The Spotify version of today’s episode can be found at this link.
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!
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.
Share this post