrussi. The duo, at Caltech, saw that there was a problem: the organisms favorable for genetic study — such as fruit flies — were very different from the organisms that were favorable for embryology — such as sea urchins. Beadle wrote, “We thought something should be done about it and finally proposed that we each gamble up to a year of our lives trying to do it.” The two met in the first place because the Rockefeller Foundation had funded Ephrussi, whose lab was in Paris, for an extended visit to Caltech.

They decided to take this “gamble” — one year of their lives — at Ephrussi’s lab in Paris. The Rockefeller Foundation could not give a Fellowship to support Beadle’s trip on such short notice because they had never met him (meeting candidates was possibly the fellowship’s only strict requirement). But the Caltech department, heavily funded by Rockefeller, was able to cover Beadle’s salary while he was in Paris with Ephrussi. (Rockefeller would later fund Beadle to continue his work at Stanford.)

It was in this year that the two began to produce experiments with Drosophila (fruit fly) eye transplants that began to set the stage for the “one gene, one enzyme hypothesis” which was extremely important to the field at the time. When they arrived in Paris, they got right to work. And, as is so common when you read the scientific histories of these (very) early researchers carving out branches, it was scrappy and disorganized work. The individual’s personalities were all over the science. Beadle writes:

I arrived in Paris in May, 1935, and we immediately began to attempt to culture Drosophila tissues. This proved technically difficult; so, on Ephrussi’s suggestion, we shifted to transplantation of larval embryonic buds destined to become adult organs. We sought advice from Professor Ch. Perez of the Sorbonne, who was a widely recognized authority on metamorphosis in flies. He said we had selected one of the worst possible organisms and that his advice was to go back and forget it. But we were stubborn and before many weeks had devised a successful method of transplantation. The first transplant to develop was an eye. It was the occasion for much rejoicing and celebration at a nearby café…

…

Before long, we had established the existence of two diffusible eye-pigment precursors that we believed to be sequential in the formation of the brown component eye pigment…This was the beginning in our minds of the one-gene-one-enzyme concept, but we did not then use that expression.

That was the beginning of a thread of knowledge that would not begin to properly unravel for several years — but an important one, nonetheless. In these very early years of branch-making work, just getting a thread started is a massive accomplishment, because usually one cannot even be sure that there is one to be found beforehand.

About five years later, Beadle would make fruitful use of the beginnings of this idea which had begun in Paris. He describes the moment it hit him. It happened as he was sitting in a fellow professor’s class at Stanford — in the very early years of branch-creation in a field, sitting in on the classes of professors from adjacent subjects can be extremely helpful. Beadle writes:

In 1940 we decided to switch from Drosophila to Neurospora. It came about in the following way: Tatum was giving a course in biochemical genetics, and I attended the lectures. In listening to one of these — or perhaps not listening as I should have been — it suddenly occurred to me that it ought to be possible to reverse the procedure we had been following and instead of attempting to work out the chemistry of known genetic differences we should be able to select mutants in which known chemical reactions were blocked. Neurospora was an obvious organism on which to try this approach, for its life cycle and genetics had been worked out by Dodge and by Lindergren, and it probably could be grown in a culture medium of known composition. the idea was to select mutants unable to synthesize known metabolites, such as vitamins and amino acids which could be supplied in the medium. In this way a mutant unable to make a given vitamin could be grown in the presence of that vitamin and classified on the basis of its differential growth response in media lacking or containing it.

There was never any slightest doubt that this approach would be successful — in my mind at least — for we had complete confidence in the one-gene-one-enzyme hypothesis.

Vital gains in knowledge had the potential to come almost instantaneously from any of the fields that were related to this fuzzy knowledge-space that was molecular biology. Leveraging related areas of research knowledge was vital to the field’s early growth — for all of its researchers. Rockefeller’s two biggest institution-based investments embodied this. The Rockefeller grants that supported molecular biology research at Caltech, in various departments, were implemented in a remarkably integrated fashion. And, every summer, Rockefeller funded free stays and use of the research facilities at Cold Spring Harbor Laboratory where researchers from a variety of related fields were brought into contact with molecular biology. Here, they were given a crash course in doing research in the subject and able to see what their fields’ toolkits could contribute to the growing movement.

Firstly, to say more on the Caltech grants. Emory Ellis, a former grad student at Caltech, writes of how integrated the research operation there was across all disciplines:

In the mid-1930’s Thomas Hunt Morgan was the chairman of the Biology Division of the California Institute of Technology, and the leader of its group of geneticists. In another part of the Institute, physicists were studying high-voltage X rays, and physicians associated with them were examining the effects of these radiations on human cancers. In the Chemistry Division, whose chairman was Linus Pauling, the tools for elucidation of molecular structure were being applied to proteins. In this small institution, these lines of research did not proceed in isolation from each other.

The importance of interdisciplinary communication is more generally appreciated today than thirty years ago, but it has always been a feature of research at Caltech. It played a part in the initial research at Caltech in bacteriophage, which came about through studies in the biochemistry of malignant tumors. Since some tumors were known to be transmissible by cell-free filtrates, it appeared that more knowledge regarding the nature of filtrable viruses would be helpful in understanding these, and perhaps other malignancies. Bacteriophage was the filtrable virus chosen for study as a model system.

Knowledge from other areas was heavily used to help shape one’s own research direction/research questions in the early years of the field — particularly at a place like Caltech. The experiments of the 1930s felt “simple and crude” to Ellis as he looked back on them almost 30 years later. But so many of them, while crude in retrospect, were only made possible in the first place through resourceful combinations of skills and knowledge from multiple fields.

And, at Cold Spring Harbor, things were also dynamic. Visconti — who would effectively abandon research after six hard years of working in the field — describes the kind of dynamic research environment Cold Spring Harbor was during the summers:

I hope to manage to portray faithfully the thrill we sensed at Cold Spring Harbor of working on the brink of new discoveries in a practically new science in the early 1950’s.

For somebody interested in testing simple ideas in science, working at the Carnegie Institution in Cold Spring Harbor between the years 1950 and 1953 was a unique opportunity. Life was easy-going and very informal, work schedules completely free, under the benevolent supervision and constant encouragement of M Demerec. One could obtain technical help of check on a literature reference in the library at any time of day or night. The field of phage genetics was developed enough that all sorts of experiments could be planned and discussed on the beach with people of different backgrounds, and then performed in the laboratory in the following days. It was enough to expound your ideas to Alfred Hershey or Evelyn Witkin to get an impression such as “It sounds good” or “It might be feasible,” and have all the materials prepared for the following day, along with some advice on the methods to follow. Collaboration was complete and the atmosphere very friendly.

And this was not some wonderful but out-of-reach place set aside for only elite members of some special group. This was the place where the early grinders of the field, such as Delbrück and Luria, brought young researchers, generally getting Ph.D.s in other subjects, to receive a crash course in the field and help teach them to contribute to it using their own toolkits. The people were very intensely interested in the work, but the structure and interactions, as described above, were lax and fun. The following is a photo of Delbrück, the field’s spiritual leader, as the lead in the lab’s production of A Midsummer Night’s Dream.

The people who gravitate to extremely early branch work are almost never very serious people. Curious? Extremely. Intense? In their own way, usually. But serious or formal? Almost never. The work just wouldn’t speak to them. The work has too much of an element of child’s play/fiddling/uncertainty.

Luckily, the same early researchers who could play Shakespearean characters brought some of that same energy to recruiting. A.D. Kaiser writes about how he found his way to Delbrück, Cold Spring Harbor, and biology in general:

Delbrück’s first entered my life in the form of the chapter heading “Delbrück’s Model” in Schrödinger’s book, “What is Life?” I read that book at an impressionable age, while still a graduate student in pre-transistor solid state physics at Purdue University. Not long afterward, at a meeting of the American Physical Society, at Bloomington, Indiana, a friend took me to visit the home of a former coed classmate of his. Her husband not only knew Delbrück personally, but even pulled a snapshot of him out of a drawer. I could not have been more impressed. The husband’s name was Salvador Luria, and it was not long before he had persuaded me to enroll in the phage course at Cold Spring Harbor. Thus I was suddenly plunged into the biology business.

Reading through the accounts, the whole enterprise has the feeling of the “putting together your crew” portion of heist movies. Old friends approaching old friends with a weird idea that these Rockefeller guys might fund, in-the-know mentors notifying young researchers that there might be a chance to make their name in a speculative area, some guys who have been around for a little longer laying the groundwork, and even…a past his prime (scientific) elder statesmen watching a tennis game at the faculty club, pondering what (if anything) will come of the rest of his scientific days.

This was Leo Szilard’s pastime at his post-World War II academic home, the University of Chicago. The atomic bomb was, in a way, Szilard’s brainchild. He was now a famous and respected physicist. He could research whatever he wanted in the field of physics and it would almost surely get funding. But what he wanted was not to research physics anymore. He wanted to do great research again. And he felt that biology, not physics, was what gave him the best chance to make another discovery that would be hailed as truly great. Aaron Novick writes of a conversation he had with his collaborator and mentor:

One spring evening in 1947, as we were leaving a meeting of the Atomic Scientists of Chicago, Szilard approached me and asked whether I would care to join him in an adventure into biology. Despite his caution to think his proposition over carefully, I accepted immediately.

Apparently he had been considering a move to biology for some time, in part because he saw that the era of excitement in nuclear physics, where one man could contribute significantly, had ended and in part because he sensed that biology was on the threshold of an era much like that of physics prior to World War II.

But at the time it was unheard of for biology departments to appoint physicists, or even chemists, to their staffs. Fortunately, Robert Hutchins, Chancellor of the University of Chicago, appreciated Szilard’s greatness and had to courage to appoint him as Professor of Biology and Sociology, with specific departmental affiliations to be worked out later.

All in their own ways, a small group of young people and more experienced researchers were finding their way into this developing frontier — with the looming hand of Rockefeller support seemingly everywhere. But, it should not be forgotten, it took ten to fifteen years for the field to build to the point that we read about in most of the above accounts. As the 1950s approached, there was a bit of a feeling that a wave was building — the wave that Weaver knew, in 1933, should rightfully occur with the right support.

This was was the payoff of years of hard work and staunch commitments by Weaver’s division. For years before that, progress was not so obvious. Those early courses of experiments, funded by Rockefeller, did not look like the kind of science you see in more developed branches. It would have been very easy for Rockefeller to abandon ship in the first five years. In spite of this, the Foundation stood firm. They knew this was all a part of the process.

Doing Science in the Dark: A field in its infancy

Experimentation and “progress” can look a bit strange in the very early stages of branch-creation.

This is the biggest reason why funding this kind of work takes an especially strong conviction in your thesis. As much as any other type of scientific work, you don’t really know where the work will end up or what the specific questions to ask even are. Not only does the scientist need to be inspired by the extreme ambiguity of the situation, but it also takes a special kind of funder.

The Rockefeller Foundation was an ideal match for the situation because 1) they trusted the researchers they funded to passionately pursue their work without much oversight and 2) they had a strong thesis that a field at the border of physics and biology should exist. This second point is extremely important when it comes to not doubting the process every step of the way. Almost none of the projects seemed to finish in the same vein that they started in. That was par for the course, as I’m sure Weaver expected. That is why the funding couldn’t have been for a specific course of experiments, the way it often is today, even if Weaver wanted it to be. Anything more specific would have been pointless.

The messiness of the whole process is everywhere in Phage. Thomas Anderson, who along with Luria was the first to identify a set of phage particles, opens his chapter of Phage writing:

As everybody knows, most discoveries in science are necessarily quite unexpected: during a planned study that is more or less routine one encounters a surprising result that must be explained. I would like to describe two or three such observations that I stumbled upon at about that time and which eventually helped us to understand some of the mysteries that surrounded phage structure and growth.

The subsection headings in the section of his “Identification of Phage Particles” chapter, which cover only one short time period of his career in the field, contain headings like: “Enter Luria”, “What Are They — Really?”, “Enzymes? No!!”, and “Sperm? Maybe?” It was all touch and go, even through the early 1940s — ten years after Weaver began this experiment. But that wasn’t things not going according to plan. That was just… science.

André Lwoff stumbled upon his Nobel Prize-winning discovery, outlined in Phage, through a series of determined failures and an accompanying “eh, what else can go wrong if we try something a bit random?” moment. He writes:

Our aim was to persuade the totality of the bacteria population to produce bacteriophage. All our attempts — a large number of attempts it was — were without result. Louis Siminovitch and Niels Kjeldgaard became very depressed, and even repressed…Yet I had decided that extrinsic factors must induce the formation of bacteriophage. Moreover, the hypothesis had been published already, and when one publishes a hypothesis, one is sentenced to hard labor. Finally, I am stubborn, so the experiments went on, day after day, and they continued to be desperately negative.

…

Our experiments consisted of inoculating exponentially growing bacteria into a given medium and following bacterial growth by measuring optical density. Samples were taken every fifteen minutes, and the technicians reported the results. They were so involved that they had identified themselves with the bacteria, or with the growth curves, and they used to say for example: “I am exponential,” or “I am slightly flattened.” Technicians and bacteria were consubstantial.

So negative experiments piled up, until after months and months of despair, it was decided to irradiate the bacteria with ultra-violet light. This was not rational at all, for ultra-violet radiations kill bacteria and bacteriophages, and on a strictly logical basis the idea still looks illogical in retrospect. Anyhow, a suspension of lysogenic bacilli was put under the UV lamp for a few seconds.

…

It was a very hot summer day and the thermometer was unusually high. After irradiation, I collapsed in an armchair, in sweat, despair, and hope. Fifteen minutes later, Evelyne Ritz, my technician, entered the room and said: “Sir, I am growing normally.”

She returned back every fifteen minutes with updates like, “I am still growing normally,” until, after about an hour, “Sir, I am entirely lysed.” This work, helping prove how induction works, would go a long way in explaining aspects of bacterial reproduction and enzyme production. Lwoff referred to this as the greatest thrill of his scientific career; while he had made important findings in other areas, he took a special joy in this work because “with induction we had been in complete darkness.”

While randomly throwing your hands up and irradiating something under the logic of, “well…we know it shouldn’t work…but I guess we don’t really know anything do we? If we did, we wouldn’t be in this situation. Why not. Let’s do it!” was not exactly the norm. But fumbling around in controlled chaos was. Controlled in that…I guess they were writing everything down. And they did know other science…just not this science, not yet anyway. And they did have theories/mental models for doing what they were doing. But it was very standard, with these small groups of researchers trying to get their bearings in young sub-areas, to change multiple parameters massively between one experiment and the next. After all, why not?

Changing one or two parameters (marginally) and leaving everything else constant from a similar experiment that worked in the existing literature seems to be the careful luxury of researchers that are already somewhere worth being — in terms of how much they know about a field. That kind of thing is what science looks like further along on a branch. In the case of a molecular biologist circa 1940, little improvements on knowing jack shit still left one with jack shit.

The researchers’ search process, in undertaking a course of experiments, had to be more ambitious. In practice, it was conceptually closer to a midpoint search algorithm: casting themselves out into open space and, of course, finding nothing in the beginning, but gradually building on the things they did learn from one experiment to the next. You find nothing each time, for a while, but find a kind of nothing that’s iteratively closer to something — even if it’s still nothing. Eventually, when it worked out, they’d strike upon something quite new and useful. Other times they’d find not much, and that was ok too.

Oftentimes, the learning was as much in the realm of learning by doing than stereotypical scientific learning. These practical learnings were often things related to how and why experiments, materials, and solutions behaved the way they did in this new area of science; the actual results of many of these finicky experiments were mostly useless. This element of learning by doing was a necessary stage of the process that would eventually allow the scientists to be able to run experiments that had stronger, more traditional scientific validity. After explaining how the publishing of the above results worked, Lwoff goes on to explain a separate course of experiments that talk a little about this learning by doing:

Irradiation of lysogenic bacteria with UV light can induce the vegetative phase of the bacteriophage. May I remind you that the first indication of induction came from the observation of a single bacteria in microdrops, that we held the medium responsible, and that we tried in vain to identify the responsible factor. Induction with ultra-violet light triggered a new series of experiments. It was finally found that thioglycolic acid and a number of other reducing substances are powerful inducers (Lwoff and Siminovitch, 1951a and 1952). Our experiments had been performed in a medium containing yeast extract. And everything went on beautifully until the sample of yeast was exhausted. The media prepared with another batch, and all other media, were devoid of inducing activity after addition of thioglycolic acid. A number of yeast extracts were prepared and one of them turned out to be “active” and others not. After numerous experiments it was found that the active medium lost its activity by treatment with 8-hydroxy-quinolein, and the responsible factor was identified as copper (Lwoff, 1952). Inactive media could be activated by the addition of copper. It is known that the oxidation of sulfhydryl compounds by copper yields hydrogen peroxide. As a matter of fact, addition of hydrogen peroxide to an organic medium induces phage development. Organic peroxides are inducers, as are a number of mutagenic/carcinogenic agents (Lwoff and Jacob, 1952). Thus an explanation of the apparently spontaneous production of bacteriophage could be provided. Bacteria produce reducing substances. If the medium contains copper, the reducing substances are oxidized and hydrogen peroxide is formed. Hydrogen peroxide reacts with organic substances. Organic peroxides are formed, which produce the alteration of the bacterial metabolism responsible for induction. Of course, this alteration could as well be the result of rare mutations of critical bacterial genes.

[Lwoff then goes on to explain the step-by-step mechanisms that they now understand, clearly, as a sub-field.]

Things are clear now, but have not always been.

In reading Phage, one is struck by the shocking percentage of useful insights that came not from the formal experimental setups, but in all the sub-explorations needed to learn things like understanding which yeasts did and did not do what when diluted, how to control temperatures in different settings, the right concentrations of fluids and substrates, etc. Painstaking explorations were required to end up with the right bacterium, right prophage, right medium, and correct conditions in the microdrops to learn what they actually wanted to learn.

Many of the groups that found success tended to be laboratory “generalists” to enough of a degree that they could innovate around their problems — sometimes even building equipment to specially fit their needs or because they could not afford to buy it. Sometimes, these generalists solved their way around an issue so well that they became known as “specialists” in the materials and methods they deployed to work their way through the original issue.

Creativity or a relentless can-do attitude (which I know sounds corny) can take one a long way when a field is at an early stage. The ability to constantly keep up with the literature counts for much less. This kind of opportunity is exactly what Szilard craved: ambiguities and open questions that could be worked through by lone researchers in many cases. It was similar to what physics was in his youth.

In this stage, the list of things you know is so small and the list of things you don’t feels terrifyingly large. The experimental and theoretical successes that advance the field may come suddenly, when they do come, but the hard and confusing process of figuring out what the right questions are and how to make experiments work is vexing you constantly.

It is unbelievably hard, on a human level, to find something that you don’t know is there to be found. To relate this to something readers might understand, when doing chess puzzles, endgames in particular, performance is far higher when individuals are told by the puzzle creators that there is a checkmate to be found — rather than simply saying “find the best move” without indicating a mate is on the board.

To do early branch-creating science, researchers and funders have to constantly exist and work well in this ambiguity.

Moving on: Why Watson and Crick’s discovery spelled a new chapter for Weaver’s division

When Warren Weaver chose to shift his division’s primary focus from molecular biology is just as interesting as how he helped build up the field in the first place. He chose to exit the field just as many felt it was entering its “classical era.”

Many view the research events described above, from around 1933 to around 1952, as something of a precursor to the massive scientific wins that were:

1. The Hershey-Chase experiments in 1952 that confirmed that genes were made of DNA.

2. Watson and Crick’s now-legendary 1953 work positing the double-helix structure of DNA.

To many, that was the start of the field just hitting its prime, the classical era of molecular biology. These were the type of discoveries that the entire field had been building toward, the type of knowledge that could be leveraged for all sorts of applications, and the reason that Warren Weaver had gotten into the molecular biology game in the first place. And, after this discovery, many of the field’s holes were rapidly filled, leveraging this vital knowledge. So, if you’re counting usable outputs or the total number of researchers in a field, Watson and Crick’s discovery was just the beginning.

But, from another point-of-view, Watson and Crick’s discovery marked the end of the great era of molecular biology. John Cairns, the lead editor of Phage which I have quoted so heavily from, wrote an interesting 1999 article in Nature titled “Last Days in Arcadia” that speaks to this point. It begins:

The entire genetic code had been worked out by 1966. In a sense, this was not really a discovery. Obviously there had to be some kind of code and, in the end, it was deciphered more by brute force than subtle argument, using short molecules of RNA to drive protein synthesis in a test-tube. But the table showing the meaning of each of the 64 possible triplets was the culmination of all that had gone before.

In the 13 years since Watson and Crick had revealed their model for the structure of DNA, the essential ingredients that handle biological information had been identified — DNA sequence, operons, repressors, messenger RNA, transfer RNA and ribosomes, plus the various classes of enzymes needed to make those ingredients. These were formidable discoveries, and they changed the science of molecular biology from an esoteric field inhabited by a small coterie into the discipline that has dominated biology ever since.

In those days, there were far fewer scientists. Conferences did not tread hard upon each others' heels, and a single symposium at the Cold Spring Harbor Laboratory in New York state could just about cover all of molecular biology.

Watson and Crick’s discovery changed the kind of science that could get results in molecular biology. They helped usher in an era where, given a sufficient amount of the biological systems in question were finally understood to a moderate level, “brute force” scientific exploration could yield dividends. By “brute force,” I think Cairns is referring to the kind of work that is now so common in the NIH-funding universe: pursuing projects that are mostly copies of things that have worked before with one or two parameters changed to some moderate degree.

With the field going from one of potential promise — for those with faith — to one that 100% was ripe for a generation of fast results, people flooded into the field. But, with this ushering in of a new era, it also became the kind of field that someone like Szilard was probably less excited by. Fields on older branches that are in the midst of their era of brute force/big science are not nearly as exciting to individuals looking to make their mark in history.

But, such is the game. This is what winning looks like. Weaver and the Rockefeller Foundation had been right. An unbelievable amount of the field’s success was underpinned by Rockefeller Natural Science’s money in some way. So, after their years of dedicated work — and probably looking crazy to the rest of the world — their bet was very publicly paying off.

What did Weaver’s Division do then?

Well…they began the process of moving on. To the world, this young and exciting field had just started. But, to Weaver, Rockefeller’s work there was mostly done. He writes in the 1953 Annual Report:

For about twenty years modern experimental biology received main emphasis in the program of this division of The Rockefeller Foundation. In fact, about 80 per cent of the financial support recommended over the period 1932-1952 was devoted to various aspects of modern biology. The remaining 20 per cent was divided about equally between support of science as a whole, and support of special projects outside the biological program, which were aided because of their unusual nature, outstanding quality, and special importance.

Over recent years, however, the Foundation has been developing an increasing interest in agriculture. Begun originally as an isolated experiment, involving activities in Mexico only, this agricultural interest has expanded in several respects.

…

The expansion of the Foundation's interests in agriculture and in longer-range food problems has entailed some curtailment of other divisional activities. Support for projects in experimental biology within the United States is being substantially reduced, although the Foundation continues to have an active interest in advancing research in such fields as genetics, plant biochemistry, and plant physiology, which will be of ultimate value to agriculture.

Molecular biology no longer needed a committed ally like Rockefeller with a vision of what the field could be one day. The field had arrived, and all of the more risk-averse, follow-on funders surely saw it too. Instead, moving forward, their money would go towards what was previously one of the Division’s side bets: agriculture. It is very possible that the 20% of the budget Weaver had been allocating to projects of “unusual nature, outstanding quality, and special importance” were, to some extent, scouting missions for what the Natural Sciences Division's next thing could be when they decided to move on from molecular biology. As we discussed earlier, one of these side bets in 1933 was Earth Sciences. Another, in 1939, was Vannevar Bush’s differential analyzer project — one of only three small side bets the division made that year. Maybe Weaver was considering the field of computing as a candidate for Rockefeller’s next big project at one point? Regardless, in the end, the Division pursued agriculture.

This agricultural work would explode in the coming years, eventually outgrowing the Natural Sciences Division with a budget and staff all its own that both exceeded those of the Natural Sciences Division. The eventual scientific claim to fame of the Agricultural Division: miracle rice, which is credited with saving millions of lives since its creation and widespread use throughout the world. The Division did it again.

Surely, Weaver could have deservedly basked in the glory of what his division helped create — continuing to fund molecular biology for another 15+ years while its applications were deployed into the world. But, just as Rockefeller’s 1933 budget showed us exactly what Weaver valued, the 1953 Annual Report does just as clearly: Weaver was not committed to molecular biology at the expense of all other things. He was committed to creating high-value branches at the expense of all other things.

The Division would not abandon its young branch — molecular biology — because it was not publicly producing in a way that would make headlines, but they would abandon their baby if they felt it didn’t need them anymore. There had to be some new, undiscovered branch out there in need of their support. The follow-on funders could take it from there.

For some people, like Weaver and Szilard, life’s too short to spend basking in the glory of what they’ve built. They’d rather do the damn thing again.

This is the end of the main piece. Stuart Buck and myself are writing a separate ‘How-To’ for individual funders and organizations looking to attempt branch-creation on their own. This will also contain additional historical details less relevant to the general audience, but very relevant to grant funders. We’re also hoping to have some bright researchers share some possible future branches in the piece that they think are worth looking into/funding! If you know any researchers who love weird and out there ideas, send them my way!

Subscribe if you don’t want to miss that. Also, feel free to reach out in the meantime. I’d love to talk!

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Citation:

• Gilliam, Eric. “A Report on Scientific Branch-Creation: How the Rockefeller Foundation helped bootstrap the field of molecular biology,” FreakTakes Substack. 2023. https://freaktakes.substack.com/p/a-report-on-scientific-branch-creation

Footnote

Books:

Phage and the Origins of Molecular Biology

Scene of Change: A Lifetime in American Science

1939 Budget Allocation Calculation

Doing the math on the 1939 budget, the following is the rough breakdown of the percentage of new appropriations to molecular biology in 1939 and how I did the approximate calculation. (This is the one I’d recommend you skip):

All experimental bio grants == $768,375

32,500 + 9,000 + 70,000 + 30,000 + 200,000 + 10,000 + 11,465.45 + 3,534.55 + 50,000 + 24,000 + 31,500 + 100,000 + 115,000 + 21,375 + 60,000 = 768,375

Fellowship grants to experimental bio = $100,000 (roughly)

In Fellowships, almost all of the RF’s $50,000 in allocated fellowships were molecular biology related. The NRC-funded ones — amounting to $180k — were more spread out. The fellowships were granted for research in the following subjects: zoology and botany, ten each; physics and astronomy, nine; chemistry, nine; geology and geography, seven; anthropology and psychology, six; and mathematics, three. We’ll conservatively say something like a quarter of those are molecular biology related for the sake of this exercise. So something like $100k of the total $230k in fellowships were molecular biology-related.

Non-biology-related general projects == $0

The three non-bio general projects add to

12,000 + 49,500 + 61,956.54 = 123,456.54

Zero of that was molecular bio related

Grants in aid to molecular bio = $144,000 (roughly)

For the grants in aid projects, all but three were molecular bio-related.

$160k in total. There were 58 in total. The three non-bio grants did look a little more expensive than average. We’ll say they were 10% of the money even though they made up only 5% of the projects. So roughly $144,000 of $160k was molecular bio-related.

In Summary: Roughly 79% of total 1939 grant dollars were given to molecular biology.

$1,012,375 in molecular biology grants out of $1,281,831.54 in total grants

Total natural sciences money allocated that year on purpose:

768,375 + 230,000 + 123,456.54 + 160,000 = $1,281,831.54

Total molecular bio money allocated that year:

768,375 + 100,000 + 0 + 144,000 = $1,012,375

As you know, a lot of what I do is outline the details of how scientific systems and research institutes of the past worked.

Tomorrow, I’ll be taking my first step in doing this kind of profile with one of the present, well-known, new science orgs! I’ll be spending a week on the ground (as well as more time in the coming months) at the lab interviewing, observing, etc.

I already have a list of things I plan on looking into. But I’d love to know what sorts of stuff you all think would be fascinating to learn!

Looking forward to your responses!

Almost all of them did some form of extremely applied work at some point in their career. For many, this consisted of one or two stints doing applied research for the military during World Wars I and II. If they were lucky, they were doing scientific work, but many would even find themselves doing statistics for some military department. Even for those who did not serve in the military, it was often not possible to avoid doing applied work. Until about 1952, a very large proportion of university funding came from industry and state governments rather than the federal government. And these groups, as funders, had practical requirements for how the funding was to be deployed. So, most scientists had to play nicely and do practical (or practical-adjacent) work a large percentage of the time whether they wanted to or not. That’s just the way it was.

One theory I hold that is not backed by extremely compelling statistical evidence is that the pervasiveness of applied research experiences in the early 1900s was great for the scientists and the innovation ecosystem as a whole. These detours, even if they were responsible for the scientists being temporarily underemployed, were, I believe, super-additive. In reading the historical accounts of the period, it is clear that many scientists — possibly most — had their research and research problems shaped by their applied experiences in one way or another.

Of course, one could argue that these great researchers would have been even more productive had they not been wasting their time working on practical problems. And I really couldn’t rigorously refute that claim. This general system of how things worked applied more or less equally to an entire generation’s scientific culture altogether in America, and the system later changed for the next generation altogether. So, there is no cute natural experiment to tease apart the effect of these applied experiences on the community as a whole.

But that, on its own, does not shake my belief in the super-additivity of applied research on early-to-mid 20th-century researchers and their outstanding outputs.

In this week’s post, I hope to help you understand why I see it this way. I am going to tell you the story of Irving Langmuir and how exactly he got started on the course of research that would win him a Nobel Prize. In the process, I hope you come to see just how effective the ‘constraint’ of industrial usefulness can be — even for basic researchers.

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Shout out to Jordan Schneider for the book recommendation that inspired this piece. Subscribe to his ChinaTalk Substack or podcast to learn all about current Chinese tariffs (and more).

The book much of this piece draws from is called From Know-How to Nowhere by Elting Morison, a remarkably out-of-print book about the massive importance of learning by doing in the history of American innovation.1

This post is another in partnership with the Good Science Project.

The birth of the lab

Irving Langmuir conducted his research out of an old barn in Schenectady, New York. That barn was called the General Electric Research Laboratory. How exactly did this barn grow into a powerhouse of applied and basic research — generating multi-billion dollar ideas and a Nobel Prize? Let me set the scene.

In 1900, the light bulb was still in its early stages. It was bad, but 24 million were sold in 1900 alone in spite of this — and the market was rapidly growing. The bulbs’ main technical problems were that they could not sustain a constant level of light, they burned out after a short period, the interior walls blackened, and they used a relatively high level of electric current.

Attempts were underway all over Europe to overcome these issues. Morison writes:

There were constant attempts to improve it and some progress. The first lamps, in 1880, used about 6 watts per candle (a candle is a unit of luminous intensity, being the light emitted by five square millimeters of platinum at the temperature of solidification). By 1900, the lamps were down to 3.1 watts per candle. But since it had been figured that a source of white light of perfect efficiency should consume something less than a watt per candle, there was some way to go. During this same period, there were constant efforts to improve the filament, the obvious source of most of the inefficiencies and distortion in the bulb. A great many materials — fish, skin, bamboo, grass — had been tried out by a good many people in several different companies. By the turn of the century, Joseph Swan’s cellulose filament seemed best but not good enough. On the continent men were trying out metal. Von Bolton was working with tantalum at the Siemens Halske plant in Germany and Alexander Just and Franz Hanaman were experimenting with powdered Tungsten in Austria. So, at the start of the new century, there were, in the matter of the incandescent lamp, an imperfect solution, several very interesting technical problems, some promising investigations, a growing demand and — self-evidently — imposing rewards for the man or agency that would first come up with a bulb that burned brightly for a long time at low cost. — From Know-How to Nowhere

That was the state of affairs when, one day in 1900, three men from General Electric Headquarters in Schenectady went to see the former executive of their company Elihu Thomson. Thomson, who was once the engineering genius of what he and a partner built up into the Thomson-Houston Company — which eventually absorbed the Edison General Electric Company— was now on the faculty at MIT. He remained a consultant to his former company and was still influential in its affairs, but was spending most of his time conducting experiments to help flesh out the developing field of X-rays.

Thomson was a true lover of the process of finding things out and happened to make a fortune in the process. Ever since his childhood, he had been conducting his own chemical experiments in the attic of his house. He had a strong conviction that “the best contribution that could be made to God’s will was to study and understand nature and use it correctly (italics my own).”

The three men who came to see him were: Thomson’s former assistant who was now GE’s technical director, the manager of GE’s pattern department who had a strong enthusiasm for GE finding a way to make better lightbulbs before the Europeans, and a German-immigrant fellow named Steinmetz who GE had more or less been keeping around to do his own technical explorations because he was brilliant and off-the-charts curious. The three came to propose a novel idea: a laboratory that would carry out fundamental physical science research within GE.

Thomson loved the idea. An internal lab somewhat separate from day-to-day operations and commercial pressures where researchers were free to follow their curiosity was just what the company needed, Thomson thought. He strongly endorsed the idea, but he would not come on as director — which the three men had wanted. This was a delicate job that would require a man who understood all of the different forces at work. Thomson would have been perfect, but was caught up with his new life and research. Instead, he thought that Willis Whitney should come on as Director and assume the role of maintaining the balance of this new fundamental research lab that still needed to produce applied research but was also to be housed within a company that happened to have investors that did not care about scientific papers but cared a lot about profits.

Whitney accepted the challenge.

‘Are you still having fun?’

The new lab itself, located in a barn behind Steinmetz’s house, was an experiment in and of itself. Starting, initially, with just a barn and a bunch of problems related to the electrical field, Whitney (MIT undergrad, German Ph.D., MIT Professor of Physical Chemistry) set to work staffing the place with the right people and organizing it in such a way to allow these people to do their best work. Morison reflected on what would come of the nascent research operation:

There seems little doubt that in the next two decades much that was done in Schenectady in electrical engineering and some parts of physics was both better done and more interesting than what was being done in those fields in any American university.

Whitney routinely came into the lab and, as he looked into the state of things in different areas of work, would ask the researchers if they were having fun. Even when the course of research in some area was going quite hopelessly, he would ask it. Morison writes:

“Fun” was a favorite word of the director and those in the laboratory came in time to realize that the question meant, “Are you still working on that problem that no one else has the answer to?” which in turn meant, “Are you still engaged in the most exciting exercise there is in life?”

It’s no wonder why Thomson chose Willis Whitney for the job.

When people like Irving Langmuir started at the lab, Whitney would greet them and tell them to look around the lab for a few days. He wanted people like Langmuir to find out what in the varied work going on at the lab interested them most, and then go work on that strand of work they most enjoyed in any way they wished. So, Langmuir took a few days to look around, ask questions, and decide which area of work seemed most fun.

GE’s first (applied) bulb research czar

Langmuir (Columbia undergrad , German Ph.D., Chemistry Instructor at the Stevens Institute of Technology) came back to Whitney in a few days and said that the work related to the new bulb was what interested him most. At this time, in 1909, the interior walls of the bulb still had the tendency to blacken after only limited use. The laboratory investigations had previously shown that the blackening of the bulb decreased as the vacuum inside the bulbs increased. So, at that moment, much attention was going towards exploring ways to reach a more complete vacuum.

Langmuir was stepping into a line of research that was as old as the GE lab itself. While the bulb still had its problems, this line of research was considered a major success so far. One of the first courses of research Whitney oversaw at the lab was observing what would happen to many different kinds of materials under extreme heat (Read: sticking a bunch of interesting materials in a furnace and writing down what happened). Elting Morison writes of what happened after Whitney stuck a cellulose filament in the furnace for a while and it came out with metal-like properties:

In that form, he further discovered, it could convert electrical charges into light more efficiently and sustain the light for a longer time. What he had done increased the economy of the lamp’s performance, it was estimated, by 17 percent, or to 2.5 watts per candle. This gave the General Electric Company a significant competitive advantage in the market. So, at a cost of a million dollars, they built a new plant to manufacture these GEM lamps. So far, so good.

If the metallized carbonized cellulose filament was better, it stood to reason that some kind of actual metal filament would be an even further improvement, or, at least, it felt worth looking into. So, in 1905, Whitney asked William Coolidge to take charge in that exploration. Coolidge (MIT undergrad, German Ph.D., MIT Professor of Physical Chemistry) started by doing a course of experiments on the metal with the highest melting point: tungsten. It seemed like the clear place to start. He was not the first one to think of this idea. The Austrians, Just and Hanaman, had already been foiled by tungsten’s hardness. In its purest form tungsten is powder-like — which complicated the process. They were eventually able to work some magic and make a tungsten filament that could convert electrical charges into light efficiently, but the modifications they made to the tungsten to make this workable brought the shelf life of the bulb down to a commercially unacceptable level.

We won’t get into the details here, just know the final output of the Austrians’ process was known as sintered tungsten. Sintered tungsten didn’t work. Coolidge was going to attempt to make ductile tungsten — meaning you could draw the tungsten out into a thread-like shape — which he hoped would work. The investigation felt unpromising. Coolidge may have used the words “very unpromising” and “pretty nearly hopeless” to describe the endeavor. But, I guess in Whitney’s book, “pretty nearly hopeless” is just another way to describe fun, indefinite fun.

There were a lot of chemical properties about tungsten working against Coolidge’s efforts to make it ductile, but he did have a few things going for him. As Morison noted:

He knew a good deal about other metals and he knew, as any old time blacksmith did, that most metals increase in ductility as they approach their pure state and they are subjected to intensive “working” or pounding. Then, from his professional training, he knew a good deal about how to put order and system into an investigation.

(Read: do a series of exhaustive experiments until you learn to make the chemicals/materials behave the way you want them to behave.)

So, Coolidge set to work running experiment after experiment, trying to learn more about tungsten than anybody knew. He would heat the metal to varying temperatures and rolled, drew, and swaged samples of the metal at all temperatures (these are just different ways of working the metal that elicit different effects). He measured and recorded the effects of different permutations of temperatures and metal-working processes on the tungsten’s chemistry and structure. He then began mixing the tungsten with other substances and performing similar experiments to see what happened. In doing this constant experimentation, he began to build knowledge and intuition.

The steps taken were not (and could not have been) all planned out ahead of time, but the analysis of the steps was always carefully recorded and learned from. Morison continues:

Some way along in the series, he suspended tungsten powder in an amalgam of bismuth, cadmium, and mercury. He then passed the resulting substance through tiny dies — drawing it — and obtained a silvery pliable wire. At that time, he thought he had reached ductility and the search was over. But when a current was passed through this wire the mercury, cadmium, and bismuth distilled out, leaving, unfortunately, a nonductile tungsten. But it also proved to be tungsten in the purest state he had yet produced.

Fun.

Through this (exhaustive) commitment to his experimental process, Coolidge was able to find success. He eventually iterated his way to a workable process where a version of the more pure tungsten (from the above excerpt) was put through a specific combination of metal-working processes at a temperature that worked that produced rods of tungsten about 1 mm in diameter. These 1mm rods could then be drawn and re-drawn through rods of decreasing size until you were left with wires of tungsten .01 mm in diameter. When put in the vacuum-sealed bulb, electricity ran through the tungsten filaments and demonstrated an efficiency of 1 watt per candle — extending the life of a bulb up to 27x.

Within 5 years, 85% of all lamps would be made from tungsten. As the project went on, more and more research chemists and technical assistants grew to be involved in the wide-ranging steps and combinations involved in Coolidge’s experiments. But it worked. GE had the factories re-fit and deployed the new bulb. Coolidge moved on to other research.

And this was the area of the lab Irving Langmuir, after a few days of wandering around the lab, pointed out to Willis Whitney. He’d like to work over there.

A new kind of (fundamental) bulb research

Langmuir was about to put a completely different spin on this line of research. First of all, it should be noted, Langmuir did not even care about lightbulbs. Well, I guess that is not technically true. The bulb interested him because 1) he thought a metal like tungsten was cool because it could accept really high temperatures which opened up options to the scientist working with it and 2) these vacuum-sealed bulbs provided a pristine environment for controlled scientific investigations. But the bulb’s purpose, primarily interesting to most as an object that literally brought daylight inside on command, seemed less interesting to Langmuir than as a playground to do his science.

People in the lab had been studying how to improve the vacuum of the bulb since they assumed the imperfect vacuum was causing the bulb blackening. But Langmuir, mainly just wanting to learn some stuff, saw this as an opportunity to conduct a completely separate investigation.

If residual gases — imperfect vacua — produced a bad effect — blackening — here was a fine opportunity to study the effects produced by different gases introduced one by one into the bulb. What he wanted to do, he told Whitney, was simply to plot the interactions of various gases exposed at low pressures to very high temperatures in the filament. Nobody knew very much about this phenomena and he wanted to look into it simply “to satisfy [his] own curiosity.” — From Know-How to Nowhere

For three years, he carried on in this line of work. Not only were there, obviously, many gases and temperatures to try, but this initial line of work led off in many unforeseen directions that demanded investigations employing different methods altogether. In the end, what he learned did not help with the vacuum problem at all. He never even got started running experiments to improve the vacuum. By that metric, not forcing him to learn specifically about the bulb vacuum itself straight away was a mistake. And that is how many research operations, both now and back then, would have allocated Langmuir’s energies.

But luckily Langmuir worked under Willis Whitney. Whitney seemed to care that one worked doggedly in the process of discovery, but it didn’t have to solely consist of Cooldige-style, one-by-one tinkering and measuring-type investigations. Langmuir was mostly free to explore as he saw fit. But it should be noted that he was obligated to strike off on his explorations inspired by an existing course of research on a GE product with known limitations/bottlenecks that needed to be overcome.

Did Langmuir do anything to help seal the vacuum 5% better? No. But, thanks to Langmuir, we know that was a stupid problem. The following (chronologically ordered) ‘best hits’ of Langmuir’s filament work should give the reader an idea of how his desire for discovery manifested itself in fundamental work that was also at home in an industry R&D lab.

1. Langmuir found that during use the tungsten filament tended to evaporate — meaning the filament gave off a vapor just as water gives off steam. These tungsten vapor particles were finding their way onto the walls of the bulb. Those particles were what was causing the bulb blackening. Put simply: it was temperature, not an imperfect seal, causing the blackening problem.

2. Different gases markedly changed the rate of evaporation. One of the gases introduced during the experimentation was nitrogen which reduced the evaporation rate by 100-fold.

3. Building on this knowledge, tungsten filament bulbs filled with nitrogen were found to not blacken. But the addition of nitrogen caused the bulb to suffer heat loss and this made the electrical efficiency of the new bulb less efficient than the vacuum sealed, no nitrogen bulb.

4. But Langmuir inferred from prior fundamental work he had done that if one increased the diameter of the filament in the nitrogen-filled bulb, the amount of heat loss would be reduced. After some experimentation, he confirmed this intuition.

5. In trying to find other ways to reduce the heat loss problem, he also found that coiling the filament to a certain degree could achieve the same heat loss reduction as increasing the filament diameter.

6. Putting all this together in one bulb, he found that if you used an inert gas instead of a vacuum to reduce bulb blackening— nitrogen in the beginning but later switching to argon — and coiled the tungsten filament one could make a bulb that required only one half of one watt per candle and lasted three times longer than any other bulb.

Langmuir’s discoveries were often born out of his investigations of anomalies he encountered in the laboratory. Many of his publications on these laboratory encountered phenomena were quite mathematical in nature and aimed at outlining/modeling the fundamental laws and properties of the phenomena which he was observing. In this way, Langmuir’s work was markedly differentiated from Coolidge’s (If you’re curious, take a look at the following papers by Langmuir and Coolidge and you’ll see just how much math and theoretical modeling Langmuir used and how little Coolidge used). To give you an idea of the Irving Langmuir Production Function, below is an excerpt from a letter he wrote to Scientific Monthly talking about his experiences with fundamental research in the GE Lab:

In working with nitrogen, I found that the nitrogen had a peculiar tendency to disappear, and was able to prove (combining high-level theory and experimentation) that this was due to a chemical reaction by which each tungsten atom which evaporated from the filament combined with nitrogen to form a compound WN₂. In order to study this reaction I needed to determine the rate of loss of weight of tungsten filaments at different temperatures. I found that this loss of weight was due to evaporation, and not, as had been previously considered, to an effect of electric discharges. When working with nitrogen at atmospheric pressure, the rate of evaporation was decreased about a hundredfold because of the return of the tungsten atoms to the filament after they collided with nitrogen molecules in the gas.

I had noticed that with nitrogen at atmospheric pressure it was possible to maintain a filament at a temperature close to the melting point for a far longer time than if the filament were in a vacuum.

The applicability and profitability of his findings was not a one-off either. Once he passed this light bulb project off to the later development and engineering stages, he set his sights on studying electric discharges in lamps. As he had learned in carrying out this previous course of research, only a few milliamperes of current would flow across the space between one end of the filament and the other even with a current higher than 100 volts. Langmuir remarked in his letter to Scientific Monthly:

This fact seemed very peculiar to me, for the work of Richardson and others had indicated that at temperatures as high as those used in the tungsten-filament lamp, currents of many amperes should flow across the space. In other words, according to the then-accepted theory of the electron emission from hot filaments, a serious difficulty should have been encountered in the construction of tungsten-filament lamps. The fact that we did not meet any such difficulty therefore seemed to me a peculiar fact that should be investigated.

With only a few days of work on the problem, Langmuir discovered what would be known as the space-charge effect. In short, Langmuir writes:

The electrons that escape from the hot filament require a definite time to cross the space to the positively charged end of the filament, and while these electrons are crossing the space they are repelling those that are leaving the filament behind them, therefore there is a definite limit to the current that can flow with a given impressed voltage.

Coolidge, who was previously working on the light bulb project, was now working on a course of research studying the use of tungsten electrodes for X-ray tubes. He was able to deploy Langmuir’s newfound understanding of high vacuum discharge to construct an entirely new kind of X-ray tube with a stronger vacuum and a hot tungsten filament as cathode.

The understanding of the space-charge effect also helped the folks in the lab understand why a device called an Audion, utilized in detecting and amplifying radio signals, inexplicably required a poor vacuum seal (which let in some gas) to work properly. This new understanding allowed the lab to construct an Audion so powerful that it could now be used for radio telephony and broadcasting.

The relationship between Langmuir and the lab was not only symbiotic in that the lab gave Langmuir money and in return he gave them research. The lab gave Langmuir a seemingly endless supply of problems and anomalies to consider in his research. The following (additional) list of Langmuir’s subsequent research in the lab show both how Langmuir continued to find fundamental research ideas in the applied setting and how his research continued to bear fruit for GE. (the reader can skip these bullets if they wish)

• Building on Langmuir’s work on heat loss from tungsten filaments, “Professor R. W. Wood showed that when an electric discharge is passed through hydrogen at low pressures atomic hydrogen is formed, and that this can recombine on the surface of metal wires and cause them to be heated.” Langmuir, seeing this and fitting it together with his past experiences in the GE Lab, led him to the belief that using hydrogen at atmospheric pressure with a high current could be even more effective. This led to a very useful hydrogen welding process that enabled the construction of sealed-in electric refrigerator units.

• He conducted some studies of the peculiar way in which tungsten vapor condensed (later also using mercury and cadmium) on glass surfaces and came to the conclusion that some of the accepted ideas about condensation were incorrect. The prior theories likened these particles’ behavior to reflecting off surfaces at certain temperatures. He showed that the phenomena “could be better explained by assuming that the molecules or atoms on striking the surface always condensed, and that then, after a certain time interval depending on the temperature, they would evaporate off.” (This was the beginning of a line of work in surface chemistry that is credited with winning him the Nobel Prize.)

• Langmuir then saw that he could use this newfound knowledge to understand and overcome limitations in the diffusion pump and then constructed the improved model, the condensation pump, which immediately increased the speed of the mercury-vapor pump from 80 cc to about 4,000 cc per second.

• The tungsten filament and gases work led Langmuir to recognize the importance of a single layers of atoms on a surface in determining the properties of that surface. He carried out investigations of these single layer of atoms on solids, liquids, and gases. This work initially led Langmuir and his team to more precisely measure the dimensions of molecules of many substances as well as measure the absolute values of wavelengths and X-rays better than was previously possible.

Coolidge and Langmuir both did phenomenal research. But for Coolidge, it was more the system of experiments and measurements themselves driving his work. Many years later, Coolidge himself reflected on what drove his success in the filament project:

I must say…that we were guided in the main by experiment itself rather than by metallurgical knowledge.

Contrary to Coolidge, Langmuir, when reflecting on the development of the gas-filled bulb remarked that it was not the product of engineering but of “lots of different lines of pure scientific work.” Morison elucidates this contrast further:

Where before men had proceeded doggedly and step by step to improve performance by improving the existing given conditions — from horsehair to tungsten, from imperfect to less imperfect vacua — he [Langmuir] had gone by a different path until he arrived at new ideas that could then be translated into a bulb of a different design based on a different concept. No lamp existing in 1911, he said, would have gained in efficiency or life expectancy by the addition of nitrogen or argon. What had been done, he concluded, was to derive a “new kind of lamp from new scientific principles.”

When applications lead to theory

There are many takeaways from this fact pattern. Langmuir’s own essay in Scientific Monthly, in which he describes much of this work, was primarily attempting to argue that some brand of fundamental research can have a productive place in industry. And, while I also believe that, that is not exactly a contrarian opinion (at all) in the progress community. What I’d like to talk about is not Langmuir’s impact on the GE Laboratory and the company as a whole, but, rather, the GE Lab’s impact on Langmuir’s work.

In the Langmuir Production Function, observing what was going on in the lab was a critical component. What can and can’t the applied researchers/engineers do and why? What are they currently doing that the literature actually says is impossible? Is there anything that should be possible that they seemingly can’t do? These were the types of questions that defined Langmuir’s career (and many like him).

In a developed world that is not exactly beset by scarcity and hardship anymore, it is hard to come up with the best areas to explore out of thin air. Pain points are not often obvious. Fundamental researchers can benefit massively from going to a lab mostly dedicated to making practical improvements to things like light bulbs and pumps and observing/asking questions. It is, frankly, odd that we normalized a system in which so many of our fundamental STEM researchers are allowed to grow so disjoint from the applied aspects of their field in the first place.

And if you still believe that Langmuir would have found problem areas as good or better if he was off on his own, that very may well be. But…Irving Langmuir himself would probably strongly disagree with you. Langmuir did, on the one hand, agree that a level of freedom in this fundamental research done within corporate R&D labs was vital. He wrote:

Such research can not usually be directed toward definite goals, for it involves un- known factors. Success in such research, if attained, is often reached by wholly unexpected methods, and the problem which is finally solved is not the problem which is foreseen.

And that is the kind of stuff this generation of scientists, who did a relatively large amount of work in applied settings, wrote down and advocated for that people tend to remember. But what is forgotten is how many of these individuals also explicitly laid out that they imagined this free-flowing, fundamental research being much more tied in with applied research than it tends to be today. Langmuir immediately followed the quote above with:

As this laboratory developed it was soon recognized that it was not practicable nor desirable that such a laboratory should be engaged wholly in fundamental scientific research. It was found that at least 75 per cent of the laboratory must be devoted to the development of the practical applications. It is stimulating to the men engaged in fundamental science to be in contact with those primarily interested in the practical applications. It is also important that the engineers in the organization should be in close contact with those having the broader scientific outlook.

Langmuir may have been able to answer a large portion of his experimental questions on his own within a university, but he would have known to ask very few of them. Small anomalies and curiosities came up in the lab’s work. He looked into them. Sometimes he found clean answers, sometimes it was even more questions, and others it was even that the academics had been getting something entirely wrong.

He was not pulling genius out of thin air. That kind of genius in science is rare, and I rarely come across individuals like this in my research. And, as a note, the product ideas were also not exactly being dreamed up ahead of time by some visionary. Langmuir reflected on the space-charge effect work, one of many areas in which these small and seemingly directionless investigations based on a curiosity from the lab’s work led to an application, noting:

There was no one in the General Electric Company who was conscious of the need of a high-powered electron amplifier. However, once we were led to the construction of such a device we could immediately think of an enormous number of applications for it.

A grand roadmap-like plan for a lab or individual is unreasonable. Pulling brand new thoughts or unseen contradictions that exist in the field out of the sky is rare. But running into problems while doing applied research and engineering development work is as common as finding a bug in a function you are trying to write. If it doesn’t happen, you’re surprised.

Pulling the vast majority of fundamental scientific researchers out of this setting was, in my estimation, a big mistake. Morison, in writing the chapters of this book strove to remind readers just how reciprocal the processes of building and discovery are, particularly when the applications are quite scientific in nature. He continues, stating that the history of this reciprocity shows:

That one can begin at either end of the process and move towards the other end—from the tungsten filament out to some “new scientific principles” or from those principles back down to the argon bulb. It suggests also the far more powerful results obtained when the connections in this reciprocal process are brought within the enforced intimacy and continuity of an organized system, that is, when the whole process is institutionalized.

I’d imagine if one were to go back in time and tell Morison that a relatively unproductive era of American innovation would immediately follow the breakdown of this reciprocal system, he’d have not exactly been shocked. Without this process, effectively organizing the process and translation of discovery is quite difficult.

(Another) Fun idea for a new science org to pilot

I believe we should find ways, wherever possible, to reintroduce fundamental researchers to the processes and applied settings to which they are meant to contribute. The better portion of a great generation of researchers who we idolize, like Langmuir, have the fingerprints of their applied experiences all over their more fundamental work.

What this process would look like would vary from field to field and based on the imaginations and ambitions of the funders and researchers involved. But the concept is quite straightforward.

Finding scientific problems and anomalies to think about can be particularly challenging. Challenging grad students and young researchers to find and fill holes in the academic literature of some field is one way to organize researchers’ energies as they attempt to contribute to knowledge/societal good. It’s not the worst heuristic and there will always be a place for some of this “hole-filling” in the literature. However, I think it is a mistake to let this continue to overpower application-based and application-inspired explorations to the extreme degree that it has.

In my Progress Studies History of Early MIT series, particularly Part 2, I outlined how this kind of symbiotic applied and basic research ecosystem can (and has been) fostered in the university setting. In this piece, I illustrated a piece of history that can serve as inspiration for any new science org looking to prove the merits of this mutually beneficial model in the setting of a stand-alone research lab or a research lab affiliated with a larger organization.

These labs really were a good bit of fun. And many talented people who read this Substack reach out to me express strong interest in working in research environments like the one I describe at the GE Laboratory. Any academic area with 1) clear ties to some real-world application (whether real science or social science), 2) that some funder is excited about, and 3) where individual experiments/analyses can be run relatively cheaply would be an ideal place to start.

If anyone is interested in discussing what this would look like in practice, please reach out to me on Twitter. I’d love to help.

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Once again, thanks for reading the FreakTakes Substack :) Please reach out on Twitter if you’d like to discuss anything from the piece.

Citation:

• Gilliam, Eric. “Irving Langmuir, the General Electric Research Laboratory, and when applications lead to theory,” FreakTakes Substack. 2022. https://freaktakes.substack.com/p/irving-langmuir-the-general-electric

This past week I was corresponding with Gerald Holton, whose 1952 work I covered in my piece When do ideas get easier to find?. Holton, now 100 years old, is obviously spending less time actively working and keeping up with the fields in which he was prolific in his heyday. Holton asked what people like me, Stuart Buck, and others in the progress movement do, and what the research and communication of ideas like “progress studies” and “good science” looks like.

“I have often thought about this concept, how it could be described and possibly measured, and how to defend it against skeptical opponents.” It was clear from his comments that Holton (and others researching these problems 70 years ago) did not see any reasonable path to the managers and administrators of scientific organizations incorporating this research into how they structured their organizations.

I felt lucky (and frankly a bit giddy) to be the one to share with him just how far this rough idea, which he’d been thinking about for over 70 years, had come. So, I told him about some of the fascinating research going on in the space. And, just as importantly, that there was now a community of chief science officers and scientific philanthropists who were not just open to this kind of evidence, but eager to consume it and learn from it.

I was fortunate to enter the field just as this wondrous new ecosystem of experimental new science organizations was emerging. But interactions with individuals like Gerald Holton constantly remind me that intelligent people have been thinking and writing about these problems for at least 100 years. And much of their writing is evergreen, written in a way that still sheds light on how to think about structuring scientific institutions today.

In this piece, I’ll detail a letter Karl Compton, then Professor of Physics at Princeton, wrote to Science in 1927. In the letter — which impressed many people with its clear accounts of the role of a university, the best way to select research topics on a university level, and how to administer departments themselves — Compton made himself known as not just a great physicist, but also a high-level administrative thinker. Members of the MIT Corporation would cite his impressive thoughts on these topics when they would make the odd choice of offering this Princeton physicist who didn’t consider himself extremely industrially-oriented the role of President of the Institute a few years later.

His thoughts are quite interesting because for many the present structure of university research departments is the most natural organizational arrangement. Most professors are given their own separate pot of money, access to their own grad students/postdocs/RAs, and are more or less in charge of their own time. But Compton, in his letter to Science, highlights a pretty natural alternative organizational structure that really doesn’t get as much consideration as it should.

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For those who are curious, I have officially left my previous role as a project leader at Steve Levitt’s social impact incubator at the University of Chicago. I am now working as a full-time Fellow with Stuart Buck at the Good Science Project and am remarkably excited to be working on progress studies full-time.

I will continue to write these Engineering Innovation pieces that often have historical components as well as begin to work on the ground diving into profiling the details of the applied work being done by progress-related organizations in the real world. I already am beginning to work with the MIT Office of Innovation as well as Arcadia Science. I look forward to keeping you all updated on the work.

Now, let’s get back to the piece!

The Context

At the time Compton wrote his letter, the US was just beginning to take the role of research and research universities as seriously as Europe had historically done.

Early in his letter, Compton takes the strong stance that research should be considered a vital university function. While he knows the readers of Science agree with him, it is clear that he is advocating for an opinion that is far from unanimous.

The three great functions of a university are to train young people in the art of living, to guide in the search for truth and actually to engage in pursuit of truth. The first two of these are universally agreed upon and endorsed, but not so universal and whole-hearted is the recognition of the third — the research function of an institution of higher learning. In some quarters the research aspirations of a university meet with distinct disapproval as encroaching upon the supposedly more serious business of the institution. In other quarters they are viewed with grudging or amused tolerance as harmless little idiosyncrasies in which scholarly men must be indulged in order to keep them contented and out of mischief. In the more enlightened quarters, however it is realized that a university can not best perform any of its functions or measure up to its opportunities unless full and ungrudging support is given to attempts to advance human knowledge.

Compton goes on to defend the role of research at a university and its vital role in training students with reasons that we’d almost unanimously agree with today. Some of his points include:

• If you want to train students to truly organize all available knowledge and use it to overcome problems and meet difficult situations, what better training than research?

• In an age where students were excited by looking forward, Compton believed, introducing students to the concept of research progress was pivotal in fueling interest in subjects in a way that static textbook knowledge could not.

• Compton, having worked at multiple universities, believed the difference in student interest levels between his previous university that heavily incorporated independent undergraduate research and those that did not emphasize student research to be incomparable. Students found it challenging in the best way possible.

He goes on to explain things like why he believed research makes an instructor better at their job, to point out how many of America’s glorified inventors built inventions that depended on research in one way or another, and how he thinks universities should be funded. I won’t cover all of that in this piece, but if you’re interested I encourage you to read the whole letter here.

At the end of the letter, he goes on to give a very insightful analysis of how he conceptualized the right way for universities to build up and manage research operations.

Better Administration of University Research

Being involved with both industrial research and university basic research at the time, Compton saw the clear need for both. He praised industrial R&D labs and their uncanny ability, where profits were concerned, to produce research outputs that seemed “greatly exceed the individual capacities of the research workers” involved.

But he personally enjoyed the goals of his basic university research more:

Basic research must…be a free and unfettered search for truth. It is the universities alone which can offer any considerable opportunity for such endeavor.

However, he did not think that the structure of university research departments was perfect. Compton observed that research was starting to become more specialized and cooperative. With that, he saw another area of major opportunity to improve university research as a whole: better administration.

At the time, no universities were heavily backing the research enterprise remotely to the extent that any research university would today. The rise of the research capacity at universities and its administration was often quite ad-hoc. This should be unsurprising because, as Compton noted above, many universities saw research as the thing they allowed their teaching men to do to appease them. They often viewed the enterprise with “grudging or amused tolerance as harmless little idiosyncrasies in which scholarly men must be indulged in order to keep them contented and out of mischief.”

The merits of specialization

In reflecting on what he felt universities should do to most efficiently produce knowledge, he makes several points that are quite non-obvious. The first is on the natural advantages of departmental specialization.

Another solution can advantageously be advanced by wise administration of the universities. There seems to be a widespread, but ill founded, feeling that all departments of a university should be developed together and kept closely abreast. Perhaps this relieves the administration from embarrassment, but I venture to suggest (though the suggestion is not new) that this is not sound educational policy except for an ideal institution which has unlimited resources. Such a policy dissipates effort, and if every institution followed it we should have the spectacle of a great many universities all very much alike and all with struggling, mediocre departments. Much more effective in advancing knowledge as well as in bringing distinction to the university is the policy of supporting to the available limit certain departments selected because of their already outstanding character, or because of the traditions and purposes of the university, or for any other reason. If these favored departments are chosen in a coordinated group, then the university becomes an active center for the development of that field and the promotion of cooperative effort. For example, one institution may choose to give particular facilities for advanced work in classics and languages, another in historical, economic and social sciences, another to physical and biological sciences, etc. If we were to examine the record of those universities of limited endowment which have nevertheless been preeminent in the life of the country, we should find that they attained this preeminence through concentration of effort. The words "To him that hath shall be given" apply here as well as elsewhere.

Through concentration of effort in a coordinated group of departments, a university has the opportunity not only to correct the dangers of overspecialization, but also to take a strategic position in fulfilling its obligations to society.

Compton observing that these policies would lead to “the spectacle of a great many universities all very much alike and all with struggling, mediocre departments” was remarkably prescient. In the field in which I read the most papers, economics, a dozen or so universities make up around 80% of the papers I read. The mass amount of resources spent producing under-utilized research from dozens of additional expensive-to-fund economics departments almost makes my head hurt.

And there is an empirical literature attacking questions like this as well. Just recently, a Nature paper by Wapman et. al was making the rounds covering a similar topic: that 80% of all professors have been trained in 20% of PhD programs.

Those dozen-ish top Econ departments which I usually read are almost exclusively housed in universities that are highly rated across all academic fields. These include your usual Harvards or Stanfords which seem to be winning the tournament model of academia. But, within those dozen are two specialized departments that have risen above the more middling ranks of their universities’ general research departments via specialization. Those two exceptions would be UC San Diego, with its department’s heavy focus on time series analysis, and George Mason, with its focus on areas such as public choice and Austrian economics.

For anybody whose knee-jerk reaction is to think those specialized departments’ researchers are more constrained in some way, I’ve never met a member of these departments who feels like they are more constrained in their publishing than somebody at a place like UC Berkeley. In fact, a noticeable percentage of the weirder paper topics I’ve ever come across have come from the George Mason department (see this paper by George Mason’s Peter Leeson on the economic efficiency of trial by combat). These schools simply acknowledged what most businesses intuitively understand and what economists say they understand: comparative advantages are remarkably productive, particularly for up-and-comers.

Yet, specialized efforts like this that productively contribute to the diversity and progress of a field are remarkably rare.

How Compton felt a research department should be run

Compton then went on to share his ideas on how to structure research departments themselves:

Much can also be done to promote cooperation and coordination through actual methods of organization. This has been strikingly demonstrated in some of the big industrial research laboratories, from which the output has greatly exceeded the individual capacities of the research workers and has been achieved only by coordination of effort. Such organization requires a very wise and far-visioned director who can visualize the big objectives and steer through the mass of petty details which must be worked out in order to attain them.

While this research model was working quite well on an industrial scale, in which labs often held hundreds of employees and researchers, he did not think such a model was necessary desirable on the scale of a university.

In a university, where the number of workers is much smaller than in a big industrial laboratory, such army-like organization does not appear feasible or probably desirable.

The management model of a research department that he goes on to propose is remarkably insightful. It is much more dynamic than a large industrial lab, but also far more structured than a department of mostly autonomous professors doing ad-hoc research with their own separate funds.

There is another direction in which more effective organization is possible within the universities themselves! Departments of a somewhat more flexible nature than those to which we are accustomed and which could, more than now, be built around one or two outstanding men in the department, could give these men an opportunity for organization and concentration of effort which is now rarely possible. This would, of course, require careful selection of men.

His comments were brief, but they are quite interesting to consider. A physics department with $20 million and two elite scientific directors able to allocate all resources as they saw fit could do remarkably different research than a department of 50 physicists with about $400,000 each. The model is also flexible in a way that makes intuitive sense for scientific work.

If the scientific directors, the “great men” as Compton referred to them, saw it as in-line with the specific goals of their department, they could spend a large chunk of the money on equipment and technicians and maintain a smaller stable of professors. They could also hire data engineers or whoever else they needed to optimally push a specific scientific area as a whole forward. And, even in a technical department like that, they could hire, fund, and give an office to a theoretician to largely do work on their own if the scientific directors felt the theoretician was too good of a talent to pass up or they valued the individual as a sounding board for others’ work.

For many, the concept of a department as something along the lines of 50 autonomous professors with 50 separate bank accounts working more or less on their own projects feels like a natural default. But, as you consider the kind of department Compton is describing, where a few scientific directors set some general goals/a mission and can then just spend the money however makes sense, it becomes clear that this “Compton model” is also a quite reasonable default.

A (possible) modern analog employing the “Compton model”

In trying to come up with a modern analog for something like Compton described, DeepMind comes to mind. Particularly in its early days leading up to/directly following its Alphabet acquisition. People like Demis Hassabis and one or two others from the early DeepMind team could be considered the scientific directors which Compton mentions. For the three year period prior to DeepMind’s acquisition, those directors dedicated their “department” of around 50 people of varying skillsets to solving a remarkably important basic research problem in the field: beating top human Go players.

The total staff of DeepMind was around 50 at the time of the acquisition and they’d raised around $50 million in total. Just doing some back of the envelope math looking at the number of faculty in the CS Department at a place like the University of Wisconsin Madison, the rough salaries of academics at different levels, and the general size of NSF grants in the area of computer science, it would seem that DeepMind’s yearly budget was not dissimilar to a department like UW Madison. Maybe it was as something like double, but probably not much more than that prior to its acquisition.

It’s harder to tell what happened with their budget in the years after their acquisition, but the comparison to UW Madison in terms of staff size post-acquisition does not seem ridiculous. Judging from the AlphaGo documentary, it seems that the team had noticeably grown from 50 since the acquisition. But, in making the comparison, it should also be kept in mind that while university departments may only have around 50 professors, each professor often has multiple grad students and post docs contributing substantial effort into projects in addition to department administrators and others adding to the total headcount. Regardless, the small details of the comparison, whether DeepMind should be thought of as 0.5 university departments or 2.5, don’t matter very much in contributing to the general point.

What matters is that how DeepMind was able to deploy its resources and staff was remarkably different than a traditional academic department. And it seems to have worked phenomenally. Using inputs not dissimilar to the University of Wisconsin Madison, a great department that produces consistently good research, it would be hard to argue that the DeepMind/Compton model didn’t produce something quite special.

The “directors” chose a fundamental research question that was widely acknowledged to be a question of massive importance to the field. DeepMind had the flexibility to staff themselves the way they needed to solve it. Of course, there were talented PhD researchers from multiple related disciplines as you’d find in academic departments, but also your workhorse software engineers and data engineers whose skills make projects like this work that are sorely lacking in most university departments.

The problem was not cherry-picked either, it was considered a common opinion in the field to expect that a Go algorithm that could compete at a world-class level was ten years away. As DeepMind moves into fields like protein folding and nuclear fusion, the organization continues to show substantial promise in a variety of areas.

The success of DeepMind’s organizational model is definitely a very strong data point in favor of Compton’s 100 year old hypothesis. Compton was not an outsider who knew nothing of being an independent, unfettered researcher within a university department. He was one at Princeton. And he was not some armchair theorist who knew nothing of the nitty gritty of what made industrial research work. He was a longtime contractor with General Electric and was so valuable to them that the GE CEO, Gerard Swope, insisted on recruiting Compton to be the MIT President in 1930 even though Compton didn’t really have much initial interest in the job.

Compton, having deeply experienced both worlds, felt like this model just made sense. It allows for a certain level of freedom in choosing problems and job security that comes in academic departments, but also a more ideal allocation of resources than you’d tend to find in a university. It does seem like this model, if it were pervasive, would be much less susceptible to some noted inefficiencies present in our current academic STEM ecosystem.

Namely:

1. The failure to compile and maintain large datasets that could be pivotal to a field

2. The failure to build and maintain software packages that could be pivotal to a field

3. And the underinvestment in instrumentalists who could continually improve upon the machinery that makes science possible/design new instruments altogether

The model might be susceptible to some new problems, as is the case with any model, but it does seem like it would likely be strong in areas in which our current model is weak.

Looking Ahead

If anybody with special knowledge about DeepMind disagrees with this characterization or has any comments, I’d love to speak with you! DeepMind is an organization I’m fascinated by and that I’d love to learn more about.

Also, I would love for readers to reach out to me with additional research organizations, successes or failures, that they think fit the Compton-model of an organization and are worth looking into. I’d love to build up a small “dataset” of these to better explore the model’s tradeoffs and when it seems to succeed vs. fail. For now, I’m left wondering just how many areas of research would turn out to be much less wicked than they currently seem if confronted by a Compton-model research organization.

DeepMind’s success on a problem closer to basic research, like it’s Go work, and applied problems, such as AlphaFold, should provide strong optimism that there are a wide variety of areas that we can make a major dent in with such an approach.

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Hope you enjoyed:) Please reach out to me on Twitter with more research organizations, present or past, which you think fit the organizational mold of this Compton model and are worth exploring.

Citation:

• Gilliam, Eric. “How Karl Compton believed a research department should be run,” FreakTakes Substack. 2022. https://freaktakes.substack.com/p/how-karl-compton-believed-a-research

As was true of the last two pieces, the majority of the MIT-related information in this piece comes from Philip Alexander’s fantastic work of history called A Widening Sphere: Evolving Cultures at MIT.

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*BIG NEWS: This will be my last piece as a part-time Substacker who writes at night after work. Starting next week, I will be working on progress studies-related work full-time. I will be doing much more than just writing. I look forward to updating you all on my plans in the coming weeks. For now, I’d just like to thank all of the readers who (somehow) found my writing and engaged with it. You all made this possible.

*This is another piece done in partnership with the Good Science Project

The first piece in the MIT series covered the early decades of MIT and its hands-on approach to educating engineers who would disproportionately end up in leading roles as builders in America’s era of peak growth. The second piece of the MIT series detailed early MIT’s radically applied approach to facilitating research that served industry, going as far as to fund certain departments almost entirely through industry contracts. In this piece, the last in the early MIT series (for now at least), I’ll explain the rationale behind MIT’s shift towards more pure research by its faculty and its increased emphasis on the broad scientific training of its students — at the expense of hands-on technical training.

To be clear, MIT is still a very applied research university that serves industry more so than competitors like Harvard. But it is clearly far more similar to Harvard now than it was 100 years ago. The differences in its education are the starkest. A large percentage of MIT graduates 100 years ago would go off and work in mining, power distribution, sewage and sanitation, infrastructure building, or construction. Even those with more scientific degrees like chemistry or chemical engineering would funnel into jobs such as chemical analysis for a paper manufacturer.

The changes in the Institute’s policies towards research were substantial, but far less extreme than the changes in education. In the early 1900s, MIT research staff like Vannevar Bush would often spend a majority of their research time working on projects in partnership with industrial firms. This was not seen as a sideshow to the actual job of being an MIT faculty member. The Institute saw this as an opportunity for the faculty to deploy their expert-level toolkits on the vexing problems of modern industry. Just as importantly, this was the best way for the professors to stay current on ever-changing industrial best practices which they would then pass on to their students. Professors being able to contribute to top-notch industrial research and educate the best engineers in the country in a hands-on, practical fashion was very strongly emphasized in the hiring and promotion of professors. Just being highly cited wouldn’t get you very far on Tech’s campus.

The major shift from this older version of MIT to modern MIT, MIT 2.0, largely began under pre-World War II President Karl Compton. At the time, many on the MIT Corporation and some of the Institute’s most distinguished alumni believed that the needs of industry were evolving. As MIT had been accustomed to doing, they thought the Institute should adapt and train their students for the new future of industrial innovation that was clearly taking shape.

Before I continue, I’d like to make two things clear. The first is that I completely understand the trends that Compton and people like him at the Institute saw that precipitated these changes. The second is that, while the Institute is different now, it’s hard to call what they did a mistake because I — and many others — would still classify MIT as the best at what it currently does. If you’re the best at the new thing, it’s hard to say a mistake was made. But, as I pointed out in the first two pieces, I do believe that it would be better for American progress if some organization, whether it is MIT or anyone else, implemented additional educational and research programs analogous to those of early MIT.

With all of that out of the way, let’s dive into what happened.

What the MIT Corporation wanted

Around 1930, the MIT Corporation (MIT’s Board) was looking for a new president. This time around, unlike previous presidential searches, the search parameters were quite specific. They wanted the Institute to hire a research physicist. The man whose name quickly rose to the top of the list, Head of the Princeton Physics Department Karl Compton, found the Institute’s interest in him strange.

Compton was quite at home in the then-Eden of professorial comfort that was Princeton, New Jersey. He was at home doing the lab work of an experimental physicist and was known to be theoretically driven. His major academic contributions included: inventing an experimental device called the Compton electrometer with his brother Arthur, pioneering work in electrical plasmas, as well as other work related to electron collisions. But, beyond his consulting arrangement with GE, he had not done much industrial-related work beyond his temporary assignments during World War I.

Still, to the MIT Corporation, he was perfect. Not only was he loved and accepted by the pure physics community, but he’d proven himself to be extremely useful in his consulting role with GE. Gerard Swope, then GE President and MIT Corporation member, was Compton’s biggest advocate on the Corporation. Even though Compton was told that he could make MIT’s physics budget as large as he wanted, he still found this offer surprising and a bit of an odd fit. What could he have to offer in the education of students who would go on to build infrastructure or work with heavy machinery?

So, Swope sent Compton to talk with Frank Jewett, the founding director of Bell Labs and MIT Corporation member. In just the same way that a VC develops a thesis of how some industry will evolve in the coming decades and invests accordingly, the Corporation had a thesis about what the future of Industrial innovation looked like and was hiring its next president accordingly. The seemingly inevitable expansion of corporate R&D labs across sectors weighed heavily on their thinking. Philip Alexander writes:

Jewett talked, Compton listened. The Institute, he said, had become stuck in neutral or reverse and needed a jump-start. Its vision —outmoded, if not exactly irrelevant — was not meeting industry needs. MIT’s founder, William Barton Rogers, had conceived and built a place that would lead in science as well as in its practical applications. But MIT had fallen behind in the former and its approach to the latter bordered on obsolete. For decades, industry had relied on MIT to supply personnel trained in certain techniques, lab methods, shop practices, and other routine functions. In turn, MIT “took on a strong slant of immediate practicality.” But Jewett’s firm (AT&T), Swope’s (GE), and others had evolved with such precise, refined, often proprietary technical demands that they quickly began training their own staffs. As this trend grew, MIT’s value as a supplier of technical expertise declined. What industry needed from MIT was not so much practical skills as graduates broadly educated in science, mathematics, and basic engineering principles—personnel with minds open to “the anticipation of technological change…some contact with the spirit and methods of research, and preferably some experience in it, so that [they] would be prepared to grasp new technological opportunities and either to participate in their development or at least to understand something of the conditions required for such development.” This pool, with its more flexible, creative mindset, would help industry take advantage of new opportunities opened up by advances in science. Jewett explained that the opportunity to break with the traditional style of engineering education, and to reinforce the pure sciences, could be realized only under leadership that would move aggressively to build a new type of faculty. There had been some tinkering around the edges under Samuel Stratton, but nothing like the transformation that Jewett was hinting at. Engineering departments, he said, must have more research faculty, whether trained as engineers or as scientists. In his mind the type of leader most likely to make this happen was a research physicist — not an engineer, or a chemist, or a biologist, but a physicist, someone like Compton, whose background and experience lay at the juncture between academic science and technological know-how.

Jewett laid out a vision that Swope had merely hinted at. This was not the MIT that Compton had heard so much about, productive yet satisfied with its traditional mission. He had dismissed the challenge because it felt like giving up a career for something opposite. But the transition was as natural as one could find — ”an opportunity,” Compton realized, “to draw on this background of experience and my scientific contacts in order to enlarge the scope of their value and influence in the educational and research fields generally.”

He understood the part that MIT had played in American science and technology. In just short of seven decades, it had grown from a small experimental school into America’s foremost institute for technological education. The first collegiate program in architecture had started there, along with the earliest formal coursework in architectural engineering. The first programs in aeronautical engineering, chemical engineering, food technology, industrial biology, naval architecture, and marine engineering — these were MIT innovations. Jewett, however, talked to Compton not about legacies, traditions, or achievements, but about where MIT stood currently, poised at a crossroads, ripe for change in a world where science and technology were moving in unprecedented directions. — A Widening Sphere

This thesis was the North Star that Compton would use to steer the Institute towards a more modern path.

With the benefit of hindsight, we now know that many areas of modern industrial innovation look far more like golden-era corporate R&D labs than others. In the sectors where the Corporation’s vision was right, MIT is, today, elite and extremely useful to industry. In the areas where golden-era corporate R&D lab-style research is less pervasive, it seems like MIT has taken a noticeable step back in the impact it has on those industries.

At the time, though, using this thesis as a North Star was probably a pretty good decision.

The new face of industry R&D

The Corporation’s vision of where industry was going was very prescient. Their predictions proved quite accurate, at least for the next three to five decades — you really can’t expect people to make predictions over a longer time horizon than that. In this mid-1900s period, corporate R&D labs grew in number, scope, and size for all types of large industrial firms. Bell Labs, GE, and DuPont are just a few very famous examples of this larger trend. (Representatives from all of those companies sat on the MIT Corporation.)

The number of scientists employed in corporate labs in the chemical industry, for example, tripled between 1921 and 1933, from 1,102 to 3,225. It then exploded again, growing to 14,066 by the end of World War II.1 And this general growth in applied R&D investments continued in the post-war years, peaking in the 1960s.

Describing some of the highlights of the corporate R&D ecosystem, Robert Gordon writes:

Much of the early development of the automobile culminating in the powerful Chevrolets and Buicks of 1940-41 was achieved at the GM corporate research labs. Similarly, much of the development of the electronic computer was carried out in the corporate laboratories of IBM, Bell Labs, and other large firms. The transistor, the fundamental building block of modern electronics and digital innovation, was invented by a team led by William Shockley at Bell Labs in late 1947. The corporate R&D division of IBM pioneered most of the advances of the mainframe computer era from 1950 to 1980. Improvements in consumer electric appliances occurred at large firms such as General Electric, General Motors and Whirlpool, while RCA led the early development of television.

For a long period, this type of work was a massive contributor to American industrial innovation. And the MIT Corporation members were right, this type of industrial R&D required MIT to output workers that were a bit closer to hands-on scientists than practically-trained workmen with a scientific base. Industry was doing actual science in its own right. The chart below shows the average citations per publication of the top 200 large industrial firms at the time compared to that of the top 25 research universities at the time. Being the average of the top 200 firms, this graphic is not the cherry-picked results of the most famous R&D labs. There seems to have been a widespread standard of scientific rigor in the R&D labs of large firms across industrial sectors at the time.

Scientific Citations Per Publication by Sector

The following graphic from Candel et al. shows that these companies represented a wide variety of industries, many of them quite industrial.

(Don’t worry too much about interpreting the numbers and parentheses. If there’s numbers in an industry column, they were represented in the 200 firms in the dataset.)

This was the real-world change that Karl Compton, a practical academic physicist, was brought in by the Corporation to shape the undergraduate curriculum towards.

MIT also modified its research priorities in response to these trends

MIT researchers had been a dominant force in applied industrial research in prior decades. In these earlier decades, MIT had been hiring researchers optimally suited to this applied work and allowed them to spend upwards of half their time in direct contact with industrial partners. Compton began to prepare MIT’s research ecosystem for a world in which large industrial firms were increasingly equipping themselves with scientifically-trained individuals and the newest scientific instruments. This investment in scientific work and constant utilization of cutting-edge science meant that firms could “readily absorb the new scientific developments and accommodate university scientists in their labs.”

This had not been the case in prior decades. One noteworthy change — which was covered more at length in the last piece — was Compton’s implementation of a one-day-a-week cap on industrial consulting. Many applied faculty, Vannevar Bush included, saw this as unproductive and thought that their time allowed for consultations was needlessly being clipped down to nothing.

The policy, along with the tax on outside income that came with it, was eventually disbanded. But its mere implementation marked a turning point in the Institute’s research policies. Compton and subsequent presidents were pushing the Institute in a modified direction. The Technology Plan-era of MIT was no more. Professors would no longer be encouraged to work with industry as much as possible. Something like 20% of their time would be more preferable.

To complement this clear signal, the introduction of the time cap on outside consulting, there is written internal correspondence that indicates MIT’s leadership also had an evolving vision of what research at the Institute should look like. In talks about MIT’s mission post-World War II, Julius Stratton, who taught electrical engineering and applied physics — whose opinion was held in high esteem by Presidents Compton and Killian — wrote the following about whether or not MIT should be occupying territory increasingly occupied by industry:

Let us agree that our primary function is educational. In fact, our entire function is educational when interpreted broadly. To prevent stagnation of our teaching, to ensure a constant flow of new ideas and new material, it is essential that a vigorous program of pure research be maintained…But MIT is an engineering as well as scientific institution, and a similar argument must be made for the necessity of pushing forwards the frontiers of engineering art. Unfortunately, these frontiers aren’t clearly marked and unless we do a little boundary work I am afraid that we may easily stray over into territory occupied by industry. Perhaps we should, on occasion, but I think we ought to know when and why. It seems to me that the excerpt cited from the charter adds to the complexity of the problem. For it states among other things that we should aid, by suitable means, ‘the advancement, development and practical application of science in connection with arts, agriculture, manufactures and commerce’ I strongly suspect that in view of the state of the arts and manufactures in 1861 the Founders mean just what they said. The development of a first-class harvester by the Mechanical Engineering Department of that epoch would doubtless have been looked upon as a practical contribution to society offsetting a lot of nonsense with test tubes and batteries, and justifying some solid financial support. Times have changed, and I submit that anyone interpreting literally that charter phrase about practical applications of science in manufactures might anticipate conflicts. As with out [U.S.] Constitution, the interpretation must evolve with the times….I do believe that it will be profitable to pursue this matter of our relation to industry further, in order to arrive at a clearer statement of policy.

Stratton did not think it was the role of MIT to continue to be a place that sought to do things like developing harvesters that could be used by farmers. While this is the sort of research work that MIT Founder William Barton Rogers himself took part in, developing methods for sanding common rocks to help Virginia farmers make fertilizers, times had changed. Stratton believed the Institute should look more like what MIT looks like today and less like its 1900 incarnation. (It should be noted that Stratton would succeed Killian as MIT President.)

Industry’s expansion into more scientifically involved R&D work, the increasing aversion of MIT leadership to engaging in too much “boundary work” similar to what was being done by industry, and the new (and ever-increasing) federal budgets for basic research in the post-war era served as fuel that pushed MIT in the direction of more pure research.

At the time, the increase in pure research and decrease in industrial research work did not seem like much of a loss to the Institute. After all, times were changing. If more and more industry innovation was happening in dedicated industrial R&D labs and less of it on factory floors, then, the thinking went, MIT professors didn’t need to play the same role in training students to be the hands-on workmen with a good scientific base that they used to. This change seemed like a better strategy for MIT to fulfill its mission of serving modern industry.

But then industry changed again…

2 However, as most of the readers of this blog know, the era of the great industrial R&D labs came and went. The era had largely run its course by 1980. Among other changes in this period: Wall Street began to press large public firms to “stick to their knitting” and divest from unrelated business units, manufacturing increasingly became offshored, and managers fell out of love with managing the odd corporate entities that were these R&D labs.

The share of total applied and basic research being done by industry roughly halved between 1960 and 2015 — from around 40% to 20%. Approximately half of this drop happened between 1960 and 1980. This decline is particularly pronounced when compared to the substantial increase in size of many corporations during the era. Take IBM and GE, for example. In 1980, net turnover for IBM was around $26 billion and $25 billion for GE. In 1998, IBM’s turnover had grown to $82 billion and GE’s $100 billion. In roughly this same time period, the number of PhD-trained employees at IBM decreased from 1,300 to 1,200 and the number of PhDs at GE shrunk from 1,649 to 475.

Arora et al. describe the winding down of these research operations:

By the 1980s, however, many corporations began to look to universities and small start-ups for ideas and new products. Large corporations’ reliance on externally sourced inventions grew, and many leading Western corporations began to withdraw from scientific research (Mowery, 2009; Arora et al., 2018). Some corporate labs were shut down and others spun-off as independent entities. Bell Labs had been separated from its parent company AT&T and placed under Lucent in 1996; Xerox PARC had also been spun off into a separate company in 2002. Others had been downsized: IBM under Louis Gerstner re-directed research toward more commercial applications in the mid-90s (Bhaskarabhatla and Hegde, 2014). A more recent example is DuPont’s closing of its Central Research & Development Lab in 2016. Established in 1903, DuPont research rivaled that of top academic chemistry departments. In the 1960s, DuPont’s central R&D unit published more articles in the Journal of the American Chemical Society than MIT and Caltech combined. However, in the 1990s, DuPont’s attitude toward research changed and after a gradual decline in scientific publications, the company’s management closed its Central Research and Development Lab in 2016.

The paucity of large firms winning R&D 100 awards is another indicator of this change. In 1971, Fortune 500 firms won 41% of these awards. In 2006, this number was down to 6%.

The world had changed again. But MIT did not necessarily revert to its older educational and research practices to better serve industries that had reduced their scientific efforts and lost a substantial amount of their scientific know-how. Some modern industries, such as those related to Silicon Valley, do maintain somewhat similar labs. Other industries, such as bio and biotech, conduct different aspects of this golden-era type corporate R&D in university spinoffs, startups, and larger companies. Other industries, conversely, have reverted to a state of R&D that is more similar to their early-1900s counterparts, but now without an early-era MIT to collaborate with.

MIT 2.0

The marked reduction in certain industries’ scientific know-how did not seem to affect the Institute’s view of its place in the world or the kinds of research it produced. As far as I can tell, to this day MIT is mostly seen as a place of pure research, but with a more technological bent than other universities. Its professors in many departments are still encouraged to spend about — but usually not much more than — 20% of their time working with industry. Its students do not tend to go work in hands-on professions and are closer to what Jewett described Bell Labs requiring of MIT graduates in the late 1920s:

Not so much practical skills as graduates broadly educated in science, mathematics, and basic engineering principles—personnel with minds open to “the anticipation of technological change…some contact with the spirit and methods of research, and preferably some experience in it, so that [they] would be prepared to grasp new technological opportunities and either to participate in their development or at least to understand something of the conditions required for such development.”

And there are still many industries that need graduates exactly like this. Tech firms have, to a significant extent, retained the mid-1900s culture of the industrial R&D labs. Many employ large numbers of highly skilled engineers and PhDs doing mission-oriented work that builds on scientific insights that serve the businesses’ ends. In addition, the life sciences/bio/biotech spaces come to mind as areas in which the large firms and startups alike, in different ways, embody different aspects of the old-school industrial R&D labs.

Not surprisingly, MIT alumni stream into all of these industries and are likely among the highest performers in them.

And that is great for those industries, but it seems clear that areas like construction and manufacturing have lost out in all of this. The Compton era was when majors like mining engineering, sanitary engineering, and construction engineering were phased out of the Institute’s curriculum.

MIT as a place for hands-on, learning by doing is by no means dead. But the Institute, in many obvious ways for those who have read Part 1, has de-emphasized these skills in many ways. When MIT became a place that saw the practical work of granting degrees in mining engineering or doing research to make first-class farming harvesters as not in scope with its mission, it stood in very stark contrast to the MIT described in the first piece.

But it makes complete sense how the Institute got from where it was to where it is today. Abruptly shifting back from a place of technologically-focused pure research to a place that once again focused on the training of scientifically-savvy but still hands-on workers would have been a tall task. Not to mention, MIT was already clearly a world leader in what it was currently doing.

But that does not make it any less true that the industrial sectors that are not widespread employers of top scientific talent and who do not heavily invest in golden-era R&D lab-style research need an old MIT more than ever.

Hope you enjoyed:)

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As I’ve said in previous posts, I am eager to connect with readers who run a research operation themselves or write about progress. If that sounds like you, please reach out and I’d love to talk!

Excited to fill you all in soon on what I’ll be doing next!

Citation:

• Gilliam, Eric. “A Progress Studies History of Early MIT — Part 3: The end of the beginning,” FreakTakes Substack. 2022. https://freaktakes.substack.com/p/a-progress-studies-history-of-early-045

End Notes

The following is an excerpt that I couldn’t slide into the piece but that readers might find interesting. It helps the reader understand the tradeoffs that the Institute was attempting to navigate for several decades.

Philip Alexander wrote of an episode at the Institute in the late 1920s:

The growing emphasis on research and graduate education led some to wonder if ‘the Institute now regards itself as primarily a research institution where a faculty man’s hopes of promotion varies distinctly with his publication output [and where] classrooms become discouraging affairs, supervised by men who do not, in general, dare to allow teaching become a primary interest.’ Stratton’s position was that without the research mindset, faculty members risked becoming “mere routine men” out of touch with their fields. But some corporate interests worried, too, about MIT losing sight of the ordinary engineer. One executive told Stratton [the then President about to pass the reigns to Karl Compton] that he wanted to support ‘some university that is not trying to make science abstruse and difficult to understand, but one that believes as I do, or one to whom I can sell the idea that the greatest contribution that all of us can make to science is to make it so simple that it can be understood by the mass of our people and its benefits applied by all kinds of people and in everyday problems.’

I will complement this story with a story from my own undergrad experience. One of our beloved data science TAs at Stanford was not just a genius, but also a fantastic teacher. He had done his undergrad at MIT. He had mentioned many times how much he liked Stanford’s CS curriculum. One day, when we pressed him for details as to why, he kind of sheepishly smiled and said something like, “Um…uh…Stanford’s CS curriculum is much more…uh…approachable.”

He was very articulate, but he didn’t want to come off mean or arrogant. At MIT, things were apparently much more “sink or swim” in comparison.

As was true of the last piece, the majority of the MIT-related information in this piece comes from Philip Alexander’s fantastic work of history called A Widening Sphere: Evolving Cultures at MIT.

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*I am eager to connect with readers who run a research operation themselves or write about progress. If that sounds like you, please reach out and I’d love to talk! (or if you just think we’d get along, please feel free to reach out as well)

*This is another piece done in partnership with the Good Science Project

The first piece in this series covered the early decades of MIT and its approach toward educating many of the engineers who would end up in leading roles in America’s era of peak growth and building. In this piece, I will cover the Institute’s differentiated approach to research. MIT was radically committed to its primary goal of serving the needs of industry above all else. This not only resulted in a curriculum that was extremely applied, but it also extended to the Institute’s approach to research in its early years.

MIT’s founder, William Barton Rogers, did not live to see MIT pursue this mission of extremely applied research on a large scale. But it was always in his grand vision for the school. Rogers himself was an academic with an applied bent. While he was a Physics and Civil Engineering professor at the University of Virginia in Charlottesville, he was made the official State Geologist of Virginia after publishing a series of articles in the Farmers' Register, a monthly publication "devoted to the improvement of the practice, and support of the interests of agriculture." The articles detailed a method for sanding rocks commonly found in Virginia to make fertilizers. The Virginia farmers, for whom the publication was intended, quickly began deploying Rogers’ methods in the field.

This type of research — requiring skills far above the level of the common worker to undertake, but producing outputs that were extremely useable by the common worker — was exactly the kind of research that the Institute would go on to perform at a much larger scale. And this style of research, if integrated into the engineering departments of top universities, could go a shockingly long way in facilitating progress today.

The First Official Labs

For many years, research had to take a backseat at the Institute. The primary goal of the Institute was training its students — and the Institute was very resource-constrained for its early life. However, around 1903, Tech’s research efforts began to pick up steam under the direction of President Henry Pritchett.

Pritchett said upon returning from a tour of several German polytechnics:

The time has come when the Institute must not only be a teaching body, but it must well lay the foundations for a school of investigation into the physical sciences…How important is the development of the research spirit as a part of national progress we are only just beginning to realize.

Upon returning, he established several labs. The first was the School for Engineering Research, a place designed for advanced engineering students to work, experiment, publish ideas, and build up an increasing pool of knowledge for engineers and other related workmen to utilize in the real world. (Tech shut down the lab soon after it began due to staffing difficulties.) The second, founded in 1903, was the Research Laboratory for Physical Chemistry. It was created largely at the urging of Chemistry Professor Arthur Noyes (’86). Several of the instructors affiliated with chemistry work at MIT were already conducting their own personal research, so establishing a lab gave them a more formal venue to continue their research. While the lab had a strong interdisciplinary bent, hiring both physicists and chemists, the research it performed was much less applied than much of MIT’s early research, making it a bit of a minority at the Institute for the following decades.

The third lab was Tech’s Sanitary Research Laboratory and Sewage Experiment Station. The research carried out at the lab typified the kind of research that the Institute would do best in the following decades. The technical contributions the lab made were extremely practical, but “always conceived in a thoroughly scientific spirit.” The goal of the lab was to address the sewage problem afflicting many American cities and towns. (MIT instructors had been working on the problem for several decades, but the injection of funds allowed the project to expand its work.) The research program was based on the hands-on testing of and experimenting with the city water supplies. Under Biology Professor William Sedgwick, the lab would invent the first techniques for measuring microorganisms in sewage and possibly the first use of sand filtration of a city water supply for disease prevention in 1893.

Many of Sedgwick’s civil engineering and sanitary engineering students would take these learnings forward with them as water systems were built in towns all around the country throughout the late 1800s and early 1900s. (I detail the massive impact of these water systems in depth here.) With the injection of funds in 1903, this course of research expanded its scope and Sedgwick hired a diverse team of biologists, chemists, and bacteriologists to push the lab’s work even further. These extra funds allowed the lab to take on even bigger roles in research as well as public health efforts more generally.

1903 marked a turning point. Tech was on more stable footing and able to take a more organized approach to research at an institutional level. The applied approach that MIT took was a natural fit for the Institute and the Institute’s labs quickly began to impress industry with their ability to solve a wide range of partners’ technical problems.

The growth of applied research at the Institute

Over the next 15 years, applied research would grow and thrive at the Institute. And, to be clear, what they called applied research at the time was much more applied than what we call applied research today — where things like experimental particle physics would come to mind as “applied”. Applied research meant things like industrial research problems or the kinds of problems they were working on at the Lawrence Experiment Station.

These applied research projects at the Institute were often done in partnership with or in service to companies. President Maclaurin, who oversaw much of this applied research expansion, strongly believed that work done by the applied and pure labs at the Institute was complementary. But given the financial constraints, MIT tended to lean towards growing the applied research projects. Alexander writes the following on research under Maclaurin:

Most lines of research introduced on his watch were engineering-based, not science-oriented. In 1911, the electrical engineering department studied ways to improve electric vehicles while naval architecture worked on ship propulsion. A research division in electrical engineering, analogous to the laboratories already in existence for physical chemistry, applied chemistry, and sanitary engineering, was established in 1913 with support from AT&T and other companies. One of its inaugural projects looked at problems of speech clarity in telephone transmission. Also in 1913 Maclaurin arranged with the U.S, Navy secretary Josephus Daniels for Jerome Hunsakar, of the naval constructors’ corp, to come to Tech to train aeronautical engineers and to promote research on “flying machines” and manned flight. A research laboratory of aerodynamics was founded in 1914, with a wind tunnel — first of its kind in America — to evaluate the impact of air currents at then-breathtaking velocities up to 40 m.p.h. Results laden with military applications flowed to the Navy in series of confidential reports. One study in 1915 assessed the influence of gyroscopic stabilizers on the motion of aircraft exposed to high wind gusts. The problems tackled by these various laboratories arose, Maclaurin observed, out of “the actual difficulties of our industrial life” and presented Tech with key opportunities in light of how rapidly such problems continued to crop up. Engineering research was vital to “the whole field of profitable enterprises,” and with German supplies cut off because of the war, chemical engineering was uniquely positioned to stimulate America’s next industrial boom. — A Widening Sphere

MIT was ideally suited to take up work like the projects above and excelled at doing this type of industrial and engineering research. In this period, Tech lost many of its faculty who were more interested in pure scientific research to other universities — as the curriculum was also becoming more applied. There was no question that the Institute existed to best serve the needs of industry and the school was increasingly doubling down on this mission. There were naysayers, but much of the school’s board (the MIT Corporation) was quite pleased because the Institute was producing useful research, building MIT’s reputation by impressing their industrial clients, and training engineers of the highest level. So, there was not much urgency to immediately begin expanding the role of pure research at the Institute.

In 1917, when the US entered World War I, the Institute continued to expand the applied research work that would contribute to the military effort. Chemical, mechanical, and electrical engineering laboratories shifted their efforts to finding ways to offset German advances in military technology. One of the more notable uses of MIT instructors was in poison gas-related work. Professor William Walker, director of the Research Laboratory of Applied Chemistry, was made commanding officer of the chemical warfare service and 18 members of the department followed him, working on poison gas and gas defense.

Financially supporting itself with applied research: MIT’s Technology Plan

When the war ended, MIT found itself in a precarious funding situation. The post-war period was a time of industrial uncertainty, and this made many of MIT’s traditional donors much less likely to come forward with large donations. Massachusetts had also cut off its yearly state gift to MIT because of a law change. In concert with a vast influx of students resuming their studies after serving in the war, MIT was in a financial bind.

But Maclaurin had an idea: self-support. MIT would capitalize on its own assets and earn money by formally offering its services to industry on a larger scale. High numbers of industrial partners had been eager to engage in ad-hoc courses of research with MIT’s applied professors, often paid for by the company, anyway. Why not turn this into a much larger, more formal program that was facilitated by the Institute? The idea would grow into what was known as the Technology Plan.

The Technology Plan is emblematic of the industrious, no complaining, get-things-done attitude of the Institute in that era. Maclaurin established a new division of the Institute, the Division for Industrial Cooperation and Research (DICR), to oversee the initiative. And they got to work.

The DICR was launched in 1919 with William Walker, the head of the applied chemistry institute, as the director. The plan was meant to attract a wide range of industry sponsors and would work as follows:

In return for an annual fee paid up-front, a company was entitled to technical advice from faculty and staff, consulting services, access to alumni records, a variety of quid pro quos. Walker, who had led Tech’s highly regarded experiment in cooperative education (the school for chemical engineering practice), employed an aggressive marketing strategy to seal contracts, totaling almost a million dollars, with 189 firms inside two months. He wanted the program viewed as a kind of exclusive club, one that members boasted belonging to, rather than as a charity to help pull the Institute out of a financial hole. Firms were offered bang for their buck, so to speak, and got it, by and large. “We want to meet the industries more than halfway,” Walker told the local press. “There could be no more legitimate way for a great scientific school to seek support than by being paid for the service it can render in supplying special knowledge where it is needed…Manufacturers may come to us with problems of every kind, be they scientific, simple, technical or foolish. We shall handle each seriously, giving the best the institute has at its disposal.” Some complained that MIT, in setting itself up as an industrial consulting service, had placed itself in competition with its own alumni. But Coleman du Pont swatted this fear aside — “If any Tech man has made such a criticism,” he said, “he must be a poor specimen of the breed, for the real Tech man has no fear of competition.” — A Widening Sphere

The program was remarkably successful and played a massive role in helping MIT survive this time of financial uncertainty. And, culturally, the Technology Plan work felt like a natural role for Tech to play in carrying out its mission to serve industry.

Some tech faculty, particularly those like Noyes and Hale — who were more on the pure research end of things — thought the Technology Plan was a slippery slope and would blur the lines of education and industry too much. But the arguments for, in the end, were far stronger in the short run. The pros, as one current student later recalled them, were:

The Institute would gain by being brought closer to Industry’s problems, to the benefit of professor and student alike; that Industry in its turn would learn that there were ways of getting benefits from the Institute other than by raiding its faculty and luring its most gifted men away for good—in those days a real vexing problem. — A Widening Sphere

The administrative machinery MIT put in place to facilitate Technology Plan contracts worked extremely well. The DICR would serve as intermediary, negotiator, and manager of all contracts between faculty members, departments, and outside firms. “Staff attached to the Laboratory of Industrial Physics operated under several such contracts, in a more or less self-supporting way. So did the Research Laboratory of Applied Chemistry, with projects carried on simultaneously in oil refining, iron and steel corrosion, paper waterproofing, automobile fuels, combustion reactions, rubber, leather, lubrication, and metallic oxidation.” The lab also consulted on textile cleansing for the Laundry Owners of New England. Several members of the chemical engineering group worked as consultants for fuel, oil, and gas companies. The electrical engineering laboratories held research contracts for research on high-tension cables and the impact of illumination on industrial efficiency. As interest in communications grew in the mid-1920s, the labs entered into agreements with Western Electric, New York Telephone, Bell Labs, and AT&T, all behemoths at the time. Projects of this sort included things like short-wave radio research.

Also notable was Vannevar Bush’s work on an electromechanical integrating device — product integraph, a form of analog computer — which vastly improved computing capacity, speed, and accuracy. Bush’s other research projects included the network analyzer, a power-system simulator sponsored largely by General Electric and completed by 1929, and, a decade later, the differential analyzer, a more advanced version of the integraph developed with support from the Rockefeller Foundation. — A Widening Sphere

And labs like biological laboratories sought industry contracts to study nutrition, vitamin values, fermentation, effects of irradiation, and applications of bacteriology in food processes.

In this era — when MIT researchers were heavily involved in Technology Plan projects — the Institute was at its best in a way. The Institute was contributing large amounts of its research resources to solving vexing industry problems while also better training young engineers to go solve problems like these in the future. And the school accomplished all of this while solving a desperate funding problem.

The Institute would surely need to find a way to strike a proper balance between these industrial research projects and research that was a little more open-ended, but the Technology Plan was an important step in MIT finding a new and creative way to make itself extremely useful to industry.

At times, things may have gotten a bit too applied

While most of the professors involved, as well as the MIT corporation, seemed quite pleased with large parts of the arrangement, there was a balance to be struck. At a certain point, the proportion of research being carried out for these DICR contracts grew to be a bit too large for the good of the Institute. Under President Stratton, they sought to reign things in a bit. Alexander writes:

The incentive underlying many of MIT’s research programs was earning power and service to industry. Department heads in the engineering disciplines argued that the Institute accrued substantial benefits from industry’s need for help with problem-solving. “The Institute,” wrote one, “true to its traditions, should occupy the first place for the training of leaders for these industries.” But by the mid-1920s, Stratton and some engineering faculty began to question this focus. Stratton [then-MIT President] appreciated funding boosts — the Research Laboratory of Applied Chemistry brought in $171,880 in outside contracts in 1927-28, while its poorer, pure-science sister, the Research Laboratory of Physical Chemistry, brought in $25,483 — as well as the professional opportunities that came students’ way because of MIT’s ties to commerce and industry. But these often turned into mixed blessings. Robert Haslam, director of the applied chemistry research lab, warned in 1924 that reliance on industry for six-sevenths of the lab’s support had prevented the program from branching out in creative ways. “While our outside relations are peculiarly fortunate and happy, this work is of necessity carried on under certain pressure that interferes with the productive capacity of the Department in its contributions to general science. The Department would regret to lose all this outside work, but if the proportion of it could be reduced, the contributions of the Department to the prestige of the Institute and to the development of the profession could be greatly increased.” — A Widening Sphere

Stratton set out to help staff devote less time to tasks and more to issues and “working out problems of fundamental importance to the industry as a whole.” Also, in a practical sense, Stratton believed it would be easier to retain applied staff members, who were lured to work for companies frequently if they were granted more freedom — since the work was similar and pay and resources far greater.

The steps that the Institute took in the 1920s to rectify the situation should serve as some proof that this extremely applied, industrial work can exist alongside a culture of pure research.

Industrial research and pure research can pair well

President Pritchett was formerly a researcher himself and recognized that pure research was, to some extent, obviously necessary to carry on a thriving engineering department that served industry. With this goal in mind, in 1924, the Head of the MIT Physics Department earmarked a portion of the proceeds from contracts with General Electric and Victor X-Ray Corporation to encourage pure science research in physics, chemistry, and biology. They also approved a new Laboratory for Theoretical Physics. Alexander writes:

Even Vannevar Bush, whose experience lay on the applied side, was excited about prospects for fruitful give-and-take between this strong group, mathematics faculty such as Norbert Weiner and Henry Phillips, and electrical-engineering faculty and staff such as Gustav Dahl, Gleason Kenrick, and Julius Stratton. — A Widening Sphere

In this period, MIT would invite famous pure research physicists, often Europeans, to come for visiting professorships and lectures, such as Werner Heisenberg, Max Born, William Lawrence Bragg, Erwin Schrödinger, and Albert Michelson. After his visit in 1929, Bragg, who eventually became the Director of the renowned Cavendish Laboratory in Cambridge, wrote the following piece of advice to President Stratton on how to balance MIT’s applied bent with the obvious need to be doing a sufficient amount of exploration.

I take it…that you wish a good deal of this work to be on fundamental problems rather than on the problems sent in by firms which require a quick solution to some difficulty that has been encountered…I think you need one or two men in the laboratory who know the theory of analysis thoroughly, and who are free to follow to its end any interesting clue which turns up, without the feeling that they must produce practical results as soon as possible. Of course the man who has the power of producing the practical results is just as important and valuable, but he draws his ideas largely from the other fellow who is doing more fundamental work.

And even if one or two of the type of researcher that Bragg describes residing in each lab does not sound like enough to the reader, one could easily substitute in a larger number of these pure researchers. The main point to take from this excerpt is that even a top pure researcher like Bragg, whose Cambridge laboratory was as traditional as it gets, believed there was a way for pure researchers to thrive in even MIT’s most applied labs — which handled primarily industrial contracts.

Pure researchers should play a role at an institute dedicated to engineering and industry. But, also, the heavy role of applied research contracts in running a successful institute of this kind just makes sense. Many other land grant universities in the pre-World War II era engaged in industrial and agricultural research like this as well. At the time, the money flowing into these universities often craved a more practical research output. As I wrote in an earlier piece:

Pre-1950, the federal government was not anywhere near the behemoth university research funder that they are now. From 1909 to 1939, federal funding was somewhere between 4% to 7% of university revenue. Instead, universities relied heavily on state and industry funding.11

Their share of revenue from state funding in this period was closer to 20% to 30%. In return for heavy state funding, research universities developed specialties that were specific to the industrial activity of their state.12 Examples of this include the University of Oklahoma pioneering innovations in petroleum engineering such as reflection seismology and the University of Illinois producing cutting-edge research in crop production that was actionable for regular farmers.

Many of the best universities also relied heavily on industry partners and contracts for funding. This was in both the form of industry-sponsored labs and studies to produce research directly related to the industry’s work or through “consulting” contracts. These consulting contracts were not seen as the sideshows to the actual teaching and research that they are today. Rather, they were seen as opportunities for the professor to produce useful and exciting research, stay sharp on how industry was actually functioning so they could better train the university students, and make the professors and their universities much-needed income.

What is the right balance?

Many believe that corporate contracts, the bedrock of the Technology Plan, should play no major role in a researcher’s job. They think it is better to let the university research departments largely subsist on federal money — often from the NIH or NSF — that strongly favors pure research — what they called applied research in the 1920s would likely be perceived as far too applied to qualify for many modern “applied” grants. But, I don’t believe this anti-industrial research bias was at all the intention of individuals like Vannevar Bush who fought for the expansion of funds for basic research.

Bush, the then MIT Professor of Electric Power Transmission, had a much more moderated view on this point than many would expect — given that many primarily know him from his authoring Science: The Endless Frontier. Bush spent a large amount of his time working on research either for or funded by General Electric. He and President Karl Compton first met in a quite heated fashion when Bush was furious at a new Compton policy.

Bush opposed Compton’s one-day-a-week limit on outside consulting and a 50% tax on outside income — the proceeds to go into a special fund that would get distributed to all faculty. Bush threatened to leave since when he began his job at the Institute he was promised the ability to do a certain amount of consulting far exceeding the one-day-a-week limit. On top of bristling at MIT reneging on its promises, he said, “And furthermore I won’t stay at a place that has so little sense it tries to clip down to nothing proper consultation on the part of its engineering professors.” Compton offered Bush an exemption which made Bush irate, “Your whole damn fool plan will resolve in a welter of exceptions.”

Bush saw one-day-a-week as his consultation time being clipped “down to nothing.” When interpreting Bush’s viewpoint in reading The Endless Frontier, it is important to keep in mind the context in which he was writing it. This was the system that raised him. He was not decrying the use of researchers on industrial applications, which had gained more acceptance as a good public investment at the time. He was raising his voice to ensure that pure research, a vital natural resource for applied research and engineering work, was emphasized as well!

The need for pieces to be written in support of more industrial research contracts at a place like MIT would never have occurred to the MIT professors at the time. They were doing that work in spades. But, in assessing our current university research ecosystem, we may now find ourselves in the opposite equilibrium. Many professors are expected to spend as much time as possible producing research that serves the academic literature. Their work on projects that serve industrial applications is, in many cases, tolerated as long as it does not affect their publishing. And their performance on these projects is generally not used in hiring and promotion considerations — those are made almost entirely based on their publishing.

That seems terrible for progress.

There is a massive opportunity for universities with large engineering departments to implement and expand programs similar to MIT’s Technology Plan. In determining what percentage of time would be ideal to allocate to these activities, we can take some hints from the stories above. Vannevar Bush thought, for a very applied researcher like himself, that 20% of his time was far too little. We will call that the lower bound. And many felt that 6/7ths of the applied chemistry laboratory’s money, we’ll say that paid for 75% of the lab’s aggregate time, was too much. So, given those two bounds, it does not feel ridiculous for a university to orient its engineering department to strive for something like a 50/50 aggregate time split between pure research and industrial research.

These research projects would carve out time for researchers to apply their toolkit to the applicable problems of industry that are most in need of their skills. It would also create a corp of instructors far more capable of training useful and innovative engineers to work on those same problems upon graduation. Producing work whose output fills some hole in the academic literature and producing work that is meant to be an input into a physical industrial process are far from the same task. Not to mention, this type of work might result in increased productivity in pure research as well.

There can and should be individuals who spend almost all of their time on pure research. But it is probably bad for future progress to allow too many of these individuals to work in an environment in which few of their peers are spending a substantial amount of time working on industrial applications and problems. No matter what, some basic research will always find a way of trickling its way down into practical industrial importance. But allowing pure researchers to be siloed from the acquaintance of those who work on industrial applications — and not just the need to work on those problems themselves — feels like it is setting the system up for inefficiency. When we look back on the era of explosive productivity in areas of basic research like physics and math in the early 1900s, even the purest of pure researchers at the time tended to have regular interactions either with industry or with researchers who did industry-related research — due to industry contracts themselves, close friends who did industry work regularly, or conscription to work on military problems.

Many fear that we have become less successful at innovating in the world of physical things. Early MIT — with its Technology Plan and its general philosophies regarding what it meant to produce research that was useful to industry — offers many hints as to what can be tried to generate more innovation that scales in the industrial world. And I see no reason why these efforts have to come at the expense of pure research’s productivity.

Engineering departments around the country should consider hiring more early-MIT-style industrial researchers and implementing Technology Plan-like programs. There’s a chance that programs like this could even be run in a self-funded way — given their goal of taking on high numbers of industry contracts. Even for the most risk-averse institution, this could be a moderate-risk, high-reward bet that is worth making.

Thanks so much for reading:) Please subscribe to make sure you don’t miss part 3 in the MIT Series! (teaser below)

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Citation:

• Gilliam, Eric. “A Progress Studies History of Early MIT— Part 2: An Industrial Research Powerhouse,” FreakTakes Substack. 2022. https://freaktakes.substack.com/p/a-progress-studies-history-of-early-001

Teaser to Part 3: Upon hearing of Compton’s policy, one of the Institute’s finest physicists (and an alum), Luis Young, immediately left and never returned. He ended up at the Gillette Company. Vannevar Bush, however, did not end up leaving and it actually brought both men a mutual respect for each other. Bush appreciated that Compton was open to looking at things from all sides and Compton admired Bush’s outspokenness. The tax on consulting lasted just a few years. It was abandoned as impractical, but it did achieve its primary goal — to establish the core principle that even where consulting brought MIT useful benefits, the faculty’s first obligation was to the Institute. That may have been the start of a changing MIT. And, while it’s hard to say that it was bad for the Institute — MIT is IMO still the best at what it currently does and its research (and other work) is still more applied than competing universities — what MIT does now is different than what it did in the era of the Technology Plan. The third piece will dive into this topic further.

Patrick Collison and Tyler Cowen opened their 2019 Atlantic piece that helped jump-start the progress studies movement with the following passage:

In 1861, the American scientist and educator William Barton Rogers published a manifesto calling for a new kind of research institution. Recognizing the “daily increasing proofs of the happy influence of scientific culture on the industry and the civilization of the nations,” and the growing importance of what he called “Industrial Arts,” he proposed a new organization dedicated to practical knowledge. He named it the Massachusetts Institute of Technology.

In my eyes, MIT is entirely deserving of this honor: being used as the authors’ first example of an organization that generated progress. Yet, despite how well-known this article has become and MIT’s prominent placement in it, many in the progress studies community still don’t appreciate just how different the Institute was in its early years — arguably the Institute’s most productive years.

Early MIT was a remarkably differentiated product from the other elite, Ivy League universities. It was an experimental school focused on training a new kind of technical man, and a remarkably successful one. It helped train many elite engineers who helped build the country in America’s era of peak economic growth, an era whose growth is largely credited to engineering and technical feats. And its faculty contributed to this growth in an even more direct way, undertaking courses of research that bordered on being so practical that many in modern times wouldn’t even call it real academic research — not to mention its extremely close Industry partnerships that the school saw as vital to its mission. MIT was a place that saw itself as existing in service to industry, and it thrived in that role.

Over the next three pieces, I hope to help those who are less aware of MIT’s early history understand what the Institute did that made it unique. The three pieces will cover:

1. How MIT trained its students (usually engineers)

2. The early philosophy responsible for MIT’s extremely applied research projects

3. How the university began its drift, resulting in a school that is much closer to other elite research universities than to the hybrid technical school/applied research institute that it used to be

In this piece, I start the series where William Barton Rogers would have wanted it to start: detailing the education that went into building a ‘Tech man.’1 But, before I dive into the educational process that made tech men, I’d like to give readers an idea of what early ‘Boston Tech’ alums were going on to build using the skills they gained at MIT.

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*As a note, much of the MIT-specific information in this piece come from Philip Alexander’s fantastic work of history called A Widening Sphere: Evolving Cultures at MIT.

* This is another post in partnership with the Good Science Project.

Tech Men: The differentiated results

As long-time MIT Chemistry Professor Arthur Noyes (’86) once put it, the Institute aimed “to produce men who have the power to solve the industrial, engineering, and scientific problems of the day — men who shall originate and not merely execute.” Many tech alums would go on to do just that on the scale of individual factories and industrial operations. This was the use case that the Institute likely had in mind for its early graduates. But, as time went on, many others would find themselves in positions to do this at scale not just by working in leadership at massive firms; but, also, by finding themselves at the helm of some of the great industrial R&D labs with which many in the progress studies community are all-too-familiar.

The era of the great industrial R&D labs was built, in no small part, by MIT men.

Arthur D. Little

The first of these pioneers was Arthur D. Little (’85), who was a trailblazer in the new era of industrial research. He worked for a period at a paper mill, starting as a chemist and later becoming superintendent of the mill — a common career path for MIT alums at the time. Then he struck out on his own to start an independent firm with one of his co-workers from the mill, Roger Griffin. This firm would specialize in chemical analyses for quality control. He later applied his skill set to other problems, such as finding a way to make film that provided an alternative to the flammable nitrocellulose film, which would frequently set fire to cinemas filled with people.

His most important venture came with the firm he later founded, Arthur D. Little, which had its first major success in 1911 when General Motors tasked Little with setting up and staffing the company’s first-ever centralized R&D department.

Little and his firm would go on to apply this industrial research skill set to seemingly any industry which was willing to seek out their services — which was many. As Claudia Flavell-While wrote:

With this success under his belt, more scientific research and process design tasks followed, spanning smoke filters, newsprint, producing alcohol from wood waste, recovering turpentine and rosin from pine-tree stumps, and even airplane dopes. By 1918 the company occupied its own building in Memorial Drive, Cambridge, and had completed more than 16,000 separate investigations.

What had begun as a simple analytical laboratory had progressed into a serious industrial research operation, where different specialists in different departments would work together to fully exploit every promising breakthrough by fundamental research and thorough investigation of all the potential industrial applications for their economy and practicality.

Little believed that good chemistry and chemical analysis were the most direct way to boost efficiency in industrial applications of all kinds. “Every waste that is prevented, or turned to profit, every problem solved, and every more effective process which is developed makes for better living in the material sense and for cleaner and more wholesome living in the higher sense.” He was a pioneer in helping make this mindset more accepted in industry.

Little pulled no punches when criticizing many of the major educational institutions of the day.

It must be admitted with regret that our […] institutions of learning have failed to seize or realize the great opportunity confronting them. […] They have, almost universally, neglected to provide adequate equipment for industrial research, and […] have rarely acquired that close touch with industry that’s essential for familiarity and appreciation of its immediate and pressing needs.”

DuPont Research

Alongside Bell Labs, the Dupont research division is regarded as one of the great dragons of this golden era of corporate research and development. Arora et. al wrote in The Changing Structure of American Innovation that DuPont’s “research rivaled that of top academic chemistry departments.” They also noted that, In the 1960s, DuPont’s central R&D unit published more articles in the Journal of the American Chemical Society than MIT and Caltech combined.

(Dupont’s research unit would also add a Nobel Prize to its name in the coming decades. The award would go to Charles Pedersen, one of the few laureates without a Ph.D., who also happened to have obtained a Master’s in Organic Chemistry from MIT in 1927)

Not so coincidentally:

The DuPont family, industrialists of Delaware, sent its sons — William (’76), T. Coleman (’84), Alfred (’86), Maurice (’88), Pierre (’90), Henry (’94), Irenée (’97) — and a host of their descendants would follow, making Tech a family tradition. — A Widening Sphere

T. Coleman, Pierre, and Irénee would all serve as company Presidents in the coming decades. While some might believe that any family that would send that many of its sons to MIT may have set up a great industrial R&D lab whether they sent their sons to MIT or not, I don’t think it is a coincidence that DuPont research was established in 1903, the year after T. Coleman DuPont took over as President. T. Coleman, a Tech man and the first of three successive MIT alums who would run the company, took over after the sudden death of Eugene DuPont, a UPenn alum, after his 13-year tenure as President.

Eastman Kodak and MIT

Eastman Kodak was a powerhouse employer of top scientific talent throughout the 1900s. If you’re curious just how in-depth the research behind a company like Kodak’s product offerings can get, I encourage you to read this 1949 Nature excerpt of an exhibition put on at one of Kodak’s labs.

While George Eastman did not go to MIT, he was an appreciator and hirer of MIT alums to an extreme degree. Not only did his top aid — and eventual Kodak President — Frank Lovejoy (’90) attend the Institute, but he made a point of hiring MIT men in very high numbers. He saw MIT as the top hunting ground for technical talent. An MIT man oversaw the construction of Kodak’s original plant and managed the operations of the plant for almost a decade. In the early life of his R&D department, which would grow to contain thousands, the department was staffed with many MIT alums.

In January 1912, then-current MIT President Richard Maclaurin was on a promotional tour on behalf of the Institute and was invited to take his longest stop on the tour at Kodak’s headquarters in Rochester. Eastman missed Maclaurin on this trip, but he seemed genuinely disappointed and asked Maclaurin to meet him in New York City when the tour was over. The two met for a drink at a hotel in New York City. It was their first time meeting. The next morning, Eastman pledged $2.5 million to MIT. This amount of money was by far the largest ever contribution to the Institute and far more than they had been receiving from the state of Massachusetts.

Maclaurin was confused. A donation of this size was not even his goal.

Flabbergasted, Maclaurin made his way back to Grand Central. On the ride home, he played out the scene over and over. Almost too easy — no probing, little discussion, few questions, no pre-conditions. — A Widening Sphere

Eastman was not looking for fame either. He requested his giving remain anonymous. He would continue to write the Institute extremely large checks, as needed, for decades.

He was just a fan of the Institute and felt he had benefited greatly from its product.

General Electric’s Research Laboratory

Willis Whitney (’90), an MIT alum and instructor, was the founding Director of General Electric’s Research Laboratory. The now-famous lab would go on to make countless discoveries that were vital to GE’s business, and oftentimes science as a whole. William Coolidge (’96), an MIT alum and researcher at the lab, conducted the experiments that led to the use of tungsten as a light bulb filament. If that weren’t enough, he later used this technology in his work for GE that made improvements to X-Ray technology that are still relevant today. Coolidge later became GE’s lab director himself.

The lab was founded in 1900, and by 1906, the size of the lab had already grown to over 100 staff. By 1930, the lab contained over 400 physicists, chemists, electrical engineers, and support staff. On top of being invaluable to GE’s business, the lab would even go on to win two Nobel prizes. One of these prizes, won by Irving Langmuir in 1932, helped lead to the technology for gas-filled light bulbs that allowed GE to muscle its way to an astounding 96% market share in incandescent light bulbs.

(I also cover the work of the early GE Research Lab in a subsequent post on this Substack.)

Thomas Edison held MIT in high-esteem

Thomas Edison was an extremely practical man, particularly for someone as off-the-charts inventive as he was. Edison loved science and scientists. One of his idols was Maxwell. He, daily, perused a wide variety of scientific publications to stay current on the applicable theories, practical experiments, and discoveries. But all of this was with a purpose. He used science to invent. And he invented with a purpose: to make things that could be profitable and that people would pay him to produce at scale.

When Edison learned that Einstein didn’t know the speed of sound, and had replied that he didn’t care to clutter his brain with facts that could easily be looked up in a textbook, Edison stated that he hoped his son Theodore (’23), who studied math at MIT, would not lapse into this impractical mindset.

Theodore is a good boy, but his forte is mathematics. I am afraid…he may go flying off into the clouds with the fellow Einstein. And if he does…I’m afraid he won’t work with me.

Valuing practicality, scientific inspiration, the experimental process, and inventiveness the way he did, MIT was a school after his own heart.

Edison, an avowed critic of the university system and what he saw as the mediocre technical workers it produced, told an MIT alumni banquet once that “more nearly than any other school or college in this country, the Massachusetts Institute of Technology meets the demands of modern American life.” Edison sent two of his sons to the Institute. And he sang MIT’s praises frequently. In the same year, 1912, Edison was quoted by the Yale Daily News lashing out at traditional colleges and in favor of Tech: “I would employ almost any graduate of that institution who came to me,” he told the interviewer, but “in my business, if a Yale or Harvard man should come to me for employment I should probably say that there was no place vacant.” To be clear, he said that to the face of the Yale Daily News reporter. At any given time, Edison counted 30 or more Tech graduates in his enterprise with only a handful of hires from the famous liberal arts universities.

The professors at MIT tended to love Edison back. He was everything they were trying to train Tech students to be: scientifically informed, good with their hands, able to apply the combination of those tools to a variety of problems, and practical. When the Institute was looking to put the names of great scientific minds on the inside of MIT’s dome, the professors were upset to learn that the current president would not allow the names of living scientists. That meant the name of a great American would not be included. If not for the rule, Edison’s name would have been up there with names like Newton and Galileo. To a modern ear, his placement with those scientific greats might sound strange. But, to a contemporary Tech man, it made perfect sense. The Edison-like blend of scientific knowledge and workman-like know-how is the bedrock of industrial innovation and exactly what the Institute existed to help facilitate.

(In a subsequent written piece and podcast, I provide further detail on how Edison ran his lab and operated his research enterprise to ensure it built towards a practical, commercial vision.)

MIT took pride in the hands-on nature of its workers

While the above recounts the contributions of tech men to the great labs that did scientifically inspired inventing and innovating full-time, it was more typical for MIT alums to go work in an environment that was more hands-on and industrial. Mining, building roads and railroads, power production and distribution, chemical manufacture, public health, sewage, and sanitation were common industries alumni went into. And they often worked their way into roles as foremen, superintendents, or internal innovators/troubleshooters for these operations quite quickly.

The Institute did not train engineers to primarily go seek employment in the major cities like many modern universities tend to do. A country was being built up and connected, and MIT wanted Tech men to go lead the charge in this building. Tech alums were known to seek employment anywhere from the densest cities to the most remote outposts. In the early decades of MIT, many prospective students had heard about the school as a result of the many alumni who were working on and in charge of building sections of the railroads being built all around the country. As Alexander wrote:

Some lived as itinerants, moving from spot to spot, from one specialty to another, as industries shifted locale or focus, or as new settlements emerged. Tech graduates were known as adventurers, risk-takers, explorers inspired as much by a thrill or a challenge as by a safe income or job security. — A Widening Sphere

The Institute and its students understood that the common problems of industrial life mattered and required an individual who understood the production process as well as scientific and engineering principles to overcome them. Even those who went to work in areas that had a less hands-on, industrial feel, like the famous R&D labs described above, benefited from this skill set.

Here is a Wikipedia excerpt describing the first project that Willis Whitney worked on with General Electric. It was the kind of problem many MIT alums would encounter and solve in plants all over the country:

One of the first problems Whitney solved at the General Electric Laboratory was that of making a furnace that produced porcelain rods with scientific precision. He noticed that many rods would go to waste because of various defects.[1]After consulting with a foreman, he found that the current furnaces had varying temperatures; especially after a certain amount of repetitions. As a result, the furnaces could not be expected to produce perfect porcelain rods after every attempt. After experimenting with iron pipes, carbon pipes, and wire, Whitney found that he could create a suitable furnace by passing a controlled amount of current through a wire wrapped around a carbon pipe.[3] The carbon pipe would have a cork or coal powder in it to prevent combustion and water-cooled clamps to regulate the temperature. After finding the perfect ratio of heat to time cooking the porcelain rods, Whitney called in the foreman. Whitney demonstrated that the porcelain came out perfectly nearly every time and G.E. began production of the furnaces immediately.

This was a classic use of an MIT brain at the time. Whitney was trained in MIT’s workshops to understand the hands-on context that a foreman works in, and was also endowed with the kind of engineering training and classroom science that would allow him to both come up with and rig up a solution to a problem like this. But, crucially, he would likely have never learned about or cared about this application of his knowledge — making slightly less imperfect porcelain rods — if he wasn’t put in a position where he was in direct contact with a foreman making the rods and observing the production process itself. Luckily, this was the work environment MIT tailor-made its curriculum for and placed students into.

Tech men would also make notable contributions to companies with high-tech-feeling outputs like those in electronics at Bell Labs, Hewlett co-founding Hewlett-Packard (Master’s ‘36), Cecil Green (’24) co-founding Texas instruments, and Wong Tsu being the first engineer at Boeing (’16). But, crucially, MIT did not see accomplishments like those as a higher calling than working on the technically complex means of production for what felt like a simpler output, such as a porcelain rod. It is so easy to forget that anything with a high-tech process is a tech company, regardless of how low-tech the output may seem — such as paper. And these companies need extremely smart, skilled workers in the weeds of how the production process works while also being trained at a high level in useful scientific principles. These individuals enable an operation to continuously find problems and be able to solve them.

A famous example of an MIT alum showing this same style of ingenuity to make a low-tech-seeming output possible happened in the design of the famous safety razor. The Gillette company may not have been possible without MIT alum William Emery Nickerson (’76). King Gillette had the idea and the patent, but there was no practicable way to press steel in such a way to make the design workable. That is, until Gillette described the problem to Nickerson, and Nickerson, after some experimenting, figured out just the tricks (see patent images here and here).

As another example, Arthur D. Little did eventually leave his role at the paper company to do chemical analysis, quality control, and troubleshooting for more than just his one employer. But, for every Arthur Little who made a name for themself on a larger scale, there were hundreds of solid MIT workers doing that effective style of work for individual employers around the country. The continuous involvement of workers trained in scientific principles and experimentation who, daily, work with the production process at the level of a foreman or line worker is how real innovation in physical things and processes tends to happen.

MIT designed its education with the specific goal of producing engineers like those named above. And, hopefully, this section gave the reader an understanding of what their results looked like.

Now, with all of that on the table, let’s talk about the education that built these men.

Tech Men: The differentiated education

In the mid-1800s, commercial interests in Massachusetts had been yearning for an effective school of applied science that could train men for regional and local needs. Except for Rensselaer Polytechnic Institute, the other efforts in this area had proven disappointing. Examples of these disappointments include Yale’s Sheffield Scientific School and Harvard’s Lawrence Scientific School. Alexander described Harvard’s Lawrence School at the time in a way not dissimilar to how many would describe the faculty in top university technical departments today:

Lawrence’s faculty…was composed for the most part of men who lacked interest in the applications of science; their primary focus was knowledge for knowledge’s sake, reinforced by institutional cultures where the useful, the practical, the vocational, the “merely” professional, were looked down on. Study science, yes, but its practical side belonged in the trade schools. — A Widening Sphere

Rogers knew that was a remarkably poor approach. Professors who are not steeped in hands-on industrial practice could not produce the kinds of workers that were immediately useful to industry. These schools were outputting the kind of men that Edison, and many others mentioned above, did not believe were meeting the needs of industry. And the technical know-how taught in trade schools was great, but an ideal institute of technology should also impart some higher engineering and scientific knowledge to students to enable them to be more innovative, intelligent problem-solvers.

So, MIT was founded to solve this problem. This school was not designed to be a place for purely lecturing and rote learning. A smattering of intelligent men from industry and university men with an applied bent to them made up the original faculty. Content was lectured as needed, but what differentiated MIT was its innovative use of the laboratory method. Instructors taught “through actual handling of the apparatus and by working on problems, shoulder to shoulder with the boys.” And the schedule, from 9-5 (with a lunch break) 5 days a week and additional class on Saturday was meant to simulate a normal work schedule and, thus, ease the eventual transition to life in the working world.

The school had humble beginnings with simple classroom and workshop spaces. In many cases, there was only one of each kind of a certain piece of equipment in the workshop. So, for hours on end, students would ogle and comment over each others’ experiments as they waited their turns to do their experiments.

At first, the Institute only offered five majors

• Mechanical construction and engineering

• Civil and topographical engineering

• Building and architecture

• Practical and technical chemistry

• Practical geology and mining

And the students who came to study at the Institute were quite diverse for the time. Some would have otherwise studied technical subjects at a place like Harvard and others would have just gone straight to work in the New England Factories if not for the Institute.

Rogers brought sons of factory workers, laborers, blacksmiths, janitors, and hackney drivers together with upwardly mobile offspring of bank clerks and factory managers, together with heirs of vast family fortunes, privileged Brahmins whose families had built Boston from scratch. — A Widening Sphere

Some of these great Boston families, often made up of largely Harvard-educated men, were sending their children to MIT because they had grown concerned about the relevance of Harvard’s curriculum in this period of rapid industrialization.

Even the ads and flyers advertising the school made no efforts to pretend this was some kind of university. They were proud of advertising it for what it was.

Some…had heard about the school from friends or family; a few had seen ads in the local papers announcing a four month course in ‘Mathematics, with practice in Geometric Drawing, and Shading in India Ink — Lessons in Descriptive Geometry, illustrated by a suite of models in relief. Physics, including elementary doctrine of Forces, and Mechanical properties of Solids and Fluids, accompanied by Manipulations. Chemistry of the Inorganic Elements, with Manipulations. Practice in the use of the Plane Table, Level, and Geodesic Circle. Free Hand Sketching. The French Language (necessary to read technical journals of the time).’ These men were practical fellows in search of a curriculum more useful, more marketable, than what Harvard had to offer. — A Widening Sphere

Boston Tech was not a place for those who considered science and technology on a lower order of learning than Latin, Greek, or history. And the math here was learned for entirely practical purposes.

The coming decades would see some slight changes to the mission based on who the president was and the funding situation, but throughout the first 70 years of the Institute, the President and most of the faculty remained quite attached to the primary goal of the Institute being: the education of men that were extremely useful to modern industry, whatever modern meant at the time. In William Barton Roger’s farewell speech to the Institute in 1882, in which he planned to pass on the Presidency to Francis Walker, he noted, “Formerly a wide separation existed between theory and practice; now in every fabric that is made, in every structure that is reared, they are closely united into one interlocking system — the practical is based upon the scientific, and the scientific is solidly built upon the practical.” He died while giving this speech, but his vision successfully lived on.

‘Not a place for boys to play’

Under new management, the Tech men continued to work hard. Tech’s schedule worked students significantly harder than the liberal arts colleges of the day. Even after the 9-5 work schedule — which often involved not just large amounts of time spent in the classroom, but substantial time spent doing physical labor to learn the skills of their trade in the workshops — students would then spend most of the night preparing for the next day’s workshops and coursework. As one said, “Men go to Tech not to have their alma mater seal them gentleman, but to make them workers.” F. Parker Emery, who had taught both at Tech and later at Dartmouth said that Tech men worked twice as hard as Dartmouth men and admiringly said of Tech’s high standards that it operated on the “law of the survival of the fittest.”

When alumni were surveyed in the late 1800s, they deemed themselves thankful for this tough but effective training. Boston newspapers would continually drag the institution as a place that worked students to an unhealthy level. To one of these articles, written in 1890, President Francis Walker retorted, “The Institute of Technology is not a place for boys to play, but for men to work.”

President after president proudly fended off sports that would be all-consuming to students such as football. If any student wrote asking about such things, the presidents would kindly inform them that MIT was not the place for students harboring dreams of top athletics. There just should not be time or energy for such things, not if students were working hard.

The Institute made a habit of purchasing as much industrial and laboratory equipment as they reasonably could to allow the students to train in conditions as similar to industry as possible. Additionally, MIT would make a habit of keeping an irregularly large proportion of its instructors as part-time instructors who, during the day, held jobs in industry — and were quite intelligent. This seemed to just be common sense given the goal of the Institute. In addition, the Institute encouraged its full-time faculty to spend a fair amount of time contracting with industry to keep abreast of the current best practices and trends so they could teach the students as effectively as possible.

While the Institute was only growing slowly in the early decades, it was clear that its alumni were meeting the needs of industry and more. As students began to graduate and gain industry experience, the Institute began to bring on high numbers of its best alumni as instructors. Many outsiders felt that this betrayed a bit of an internal bias, but the Tech alums thought this just made sense. The Institute had a unique curriculum. In their eyes, Tech alums proving themselves to be the best applicants to teach it was just a sign of the education working.

Working upward, reaching downward

Tech was always looking to do more research, but, in the early decades, this priority often fell by the wayside as resources were extremely limited and the top priority was always educating students. But, around 1900, Tech began to take more substantial steps in this direction with the opening of three successful labs. (I’ll speak more on the research functions of all of these labs in the next piece.) The educational component of these applied labs was quite important in the Institute’s eyes to optimally educate the students to be the level of problem solvers the Institute hoped to produce. One of these labs was the School of Engineering Research which was established to allow advanced students a place to work, experiment, develop ideas, and possibly publish in engineering-related disciplines. And while the Eng.D., a doctorate in engineering, would be offered, the focus was to be on the research and not the credentials. (This particular lab would end up shutting down due to staffing constraints, but the Institute would successfully offer learning opportunities like this to students in the coming years.)

Meanwhile, tech was also doubling down on its mission of professional/practical usefulness. The goal was for the Institute to begin to “work upward” towards some kind of research excellence, in its own way, and to simultaneously do work that “reached down” to serve the needs of “men who stand between the unskilled worker and the engineer.”

In the same time period in which President Pritchett was pushing for the creation of these labs, Tech professors would also often be expected to teach night lessons to local tradesmen on industrial design and practical mechanics. The Tech professors, finishing up their workday, would meet the tradesmen, who had just finished their workday, for an evening of lectures, recitations, and lab experiments. As Alexander wrote:

The students, all men, came from service jobs in industry. From motormen to machinists, electrical workers to draftsmen, they ranged in age from teenagers to fifty-somethings. The teaching staff, also coming off a full day’s work, got extra pay for staying on at night. Many were less interested in the income than in the notion that this would benefit the community and that it would keep them abreast of changing conditions in local industry. Pritchett viewed the program as an affirmation of Tech’s hands-on tradition. — A Widening Sphere

Individual MIT Presidents each had their own new ideas about how to best build symbiotic ties with industry and train the students. President Maclaurin, who succeeded Pritchett in 1909, began a program in chemical engineering intended to link the curriculum directly with industry. Students were assigned to different ‘stations’, usually a company plant or factory, to gain hands-on experience in various processes and production methods. Various local companies allowed the students hands-on experience in processes such as: paper manufacture with the Easter Manufacturing Co., electrochemistry with the Carborundum Co., high-temperature processes with New England Gas & Coke Co., dyes with American Synthetic Color Co., and grinding and crushing processes with Atlas Portland Cement Co. In the following years, a similar program in electrical engineering was set up in partnership with General Electric. An industrial biology option was also later added.

The solidifying reputation of the Institute

Around the time when President Maclaurin took over, it was becoming clear that MIT had built something special — to New Englanders as well as those in other regions.

Upon taking office in 1909, Maclaurin compiled a record of the Institute’s role in national, state, and municipal development. The list included nearly a hundred items such as: power transmission, telephone technology, locomotive efficiency, control of steel and iron corrosion, recovery and disposal of industrial waste, reinforced concrete, fire-resistance, synthetic rubber, sewage management, traffic control, and more. With this list, Maclaurin was able to convince the state to quadruple the size of the yearly grant. And this was an impressive feat given that previous presidents had often failed to get extensions to previous grants or increases in size.

And other regions saw the value of MIT as well. When they heard MIT was pleading for a larger tract of land in 1911, other regions were willing to bend over backwards to attract the Institute to leave Boston. They believed MIT would likely bring with it substantial improvements to their regional industrial capacity. Springfield, Massachusetts offered a free 30-acre tract of land for the Institute and a merger between Worcester Poly and Tech — with extremely favorable terms for Tech. The Chicago Evening Post, the local paper of the industrial powerhouse that was Chicago in that era, ridiculed Boston for not appreciating what it had: “We could support a ‘Boston Tech’ with our loose change, and we wouldn’t, like some cities we know of, have to search all the hinterland roundabout to find the money.” They couldn’t believe that an obvious industrial force-multiplier like Tech had to grovel the state for small amounts of money every few years.

The money eventually did come, mostly from Coleman DuPont. Some raised concerns that the patch of land the school chose was of poor quality and that the new buildings might sink into the soil. That was the main reason that many had overlooked that particular piece of land for years. Maclaurin understood these concerns but was largely unconcerned. He was a proud father of the Institute and its outputs. These were the kinds of technical problems that Tech trained men to figure out and overcome. It would be fine.

(To this day, the Institute’s buildings, to my knowledge, have not sunken into the ground)

The start of Tech’s military ties

Around this time, the military also began to appreciate the extreme applicability and effectiveness of the MIT curriculum. Prior to this point, the military academies had possibly the best practical technical education that could be found. But during World War I it became clear that MIT was now head and shoulders above the military academies in many areas. After a conversation with President Woodrow Wilson in which Maclaurin had shared his theories about modern warfare being 90% engineering, he had piqued Washington’s interest in the Institute as having strategic military value.

Maclaurin’s theory intrigued Wilson’s Secretary of War Newton Baker, who appointed a board to survey the Institute’s course offerings and to assess what the military branches might gain from them. The board’s report, issued in March 1917, called MIT’s resources in several areas — civil, sanitary, mechanical, electrical, chemical, and engineering administration — remarkably impressive, far better than those in the military academies. In addition to recommending that members of the Reserve Officer Crops be required to take MIT courses whenever possible, the report also urged the Institute to devise additional courses of a shorter, more specialized type — the chemistry of explosives, for example — which officers could be assigned to register for on a limited basis

When war was officially declared on Germany in 1917, Maclaurin was eager to ensure the Institute did as much as it could to serve the nation. MIT committed buildings, personnel, equipment, and other resources to the government. “The campus shifted from civilian to military purposes overnight.” Buildings and offices turned into makeshift barracks. Special schools of aeronautics, naval aviation, engineers and navigational officers in the merchant marine, naval architecture, sanitation workers, and more servicing as many as 300 students at a time. Many professors, being quite effective engineers themselves, were sent out to run complex engineering field assignments. These were common assignments for the civil engineering and sanitary engineering professors who proved very useful to the military in these roles. The school’s labs and professors were enlisted for research work as well (more of which will be covered in the next piece).

The army seemed quite happy with this relationship. They would continue to enlist Maclaurin for other services for years, such as setting up a bigger Student Army Training Corp since he had done such a fantastic job with the services on MIT’s campus. And they would double down on their intensive partnership with the Institute when World War II came around.

Evolving to stay useful

MIT always strove to meet contemporary industrial needs, so its curriculum expanded to serve new industries. By the end of the 1800s, the number of majors had expanded from the original five to also include electrical engineering, sanitary engineering, naval architecture, chemical engineering, geology, biology, and physics. And, it should be noted, that MIT’s biology major was not exactly what many readers would associate with a modern biology curriculum. The major consisted heavily of sanitary science, bacteriology, epidemiology, and industrial biology. Sewage disposal, air and water quality, plant and human diseases, food preservation, and fermentation were some topics of major importance.

New majors would often branch off from the common combination of two existing majors if it became clear that they were extremely complementary. President Walker demonstrated impressive foresight in the late 1880s, in creating the sanitary engineering major, when he noticed, “the increasing necessity for co-operation between the engineer, the chemist, and the biologist, in dealing with questions affecting public health.” Similarly, chemical engineering grew out of the chemistry major. Chemistry, initially, consisted of an organic and industrial track. The second track eventually broke off to become chemical engineering to satisfy the exploding demand for graduates with specialized knowledge in and experience with fuels, lubricants, dyes, textiles, metallurgy, fertilizers, and other industrial lines.

This evolution happened quite continually. In the 1920s, the mechanical engineering department strengthened its automotive and engine-related programs, civil engineering introduced coursework in aerial mapping, biology would develop a sub-track called industrial biology that had a heavy focus on food technology, EE shifted resources towards communications such as radio and telephones, a major in building construction was added — and the list goes on.

Why Tech rejected proposed Harvard mergers

I’d be remiss if I didn’t say something in this article about Harvard’s constant efforts to merge with MIT in the early years of the Institute, since it says a lot about Tech’s culture. These mergers were something that the most ardent supporters of Tech’s mission among Tech alumni, students, and faculty felt very strongly about. And that strong feeling was often, ‘Absolutely not!’ Tech Presidents were always expected to hear out these merger offers, as Tech was quite poor and always in need of funds and space which Harvard did have. And the Presidents were on one or two occasions quite enthusiastic about the idea because they understood all too well just how dire MIT’s financial situation was. But the ardent students, alumni, and faculty were never so enthused. They did not trust Harvard. And culturally, it was just different.

Pritchett, while by many accounts a great President, was eventually run out of office. His cardinal sin: seeming a little too open to Harvard’s courting of a merger. Also, many did not like his propensity to compare how Tech did things with how Harvard or Yale did things. His attempts to tinker with Tech terminology, such as referring to workshops as laboratories, were not viewed as in line with Tech culture. Students were proud of workshops as places where they went to learn the parts of their future professions that required getting their hands dirty. A place, as Alexander referred to it, “where for decades students had proudly carried out grubby functions in grubby settings.” One student mockingly wrote in 1902:

A fellow used to walk through the mud of the alley into the shops, then jump into his overalls, and start to work like a man. Now he must promenade through the avenue into the ‘laboratories,’ clothe himself in a protective raiment, and practice the mechanic arts. — A Widening Sphere

Tech men were proud of what Tech was. They’d chosen this. They were starting to feel they had a President who would rather be something else.

They understood why Harvard wanted them. Harvard, a place that prided itself on its excellence, had a school of applied science and engineering just across town that was likely better than they were. Why not try to merge forces?

And the Tech men were likely right to have their concerns. The schools had very different approaches on how faculty should be spending their time, for one. At one point, the schools ran a (brief) joint experiment by allowing students in certain majors to obtain a joint degree from the two schools. Alexander wrote:

Lowell [the Harvard President] insisted that leaves be granted for recreation, study, or book writing only, while Maclaurin [the MIT President] argued that Tech’s policy — allowing a faculty member to consult for industry, teach somewhere else, work in a laboratory overseas, conduct experiments, get involved in whatever would keep him abreast of developments in his field — made more sense from the engineering educator’s perspective.

The schools also had very different ideas about how to manage students. Lowell fussed about the dangers of sending students out to do field work as he was concerned about the safety of his students. Maclaurin retorted that all would be well, “provided our men do not play the fool.”

If the schools would have merged, it is very likely that the MIT side’s fears of ending up as a richer Institute with more floor space, but with traditional academic masters who did not grasp the culture of their school would be realized. MIT served its mission above all else. When the decision came up in 1927 on whether or not MIT should allow students to have a Flying Club, despite the obvious dangers of students flying dangerous aircraft, the Institute allowed it. President Stratton wrote:

Aviation is growing by leaps and bounds; fatal accidents do not check its progress in the slightest degree, any more than the enormous loss of life on account of automobiles has checked the growth of that industry.

This is just how MIT was.

The need for a new, early-era MIT

It seems clear, given MIT’s transition to a more university style of education, that we are left with a hole. We do not have an elite hybrid technical school/applied research institute like this that can draw top talent away from places like Harvard and Stanford to its more hands-on style of education. But, as a country where the manufacturing sector is shrinking (and median wages aren’t doing so well either), we may need a new MIT now more than ever.

There are plenty of individuals at top schools who could be swayed to attend a place like this. Speaking for Stanford, where I went to undergrad, there was a large population of people who majored in mechanical engineering and were disenchanted because they did almost exclusively problem set work and very little building of anything real. And I knew even more people majoring in other subjects who abandoned mechanical engineering and majors like it for this reason! “We’re training you to be mechanical engineering managers, not traditional mechanical engineers,” was a common line used in the department. And, while that is a fine goal for a program, it is not what many of the students seem to want. What if I just want to be a top-flight regular engineer who can build awesome stuff?

An institute that trains and applies top minds to truly technical work could be an invaluable way to reallocate this underutilized talent pool. Dan Wang’s fantastic piece, How Technology Grows, outlines just how hard it is to innovate when you are not involved with the production process.

Both the design process and production process generate useful information, and dislocation makes it difficult for that information to circulate. I think we tend to discount how much knowledge we can gain in the course of production, as well as how it should feed back into the design process…

…I think that the weakness of the US industrial robotics sector is instructive. The US has little position in making high-end precision manufacturing equipment. When it comes to factory automation systems, machine tools, robot arms, and other types of production machinery, the most advanced suppliers are in Japan, Germany, and Switzerland. I think the reason that the US has little position can be tied directly to the departure of firms from so many segments of manufacturing. How do engineers work on the design of automation systems if they don’t have exposure to industrial processes?

A quote from the article: “A report to President Barack Obama on advanced manufacturing, prepared by his council of science advisers in 2012, concluded that the ‘hard truth’ was that the U.S. lagged other rich nations on manufacturing innovation.”

I don’t see enough Americans being troubled by the idea that America isn’t making advanced industrial robots. It might be fine to think that robots will be doing all the manufacturing work in the future; but someone has to build these robots, and own the IP of advanced robot making, and for the most part, that someone is not the US. It can’t be an accident that the countries with the healthiest communities of engineering practice are also in the lead in designing tools for the sector. They’re able to embed knowledge into new tools, because they continue to generate process knowledge.

And Wang’s point is made even stronger given how weak the US is in this area despite its massive allocation of capital to academic AI research. The work that Wang describes is exactly the kind of work that early-era MIT trained students to do at a high level. (I will talk more about how MIT’s transition to its current form happened in the third piece in this series.)

Major universities will most likely not be willing to entirely revamp their curriculum, faculty, and equipment to implement an early-era MIT-type environment. Even if they wanted to, there are likely too many internal entrenched interests and too much administrative inertia to make such a transition workable. But, I see little reason that one of two things could not be possible:

1. A large, possibly-elite university can start an adjacent institute dedicated to the principles of early-era MIT

2. A high-net-worth individual who has some cultural sway with young people, a Peter Thiel type, can either start their own modern-era MIT from scratch or buy out an existing trade school and attempts to turn it into one.

MIT was once a startup, experimental school with meager resources and few students. In the beginning, an incoming class at MIT was only about 15 people and offered only five majors. And it did some of its most impressive educational work in these early decades! There’s no reason a modern-day William Barton Rogers could not do this again. Building a place for these hyper-intelligent true builders to let their skills and curiosity for physical things shine could prove remarkably productive for US industrial progress.

An enterprising individual or university could identify which areas of manufacturing the US has managed to keep intact and which areas are likely to grow in the coming decade. Then, they could identify a handful of majors in which a hands-on technical education + training in the right scientific principles could optimally serve that industry. Top that off with about ten or so of the right instructors, possibly many of them part-time, to cover hands-on education as well as the science, and you have yourselves the makings of a 21st century analog of the experimental school that was MIT in the 1860s.

It wouldn’t be trivial, but in a world where everyone seems to be vexed by what do to about our manufacturing problem and difficulty innovating in large-scale industry, trying what seemed to work the last time doesn’t seem like such a bad idea. Setting up a new MIT could prove to be a shockingly fruitful experiment for what it costs.

And, at least to me, it sounds pretty fun.

Hope you enjoyed:)

The second piece in the MIT Series can be found here:

FreakTakes

A Progress Studies History of Early MIT— Part 2: An Industrial Research Powerhouse

Each piece in the MIT series can stand alone for the most part, but I’ve written them in such a way that they build off each other. So, I’d recommend reading Part 1 before this piece for optimal pleasure…

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4 years ago · 13 likes · 1 comment · Eric Gilliam

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Citation:

• Gilliam, Eric. “A Progress Studies History of Early MIT — Part 1: Training the engineers who built the country,” FreakTakes Substack. 2022. https://freaktakes.substack.com/p/a-progress-studies-history-of-early

If any of you are interesting in further discussing how to make this happen in detail and what this setup process could look like, please just DM me on Twitter and I’d be happy to discuss.

In the next piece (which will be released a day or two after this piece), I’ll be discussing how research projects at the Institute worked differently in the early decades and what made them remarkably effective.

P.S. I have freed up some time in my schedule and am looking to take on more progress studies-related work. If you’d be interested in partnering on anything, please reach out! I’m fascinated by everything related to the space and love doing applied work as well as things like writing.

I’ve been working on a series of (at least) three pieces that serve as a bit of a (short) progress studies history of MIT. This is a set of pieces that I specifically had in mind when I started this newsletter and I’m extremely excited to have the opportunity to share them with you all. The delay has been because I’ve had to work on the research stages of all three pieces at once to ensure continuity between them.

By the end of July, all three pieces will be released, with the first coming out later next week. The three pieces will largely detail:

1. The vital, differentiated training that early MIT provided its engineers

2. MIT as an applied science powerhouse in the early 1900s

3. And the beginnings of MIT’s transition from something of a research-oriented technical school to the university we know it as today

I’ll outline how each of these played a role in helping America in an era of explosive growth/building and explore what lessons we can learn from the early success and changing policies of MIT when it was a young and scrappy startup school.

For those who are eager for more content in the meantime, I’d recommend reading a piece I wrote in February, Is America’s applied and basic research really “applied” or “basic”?, my second piece for the Substack. It was written back when the substack had few followers and I believe most subscribers have not read it.

The piece was inspired by a statistic from Li et. al that many believed to be a good thing, but I took to be evidence that something may have gone awry with our research ecosystem. Namely, the likelihood of being cited in a patent for applied and basic NIH-funded research was remarkably similar, even in the short run. Many on Twitter seemed to take this as a victory for the usefulness of basic research. And, while I love basic research, I’m not sure that’s the best interpretation of that fact pattern. In the short run at least, basic research is, in many cases, supposed to underperform applied research in terms of patenting. The ROI of basic has generally been intended as something that should accrue over the long term and might not even show up very well in the data.

This statistic led me to believe that either our applied research is not so applied, our basic research is not so exploratory, or both. Dive into the piece to read more!

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Thanks so much for reading and engaging! As always, please reach out with any ideas for new pieces or questions you have for me!

If you like it, please let me know on Twitter. If not, I LOVE writing pieces that combine early 1900s scientific history and the current social science literature, so I’m also more than happy to continue doing that. 

Regardless, please feel free to DM me any feedback on what you’d like to see.

Enjoy! And please reach out to me if you’d like to talk about how anything I write about could be used in your own organization. Some readers have already been doing that and I take a lot from these conversations.

(This post is another written as a Fellow at the Good Science Project)

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Building successful entrepreneurial business ventures out of academic research is tough. And it’s not hard to understand why. There are ‘business risks’ in all new enterprises that arise from the uncertainty of building a business from scratch, finding customers, and many other things. And, in the case of companies that are spun-out from academic research, there is also ‘technical risk.’ Your research may never get to the point where it is commercializable.

Those risks are known and are a cost of doing business in cutting-edge research areas. But risks in these kinds of businesses can still be minimized. Programs have been popping up at top life science research programs that aim to do just that. In this piece, I’ll talk about a program that has been doing exceedingly well at helping researcher-founders bridge the gap between a course of research and a successful technical enterprise. The program, SPARK at Stanford Medical School, is quite straightforward and has experienced fantastic results. And, as shocking as it may be to some, the success of this program may be largely in how it treats world-class scientists not dissimilarly to how an organization like YCombinator treats its technically bright, but new to business, young founders.

The success of this program provides a concrete example of what it can mean to pass on the ‘practice of entrepreneurship’ to help scientific founders not just take the plunge, but also maximize their chances of succeeding.

The ‘idea’ of being an entrepreneur

The ‘ideas’ of innovation and entrepreneurship should not be taken for granted. To many could-be entrepreneurs, the ‘idea’ of innovation simply does not occur to them. As Anton Howes, author of the Age of Invention Substack, wrote:

The more I study the lives of British innovators, the more convinced I am that innovation is not in human nature, but is instead received. People innovate because they are inspired to do so — it is an idea that is transmitted. And when people do not innovate, it is often simply because it never occurs to them to do so.

Incentives matter too, of course. But a person needs to at least have the idea of innovation — an improving mentality — before they can choose to innovate, before they can even take the costs and benefits of innovation into account.

Matt Clancy, also a fan of Howes’ perspective, expanded on these ideas in two of his pieces. The pieces, Entrepreneurship is contagious and The ‘idea’ of being an entrepreneur, build on this concept by surveying empirical work in the area. Clancy observes that it does not just seem to be the idea of entrepreneurship occurring to a person that is important, but, also, that there are substantial effects when it is a person more similar to you. And, also, it seems that the effect is lost when you are a person who has already considered that entrepreneurship is a real possibility for you. Put differently, the idea of entrepreneurship can be most impactful to those who are capable of doing it but don’t fully realize that. And it’s even more impactful when it comes from a person similar to them.

Clancy summarizes the main pieces of evidence arising from the literature in the following way:

1. Entrepreneurs are often found in social clusters (workplaces, neighborhoods)

2. Quasi-random exposure to entrepreneurs increases the probability of becoming an entrepreneur

3. Entrepreneurial influence seems stronger when entrepreneurial peers occupy a more similar social position

4. The effect of exposure to entrepreneurs is much weaker for the people most likely to already be considering a career in entrepreneurship

This begs the question: how can we build on this? Can we use these insights to help engineer a system that produces more entrepreneurs?

The valley of death

Translational medicine is hard — hard enough that the term ‘valley of death’ has been coined to describe the massive difficulties that promising basic research findings have in making it into and out of clinical trials. One of the best ways that we can increase entrepreneurship among academics is to get people through this valley.

Many assume that the factors that contribute to these difficulties are almost exclusively scientific. However, Gehr and Garner write that many of the issues scientists run into point to a larger problem: “scientists and clinicians do not fully understand how industry works or what is needed to make their inventions attractive for further development and/or commercialization.”

Even as the NIH began putting emphasis on this area of translational research in the mid-2000s, with the establishment of the National Center for Advancing Translational Sciences (NCATS) and launching the Clinical and Translational Science Award (CTSA) program, translational research has often still felt like a wicked problem. University tech transfer offices putting more financial resources into the problem has, in many cases, been of little use. The attrition rate in the valley of death is still massive, with only about 10-20% of biomedical research projects ever progressing to human trials.

But, it’s not all bad news! Many life sciences research centers have been starting programs that attempt to help researchers overcome this problem. SPARK gives us a fantastic example of the kind of ideas we need to be transmitting to PIs to make the translational research pipeline less daunting.

What is SPARK?

Andrew Lo, Paige Omura, and Esther Kim have a fantastic, simple paper that outlines what goes into the translational research program at Stanford Medical School, SPARK, and the outcomes of the program. The program helps make the leap from researcher to technical entrepreneur feel smaller and more gradual. This process is a bit of a black box to many academics, even those who theoretically know they could be an entrepreneur. What prevents many from taking the entrepreneurial leap is a feeling of not understanding how to be an entrepreneur. The program does not just make it easier for a researcher to become an entrepreneur, but to make it through the so-called ‘valley of death’ with flying colors.

The program was started in 2006 by Dr. Daria Mochly-Rosen to help educate, mentor, connect, and partially fund Stanford scholars working on unmet clinical needs who had dreams of their work crossing the valley of death. Mochly-Rosen had just taken a leave of absence to found her own company, KAI Pharmaceuticals. While KAI was very successful, Mochley-Rosen found bridging the translational research gap to be extremely unintuitive in spite of her extensive research experience. With that in mind, she founded SPARK and began to build the program along with her co-Director, Dr. Kevin Grimes.

SPARK aims to establish partnerships between academics and experts from industry who are interested in overcoming the hurdles involved in translating academic discoveries into deployable drugs and diagnostics. Every year, a new cohort of scholars, primarily working on unmet clinical needs, is selected. To give some perspective: as of Lo et. al’s writing, 30% of projects addressed orphan diseases and 32% were related to child or maternal health issues. These are far from the easiest areas to succeed in from a business perspective, but their social good implications are obvious.

While the science is complex, the inputs that go into running the program are quite simple. As of Lo et. al’s writing, the cohort of Stanford researchers received:

• $50,000 annually for two years (a meager amount by life science’s standards)

• Access to clinicians

• Educational mentoring from SPARK-affiliated advisors

• A requirement to attend weekly Wednesday cohort meetings along with advisors

The money

Funding was distributed as project milestones were met. Once they were met, additional funds could be requested for further stages of development. And researchers were able to make these relatively modest amounts of money go a long way, having access to Stanford’s facilities and resources.

Access to clinicians

Very likely, a massive factor in the program’s success is the scholars’ access to and encouragement to speak with clinicians to better think through the clinical implications of their research. As any entrepreneur will tell you, this customer interview-like process is absolutely vital to building products that are useful to end-users. Anecdotally, it seems like this is exactly the kind of process that academic researchers taking the translational plunge often don’t fully appreciate and emphasize, possibly even de-prioritizing it to the point that it never gets done.

In SPARK, scholars learn not to work on parts of a problem just because they are the most interesting or fill the biggest hole in the literature. As Lo et. al write:

A key element of the SPARK training is teaching investigators to think using a translational approach. The scholars learn to identify the unmet clinical need of the patient and to understand the problem in tandem with product development. In other words, they are trained to ‘keep the end in mind’ throughout the process. SPARK uses project management tools such as target product profiles and project timelines to help teams plan and identify key milestones, necessary endpoints and crucial decision points.

The SPARK advisor network

The SPARK advisor network helps fill large holes in most researchers’ knowledge and networks. These advisors come from the industry-end of the translational pipeline and understand what it takes to attract follow-on investments into a course of research. Lo et. al describe the advisors:

As of 2016, SPARK had over 100 advisors with significant entrepreneurial or industry expertise in drug development, generally in a specific therapeutic area. On occasion, advisors are organized into working groups, focused on areas such as medicinal chemistry, biologics, financing and venture capital, business development and clinical trial design.

These advisors do not possess ownership rights to any inventions or IP from the program. They volunteer their time to work with SPARK projects, attend weekly meetings, and evaluate projects because of their interest in the research areas behind the projects and for the opportunity to be a part of a high-level network of industry and academic experts. In addition, mentoring also allows the advisors to deploy their knowledge to further drug development in a mission-driven environment which may be more focused on social good than many industry employers.

The weekly meetings

The final component is the Wednesday meetings. SPARK scholars are required to attend these weekly meetings which include lectures from industry experts and project updates that occur on alternating weeks. In addition to the obvious information-sharing and question-asking roles of the meeting, I’d imagine these meetings in which scholars update the group on their progress serve as a valuable accountability mechanism in making sure they keep a reasonable pace on their projects.

Analogous founder meet-up groups, in which groups of early stage founders meet regularly to update one another on their respective progress and challenges, have sprung up around Silicon Valley for exactly these reasons. Sometimes the group can answer your questions, but it is ALWAYS embarrassing to show up and tell the group that you haven’t made progress on tasks which you obviously should have made progress.

In the academic context where deadlines have become quite loose, these meetings may be a shockingly effective accountability mechanism.

Does SPARK work?

Lo et. al write in their 2017 analysis of the program:

The SPARK program has a unique and rigorous success metric. A project is deemed successful only if it enters a clinical trial, is licensed or transferred to an existing biopharmaceutical company, or leads to the founding of a new startup. In the 10 years since SPARK was founded, 74 projects have graduated from the program. Of these, 24 were licensed to startup companies, eight were licensed to existing companies, four have been transferred to industry without licenses and 31 are in clinical trials (ten without licenses). Together, this amounts to a success rate of 62%.

The SPARK scholars’ projects generated sizable follow-on grants as well. The program invested a total of $7.1 million in 74 projects and these projects generated $38.7 million in additional grant funding. SPARK projects, which largely attack areas of unmet clinical needs, are proving very attractive to investors and are surviving the valley of death with flying colors.

What SPARK failures can tell us about why the program succeeds

62% is a remarkable success rate given the high baseline attrition rate in the field. Surely, many readers will believe that this success is at least partially due to selection effects — because the success rate was far too high above baseline to not have been substantially impacted by project selection. Even if that is true, I think there is still reason to believe this program (and ones like it) can have substantial impacts, selection effects or not.

Lo et. al’s failure analysis looking at those 28 projects that were not successful provides us a lot to learn from. 6 of the 28 failed projects, 21.4%, were simply unable to obtain commercial funding, scooped by industry, or the researcher left before the program was completed. In those cases, the scholars took advisor advice, did what they needed to do operationally, and did not fail due to inability to overcome scientific obstacles. 12 of the projects, 42.9%, failed for scientific or technical reasons, such as failing to develop an acceptable drug candidate or to demonstrate benefit in preclinical models. Lastly, 10 of the projects, 35.7%, simply failed to execute.

What does ‘failure of team to execute’ mean in this context? As Lo et. al explain the category, “In these cases, the SPARK scholars became disengaged from their project, had inadequate primary investigator engagement or personal conflicts, or ignored advisor input and misused funds.”

Even amongst the minority of failures from the cohort of SPARK scholars, the reason for failure was almost as likely to be basic operational reasons as it was technical/scientific ones. This should leave one remarkably optimistic. While tackling technical and scientific obstacles can be a wicked problem, overcoming operational and networking problems is almost mundane in comparison.

The concept of providing a small amount of funding, a network of industry advisors, regular project check-ins, and access to potential customers is not a foreign model. In fact, that is generally YCombinator’s model. YC was built to help batches of young, technically skilled entrepreneurs make headway in starting a company even if they had minimal business experience, and there is little reason to think the model shouldn’t apply to professors as well.

While professors may be world-class experts in their particular fields of research, many also have little to no work experience outside of academic labs. And, when put in that light, one should not have the expectation that they should know far more about building a business than the bright young people who enter an accelerator like YCombinator. Even the brightest people need a crash course in how to do things the right way. And that is okay, because those are lessons that a program like YC has had success teaching at scale.

The concept of transmitting the idea of effective entrepreneurship should not be overlooked as a pivotal lever that can be used to overcome problems in the innovation pipeline. SPARK is just one great example of a program doing just that to overcome the famous ‘valley of death’ in translational medicine.

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Thanks for reading. Please feel free to share this piece with anyone who will find it interesting! Also, I’m very eager to start working closely with individuals running research labs/related orgs that are looking to do things a little differently. If you know anyone like that, please send them my way!

Citation:

• Gilliam, Eric. “Unpacking the ‘idea’ of entrepreneurship: A case study in successful translational medicine” FreakTakes Substack. 2022. https://freaktakes.substack.com/p/unpacking-the-idea-of-entrepreneurship

End notes

For those who are curious.

General

This piece drew heavily on Lo et. al’s analysis of SPARK, Mochly-Rosen and Grimes (the SPARK directors) short book on the program, and Gehr and Garner’s paper on the larger space of translational research programs.

Other programs like SPARK/SPARK spinoffs have been popping up at other institutions around the world. If any readers come across a similar analysis of any of these SPARK-like programs, please send them along! I’d love to do a follow-up looking at successes and difficulties in replicating the program. Replicating the winning habits of a successful organization is never easy, so I’d be very curious to do some research on how similar programs have held up.

Additonal reading on these other efforts and the area in general can be done at the following links:

• https://www.cell.com/cell/pdf/S0092-8674(16)30488-3.pdf

• https://www.nature.com/articles/519402a

• https://www.science.org/doi/full/10.1126/scitranslmed.aaa0599

Baseline success rates of translational life sciences projects

I have seen estimates in the literature that the industry standard success rate for projects like these is as low as 5% compared to SPARK’s 62%. An example can be found in the literature here and on SPARK’s website here. However, since I was not able to successfully find the source of this lower number in the literature, I chose to use the statistic stating that 10-20% of biomedical research projects never progress to human trials as the baseline statistic instead. If anyone can locate the paper that is the source of the 5% statistic, please reach out to me on twitter and I’ll update the article.

SPARK management

For those curious, Lo et. al briefly described the management and funding structure of SPARK as follows:

The SPARK program, currently led by Drs Mochly-Rosen and Grimes, operates with a management team of five individuals that oversees communications with project teams, runs its weekly meetings, oversees SPARK funds and otherwise manages operations. Although the majority of the funds for SPARK comes from the Dean’s Office, the program operates independently within Stanford University and is managed solely by the SPARK team.

Enjoy and please subscribe if you’d like to see more posts from me and the Good Science Project! Another link to this piece along with an executive summary can be found here on the Good Science Project site.

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Predictions of future economic progress from our current vantage point place major emphasis on continuing advances made possible by medical research, including the decoding of the human genome and research using stem cells. It is often assumed that medical advances have moved at a faster pace since the invention of the antibiotics in the 1930s and 1940s, the development from the 1970s of techniques of radiation and chemotherapy to fight cancer, and the advent of electronic devices such as the CT and MRI scans to improve diagnoses of many diseases. Many readers will be surprised to learn that the annual rate of improvement in life expectancy was twice as fast in the first half of the twentieth century as in the last half. — Robert Gordon, The Rise and Fall of American Growth

No other documented period in American history even comes close. In this piece, I’ll go over what caused this massive decline in mortality rate and what we should have learned from this period — but didn’t.

One major cause of death almost disappeared

This effect is well-explored in Robert Gordon’s book, The Rise and Fall of American Growth. Before around 1880, there was little to no improvement in American mortality rates or life expectancy. In 1879, male and female life expectancy at age 20 was similar to their counterparts in 1750. Infant mortality rates, around 215 per 1,000 live births in 1880, were similar to infant mortality rates dating as far back as Tudor England.

But, suddenly, things began to improve. For example, giving birth became much safer. In the figure below, for every 1,000 births, the number of lives saved by improvements from 1890 to 1950 was 188, while the number saved from 1950 to 2010 was just 21. Gordon plots this steep decline.

This reduction in infant mortality was primarily due to the reduction in infectious disease deaths. But infectious diseases were a problem for all. Gordon goes on to show a graph that demonstrates just how much of the massive improvement in mortality rates was due to reductions in deaths due to contagious diseases.

This trouncing of the infectious disease problem made society’s most dangerous medical problem almost obsolete within half a century. In 1900, 37% of deaths were caused by infectious diseases. By 1955, the number was down to less than 5%. Today, it’s down to around 2%.

What did NOT lead to this victory over infectious diseases

In the early 1970s, it was becoming clear from the mortality statistics that we were not seeing the same rate of progress that we’d grown accustomed to in recent decades.

John and Sonja McKinlay’s outstanding paper, “The Questionable Contribution of Medical Measures to the Decline of Mortality in the United States in the Twentieth Century”, attacked the common belief that the introduction of more modern medical measures such as vaccines and the expansion of the modern hospital were largely responsible for this mortality decline.

They lay out their initial reasoning:

If a disease X is disappearing primarily because of the presence of a particular intervention or service Y, then clearly Y should be left intact, or, more preferably, be expanded. Its demonstrable contribution justifies its presence. But, if it can be shown convincingly, and on commonly accepted grounds, that the major part of the decline in mortality is unrelated to medical care activities, then some commitment to social change and a reordering of priorities may ensue. For, if the disappearance of X is largely unrelated to the presence of Y, or even occurs in the absence of Y, then clearly the expansion and even the continuance of Y can be reasonably questioned. Its demonstrable ineffectiveness justifies some reappraisal of its significance and the wisdom of expanding it in its existing form.

Building on this line of logic, they go on to show a series of graphs that should put to bed any reasonable hypothesis that the modern vaccines and medicines for these contagious diseases were the primary mechanisms that saved lives. The graphs below—with their 1970s visual simplicity— are extremely effective communicators of the authors’ point. The line in each graph represents the decreasing mortality due to that disease. And, above each line, there is an arrow showing when a formal “medicine” for that disease became common.

One can argue that these medicines and vaccines were a second, useful measure in ensuring that these contagious disease rates continued to decrease longer than they may have otherwise. But it seems clear that the battle was largely won long before these medicines came along.

The authors go on to estimate that 3.5% probably represents “a reasonable upper-limit” of the total fall in the death rate that could be explained due to the medical interventions in the major infectious disease areas. And, while surely one could dispute whether the true effect was something slightly higher, the effect cannot have been substantial since so much of the work was already done by the time the treatments came around. Something that looks much less like ‘modern medical science’ had solved the problem already.

Also, it should be noted that this reduction almost entirely preceded the modern phenomenon of skyrocketing American spending on healthcare that brought advanced therapies and medicines through the hospital system.

The McKinlays show this in the graph below.

This graph ends in about 1972, but the increase in US medical spending did not. The percent of GDP spent on medical care today is around 20%.

If not medicine, then what was it?

The McKinlays work went a long way in establishing that the main cause of this improvement in mortality rates was not what people seemed to think it was: the modern medical system. Later work would go further in identifying the causes of these trends. And, based on that literature, it seems like many changes affecting public health from the early 1900s played a role. These include: the expanded use of window screens to keep disease-carrying bugs out of the home, the establishment of the FDA, horses being phased out by the internal combustion engine which left streets much more sanitary, and more.

But, based on the work of Grant Miller and David Cutler, there seems to be a single intervention that might have been almost as important as all the others combined in bringing about change: cleaner water sources. The implementation of these improved water management systems might be the most impressive work ever carried out by this country’s city governments.

The introduction of these systems directly coincided with the drop-off in mortality due to infectious diseases. The percentage of urban households, who were particularly afflicted by the infectious disease problem, with filtered water in the US was: only .3% in 1880, 6.3% in 1900, 25% in 1910, 42% in 1925, and 93% by 1940.

Cutler and Miller went on to identify all of the major cities with clear records of when water chlorination and filtration technologies became widely available. The precise year in which these technologies were built in each city was quite arbitrary because they were the result of often decades-long partisan bickering, planning delays, etc. For these 13 cities, the authors made a graph for each showing the mortality rate of typhoid fever and when the city-provided chlorination or filtration systems began reaching the majority of individuals. (as a note: these technologies are substitutes to some extent)

All 13 graphs, more or less, generally look like the following, with major drops in mortality immediately following the implementation of a clean water system.

Some of the reductions seem to begin immediately before the vertical lines, which is to be expected, because the authors drew the line to coincide not with the first year a clean-water system was implemented but, instead, the year in which it finally reached the majority of citizens.

The authors then go on to use much more robust statistical methods to estimate that clean water and filtration systems explained half of the overall reduction in mortality in the early 1900s, 75% of the decline in infant mortality, and 67% of the decline in child mortality.

And this was all comparatively cheap too. It was estimated that this whole process cost roughly $500 per life-year saved. And that’s if you assume that cities were only doing this to save lives, which was not at all the case.

The city governments did not fully understand the potential impact of these water systems prior to building them

The germ theory of disease was beginning to become more widespread, but that should not be mistaken as the primary reason this water infrastructure was undertaken when it was. As Miller and Cutler point out in a different 2004 piece:

Dirty water was believed to be causally linked to disease long before the bacteriological revolution. The first demonstration of the link between unclean water and disease was John Snow’s famous demonstration of how cholera spread from a single water pump in London in the 1850s. Snow had premonitions of the germ theory, but it took several more decades for the theory to be fully articulated.

The prevailing theory at the time, the miasma theory of disease, held that a variety of illnesses are the result of poisonous, malevolent vapors (“miasmas”) that are offensive to the smell.

The general knowledge that dirty water was likely connected to the spread of some diseases and, to some extent, could be mitigated was not new. Since ancient times, people have understood that keeping feces away from food and water was good for health. What was new, as Cutler and Miller point out, was the ability to more easily raise bonds to build infrastructure like these water systems at the turn of the century. So they built!

And, even with the germ theory of disease technically in existence, it seems clear that people were quite confused. For example, a noteworthy event that encouraged urban populations to push to adopt clean water systems was the Memphis yellow fever epidemic of 1878 which killed 10% of the city’s population. Many thought it was due to contaminated water and, naturally, this led individuals in other cities to be more eager to adopt new water infrastructure. But the Memphis yellow fever epidemic was not caused by contaminated water at all. It turns out that the Memphis epidemic was caused by mosquitos.

And, even though it was understood that cleaner water would save some number of lives from some diseases somehow, it’s clear that this need was considered a bit amorphous. The need didn’t seem as tangible in a city government committee as, say, the need for water to put out fires. In a 1940 text on public water supplies written for use by instructors in technical schools, Turneaure and Russell write:

Too often a [water] supply for a village is designed with almost exclusive reference to fire protection, and little attention is paid to the quality of the water, the people expecting to depend on wells as before.

Even as late as 1940, the priority of a water supply for many, particularly in smaller towns, was to put out fires. This is not because they irrationally feared dying in a fire far more than dying from an infectious disease. Rather, it was widely understood that these public water supplies reduced insurance rates by orders of magnitude. It was a bargain!

It was much easier to count dollars saved than hypothetical added life years. To this point, Turneaure and Russell’s text even went on to note that a clean water supply could enhance property values. Writing their text for the nation’s future engineers of these water systems, they understood that these were the data points that might sway a frugal city government to put these measures into action.

Progress can be made without understanding all of the scientific mechanisms of a disease

All things equal, of course, it is better to understand everything about how a disease works before attempting to fight it. But the war on infectious diseases shows that this is not always a necessary step. With a somewhat hazy understanding of the science, cities across the country helped engineer one of the greatest public health interventions ever.

We should be doing everything we can to achieve reductions in the mortality rate anywhere near those of the early 1900s. Compared to what happened before 1955, the progress in the decades since feels almost minuscule.

And that is not because we ran out of problems to solve. While infectious disease deaths were greatly reduced, total deaths in other disease areas often remained relatively similar or worsened. In the same period when infectious diseases fell from 37% of total deaths to less than 5%, other diseases became our new ‘major problems’. Deaths due to heart disease, cancer, and strokes grew from 7% of total deaths to 60% of total deaths. Fewer people were dying, but we still had major problems left to solve.

One area of particular emphasis has been the ‘War on Cancer.’ The vast majority of the tens of billions spent on the War on Cancer over the past 50 years have been mostly targeted at medical interventions and therapies. And, while this work has made some progress, many are quite disappointed with how little we’ve accomplished in that time. And, for those people who are not satisfied with the current rate of progress on the cancer problem, the history of how we tackled infectious diseases should serve as an inspiration! Just look at the chart below. There are ways to fight diseases outside of the traditional university lab or the hospital.

There might be equivalent public health measures that could help us make headway in eliminating current medical problems. Let’s take environmental cancer-causing agents as one example. Many in the cancer research and public health community have argued that the government should put more serious resources into the fight against environmental causes of cancer—albeit with limited success.

The war on infectious diseases might have a lot to say about how we could effectively pursue this goal. Understanding the environmental aspects of what causes cancer is not such a different problem from the infectious disease problem in the early 1900s.

Similar to how many felt about infectious diseases at the turn of the century:

• It feels like carcinogens are everywhere and are almost an inevitable presence in our lives.

• Sometimes when you come in contact with a (most likely) carcinogenic material you get cancer, but many times you don’t.

• It’s very hard to disentangle which of the many materials that make up a cancer-causing entity are the problem and which are just correlated with the problem.

Even if we only have a middling level of scientific understanding of the disease, why can’t we hope to halt these deaths from cancer due to environmental reasons?

As with all novel lines of research, there are no guarantees this would work. Obviously, these are not the exact same problems on a micro-level, but given the structural similarities, it seems that a solution that worked well on one might lend some insight to the other. We know that environmental risk factors are a major contributor to the disease. A paper in Nature by Wu et. al estimates that up to 90% of the risk factors in cancer development are due to extrinsic factors. And basic cancer researchers are increasingly embracing top-down, organicism approaches to viewing the problem as opposed to the bottom-up, reductionist, cell-focused approaches that were once more common than they are now.

With 1.75 million new cancer cases in the US every year along with 600,000 deaths, our high spending levels researching the problem are understandable. With even a modest fraction of the brainpower and resources that have gone into trying to cure cancer through the hospital, we could potentially make great strides in isolating carcinogen-creating materials and locations with a much higher level of certainty. The whole process could be inspired by the methodology of those who have been studying environmental risk factors of cancer for decades (pieces like this delve into many specific studies), but on a much larger and more thorough scale.

The government resources in this larger-scale effort could be used to compile relevant public records and datasets into one place, employ health researchers to identify strategies for flagging possibly carcinogenic materials and areas, paying for exploratory medical screening to be leveraged for further research when something is flagged as carcinogenic, and rapidly dispatching field researchers to follow up on any leads to obtain more information on the ground.

The federal government and the medical research ecosystem currently attempt efforts like this, but the conclusions are limited by lack of funds, lack of data, and limited populations to sample from. With all of these efforts scaled up and coordinated, we could possibly drastically reduce the effects of environmental cancer-causing agents. This would be expensive, but this is very possible given the resources we spend on cancer—if there’s political will.

It is also important to remember that, for legal reasons, the burden of proof required to regulate something out of existence may be more stringent than the burden of proof required to convince a scientist that something is likely carcinogenic. So, while we’d hope this proposed process would discover countless new carcinogens which we could eradicate, you could imagine the process paying for itself solely by increasing the number of known carcinogens for which we are able to compile additional evidence and eradicate through the legal/regulatory process.

My advice for those who are interested in setting a program like this in motion:

• Advice for Public Sector: More of the ~$40 billion NIH budget deserves to go to explorations inspired by the war on infectious diseases that was so decisively won. The interventions employed there were responsible for the biggest mortality rate improvement in American history. There are likely more massive wins that can follow from learning from this playbook.

• Advice for Philanthropists and New Science Funders: Exploratory, proof-of-concept research projects in this area could be an extremely high-leverage use of money. The government would likely be best suited to take over the process at some point, but they might not be optimally suited to undertake the proof-of-concept stage. If one of these funders could prove this to be a ‘winner’ and give a sense of the costs it would entail, the government might become quite interested in investing and scaling the operation.

We won the war on infectious diseases. Why can’t we do it again?

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The public has a distorted view of science because children are taught in school that science is a collection of firmly established truths. In fact, science is not a collection of truths. It is a continuing exploration of mysteries. - Freeman Dyson

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Since the last article on WW2-era German science was so well-received, I’ve decided to keep the theme of great pieces of scholarship about scientific history going. This week’s post is largely drawn from the essays of Gerard Holton. Holton’s work is, similar to the scholarship covered in the previous post, criminally under-talked about in the progress studies community. The Holton essays I talk about in this post, largely written between the early 1950s and 1970s, have lasting relevance today.1

Holton would have been best described as a scientific historian; however, as you’ll see in the modeling section of this post, his contributions go beyond that of an ordinary historian. The application of his physicist’s mind and toolkit to the problem of scientific innovation was incredible. Nowadays, we might consider him a social scientist who studied science itself, an early progress studies scholar. And a great one.

In this post I’ll go over:

1. Holton’s thoughts on why it was VITAL that we establish a science of progress, which he called S₁

2. Holton’s assumptions under which ideas get harder to find vs. easier to find over time

3. And how we may have built a world where ideas are now becoming harder to find; also, why new science orgs should be investing in ‘branch-finding’ to try to help regain our once-explosive idea-finding productivity

S₁: The Science of Progress

Princeton physicist, H.D. Smyth, said at the time of Holton’s writing, “We have a paradox in the method of science. The research man may often think and work like an artist, but he has to talk like a bookkeeper, in terms of facts, figures, and logical sequence of thought.” And while this staid, accountant-like language helps in communicating public findings and settling scientific disputes, it is not helpful in the study of progress itself.

Holton noted:

Most of the publications are fairly straightforward reconstructions, implying a story of step-by-step progress along fairly logical chains, with simple interplays between experiment, theory, and inherited concepts. Significantly, however, this is not true precisely of some of the most profound and most seminal work. There we are more likely to see plainly the illogical, nonlinear, and therefore “irrational” elements that are juxtaposed to the logical nature of the concepts themselves. Cases abound that give evidence of the role of “unscientific” preconceptions, passionate motivations, varieties of temperament, intuitive leaps, serendipity or sheer bad luck, not to speak of the incredible tenacity with which certain ideas have been held despite the fact that they conflicted with the plain experimental evidence, or the neglect of theories that would have quickly solved an experimental puzzle. None of these elements fit in with the conventional model of the scientist; they seem unlikely to yield to rational study; and yet they play a part in scientific work.

He was acutely aware of the overwhelming evidence that all too often, “there is no regular procedure, no logical system of discovery, no simple, continuous development. The process of discovery has been as varied as the temperament of the scientists.” Oftentimes, the chaotic nature in which scientists succeeded and failed was shocking. Some of the most important scientific contributions were built upon bad experiments, incorrect hypotheses, misinterpretations of data, etc. Some simple experiments yielded massive discoveries and some very expensive experiments yielded nothing. An extreme example that Holton cites was John Dalton, whose atomic theory was built on FOUR fundamentally incorrect assumptions but still revolutionized our understanding of the makeup of the chemical world.

A science of progress felt daunting, but Holton believed it was extremely worth doing. He believed that the study of the messy personal context of discoveries could soon come into its own as a full-fledged field. He understood that the basis of a field being the unstructured testimonies of scientists was frightening off investigators rather than attracting them. Nevertheless, he believed this area of scholarship would soon become a central part of scientific studies because it could grow the field of science with its learnings. So, he opted to embrace the mess.

In taking this prescient step, he drew a key distinction. He believed that we should be much more clear in communicating exactly what we mean when we use the term “science.” He writes in the introduction to a book in 1952:

The dilemma is resolved...by distinguishing two very different activities, both denoted by the same word, “science”: the first level of meaning refers to private science (let us term it S₁), the science-in-the-making, with its own vocabulary and modes of progress as suggested by the conditions of discovery. And the second level of meaning refers to the public science (S₂), science-as-an-institution, textbook science, our inherited world of clear concepts and disciplined formulations. S₁ refers to the speculative, creative element, the continual flow of contributions by separate individuals, each working on his own task by his own, usually unexamined methods, motivated in his own way, and uninterested in attending to the long-range philosophical problems of science. S₂, in contrast, is science as the evolving compromise, as the growing network synthesized from these individual contributions by the general acceptance of those ideas which do indeed prove meaningful and useful to generations of scientists. The cold tables of physical and chemical constants, the bare equations in textbooks, for them hard core, the residue distilled from individual triumphs of insight, checked and cross-checked by the multiple testimony of general experience.

He later wrote:

A very different set of rules holds in S₁ than in S₂. I do not doubt that solid knowledge about S₁ can be achieved. A science of S₁ must be possible. Though scientists themselves may for a time frown on such an enterprise, one may take comfort that the best of them—for example Einstein and Bohr, as demonstrated in these pages—would not.

Holton believed that S₂’s strong commitment to statements that can be categorized as 1) empirical matters of fact—which usually boil down to physical measurements—and 2) statements concerning logic and mathematics was a major reason that science had grown so rapidly since the 1600s. Limiting most public scientific statements to these areas helped scientists be sure that they were communicating their hypotheses extremely clearly. This minimized the amount of time spent on dealing with the ambiguity of statements and, instead, let the scientists focus on publicly verifying or falsifying statements. In all, he believes this propensity towards S₂ helped “forge a wonderfully strong and successful profession.”

When philosopher and mathematician Alfred North Whitehead said, “Science can find no individual enjoyment in Nature; science can find no aim in Nature; science can find no creativity in Nature,” Holton believed he surely must be referring to the “stable” aspect of science, S₂, and not S₁.

Even the generation of hypotheses, which scientists then use the scientific method to rigorously test, is often quite unscientific. “The process of building up an actual scientific theory requires explicit or implicit decisions, such as the adoption of certain hypotheses and criteria of preselection that are not at all scientifically ‘valid’ in the sense previously given [in the scientific method] and usually accepted.”

A prominent example is that, in the writings and accounts of many great scientists, it is very clear that they saw their scientific explorations as a way to prove the existence of God and find his fingerprints in the natural world. Kepler believed this to an extreme extent, having initially planned to enter the clergy but later becoming a scientist. He believed science was an equally valid path to understanding God’s work. Descartes makes clear in his own formulation of the Law of Conservation of Momentum that the law springs from the invariability of God. Galileo saw the laws of nature as proofs of the Deity equivalent to the Scriptures. Newton once wrote in a letter, “When I wrote my treatise [Principia] about our system, I had an eye upon such principles as might work with considering men for the belief of a Deity; and nothing can rejoice me more than to find it useful for that purpose.” And in each of Einstein’s three great papers of 1905, which are written in quite different areas of physics, the common thread is that each helps fix asymmetries or incongruities of a “predominantly aesthetic nature.” ‘God probably wouldn’t have done it like that,’ was the ethos.

Scientists have since replaced the use of ‘God’ with something like ‘Mother Nature.’ Maybe that hasn’t changed much in the way we go about science. Or, maybe it leaves us much more liable to accept ugly equilibria and asymmetries when we view the creator as a ‘tinkerer’ rather than an ‘intelligent creator.’ Examining the effect of this change on science seems like an excellent question for modern scholars of progress. For now, I hope this passage establishes the importance of S₁ and highlights just how prescient Holton was in publishing these thoughts as early as 1952, almost 70 years before Tyler Cowen and Patrick Collison wrote their famous Atlantic article calling for a ‘new science of progress.’

And Holton’s writing went far beyond the mere accounting of historical accidents and anecdotes. He even attempted to model a question that still vexes modern scholars of innovation, “When do ideas become easier to find?”

The model is quite eye-opening.

When do ideas get easier to find?

The apparent decrease in the productivity of scientific research is much talked about by innovation scholars. The most famous piece of scholarship is Bloom et al.’s Are Ideas Getting Harder to Find? which outlines the substantial decline in research productivity across numerous fields in recent decades.

(I briefly go over pieces of the paper in this post and Matt Clancy does a much more thorough job here)

When people hypothesize about what is causing this decline, they tend to credit the so-called ‘burden of knowledge’ as being responsible. The belief is, in essence, that as fields become more and more complicated, it takes longer to become expert in them and harder to discover new ideas in the field. And, when looked at this way, many feel like diminishing returns to research productivity are natural.

But Holton’s models, from 1962, of what assumptions lead to rising vs. falling research productivity make it clear that there are clear steps we can take to try to increase research productivity. We are currently doing the opposite of these steps in many cases. For those who believe that falling research productivity is somewhat ‘inevitable’, I hope this section opens your mind up to the possibility that this problem might have been ‘man-made’ by flawed incentives.

Holton’s “Zeroeth-Order” Approximation

Holton set out to sketch a rough model for the growth of research ideas in science. He knew that the model would not tell us everything about “how science works,” but that it would help explain some of the more marvelous aspects of scientific growth. And, so, he began with a zeroeth-order approximation that he knew to be inadequate from the beginning. But he felt it would be useful to improve upon to attain a more accurate, first-order, approximation later on.

He uses the analogy of a voyage of discovery to describe the research enterprise. On average, a single voyager will expect the number of new islands they discover to increase more or less linearly in proportion to their time spent exploring. The same will be true if there are multiple ships exploring, but not so many that they are in contact with each other or overlap with each other ships’ search patterns. So, the number of unknown islands that remain to be found in a finite ocean—the number of interesting ideas—will be expected to linearly drop off over time because every island that is found is one less island left for another explorer to find.

As more and more islands are found, more voyagers will begin to set off on explorations because interest in these types of explorations will be growing. This increase in participation will guarantee that the decrease in islands left to be found decreases more exponentially than linearly. This exponential decrease in islands left to be found is due not just to the increasing competition, but also due to the increasingly overlapping community of voyagers sharing tips and tricks on how to better find new islands.

Eventually, with the number of explorers growing, the domain knowledge of each explorer ever-increasing, and the number of islands left to be found decreasing, the field will become less attractive and the number of explorers will diminish.

The graphs below visualize pieces of Holton’s zeroeth-order approximation:

• (a) Visualizes I: the linear decrease in ideas to be found over time when there are few enough researchers that they are not encroaching on each other’s territory or sharing ideas

• (b) Visualizes P: the number of people who crowd into a field as it gets hot and leave as it gets too crowded and the number of ideas left to find diminishes

• (c) Visualizes I’: the interesting ideas that are left over time as researchers begin to crowd each other out and share ideas

This approximation obviously does not explain why science as a whole increases its scope over time rather than deteriorating. That will be accounted for in the first-order approximation. Holton writes:

Nevertheless, we already recognize that for some specific and limited fields of science this model is useful. Thus in 1820 Oersted’s discovery of the magnetic field around wires that carry direct current, and the theoretical treatments of the effect by Biot, Savart, and Ampére in the same year, sparked a rapidly rising number of investigations of that effect; but it was not long before interest decreased, and by the time of Maxwell’s treatise (1873) no further fundamental contributions from this direction were being obtained or even sought.

The following graph further applies all of the above ideas into one graph with the addition of curve A, the number of ideas known and applied, which mostly mirrors line I'—which tracks the number of ideas left to discover.2

This concept of a curve A is further developed in the first-order approximation.

This zeroeth-order model makes clear that, under its assumptions, one would expect ideas to get harder to find over time. However, there are some key behaviors it does not account for.

Holton’s First-Order Approximation

Holton goes on to build a first-order approximation to model the growth of scientific ideas, iterating on the model above. He wanted this first-order approximation to account for how research ideas and fields grow and branch off of one another, which the zeroeth-order model did not account for.

Examples of this key behavior include two figures he shared which will most likely be illegible to the reader, but should still give you a sense of the expansion and branching he was talking about. The first graphic attempts to show how just a small subset of fields in math, physics, chemistry, and aerodynamics arose from more general lines of research in the early 1900s.

The graphic is obviously far from exhaustive, but it should paint a pretty clear picture of how fields of science organically develop from each other’s explorations.

He then goes on to paint a much more fine-grained picture of this phenomenon by showing the massive branching out of new fields of physics related to molecular beams, magnetic resonance, and other work that was spawned by I. I. Rabi’s work in developing the original molecular beam techniques—represented by the black box at the bottom which begins to branch upwards—and stimulating a group of productive colleagues and students to explore these problems further.

Just some of the names in those tiny boxes include key work by the likes of:

• Niels Bohr

• Richard Feynman

• Freeman Dyson

• Shinichiro Tomonaga

• Julian Schwinger

• Otto Hahn

• Emilio Segré

• Otto Frisch

• Eugene Wigner

While this expansive tree is a case of science growing at an ideal rate, the reader can picture the more modest branching that a modest tree would exhibit as well. It was this fundamental, branching aspect of science that Holton set out to incorporate into his first-order model.

He begins with Figure A, where the curve D, the number of basic ideas published in an area, is simply the mirror of the curve I', the number of ideas left in a field to be published. This image should be familiar from the above zeroeth-order approximation.

Holton then extends on this concept of a single, independent curve D with a decreasing slope. Instead, he begins to explain how D can be the starting point for a branching process of discovery.

The beginning of curve D indicates necessarily the occasion that launched the expeditions in this field, say the discovery in 1934 of artificial radioactivity by Joliot-Curies while they were studying the effect of alpha particles from polonium on the nuclei of light elements.

Up to this point their research had followed an older line, originating in Rutherford’s observation in 1919 of the transmutation of nitrogen nuclei during alpha-particle bombardment. The new Joliot-Curie observation, however, inaugurated a brilliant new branch of discovery. We suddenly see that the previous model [the zeroeth-order approximation] was fatally incomplete because it postulated an exhaustible fund of ideas, a limited ocean with a definite number of islands. On further exploration, we now note that an island may turn out to be a peninsula connected to a larger land mass. Thus in 1895 Röntgen seemed to have exhausted all the major aspects of X-rays, but in 1912 the discovery of X-ray diffraction in crystals by von Laue, Friedrich, and Knipping transformed two separate fields, those of X-rays and of crystollography. Moseley in 1913 made another qualitative change by showing where to look for the explanation of X-ray spectra in terms of atomic structure, and so forth. Similarly, the Joliot-Curie findings gave rise to work that had one branching point with Fermi, another with Hahn and Strassmann. Each major line of research given by line D in Figure A [below] is really a part of a series D₁, D₂, D₃, etc. as in Figure B. Thus the growth of scientific research proceeds by the escalation of knowledge—or perhaps rather new areas of ignorance—instead of by mere accumulation.

Holton goes on to explain that when an important insight or some chance discovery causes some new branch line, D₂, to be created and branch off, fruitful research does still continue on the old branch line, D₁. But many researchers, including an inordinate number of the more original ones, will transfer to D₂. And in this new branch they will apply their original minds as well as whatever applicable experience they acquired working on D₁.

These new, exciting branches often tend to experience inordinate growth, draw a disproportionate number of graduate students, and, hopefully, this group will continue to make discoveries that create further new branches that they or their graduate students can transfer to.

And, to prove this is not all theoretical, Holton shares a graph showing the exponential growth in the energy of particle accelerators in the mid-1900s, along with the branches of research underlying this growth. Each of these technologies, from DC generators through proton synchrotrons, contributed to this constant exponential growth that was entirely the result of the continual branching of curves D₂, D₃, etc.

Particle accelerators are a case of research in which, aided by groups of researchers both sharing information but also working in locations some distance from one another, researchers were able to do more than march along building on each others’ insights, they were able to leapfrog each other.

One research team will be busy elaborating and implementing an idea—usually that of one member of the group, as was the case with each of the early accelerators—and then will work to exploit it fully. This is likely to take from two to five years. In the meantime, another group can look, so to speak, over the heads of the first, who are bent to their task, and see beyond them an opportunity for its own activity. Building on what is already known from the yet incompletely exploited work of the first group, the second hurdles the first and establishes itself in new territory.

Holton was writing this at the end of a bit of a golden-age of basic research where many new areas had been spawned and experienced explosive growth and branching. Accelerators were not a particularly unique case of explosive scientific productivity at the time. What was unique about accelerators was that progress was easy to measure and the data were readily available. He saw this first-order model as a qualitative one that effectively modeled the growth in the depth of knowledge of many types of theoretical and experimental ideas that resisted quantification. Particle accelerators were simply a case where the ‘depth of knowledge’ lent itself to easy quantification.

Another interesting detail to take note of is just how quickly the rate of progress curtailed for most of the individual accelerator branches in the graphic above. And there’s a lesson to be learned here: the slowing rate of progress for the individual curves did not matter much at all. While it was all too common for a single branch to rapidly curtail in research productivity, almost all new branches had explosive growth in their early stages. So, as long as new branches were being created frequently, growth was explosive.

Holton did point out that the single assumption that was vital in making his first-order approximation more accurate than his zeroeth-order approximation was that researchers were willing and able to learn from each others’ research from various areas and begin building off of it. To him, that was how branch-making thrived.

At the time, teams of interdisciplinary basic researchers were one vital way of enabling this ongoing learning process across fields. He may have taken for granted that this would obviously be the direction in which science would continue to go. It’s easy to see why. He was writing in the aftermath of the smashing success of large labs and projects that married physicists, chemists, mathematicians, electronics engineers, and many others into the same spaces and on the same teams. These labs and projects included the Cavendish Laboratory, E.O. Lawrence’s lab at Berkeley, the Manhattan Project, the MIT Rad Lab, the Harvard Radar Countermeasures Laboratory, and others. Even when these researchers didn’t publish together, they would work closely together day-to-day and discuss each other’s problems. These new branches continually came from the greats in their respective fields working on and discussing the problems of other fields with great researchers from that field. To get a clear idea of just how prolific these combinations could be in spawning new branches, please visit my John von Neumann piece to experience just how many branches one great mind could create working in this way.

And, if two fields felt too far apart for a pair of researchers to understand each other, the presence—and often friendship— of researchers from intermediate fields usually smoothed this process. As Holton writes:

While an applied organic chemist, say, and a pure mathematician, by themselves, may not understand each other or find anything of common interest, the addition of several physicists and engineers to this group increases the effectiveness of both chemist and mathematician, if each scientist is sufficiently interested in learned something new.

Holton later even goes on to state that, with the constant branching off of one subject, such as mathematics, to a separate subject, such as physics or chemistry, that, “It is becoming increasingly more evident that departmental barriers are going to be difficult to defend.”

Exactly the opposite happened.

We built silos, not branches

Much has been made in the progress studies community on the problem of ‘good ideas becoming harder to find.’ And, while we can’t be sure that the ‘burden of knowledge’ isn’t responsible for this, it seems quite likely that this problem might be man-made. Holton, initially publishing this model in 1962, was writing at the end of a decades-long run that is seen as a scientific golden-age for qualitative reasons, like the birth and development of fields like relativity and quantum mechanics, and for quantitative reasons, looking at metrics such as TFP growth.

In that era, there was a distinct feeling that ideas were getting easier to find. So, why does it feel like we’ve reverted to Holton’s zeroeth-order world rather than continuing to live in his first-order world?

In short, it seems that there is less and less incentive for researchers to do the kind of research that creates new branches. And, if the possibility for a new branch to be fleshed out does arise, the incentives are not there for a researcher to jump ship and help develop this new area of research. And, without a critical mass of researchers, a branch never really takes off at all.

Looking at just a few pieces of the modern innovation literature paints a pretty clear picture of how the opposite of what Holton hoped for has become a reality.

The Pivot Penalty

Firstly, Hill et al. point out that, since the 1970s, it has gotten riskier and risker to pivot further and further from your main area of publishing. Your likelihood of becoming highly cited after a major pivot is less than half as likely today than it was in the 1970s. The negative slopes of the lines below indicate that you are less likely to write a highly cited paper the larger your pivot is.

And, while it’s unclear if the slope of a line from, say, the 1950s would be positive, meaning that researchers would be more likely to become highly cited if they made a major pivot in their research instead of a small one, it anecdotally feels very clear that the 1950s line would at least have a less negative slope than the 1970s line. The probability of a researcher winning a Nobel in a different field than the department they worked in or having the ability to gain tenure in multiple different types of departments has likely been going down since at least the 1970s.

Furthermore, Hill et al.’s analysis of research pivots and Covid-19 research showed that:

1. Younger, less established researchers were less likely to make a large pivot to Covid-19 research and

2. Those who relied on grants for research funding were increasingly less likely to be able to make a large pivot to Covid-19 research

The first point is particularly troubling because, as Holton pointed out, younger researchers joining a new branch of research was particularly important to help a new branch begin to flourish. In addition, younger researchers often depend on grants and are less likely to be sitting on the piles of extra research funds that seem to enable pivots like this.

Novelty doesn’t get you tenure

Wang et al. look at the novelty of scientific papers and their likelihood of becoming a top 1% cited paper written in their field. And, in an exciting turn of events, highly novel papers are far more likely to become blockbuster papers, rewarding the researchers for their risk!

But there’s a problem. It takes years for those citations to accumulate and for your paper to become appreciated. Like, enough years that your tenure vote may come and go without the paper being appreciated. At the 3 year mark, you may still have about the same number of citations as the completely non-novel research on average, possibly less.

Not to mention, when your day finally does come, the influx of citations often comes from a foreign field and not your own. So, not only will you need to wait up to 15 years for the sun to shine on your innovative work, but your recognition will possibly come from researchers who don’t even work in the same building as you do.

If academics are often incentivized to seek tenure and recognition from their peers, then this is not good news. Even if you are happy to receive the warm and fuzzy praise from people in a different department 15 years down the road, it’s not the kind of praise that you can trade in for a higher salary from a department in your field in many cases.

Furthermore, Bhattacharya and Packalen construct a model that demonstrates just how devastating the emphasis on citations and h-index can be in disincentivizing real scientific exploration. Because, while citations are one important metric in science, actual scientific progress depends on a steady flow of exploratory tinkering and new ideas. New ideas are risky to work on because, in the beginning, it is difficult to distinguish between ideas that could become a great branch one day and complete duds. And this base of exploration, this tinkering around, is what real breakthrough discoveries, branches that then spawn extremely productive second-order branches such as Rabi’s crystallography work did above, often depend upon. And, since citation-based metrics and decisions make little effort to distinguish between this exploratory work and incremental work on well-established research areas, all incentives steer rational researchers to got to “hot”, well-developed areas where well-done incremental work can garner high numbers of citations. All of this renders science less vibrant.

This is especially problematic if you subscribe to Holton’s view that it often takes a great mind to “turn to his full advantage the illogical and unexpected.” These words, written in reference to John Dalton’s atomic theory coming out of four completely incorrect assumptions, could possibly apply to any scientist engaging in exploratory work that attempts to create vibrant branches. If these great minds are also the minds that can reliably generate high-citation counts doing incremental work in “hot” areas, then all of science is losing out on their true potential.

Of course, it’s hard to do new research on an older branch!

If more and more researchers are working further along fewer branches of knowledge, then of course ideas are getting harder to find! That’s exactly what you’d expect. Our current equilibrium could be understood as something not dissimilar to the point in Holton’s zeroeth-order model when the number of researchers is peaking but a large proportion of the good ideas have been found already. Of course, the truth is likely somewhere in the middle of these two models because we do still discover some branches. But it does seem clear that the current state of things should be classified as far closer to Holton’s zeroeth-order model than science was at the time of his writing.

Being so much closer to the zeroeth-order approximation, it’s no wonder that average ship captains are getting older and older and the size of the team it’s taking to find an island is getting larger and larger. It’s important to remember that some new branch, D₂, only partially builds off of its parent branch, D₁. So, while experience working on D₁ is helpful in making discoveries on D₂, much of the knowledge on D₁ is not helpful at all. So, for researchers on D₂, some creativity and an eagerness to explore is far more important to making discoveries on D₂ than esoteric bits of knowledge about D₁. But, if all the scientists are crowded on D₁, then it’s clear to see how time in the field may outweigh creativity more so than it would on a new branch.

This, also, is not simply theoretical. At the time of writing, in 1962, Holton cited work by M.M. Kessler which found that 50% of the references cited in research papers published in the Physical Review, the top physics journal at the time, were less than three years old. And only 20% were more than seven years old. Decades on from the paradigm-changing discoveries of relativity and quantum mechanics, physics researchers had still been rapidly creating new branches of research and leapfrogging each other in the race for human progress, constantly citing younger and younger papers and letters. Science was moving so fast that a non-negligible number of citations in the journals were citing personal correspondence and conversations with other physicists as opposed to published papers.

Holton believed that we might see the end of departmental barriers and a system that evolved to incentivize these all-important branch creations. And he has lived through just the opposite.

Obvious Advice

If you buy into the model described here, it seems the single greatest thing a new science organization could do, even if it’s at the expense of ALL other things, is facilitate the creation and early development of new branches of science. These branches, when they are discovered, tend to experience periods of explosive growth, have a high likelihood of spawning other new branches, and these new branches are also likely to do the same. Without these new branches, good ideas WILL get harder to find.

Much of what this looks like is likely quite self-explanatory from the rest of this post. But, if you’re looking for some kind of bulleted list. Activities that empower researchers to create branches would include:

• Put your researchers from diverse fields in the same place and give them incentives to talk with each other, explain things to each other, and work on things with each other that don’t look like anything going on in their individual fields.

• Give them incentives to play (scientifically). Watching Real Housewives might not be a good use of lab time (maybe it is?), but fiddling with interdisciplinary ideas only loosely related to their current work should be okay. The researchers should be viewed not individually, but more as a portfolio. You want some new branch to come out of every X number of researchers, but you shouldn’t require proof that each individual is making linear progress towards this goal. Many researchers might have no progress to show for it, and that’s ok. Similar to working in VC investing, it’s about the hits.

• A good rule of thumb might be: be the place that gets the most out of the odd, eccentric, exploratory minds that feel like academia is no longer a great place for them the way it used to be in the era leading up to Holton’s writing. This will likely help you recruit the researchers best-suited to creating more branches AND get the most out of them. MIT and Bell Labs both understood that this was the way to get the best out of a mind like Claude Shannon.

Not to belabor the point, but Vannevar Bush even made a concerted effort to push Shannon to work on genetics problems for a period of time, when Shannon finished his work assisting Bush’s Differential Analyzer project, not because he saw Shannon as a career geneticist, but because he saw him as the kind of playful mind who appreciated new problems and who could do branch-creating work on many of them.

Sometimes, science should feel like play. In the time since Holton’s writing, we seem to have forgotten that.

If you’d like to know more about what Shannon’s path looked like qualitatively and how to foster more of him: Read Jimmy Soni and Rob Goodman’s fantastic biography of him, A Mind at Play.3

If you’d like to know more about what a career of creating less ridiculously-novel, but still quite novel branches in insane amounts looks like: Read my piece on John Von Neumann and what his career can teach us about how to generate more discoveries like his.

And, lastly, if you’d like to talk to me about any of these ideas: just DM me on Twitter at eric_is_weird

Hope you enjoyed. Please, if you know anyone who could make use of this post, send it their way! We need more room for exploration in this all-too-boring world. I’m hoping one of these new science orgs having a little fun is a way to make that happen!

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Citation:

• Gilliam, Eric. “When do ideas get easier to find?” FreakTakes Substack. 2022. https://freaktakes.substack.com/p/when-do-ideas-get-easier-to-find

This Week’s Article

The primary reason I’m writing this update is to inform subscribers that the article that was slated to come out this Friday will be a few days late. I came down with an infection this week and progress was a bit slow as a result.

The planned article will incorporate a lot of ideas from Gerald Holton, a physicist/science historian and all-around fantastic thinker. He was been writing illuminating essays on the nature and history of scientific innovation since the 1950s. He just turned 99 a few months ago and is still winning awards as you can see below!

I’m excited to share more about his ideas and how they can inform the progress studies movement. I can’t wait to share more. Stay tuned!

Moving Forward

In the next week, I’ll be announcing a new partnership between myself and a think tank dedicated to progress studies questions. As a ‘Fellow’, some proportion of my writing will appear on their platform, which I’ll be sure to link to Engineering Innovation Subscribers.

But I will still continue to post my own individual pieces to this Substack as well! More on that soon.

Who I am

I’ve been extremely excited by the growth of high-quality subscribers on this Substack. While my total number of subscribers is only in the low hundreds, an extremely high percentage of you have high-impact jobs, run progress studies organizations, write related Substacks, or are just all-around fascinating people. It’s been a pleasure to write for you and I hope to continue doing so for a while. Please email/dm me if you ever have any questions or commentary. Or even if you’d just like to chat, that’s great too!

In case it’s relevant to anyone who’d be interested in chatting, I also have a day job. I work a full-time job running social-impact incubation projects at the Center for Radical Innovation for Social Change at UChicago. It’s run by Steve Levitt and, more or less, what I do is try to come up with interesting projects/orgs that could do high-ROI social good if they existed. And then I try to bootstrap them into existence.

I come up with a lot of ideas, fail a lot, move on, repeat, etc. And, luckily enough, some things work out!

A few of the current projects I’m working on currently can be found below (I made up titles just now to make them sound flashy):

• Losing Weight, Saving Lives: It turns out that almost half of the people who enter the health screen to donate a kidney/liver to a loved one get screened out for health reasons. Some of these, such as hypertension, aren’t considered medically reversible. But the most common reason, high BMI, is absolutely medically reversible. But, in the current equilibrium, these overweight individuals are kind of shooed out of the hospital once they are deemed too heavy to donate/some hospitals won’t even see them based on their BMI. So, the idea I had was essentially to put as many of these people as possible on free weight loss programs (paid for by my center) to give them a fighting chance at donating their kidney/liver to their loved one. We’ve partnered with a large hospital system and are piloting the program now. With these programs costing in the hundreds of dollar range, many donors being within 10-15 pounds of donation weight, and a human life often being valued in the millions, I like our chances of doing extremely high ROI social good.

• OpenMolecule: Think ‘Human Genome Project but for screened molecules.’ Very few areas of academic biology have publicly accessible repositories of screened molecules that are suitable for machine learning tasks. This is a huge deal. Because, as things stand, if a researcher wants to do something like try to find a new antibiotic, they often need to just screen A LOT of molecules manually. Like a lot. Like possibly a hundred thousand. And it doesn’t need to be this way. When one of our project partners, Jon Stokes, was at MIT he helped show that this didn’t need to be the case.

  He made his own training set of screened molecules similar to existing antibiotics, trained a model to predict which molecules in the search space of existing molecules were most likely to be good antibiotics, and manually screened the 50 most likely candidates as determined by the model. Of those 50, two ended up not just being antibiotics, but had success in killing types of bacteria that are currently resistant to most antibiotics! A large dataset of screened molecules would make this workflow possible for all variety life sciences research!

  We’re trying to find a way to make a dataset of about 10 million wide-ranging molecules available to all academics to not just help in the fight against bacteria, but fungal infections, viruses, cancer, etc. These molecules have largely already been screened and are in the computers of various labs. We’re working to find a way to get them out and into the same place.

  Jon Stokes talks more about what he did below and it’s fascinating.

• Antibiotic Resistance: More and more people are dying from bacterial infections every year because bacteria are growing resistant to existing antibiotics while we fail to develop new antibiotics to which they are not resistant. This is the case because, unlike just about everything else, Americans don’t have a very high willingness to pay for antibiotics. So, while these drugs cost about $1.3 billion to develop due to the ridiculously high administration costs of US drug trials, they only make about $50 million per year. So, with those financials it obviously doesn’t make sense for Big Pharma to pursue. But…it seems like there might be a way to run an antibiotic trial and reduce the administrative costs by an order of magnitude! This project is in the early stages but I’m quite excited about it. Please reach out to me if you’d like to know more about it!

I would love to talk with any of you about any of these ideas or any ideas you may have! I’m just trying to do some good and have some fun doing it. No idea is too wacky or strange.

Thanks so much for reading every week and sorry there’s no new article this week. Hopefully hearing about a few of my projects was at least a little bit of a consolation. If you liked it, let me know and I’ll share more ideas in the future that are in the early stages! It could be a fun short newsletter to break up the pattern of longer, more complicated pieces.

Happy Wednesday,

Eric

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