Fortunately, there is a narrower (albeit more delicate) path, as long-time FreakTakes readers know: BBNs.

Originally named after an ARPAnet contractor named Bolt, Beranek & Newman, a BBN is just a funding mechanism for scientists to work on ambitious ideas. Unlike academia, BBNs focus on applied problems. Unlike VCs, BBNs are not concerned with making billions of dollars in the next decade. And unlike FROs, BBNs can launch quickly — often with a few hundred thousand dollars — and extend their runway by winning grants and contracts. BBNs and FROs can share essentially identical technical ambitions, so the distinction is mainly funding. FROs begin with a large upfront endowment ($10–100M) that lets them pursue a big goal from day one, whereas BBNs pursue the same kinds of goals but more steadily.

A few weeks ago, when Eric Gilliam and I sat down to lunch, I riffed on some BBN-shaped ideas for biotechnology. He asked me to write them down, and I agreed. There were two reasons for my doing so: First, I think more people ought to know what a BBN-shaped idea is; and second, ideas are a limiting ingredient in launching more BBNs.

In this short article, I riff on three biotechnology ideas which might be suited to a BBN: “Flowers by Design,” “A Biosensor for Everything,” and “Proteins for Pennies.” Readers may reject or disagree with elements of these ideas, but my hope is that, by writing them out explicitly, people will at least be inspired to start BBNs.

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Eric is in Boston through March 27th, and he’s eager to talk to anyone with interesting BBN ideas. If you’re around, reach out at gilliam@renphil.org.

Three Quick Ideas

Flowers by Design

The first idea, “Flowers by Design,” is not my own; there is already a small yet serious group of people using genetic engineering, pathogens, and other molecular tools to create entirely new types of flowers. (I wrote about one such flower designer for Asimov Press.)

These designers, all of whom are also plant biologists, make engineered flowers with unique patterns, colors, and shapes. They tend to be brilliant not only because they are adding beauty to the universe (a goal one should not scoff at), but also because, by mixing these methods together, they are making important discoveries about how plants actually work. The “big” goal of a flower design BBN might be to develop a general theory of plant programming, such that one can control the traits and growth patterns of a wide array of plant species.

Any tools created to engineer flowers would also unlock capabilities in food crops. Flower designers work across dozens of species by necessity; far more than the handful of model organisms that academic labs use. Also, the DNA delivery methods used to engineer a dahlia or a morning glory are the same methods needed for sorghum or cassava, two crops where transformation efficiency is currently so poor that most genetic engineering efforts fail.

The same transcription factor proteins that control flower structure — petal number, organ boundaries, and symmetry — are also closely related to the genes which determine grain size, seed coat thickness, and fruit morphology in food crops. Engineering flowers is thus a way to create beauty in the universe while discovering the developmental and genetic principles that matter for food yield.

Unfortunately, flower design does not easily fit into existing career paths. It is not an obvious VC play because it can take several years to circumvent regulatory barriers alone, and returns often take more than a decade. (The Juliet Rose took 15 years to create, at a cost of $3 million, but is profitable today.) If any genetic engineering methods are used to make a flower, scientists must abide by USDA regulations overseeing how that flower is shipped across state lines.

More important than regulations, though, is the simple fact that everyone I’ve met who calls themselves a “flower designer” is extremely idealistic; almost allergic to business. They see themselves as artists and scientists first and foremost, and they don’t want to spend several years making one plant just to sell it repeatedly. Instead, they want to make hundreds of different flowers, with thousands of bespoke designs, and this takes a lot of time and money.

This isn’t an obvious fit for academia, either. The goal of flower design is to make beautiful objects, rather than publish papers. It also isn’t an obvious “pure” philanthropy play, though philanthropy would be better suited to this idea than academia or business. It just isn’t clear, to me, that a wealthy person would give $10 million to a person making flowers when that money could instead go toward curing cancer or something with more “social capital.”

Fortunately, there are many contracts and grants available for flower design, which could be used to bootstrap a BBN. Japan funded an effort to make a genetically-engineered morning glory for the 2020 Olympic Games, though the project later fell through. (Japan, in fact, has one of the largest flower industries in the world, commercializing about 40,000 new varieties each year.) A single USDA SBIR Phase II grant (~$2M over two years), paired with one or two annual contracts from plant biotech companies interested in new ways to engineer traits in flowers (typically $100–300K each), could plausibly sustain a small team of three to five people indefinitely.

Biosensor for Anything

My second idea is called a “Biosensor for Anything.”

Biology has evolved, over billions of years, to sense millions of unique molecules. Our noses can differentiate two molecules differing by a single atom, or even mirror images of the same molecule (S-carvone smells like spearmint; R-carvone smells like caraway seeds.) And we don’t only sense molecules, either, but also other ‘forces.’ Some birds migrate thousands of miles by sensing magnetic fields, for example, and proteins inside cells can sense individual metal atoms, like zinc or iron.

I suspect there is a BBN-shaped idea around using biotechnology — especially engineered cells or AI-designed proteins — to sense a wider array of molecules and forces. (There is a related ARIA program focused on building so-called “Hypersensory Intelligence.”) Whole-cell biosensors can be created using genetic circuits, where one protein binds to a molecule and a second protein emits an output, such as fluorescence or a color change, in response. A platform technology BBN, focused on building tools to make virtually any biosensor, would help us respond to outbreaks more quickly, or create cheaper diagnostic tests. (About 500,000 children in the U.S. have lead poisoning, for example, and the main way to test for it is with a $5,000 device.)

Specifically, I’m envisioning a BBN that systematically collects large datasets on protein sensors — the biological molecules that detect a signal — and the output modules that report what they’ve found, perhaps by emitting light or changing color. These datasets would be used to validate which sensors work reliably across many different cell types and experimental conditions, and to build predictive models that help scientists design better sensors without having to test every possible combination by hand. The most promising sensors would then be put through field trials in the messy, real-world environments where they’d actually be deployed: sand, soil, water, blood, and so on.

A few years ago, there was lots of excitement about paper-based diagnostics. The basic idea was that scientists could engineer a biosensor in living cells, and then kill those cells and extract their “juices,” including the synthetic DNA. This “juice” could then be coated onto a piece of paper and freeze-dried. When scientists added liquid back to the paper, the genetic circuit would reactivate and change color if the molecule being sensed was present. These paper biosensors cost pennies to make, yet I’m not aware of any companies that have successfully commercialized them, either because the paper strips were not accurate or reliable enough for clinical diagnostics or because — in places where accuracy matters less — the amount they could be sold for was too small to generate large returns.

This idea, much like flower design, isn’t obviously suited for pure academia or philanthropy. The work requires deep expertise across multiple disciplines, including computational protein design, genetic circuit engineering, and materials science. One lab can’t do all of this. And even though philanthropists might fund the creation of a specific diagnostic test for a narrow disease, they’re less likely to fund a much broader effort to make “biosensors for anything.”

That’s why this feels like a BBN-shaped idea to me. A small team could win contracts and grants to build biosensors for underrated diseases, using that money to engineer proteins and prototype devices. Domain-specific contracts — from funders like Arnold Foundation on lead, or from the EPA on environmental monitoring — could cover much of the operating cost of a BBN in this space, but the group would also need about $300–500K in unrestricted funding each year to keep doing R&D and make sure they don’t drift down a narrow diagnostic path. Over time, the BBN would use what they learn to build better reporters, more stable freeze-dried systems, and also better computational design tools to speed up prototyping.

Proteins for Pennies

A third idea, and my personal favorite, is “Proteins for Pennies.” The overarching aim here is to make a “protein fabricator” such that scientists can create any protein, of any amino acid sequence, for a few pennies; ideally within a few hours. We are nowhere near achieving this, but doing so would not require breaking any laws of physics. Cells “eat” nutrients, like sugars and nitrogen, and turn them into useful biomolecules. Indeed, a single cell synthesizes tens of thousands of proteins simultaneously, using only the atoms repurposed from its environment. Why can’t we do the same, but synthetically?

There are currently two main ways to make proteins in the laboratory. The first option is to order a DNA sequence encoding a protein of interest. Each nucleotide costs about $0.07 to order from a DNA supplier. Given that an average protein has about 300 amino acids, this means scientists must order a gene with at least 900 nucleotides (three “letters” of DNA encode one amino acid) to make such a protein. In this scenario, the DNA sequence alone costs at least $63. And even after the DNA sequence is made, scientists must then clone it into a microbe, grow those microbes in large batches, and purify the protein. This takes time and money.

The second option is chemical synthesis, where chemists click amino acids together, piece by piece, until the full protein is completed. The problem with this approach is that each step has a particular efficiency — say 99% — and a single error is enough to ruin the entire molecule. (For a theoretical protein with 300 amino acids, a per-step accuracy of 99% would yield just 5% of proteins with a perfect sequence.)

A BBN could work towards lowering the costs of protein synthesis by 100x. Protein-based therapeutics, some of which are currently too expensive to manufacture for rare diseases, could be made on-demand. The cost of protein design would also fall sharply, since wet-lab testing of computer-generated designs is the main cost — and most time-intensive part — of the whole process.

A BBN focused on protein costs could begin by miniaturizing and automating existing protein synthesis technologies. With enough scale and multiplexing, perhaps costs could fall by 3-5x. A recent paper from the Baker lab, for example, describes a semi-automated workflow for purifying and characterizing hundreds of designed proteins per day using standard laboratory equipment. This reduced the cost of testing each protein design to just five dollars per construct. Still, my suspicion is that radical price reductions will require a fundamentally new technology; something with near-100% accuracy (like living cells have) without requiring a DNA template to build the proteins.

Previously, I wrote about one “Protein Printer” idea together with Julian Englert, CEO of AdaptyvBio, a protein testing company. Englert’s idea was to build a circular loop of RNA containing a codon for each amino acid, attach a ribosome to it, and then move that ribosome back-and-forth to each codon to make a particular protein. Perhaps this could be done using flashes of light, where a “blue” wavelength triggers the ribosome to move one codon forward, and a different wavelength triggers it to move back one codon; akin to a rotary telephone. In this way, scientists would not need to synthesize an original DNA template for each protein; they could just use these engineered ribosomes and circular loops of RNA to make any protein using light. But this is not the only idea to make a “protein printer.”

Grants could easily be used to bootstrap this BBN. Many funders are excited about the intersection of AI and biology and, again, protein synthesis costs are a major bottleneck for testing computationally-designed proteins. Therefore, the cheaper we can make proteins, the larger the datasets we can collect for a given amount of funding, and the faster we can improve AI models.

ARIA recently announced a £50M Universal Fabricators program, specifically to develop scalable protein-based manufacturing. If a team of three to four people could win some grants to build a fence around R&D efforts, they could then go chase after contracts for more narrow efforts (like bespoke protein manufacturing for therapeutics companies.)

Everything in this essay is me shooting spitballs against the proverbial glass window. But I hope this article inspires others to think of BBN-shaped ideas in their own fields. Which ideas would move your field forward in a meaningful way, yet are not well-suited to academia, VC, or large-scale philanthropy? Write them down!

Niko McCarty is a fellow at Astera Institute and a founding editor of Asimov Press.

Ivan’s program has some very BBN-shaped pieces of work, and he believes some of his most ambitious applicants might see his call for proposals as their chance to launch a BBN of their own. If that sounds like you, and you can solve the problems Ivan outlines below, reach out to him here. (To learn more about “BBNs,” see this prior FreakTakes post.)

As a bit of context — for those that did not see my interview with ARIA’s founding CEO — ARIA PDs are empowered to fund brand new R&D orgs into existence if it suits their program’s needs. The org covered in the most recent FreakTakes post, Syntato, is a case in point. ARIA’s Programmable Plants work needed a group to build tools to transgenically gene-edit crops. Using its ARIA contract to do just that, Syntato was formed.

Ivan’s program may offer similar opportunities. In our discussions, Ivan was particularly excited about the idea that, at their best, BBNs can be technology-maximizing firms. I hope that a few of your pitches live up to that bar.

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Two quick notes.

1. I initially intended this series of BBN-related guest posts to be a weekly series. That was overly ambitious. I get over-eager sometimes, sue me. The new cadence will be two or three pieces a month.

2. In the UK, many have begun to call BBNs “Frontier Research Contractors” (FRCs). Ivan uses that terminology below.

Universal Fabricators

By: Ivan Jayapurna

Ages of human history are defined by new materials: Stone, Bronze, Iron. However, civilisation-defining materials, from steel to optical fibres, changed the world not at discovery, but only when processes were developed to make them cheap and abundant. Our physical world is still dominated by ancient materials (wood, concrete) and antiquated ones (steel, plastic) built using brute-force heat and pressure. Continued reliance on manufacturing paradigms from the Iron Age and 1900s chemical engineering has trapped us in brittle global supply chains, resource conflicts, and a tiny corner of the total possible materials design space. Despite advances in material synthesis, many desired electromagnetic, thermal, optical, and mechanical properties remain inaccessible.

Mass manufacturing with molecular precision is crucial for state-of-the-art material performance, and proteins represent a uniquely powerful toolkit to achieve this. Yet despite recent breakthroughs in protein engineering (e.g., Alphafold, de novo design, directed evolution, non-canonicals, cell-free synthesis), subsequent investment and applications have primarily been in pharmaceuticals and biocatalysis, leaving the potential of proteins in materials assembly severely underexplored. Today, most protein engineers only design drugs and enzymes. If this programme is successful, they will design next-gen materials across electronics, energy, infrastructure, and more — and proteins will become “universal fabricators.”

As an ARIA programme director, I don’t have a lab of my own. My role is to design the programme, select contractors to fund, and orchestrate them towards the programme’s North Star technical vision. As such, success is almost entirely dependent on the programme’s contractors, who will develop proteins into universal fabricators. I need people and labs that are excited to become universal fabricators. It’s possible that FRCs — or BBNs as they’re also known — could be ideally-suited to do substantial portions of work for this ambitious, engineering-heavy, and radically interdisciplinary programme.

Why FRCs

As Eric has written in a prior FreakTakes piece:

[FRCs] will tend to have ambitious goals that are too engineering-heavy, multidisciplinary, or applied for academia. And they will tend to focus on markets ill-suited to VC — either (a) because these are not billion-dollar markets, or (b) because the financial impact of the work could be massive, but will not be realized within the ~10-year life of a VC fund.

Of course, there are some select academic research groups able to overcome these barriers. Often, these labs are well-funded, highly interdisciplinary, and have worked with ARPA-style agencies before (DARPA, ARPA-H, etc.). These labs have a culture of spinning out companies, allowing for R&D to be distributed between basic scientific research in the main lab and more “engineering-heavy” or “user/product-focused” work in spinouts. However, these labs are few and far between; and where they do exist, their spinouts are often subject to the constraints of venture capital funding.

For example, it is all too common a tale that an exciting materials startup with dreams of building revolutionary platform technologies is pushed by market and investor incentives towards a niche in the pharmaceutical industry, or incremental advancements on existing systems. These are all useful, but tend to fall short of the founder’s original ambitions. For profit-maximising firms this is understandable, but once you narrow in the technical scope to only those markets that fit VC constraints, many lines of societally exciting technical inquiry are lost.

I view FRCs as technology-maximising organizations that seek contract revenue from customers not as the objective to maximize, but as fuel to develop coupled science-engineering breakthroughs. These groups should seek to do work at the edge of the impossible. For that reason, FRC-like groups are a great fit for a programme like ours.

Universal Fabricator FRCs

The majority of our £50m programme will fund a small number (<10) of teams developing proteins into universal fabricators. There are multiple different renditions of what an FRC that could successfully build a universal fabricator could look like. One variant might look something like a team made up of the following archetypes:

• Protein Engineer — Designs the building blocks and interactions on the molecular scale.

• Complex Soft Matter Expert — Manipulates short- and long-range interactions between the building blocks, such that they assemble at the right length scales and time scales.

• Inorganic Materials Mineralization Expert — Programs nucleation and growth of crystalline or amorphous inorganic matter into highly valuable functional materials.

• Process Engineer — Designs reaction environments to create “error-correcting” assembly systems that impose selective pressures for assembly through fields and flows.

No matter how they are structured and composed, these teams should be able to rapidly iterate design-test cycles — quickly going from a sequence, to the design of single molecules, to ensemble design, to field/flow-aligned assembly (liquid → slurry → solid).

To further emphasise, this all-star team is just one vision (mine) of how to design a universal fabricator FRC. We’re looking for creatives with their own takes on team composition, and imaginations that exceed our expectations to fill the white space that sits between:

• Biology and solid-state physics,

• Protein assembly + templated mineralisation (sequence → structure → function) and scalable materials manufacturing (processing → structure → performance)

If successful, I hope these universal fabricators can do the work that defines the next era of human history. I want to read proposals from any team with a vision of how to make that happen.

Protein Production FRCs and Beyond

The programme will likely benefit from other FRC-shaped groups, beyond teams building protein-programmed fabrication platforms. One big challenge that will need to be solved is scaling up protein sequence-to-function design-test cycles. Today, in silico screening and automated assaying is done efficiently at the molecular scale. Scaling this up by many orders of magnitude, to the materials scale, today, would optimistically take months. Ideally, we want to shrink this timeline to under a week, to match the current state-of-art in drug design pipelines.

An FRC focusing on advancing rapid turnaround — large quantity, bespoke, engineered protein production — would likely be one of the most important suppliers for our programme. Specifically, I’m looking for a group to develop a system where, if I give you an arbitrary protein sequence, within a week you can give me enough material to e.g. template the assembly of a magnet large enough to measure (BH)max. Today, this would likely be done by living systems, but it’s conceivable that it could be achieved by drastically improved non-living production systems (e.g., cell free, protein printer). If a group has the capacity and ambition to substantially improve the state-of-the-art, it would be a valuable organisation for us to potentially nucleate into existence.

We expect this service to be exceptionally useful to a variety of customers, beyond the needs and length of our material science programme. In the near-term, we expect that a sustainable inflow of contracts could also be sourced from markets ranging from pharmaceuticals and biocatalysts to food, fibres, and packaging. Contracts like these, in addition to the sizable needs of our own program, would allow for the steady funding required to knock down technical barriers in pursuit of ambitious long-term goals in this space.

These are just two examples of possible FRCs aligned with my programme’s needs. I’d love to read your pitches for more of them. For example, FRC proposals in an area like metrology would be very welcome. Is there an FRC-shaped group that could quickly measure defect-free incorporation of proteins into macroscopic structures?

Call To Adventure

Prior to joining ARIA, I was a researcher trapped at the interface of materials and biotechnology — the only non-healthcare company in a biotech incubator, the only biotechnology in a climate accelerator — as well as between academia and profit-maximising startups. ARIA offered me an alternative, more direct path towards achieving my North Star of ‘Manufacturing Abundance’. Through the Universal Fabricators programme, I hope to open alternative paths for others. If this piece resonated with you, let’s go on this journey together.

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Karen is the perfect founder to present the first example of a modern BBN in this series. Syntato has both an extremely ambitious technical goal and a great customer — one that has enabled the org to be a break-even operation from day one. Beyond those attributes, Karen is an exceptionally effective writer.

While Karen’s name may be new to readers, his work might be more familiar; Karen previously co-founded Light Bio. Light Bio inserts genes from fungi into petunias to make them glow (see below). Syntato’s work builds on methods developed at Light Bio and ideas from Karen’s research group at London’s MRC Laboratory of Medical Sciences.

In today’s piece, Karen will paint a picture of where Syntato hopes to go. In reading it, I hope readers develop confidence that BBNs can swing big in the modern era while covering their own costs.

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This piece is a part of a FreakTakes series on BBNs and the BBN Fund. To read more about the BBN Fund itself — and how great BBNs from ARPA history contributed to breakthroughs like the ARPAnet and early autonomous vehicles — see the opening piece in this series. TLDR: the BBN Fund will be a time-bound, thesis-driven fund at Renaissance Philanthropy, headed by Janelle Tam and me.

Our goal is to be for the BBN ecosystem what the best ARPA PMs are to speculative areas of R&D. As an alternative framing — to steal a new term from Nan Ransohoff’s excellent piece from a few weeks ago — we will be “General Managers” for the modern BBN experiment, directly responsible individuals dedicated to finding ways to lower the barriers to founding ambitious BBNs in the modern era. For us, success will mean paving the way for dozens of BBNs like Syntato to be founded per year. And we are actively seeking our first funders to make this happen. So if you are a funder interested in partnering with us, please reach out at eric.gilliam@renphil.org and janelle.tam@renphil.org!

With that, I’ll be out of your hair! Enjoy:)

From primitive engineering to the design of new plants.

By: Karen Sarkisyan

— How can we design a novel crop?

— Or program the behaviour of a house plant?

— Or turn a field into a super-organism that breaks the growth-defense trade-off through division of labour?

— Can we domesticate marine plants to produce food without deforestation?

Today, our ability to engineer plant traits is primitive. We are able to write one, two, and sometimes three lines of the lowest-level DNA code, and these programs are typically species-specific. None of the engineered plants on the market goes beyond the line:

      always express genes A-G

In the future, we may be able to design plant traits we need. But with the current rate of progress, this will not happen before our existing agriculture practices and need for energy and materials destroy most of the planet. (This image of Borneo deforestation, below, is one of the saddest things one can find on the internet — and there seems to be no realistic solution, except possibly an economic shift driven by biotechnology.)

— Is it possible to have a truly novel crop on the market in 10 years, by 2036?

— Probably not. Not with the current tools. And which team is even in a position to work on that?

Surprisingly, across the world, there are almost no competent teams working on ambitious plant engineering from first principles. Even the startups supposedly doing “cutting-edge” plant biotechnology almost always create yet another version of “overexpress genes A-G”. And most effort — shaped by regulations — goes into modifying existing plant genomes, one small edit at a time.

Several factors limit accessibility of deep plant re-engineering to biologists, most importantly:

1. difficulty of transforming and regenerating most plants, especially non-model cultivars,

2. lack of predictable building blocks to program plant traits,

3. immature “hardware” technology: molecular tools to build, host and update large DNA programs in plants.

Fortunately, plant transformation and regeneration (=1) has seen a lot of progress in recent years: a variety of novel tissue-culture-free (as well as tissue-culture-based) approaches have been developed [1, 2], with many studies already expanding way beyond model plants [3, 4, 5, 6]. We are certain that in the next 5-10 years, hundreds of academic groups will be trying out diverse approaches, largely removing this bottleneck without the extra help.

In contrast, predictable building blocks for programming plant traits (=2) remain scarce. Over the last decade, great work has been done standardising molecular infrastructure and creating collections of lowest-level DNA parts (promoters, genes, terminators) for different species of dicots [7, 8, 9, 10, 11] and monocots [12, 13]. However, very little work has been done at the higher level of genetic circuits and metabolic pathways.

Configuring pathways into openly accessible and easy-to-use building blocks lowers the technical “activation energy” barrier — with a non-linear, catalytic effect on their adoption. An illustration of this is the reporter RUBY which encodes biosynthesis of a red pigment: after being configured into the easy-to-use form of a single transcription unit in 2020, it is on the way to become one of the most popular reporters in plant biology [14, 15].

Let’s review a hypothetical program (on the left) and the building blocks needed to execute it (on the right). This program enables a farmer to deliver a critical weather forecast using a drone-sprayed chemical signal, helping plants survive environmental stress and maintain crop yield. To reduce costs for the farmer, the plants themselves propagate the information from the spray site throughout the field

Some of the building blocks required for such programmable traits have not been developed, despite the availability of components; others have only been shown to work as a proof of concept, but not as robust plug-and-play tools. An assessment of block compatibility and joint performance within higher-level programs has not even been attempted. There is no validated library of low-level genetic abstractions one can use to build a DNA program in plants.

Plant “hardware manipulation” technologies (=3) are at a similar place: we do not have solutions to routinely build and manipulate plant synthetic chromosomes, let alone do so at a cost compatible with iterative prototyping of large DNA programs. (This problem is the focus of Syntato’s ongoing ARIA-funded work — to create a technology to inexpensively build plant synthetic chromosomes.)

Due to GM regulations and the cost of obtaining regulatory approvals [16], there is little economic drive for enabling more complex plant programming. In the absence of such a drive, the current lack of tools and low-level genetic abstractions is unlikely to change soon: we are stuck without having the tools, despite the technology components already in place. A well-funded academic lab may attempt to work on this, but as the effort does not necessarily yield scientific novelty, but instead requires large-scale multi-year iterative refinement of genetic designs, it will be misaligned with the academic incentive structure. A startup cannot afford to do this general-purpose work, as it is too broad, expensive, and far from the market. A large seed company is unlikely to approve such spending as it’s not directly aligned with the goals of their crop development efforts. Without a focused effort for large synthesis of available technology to make good tools (“molecular hardware” & “DNA software libraries”), the activation barrier will stay high enough to prevent crop design from becoming accessible to a broad range of bioengineers.

By focusing on building tools, we aim to help move the field from the current primitive plant engineering towards the design of novel complex, adaptive traits — and eventually, just like we design computer chips today, we will design and manufacture genomes of new plants.

Contracts and grants

Syntato is the lead contractor on an ARIA-funded project to create plant synthetic chromosomes technology. It is a 3-year £4.1M+VAT contract, the budget of which is shared with collaborators and subcontractors. The contract with ARIA allowed us to buy equipment, build a small team, launch lab operations, and create a frontier screening platform for plant engineering work – all in under 9 months. This initial investment into the robotic infrastructure and technology created a basis to amplify the value of future grants and contracts: an opportunity to follow a BBN-style organisational path.

The platform we developed enables high-throughput experimentation in fully intact plant cells, with the highest reproducibility we’ve seen among plant biology transgenesis platforms. We offer two types of contracts:

• Standard screening of customer’s genetic designs on our pipeline (cheaper, simple paperwork, no custom assay development, no IP ownership).

• Tailored co-development of custom plant-based assays (more expensive, IP may be shared).

Syntato’s platform is universal and can be adapted to any plant species. It can be used for large-scale herbicide screenings, testing of AI-designed protein binders, directed evolution of proteins in plant cells, genetic circuit prototyping, and optimization of natural product biosynthesis. These services are particularly valuable for organisations without a strong plant engineering team or high-throughput plant testing capabilities. A use-case example would be a player in the horticulture industry interested in engineering a biosynthetic pathway to produce a pigment in an ornamental plant. Or a newly established startup that chooses to derisk their proof-of-concept on our platform instead of launching a fully functional lab. Or a seed company that outsources their protein engineering work instead of building that expertise in-house.

Essentially, if an organisation has a trait design project, we are excited to work with them. What makes the contract worthwhile for us is the customer's willingness to fund the upstream R&D necessary to make the desired outcome possible — allowing us to build tools and methods that get us closer to our technical vision. In that context, contracts that help move the whole field forward, such as those from philanthropic or government funders, are especially interesting.

What’s next

In Eric’s BBN Fund post, he wrote how the long-run organisational goals of BBNs will vary. One of the goals he mentioned was the possibility of using a BBNs base of contracts and grants to build up the equivalent of an academic department. This resonates with Syntato’s vision: we aim to use our contracts and grants to eventually grow into a larger research organisation, an engineering bureau that designs and creates plants. Doing this well would not just mean building up the technical equivalent of an academic department, but an entire research institute.

What would it take to reach that stage? We estimate a required volume of contracts and grants in the range of $3-7 million per year for about 10 years. We would love to work with a philanthropic funder willing to accelerate this work — please reach out to karen@syntato.uk if you have a lead. At the same time, we also feel that the customer-focused BBN path — the one which keeps us closely tied to industry’s real challenges — is the best path for Synato.

Thanks for reading:)

Karen’s LinkedIn, Twitter, and email — karen@syntato.uk .

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Please let me know if you found this structure of today’s BBN write-up useful. The structure I personally tend to use is a bit more detailed, but in the same spirit. It goes something like: technical vision, contracts and grants, initial steps, distinct advantages, recruitment strategy, growth strategy, key winners, midterm assessment, and asks. We presented a simplified structure today, but I’m happy to adjust/expand based on reader feedback!

Since then, some version of the following paragraph has graced the top of an astonishing number of operational documents I’ve written.

A close reading of ARPA’s early history yields a key lesson: exceptional projects were usually the result of exceptional contractors. Now-famous ARPA success stories like the ARPAnet and early autonomous vehicles depended on a common shape of R&D organization — one structured, incentivized, and staffed differently than typical academic labs or VC-funded startups. I call this shape of organization a BBN-model org — named after ARPAnet contractor Bolt, Beranek & Newman (BBN). If R&D funders plan to chase more early ARPA-style outcomes, we should build more BBNs to do it.

Like FROs, BBNs pursue ambitious technical goals, ill-suited to the incentives of VC, that are too engineering-heavy or multidisciplinary for academia. Unlike FROs, BBNs primarily fund this work with a mix of contracts and applied grants, rather than a $10 to $100 million upfront fundraise.

This past year, I’ve embraced the role of a ‘field strategist’ for the BBN ecosystem.1 In this period — Stage 1 of the modern BBN experiment — I sought to verify that there was both demand for BBNs from ARPA-like funders and a supply of top researchers eager to found BBNs. Thanks to the UK’s Advanced Research + Invention Agency (ARIA), both have now been resoundingly verified. To provide just one data point in support: according to ARIA’s most recent fiscal year data, a small set of scrappy BBNs won more in ARIA funding during the year than every lab at the University of Cambridge combined. Stage 1 of the modern BBN experiment is now complete.

It is now time for Stage 2 of the experiment: building a “Convergent Research for BBNs.” The BBN Fund’s objective will be simple: seed a modern ecosystem of BBNs and work to maximize their overall technical ambition.2 If successful, we will forge a new pathway for today’s best applied, ambitious researchers to pursue ambitious R&D agendas — as Convergent Research has done with FROs. The team’s functions will fall into two basic buckets.

• Capital Deployment. Using the capital we raise for the BBN Fund, we will deploy funds to drive the creation or growth of the most promising BBNs — using a mix of financial instruments including revenue-sharing agreements, revolving loans, and undirected R&D grants.

• Field Building. Using the time of BBN Fund staff and affiliates, we will cultivate BBN founders, source new BBN customers and funders, and develop the scaffolding needed to grow the BBN ecosystem.

I will be founding the BBN Fund at Renaissance Philanthropy with Janelle Tam, formerly Convergent Research’s Head of Programs. She also built and ran Y Combinator’s Series A program, where she advised hundreds of early-stage startups on fundraising and growth. We are aiming to raise an initial philanthropic fund of $10 million to fuel this mission, and are looking for our first funders. Beyond the baseline costs of staff and field building work, for each additional $1 million, we believe we can help found or scale another ~5 BBNs. If we succeed, the J.C.R. Lickliders of our time will be able to build their life’s work within a BBN, rather than shoehorning their best ideas into academic-paper- or VC-shaped boxes.

In today’s post, I will paint a picture of our grand ambitions for the BBN ecosystem, and how the BBN Fund can get us there. The first section summarizes the BBN model for those who have not read prior FreakTakes pieces on the topic. The second section provides an overview of Stage 1 of the BBN experiment — ARIA’s embrace of BBNs and its partnership with Renaissance Philanthropy to provide grants and support to fledgling BBNs.3 I will end by presenting our vision for the BBN Fund.4

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Today’s piece marks the start of a series. Each Friday for the next two months, I will turn the Substack over to someone in the growing BBN community, usually a founder, to write a piece on a new BBN-related topic. This will include:

• Janelle Tam, my cofounder, on the potential to unlock large pools of capital for BBNs by demonstrating their potential as an investable asset class.

• Karen Sarkisyan, a BBN founder in the UK, on his new applied crop genetics BBN.

• Henry Lee, CEO of Cultivarium — the non-model organism FRO — on the prospect of transitioning his FRO into a BBN.

• Tom Milton, CEO of Amodo Design — a BBN with the desire to fold toolmakers back into the early stage science process — on the rate at which BBNs can grow, and what drove his org’s ability to increase its largest contract by an order of magnitude four quarters in a row.5

• And more! Stay tuned.

If you are (or know people who are) interested in becoming a BBN funder, founder, or customer, reach out to us at eric.gilliam@renphil.org and janelle.tam@renphil.org.

The BBN Model

Simply put, BBNs pursue ambitious North Star technical visions with a mix of contracts and grants. The shape of technical ambition will vary. It can range from an FRO-like technical goal, such as developing methods to cheaply map mammalian brains, to building a center of excellence in an area of R&D in which academia struggles, such as bespoke biotech instrumentation or chip building.6 Some BBNs may even pursue the speculative work necessary to help establish new subfields of research, e.g. computational law. What unites BBN founders will not be the shape of their technical visions, but their capacity to fund them by solving real problems for paying customers en route to these visions.

At the original BBN, J.C.R. Licklider leveraged the model masterfully to pursue his technical vision: building a future of interactive computing. It was at Bolt, Beranek & Newman that Licklider took his first step away from his MIT professorship and towards building this future. Similarly, CMU’s 1980s autonomous vehicle teams leveraged the BBN model to tackle their own FRO-like problem, succeeding in building autonomous vehicles where DARPA’s prime contractors could not and academic computer science would not.

In pursuit of Licklider’s vision, a series of technical problems related to both UX and real-time computing needed to be knocked down. The BBN computing group did just that in the 1960s by utilizing a set of cleverly assembled contracts and grants from groups like the NIH, NASA, ARPA, consulting projects with industry, and other contract partners. The group did this while building a research culture at the firm that earned the admiration of MIT professors and affiliates, many of whom described the original BBN using phrases like “the third great university of Cambridge,” “the Cognac of the research business,” and the true “middle ground between academia and the commercial world.” Licklider and others left positions like MIT professorships to join the firm. They felt it was a far more resonant research environment for their applied, ambitious research than MIT.

BBN’s computing team was able to strike this balance between ambition and contracting because they only worked with customers whose needs were exceptionally aligned with their technical vision. One example of an aligned contract was the firm’s contract to build an NIH-funded hospital time-sharing system. This contract, which was key in funding BBN’s real-time computing progress, was ostensibly a contract to build an administrative computing system for Massachusetts General Hospital. While BBN did not necessarily care that much about building computers for doctors, the team embraced the work because it funded years of real-time computing R&D en route to its technical ambition — R&D that was then too speculative for industry and ill-suited to MIT.

Like FROs, BBNs will tend to have ambitious goals that are too engineering-heavy, multidisciplinary, or applied for academia. And they will tend to focus on markets ill-suited to VC — either (a) because these are not billion-dollar markets, or (b) because the financial impact of the work could be massive, but will not be realized within the ~10-year life of a VC fund. The latter scenario was likely the case for both the ARPAnet and autonomous vehicles.

Like FRO founders, common BBN founder archetypes will include applied-minded postdocs, research-minded engineers, defected professors, and former deep tech founders who crave the longer R&D timelines and research flexibility that the BBN model allows. BBNs won’t build and hire as fast as FROs on day one, as they will usually have much less capital. In choosing the BBN pathway, founders trade the practicality of an upfront ~$10 million FRO fundraise for a different kind of practicality: finding a set of customers and applied funders whose needs are aligned with their technical vision. Like startups, if they are able to tap into a sustainable base of funding, they can steadily expand in pursuit of their technical vision, learning as they grow. Many inspired technical visions will not have a corresponding customer base, of course. But wherever you have an ambitious researcher with vision and an aligned set of customers/funders, you might have a BBN.

Early ARPA’s best BBNs shared three distinct traits, rarely found together in R&D labs. Each:

1. Was novelty-seeking or technically ambitious, with a strong preference for projects that pushed the technological frontier forward substantially.

2. Built useful technology for paying customers. This entailed professional contract management and a willingness to focus on difficult systems engineering tasks. Many BBNs were relatively indifferent to market size, so long as they could find adequate contracts and grants to pursue their North Star technical vision

3. Used more flexible team structures than academia. When compared to academia, they more effectively hired, organized, and incentivized researchers, engineers, and other experts to collaborate on applied projects in a common-sense fashion.

With a set of aligned contracts and grants, BBN founders can often begin working towards their technical goals with only a few hundred thousand dollars — some BBNs can even be bootstrapped. This path comes with a level of ongoing financial risk not present in FROs — at least not FROs that have successfully fundraised. But fundraising for FROs is a bottleneck that few presently pass. The BBN model empowers talented, practical individuals to get in the game using a scrappier model. We believe that by lowering the barrier to entry, in five years, dozens of BBN teams could be founded each year. That means dozens of founders or technical leads setting out on the path towards their ambitious technical vision in a research environment that is both resonant with their goals and cost-offsetting.

Stated plainly: the goal of The BBN Fund is to enable the work of the next J.C.R. Licklider. And based on the exceptional results of BBNs with ARIA so far, we believe this is a realistic goal.

(For a thorough piece synthesizing the BBN model, see A Scrappy Complement to FROs: Building More BBNs.)

Stage 1: BBNs’ Success with ARIA

Stage 1 of the BBN experiment sought to verify the demand for BBNs from modern customers and the supply of talented potential founders. The UK’s Advanced Research + Invention Agency (ARIA), led by fellow metascience nerd Ilan Gur, was singularly important in running this stage of the BBN experiment. But Ilan and ARIA were not specifically trying to run this experiment. They were just trying to find some way, as Ilan might frame the goal, “to find the right people, in the right institutional environments, with the right incentives” to drive ARIA’s technical agenda forward.7

ARIA’s flexible procurement rules made this possible. Its Programme Directors (PDs) are empowered to make large bets — even multi-million dollar bets — on orgs that are young or brand-new, run by individuals ARIA feels are the best on Earth to get a job done. How flexible were these policies, exactly? As Ilan proudly shared when I interviewed him for Asimov Press, when individuals like postdocs fill out ARIA grants, ARIA has taken the unusual step of enabling them to check a box that allows them to accept the grant as new, independent research orgs. They can staff themselves with multidisciplinary researchers and engineers, negotiate contracts without involving university admins, tackle projects academia does not incentivize, pay people market rates, etc. In essence, they can spin up BBNs.

Less than two years into funding R&D projects, ARIA-funded BBNs are performing exceptionally. To contextualize how exceptionally, I’ve put together the following table using the agency’s recent fiscal year data. The table seeks to answer the question, “If the few BBNs in the ARIA ecosystem were a university, how would the ARIA funding they win compare to other UK universities?” The answer: BBNs won more ARIA contracts than every university in the UK except one, outperforming even the University of Cambridge.

Amodo Design — whose CEO will write a guest post in this series — was, on its own, neck-and-neck with the University of Oxford. And excluding Amodo, the rest of the combined set of BBNs still won more contracts than top universities like the University of Edinburgh. And more BBNs are coming. Syntato, an ARIA-funded BBN with a technical ambition to build an ARM chip design for plants — whose proposal you will read in Week 3 of this series — was not even included in this data, for example. While any specific ranking in that table should be taken with a grain of salt — contract award data is lumpier than reality — the fact that BBNs immediately find themselves in the mix with the UK’s historical research giants is a major early data point indicating that BBNs might have as big a role to play in this century as they did in the last one.

The question is no longer, “Is there any demand for BBNs from modern funders?” Stage 1 of the modern BBN Experiment has been completed. Ilan Gur and the team at ARIA — in their search to have their problems solved by aligned R&D groups — have seen to that.

Momentum is building. ARIA has even set aside a yearly pot of £400k for a program with Renaissance Philanthropy to help found and scale BBNs aligned with ARIA’s goals. Several individuals from ARPA-like agencies in other governments have also begun reaching out to discuss similar programs to serve their own needs. Most importantly, the BBN founders themselves — a boundless source of ideas — are constantly finding ways to reach new types of customers — from hedge funds to academic labs — that can preserve their technical ambition and pay the bills. The time is ripe to undertake Stage 2 of the BBN experiment: the BBN Fund.

Stage 2: The BBN Fund

The BBN Fund will act as the vehicle to orchestrate this experiment in “applied metascience.”8 Our focus will be to help build more and more ambitious BBNs. In operating this experimental, nonprofit fund, we plan to deploy funds in ways that answer questions relevant to BBN-curious funders — both nonprofit and for-profit. How technically ambitious can BBNs become with a modest amount of undirected R&D grants? Under what circumstances can investments in BBNs not only push the frontier of scientific progress, but also beat index fund returns on a risk-adjusted basis?

We plan to answer questions like this with economy and speed. The capital we raise will be used to seed BBNs, and we will learn, by doing, how to found and manage BBNs in the modern era.9 The two levers we will rely on to do this work will be the time of BBN Fund staff and capital from the BBN Fund itself. The rest of this section will summarize our approach to using both.

Capital Deployment

An exciting characteristic of BBN founders is their ability to balance practicality and grand ambition. From day one, BBN founders design their org with practical realities, such as customer sales cycles, in mind. But even with practical planning from the founder and a set of aligned customers, several financial problems hamper the creation and growth of BBNs. The BBN Fund will leverage three financial instruments to overcome these problems. Each instrument, in its own way, will enable us to leverage the practicality of the BBN model to stretch R&D funding dollars abnormally far.10

But before discussing these instruments, let’s talk about the problems. The first is temporary cash flow problems. Even if a new BBN wins some contract, it may have cash flow problems for several months (at least), as contract expenses are often front-loaded. The second problem is startup capital needs. Many BBNs will require a modest injection of funds — the equivalent of a seed round — to do the technical and operational work necessary to become self-sustaining organizations.11 The third problem is ongoing research funding needs. For many BBNs, the flexibility provided by winning something like ~20% of their budget as undirected, NSF-style R&D funds — for investigations, core technology development, etc. — can make the org ~twice as technically ambitious.

The three financial instruments the BBN Fund will experimentally deploy to help founders overcome these problems are low-or-no-interest loans, revenue-sharing investments, and undirected R&D grants. While loans and revenue-sharing agreements are peculiar instruments in the world of philanthropy, we believe they might enable us to stretch a fixed pot of capital exceptionally far. Below, I describe the promise of each instrument in more detail.

A Revolving Loan Fund. Low-or-no-interest loans with no collateral requirements will enable far more founders to spin up BBNs. Several existing BBNs had to bootstrap, including Amodo Design. That is admirable, but presents a barrier to entry for many prospective BBN founders, limiting the scalability of the model. Judiciously applied, low-interest loans can provide instant access to capital to cover the salaries, equipment, leases, and other expenses BBN founders have to pay upfront to win and execute contracts. These instruments will have the same limited downside risk for founders as VC funding. Given out as loans instead of grants, the revolving loan fund offers the opportunity to spend dollars multiple times. Any repayment above 0% will drive a higher ROI than the status quo. That being said, with prudent decision-making, most of the capital loaned out can be paid back into the fund — many BBNs asking for loans will have a high payback rate, as they will already have warm contract leads. In the case where ~80% of funds loaned out are revolved back into the fund within 18 months, we can create ~five times as many BBNs using a fixed pot of capital, compared to deploying the funds as undirected R&D grants.12

Revenue-Sharing Agreements. The BBN Fund will experiment with BBNs as an investable asset class. We will identify scenarios and strategies in which investing in BBNs can be attractive to certain private investors and philanthropic funders. In my discussions with BBN founders, revenue-sharing agreements have been the most common category of instrument proposed to facilitate these investments. And I have yet to meet a BBN founder who, for a fair price, is categorically against partnering with a for-profit investor, sharing the upside with them. To lower the barrier to engaging in these revenue-sharing agreements, the BBN Fund will design a fit-for-purpose, YC-SAFE-style instrument to facilitate these agreements. Ideally, this instrument would allow the following deal terms to be customized to match any given situation:

• Percent of Revenue Shared

• Revenue Base (i.e., is revenue calculated from overall revenue, a certain line of business, etc.)

• Sunset Clauses (e.g., no payments after 8 years, once 5x the original investment is paid back, no sunset, etc.)

• Grace Period (e.g., no repayment expected for first 18 months)

Even in cases where the returns on these agreements do not outperform index funds on a risk-adjusted basis, they can still prove to be an exceptionally cost-effective tool for philanthropists and impact investors.

Undirected R&D Grants. Many BBNs require modest levels of undirected R&D funds to effectively pursue their technical visions. These funds do not need to be the majority of their budget, but can often be in the range of ~20%. This minority of funds, and the flexibility they provide, can be vital in differentiating the work of certain BBNs from a typical, unambitious contract research organization. While it will only be a minority of the fund, when it is cost-effective, the BBN Fund should deploy undirected R&D grants to BBNs. One exciting characteristic of even this ‘free money’ is its relative cost-effectiveness when compared to undirected R&D grants to labs that don’t take on contracts. E.g. If a BBN can fund ~80% a course of R&D via contracts that other groups would have asked philanthropists or the NSF to wholly fund via undirected grants, the extra ~20% in undirected grants needed to top off their budget should come as an obvious bargain.

Through our efforts, we hope to make BBNs a legible vehicle for investment for both philanthropic funders and for-profit investors. While we are a nonprofit fund that will reinvest any revenue-sharing profits into BBNs, we hope as many types of BBNs as possible prove to be profitable. That is because one of our goals is to stimulate a BBN investment market into existence. Profitable investments from our portfolio will serve as a proof-of-concept to investors that certain types of BBNs are a profitable asset class. And in those areas in which funding BBNs carries a negative profit margin, and seek philanthropic backing, we will obsess over cost-effectiveness all the same. We aspire to become one of the most cost-effective forms of scientific philanthropy on Earth — the group that, while ruthlessly selecting for ambition, still found a way to spend each dollar multiple times.

BBN Central Office

If the goal of the BBN Fund’s capital deployment is to create and amplify the ambition of BBNs via financial investments, BBN “Central Office” will do so through the direct effort of a small group. This group — Janelle and I for now — will be the hub of BBN field building, dedicated to addressing the non-financial bottlenecks that currently limit the growth of the BBN ecosystem.

In many ways, Central Office will be looking to scale and expand on my own field strategy efforts over the past year. At Renaissance Philanthropy, wearing my BBN field strategist hat, I spent significant time on the following tasks:

• Sourcing new BBN funders and customers, helping them understand which of their problems are BBN-shaped, and how I might source a BBN founder to solve those problems.

• Cultivating new BBN founders, finding exciting founders with aligned ambitions, and helping them understand that a BBN might be an exciting vehicle in which to pursue their life’s work.

• Field Building. In addition to my ARIA work, I’ve been able to use FreakTakes as a vehicle to excite readers — some of whom inhabit important positions in the R&D ecosystem — about the possibilities of the BBN model. This has driven an increasingly impressive flow of founders and funders my way, as well as helped bring existing BBNs together under one banner, with one common vocabulary.

Through my and Renaissance Philanthropy’s field strategy efforts, we’ve already had a hand in unlocking over $10 million in funds for BBNs.13 Our goal is for every dollar spent on BBN Central Office to unlock 10X as many funds from other customers and R&D funders through similar efforts. So far, we’re on track.

Scaling the above tasks will include accomplishing key goals like ensuring that, for every BBN founder, every aligned ARPA-style PM or philanthropic grant officer on Earth is one warm introduction away, and ideally is briefed on what BBNs can do for them before calls for funding go out.14 We’re excited to find ways to tackle these problems. In addition, we will concern ourselves with a variety of other bottlenecks that repeatedly come up when talking to founders. Each could unlock an order-of-magnitude more capital for BBNs than they cost to address. A sample of these tasks includes:

• Sourcing aligned, practical mentors. While BBNs are meant to be far more ambitious than typical contract research organizations (CROs), some have CRO-like revenue streams. That’s great, if it can fund their technical vision! But there’s a problem: many PhDs from places like MIT have never met anyone who runs a CRO. As top researchers now look to build BBNs in this area, we need to find mentors to show them the ropes.

• Sourcing aligned contractors. Similarly, Central Office will establish relationships with individuals needed to make commercial sales. Some BBNs have floated the idea of selling data from instruments they build to commodity traders, to offset costs. If this proves to be a common need, we will find data brokers who can explore and facilitate these contracts.

• Unlocking NSF-style grant funding. NSF and NIH grants can prove to be reliable sources of R&D funding for BBNs. But accessing NSF-style funds is not yet as straightforward as it should be. Certain BBNs claim they cannot win NSF grants at the rate they did at universities. One advisor believes this might be a problem of know-how, and is eager to work with a few BBNs to try to increase their win rate in applying for these grants.15

One way or another, it is our job to solve these problems for BBNs.

Small Teams, Large Shadows

The biggest upside of funding BBNs is not even their cost-effectiveness, but their potential to unlock categorically different research than existing institutions can provide. The original BBN delivered the first four nodes of the ARPAnet on time and under budget, for approximately $8 million today. This was a contract that companies like IBM ‘no-bid’ because they thought it was impossible. Early CMU’s autonomous vehicle teams accomplished technical breakthroughs that DARPA’s prior prime contractor failed at with 10x their budget.

The 20th Century’s great BBNs demonstrated that in R&D, with a differentiated model, small teams can cast a large shadow. Charting their own research path with a mix of contracts and grants, BBNs have a measure of freedom to direct their research agendas towards differentiated outcomes — with no worry for what’s unpopular in academia or ill-suited to venture incentives.

For years, I’ve obsessively studied historically-great R&D operations of many shapes and sizes. Based on my experiences with BBN founders and customers this year, I believe the BBN model can be a vehicle for the right founders, in the right situations, to fund a range of these orgs into existence. This includes:

• Bootstrapping new academic departments. The BBN model can enable founders to bootstrap (what are essentially) new academic departments into existence, outside the university.16 17 18

• Funding industrial R&D labs into existence. BBNs are, in many ways, self-sustaining frontier labs. Under the right circumstances, the BBN model may prove to be a way to make a dent in the problem of funding more groups like early DeepMind into existence — without the pressure to appease investors and exit to a high bidder.19

• An alternative approach to deep tech VC. With a bit of taste, we might demonstrate that investors can reliably pick modestly profitable firms when making revenue-sharing investments into BBNs. If savvy investors can reliably identify 3x outcomes, with 20x outcomes from time-to-time, a world of possibilities opens up in which BBNs can not just beat index fund returns from a financial perspective, but fund wildly ambitious R&D projects along the way.20 (Janelle will dedicate next week’s post to painting a picture of this possibility.)

The BBN Fund is being created to run this experiment and find out what’s possible. If the model proves capable of creating any of these types of orgs, in bulk, that would be a big deal. As of now, we believe the model might be capable of doing all of the above, at least some of the time.

While the Midwesterner in me blushes to speak of grand ambitions, in philanthropy, I believe ambition is a moral duty. We will not aim small. Our ambitions, over the long run, should be measured in metrics like Turing Awards per dollar, number of BBNs doing the most interesting work in their area, or the number of entirely new industries created. If the NSF and NIH annually spend $50 billion to return ~4 Nobel prizes, we will strive to be 100x as efficient.21

These are grand goals, but they are not crazy goals. The $8 million spent on the ARPAnet seems to be less than 1% of that year’s NSF budget. CMU’s initial NavLab vehicle breakthroughs were done for ~1/1000th of that year’s NSF budget. These were exceptionally cost-effective uses of R&D dollars — maybe some of the best in the history of US public R&D — and they were done by BBNs.22 Let’s build more of them.

If you are an interested funder, customer, or aspiring BBN founder, please reach out — eric.gilliam@renphil.org and janelle.tam@renphil.org, or dm me on Twitter.

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As always, thank you to my faithful editors, Toren Fronsdal and Tristan Wagner. They have edited this and every other FreakTakes piece. Every piece would be longer and less intelligent without them.

And thanks to Adam Marblestone,23 Tom Kalil, Janelle Tam, and Tom Milton for each —in different ways — changing how I conceptualize what might be possible with the BBN model.

If you’d like to read more about R&D groups from history that worked in BBN-like ways, or with lessons to teach modern BBNs, check out the following FreakTakes pieces. Each paints a picture of how orgs fueled by contracts can raise the ambition of the R&D ecosystem.

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

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

• Edwin Cohn and the Harvard Blood Factory, for Asimov Press

• A Progress Studies History of Early MIT— Part 2: An Industrial Research Powerhouse

• ILLIAC IV and the Connection Machine24

• MOSIS: The 1980s DARPA ‘Silicon Broker’

• Managing Lockheed’s Skunk Works

• How did places like Bell Labs know how to ask the right questions?25

I met Alex last month at the ARIA Summit. At the Summit, I got to spend several days talking with ARIA staff, incoming PDs, and ARIA ‘Creators’ — ARIA’s word for R&D contractors. My discussions with the ARIA creators and incoming PDs who read FreakTakes were particularly informative. In these discussions, we were able to quickly get into the weeds on ideas explored on FreakTakes that these researchers had already read, considered, and about which they had practical thoughts they wanted to discuss.

My brief interaction with Alex was one example. Alex attended a session at the Summit in which we discussed not just the possibilities for BBNs in the ARIA ecosystem, but the practical financial problems BBNs might encounter. Several days after the session, Alex reached out because he had drafted a blog post outlining his understanding of the financial problems and several concrete ways they might be overcome.

I loved Alex’s framing of the problem and shared his excitement to move the brainstorm into a public forum. I quickly shared a summary of Tom Kalil’s thoughts on the four biggest financial hurdles great BBN founders would need to deal with, and, with that, told Alex I’d be happy to hand over the reins to FreakTakes for the day.

I’ll let Alex take it from here!

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Wanted: New Instruments to Fund BBNs

By: Alex Obadia

BBNs are entities that provide services critical to R&D breakthroughs. The acronym ‘BBN’ (coined in this blog!) comes from a famous example — Bolt, Beranek, & Newman, which was instrumental to the creation of ARPAnet. BBNs are often compared to Focused Research Organizations (FROs) because they’d attract similar people. But while FROs require significant funding, BBNs would be the consulting-ish approach to FROs, contributing to R&D by servicing others in need of R&D support.

Like FROs, BBNs do not fit into purely the academic funding bucket, nor do they fit into the VC funding bucket as they’re not aiming to make heaps and heaps of money. Rather, they want to do impactful R&D in an organization that can stand on its own. The closest type of org that I use to conceptualize BBNs is simply a traditional business, but with a focus on frontier tech and R&D, which is not traditional — hence the need for a new name for them!

In a sense, BBNs are a more realistic FRO — one where someone can get started building ~today instead of looking for altruistic funding. One (imperfect) analogy to think of them: FROs are like venture-backed startups, BBNs are bootstrapped startups.

At last week’s ARIA Summit, I attended a workshop on the topic of BBNs led by Eric. While the conversation was initially focused on unearthing what BBN-shaped problems exist out there, it quickly moved to a more “horizontal” focus on whether there are any organizational or coordination innovations that could enable more BBNs — much like the YC SAFE was a coordination technology that allowed early stage startups to raise unpriced rounds easily on standardized founder friendly~ish terms. (And similarly, their series A template).

A few ideas flew around, such as the possibilities of new legal entities like Asterisk Labs’ cooperative model or a standardized university grant contract to make it easier to fund academic researchers rather than the lengthy back & forth with universities on terms — sometimes creating a period of multiple months between getting the “yes” on funding to getting any money.

One idea that stuck with me — and hence why I am writing this post — is the idea of an R&D lending facility [1]. While BBNs seek sustainability (i.e., to make more money than they spend), just like other businesses, they have capital needs that sometimes do not match their inflows from contracts and grants. Four foreseeable categories of problem that might stand between exciting BBNs being founded or continuing to exist include:

• (Temporary) Cash Flow Problems. The BBN has won some contracts/grants, but will have a cash flow problem for at least several months.

• Startup Capital Needs. Some BBNs might be very solid operations if somebody could buy them some expensive equipment they need to get started. E.g., a BBN that brings in contracts via a CRO-style service might need a $500k mass spectrometer to get going.

• Rainy Day Fund. Many BBNs might require rainy day funds in the case that contracts or grants in some area temporarily dry up, for one reason or another.

• Risk Capital Needs. Just about all BBN founders could use a more robust risk capital budget to pursue their ambitious technical visions. For a large percentage of existing BBNs, something like ~30% of their budget existing as undirected funds for ambitious investigations or core technology development could make them something like twice as ambitious. [2]

I can already hear you say, “We have SME loans already.” That’s true. Yet it turns out that today’s system may not be fully equipped to lend to this type of org. [3]

And so the question becomes: Do there exist 3-4 key financial products that are widely needed among budding BBNs and require an R&D-knowledgeable lender to price risk (and therefore premiums) appropriately? [4] If the answer is yes, and if we can spec out those products, it could allow us to fund BBNs outside of solely philanthropy, and to potentially create a set of new financial products (R&D bonds anyone?), that can be bought by the public, allowing a thousand BBNs to bloom.

Once upon a time, dividend-style arrangements fueled the ambitious building and expansion of things like canals and electric utilities in early America. While times and the state of finance have changed, the lessons of these groups in financing work that was ambitious might be evergreen.

To get the brainstorm started, Eric and I put together some concrete ideas, past experiments, and additional context in the footnotes. Have a look! Eric is hoping to figure out what it might look like to raise funds and pilot solutions to each of these problems, and he's eager for your input.

If you’re a would-be BBN who could use some of this funding, a BBN who wishes these products had existed when it started, a funder interested in piloting solutions to these problems, a lender who groks deep-tech risk and has a good idea of what these products could look like, or are simply enthusiastic about the topic, Eric and I would love to hear from you! Reach out at gilliam@renphil.org or on Twitter.

Thanks to Eric for letting me guest post on his blog and helping shape the post, and to Tom Kalil, Ilan Gur, and Tom Milton for their suggestions and reviews!

Notes

[1] From Ilan Gur, the CEO of ARIA, founding PM at ARPA-E, and founder of Activate:

We prototyped this at Activate — we called it a “working capital fund” for early science-based startups. The implication for this sort of working capital fund is much bigger than BBNs — it’s any research based startup that is pre-venture or not venture aligned, and especially low risk capital for those that have been awarded a grant from a reputable org (that pays in arrears) — that’s one of the big reasons we did this at Activate i.e. because our fellows were winning lots of grants but didn’t have working capital because they hadn’t raised yet.

[2] From Tom Milton, CEO of Amodo Design. Amodo is a BBN-style org doing exceptional bioengineering and electrical engineering work for ARIA. Tom says:

Today, the paths for this are A) retained earnings/profits, B) traditional external funding, and C) sometimes raising VC funds. Some examples: A) Argon&Co used its retained earnings to develop its own IP and spends ~30% of their time running their own projects, B) applying to an ARIA funding call, C) Cambridge Consultants launching a $10m spinout fund that invests exclusively in the technologies they’ve developed in-house

[3] From Eric, purveyor of FreakTakes:

I view the question of whether SME loans can be used to found new BBNs to be a hole in our knowledge; it’s the kind of hole we hope this piece might help fill. To this point, no BBN founders I’ve come across (that I can recall) have leaned on SME loans. Whether this has been because a founder did not wish to put personal assets at risk or there did not exist a lender technically savvy enough to price the deal appropriately, these instruments have simply not yet been an enabler of new BBNs thus far. If there’s someone out there eager to help us figure out how to use existing instruments/loans differently to act as enablers for BBNs, that’s great! E.g. I can imagine some Will Manidis-type, obsessed with bespoke banking stuff, maybe having an idea.

[4] From Tom Kalil, CEO of Renaissance Philanthropy. The following are some of Tom’s (paraphrased) suggestions to the problems listed above, to get your creative juices flowing:

• Revenue-Based Finance. Instead of fixed payments that may hamper a young BBN or prove too risky, loans are repaid as a small percentage of monthly revenue. This aligns the incentives of the lender and the BBN — the lender obtains revenue if the BBN does. These loans would often include a grace period to allow the BBN to find its footing. There may also be some reasonable repayment cap (e.g. 5X the principal) or time horizon in which payments are no longer owed (e.g. 8 years), depending on what is desirable for both founders and investors.

• Low-Interest Loan. A below-market rate, low-interest loan from a philanthropy or government agency. The purpose of the loan would be to help fund one-time, start-up costs involved in creating a new BBN or a new R&D capability within a BBN. While this pool of capital would not achieve the financial returns a private market investor might look for, it’s an exciting way to stretch a pool of philanthropic capital much further than it might go as individual grants. Given a BBN’s goal to both pursue ambitious work and substantially offset their costs in the process, low or no-interest loans from philanthropic entities might be a natural, capital-efficient instrument to catalyze new BBNs.

• Revolving Door Loan Fund. This instrument would help solve the 'grant-to-cash' gap. A BBN may win a major grant, but the first payment is months away. This fund provides immediate access to capital to cover salaries, equipment, a lease, and other expenses. When the grant money arrives, the BBN repays the loan, and that capital is “revolved” back into the fund for the next BBN facing a similar problem. This instrument acts as a crucial liquidity bridge, smoothing out the lumpy reality of R&D funding.

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By "exceptional," I mean contractor groups who were not just staffed with elite talent, but uniquely aligned with ARPA’s mission. All three aforementioned ARPA success stories had contractors — which DARPA calls performers — that shared three distinct traits, rarely found together. Each performer:

1. Was novelty-seeking, with a strong preference for projects that pushed the technological frontier forward substantially.

2. Built useful technology for actual users. This entailed professional contract management and a willingness to focus on difficult systems engineering tasks.

3. Used more flexible team structures than academia. When compared to academia, they more effectively hired, organized, and incentivized researchers, engineers, and other experts to collaborate on applied projects in a common-sense fashion.

I call orgs that check all three boxes BBN-model orgs — named after Bolt, Beranek & Newman (the ARPAnet contractor). In this piece, I make the case for the BBN Model and why it can be a fantastic complement to the FRO Model for the R&D community.

In the first section, I outline how BBNs compare to FROs and the bottleneck they address. In the second and third sections, I'll summarize how historically-great DARPA performers like BBN and CMU's early autonomous vehicle teams used the approach to set themselves apart from other academic departments and firms. In the fourth section, I'll list examples of problems this model is optimized to pursue and briefly discuss what is needed to get BBNs off the ground.

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I've limited the scope of this piece to simply introducing the concept of BBN-model orgs. While this approach does not apply to every area of R&D, the idea is already finding traction with a small number of founders and funders. Just last week, a bootstrapped BBN, Amodo Design, was made one of nine ARIA activation partners — alongside groups like DeepMind and Convergent Research. I’ll share more details about Amodo and other aspiring BBNs in coming pieces. In the meantime, if you are an entrepreneurial scientist or philanthropist who would like to discuss this topic, please reach out (egillia3@alumni.stanford.edu).

Thanks to Thomas Milton, Corin Wagen, and Adam Marblestone for their comments and ideas on the draft.

BBNs: A Complement to FROs

In 2022, Adam Marblestone et al. published their now well-known Nature piece detailing the vision for Focused Research Organizations (FROs). The team made clear the problem they planned to address:

Our goal is to create a model to support an ecosystem of small-to-mid scale projects that fall between the cracks of what start-ups, academia and other organizations do.

The authors paint a picture of time-bound, nonprofit R&D startups wholly funded to pursue a well-defined goal — usually to build a specific thing like a dataset or tool. They point to "grand projects" like the Human Genome Project, Large Hadron Collider, Hubble Telescope, and Human Cell Atlas as having similar goals. Less than three years on from that piece, Convergent Research has brought six FROs into existence (and counting). Adam and the team have proven that you can recruit teams of the very best researchers to join these orgs, make them high-status, and get the operational scaffolding in place to begin doing great work with minimal delay. Convergent’s experiment in scientific structures is off to a great start.

But fundraising is a clear bottleneck to the creation of new FROs — often costing $20 to $100 million. There is, of course, an upside to this tradeoff. FROs raise so much money upfront to ensure they will have all the money they need to pursue their vision from day one. But until groups like universities or the NIH are convinced to set aside substantial war chests to fund and run FROs, fundraising will continue to be a bottleneck to FRO creation. In the meantime, many with the talent and technical vision to found and run FROs will not be able to do so if they are not one of the lucky few to complete a successful FRO fundraise.

BBNs offer an alternative path for these talented individuals. BBNs raise less money upfront than FROs. Instead, they heavily incorporate a contract research approach to build towards the ambitious technical vision of their founding field strategist. They can operate as firms or nonprofits, drawing on a mix of R&D grants and contracts to fund their technical agenda. Project by project, BBNs can make strides in key areas of R&D — as BBN did with real-time computing and the CMU teams did with autonomous vehicles.1 The approach limits BBN founding areas to those in which funders are eager to pay for contracts aligned with some ambitious technical vision. But where those markets do exist, BBNs can be spun up for an order of magnitude less upfront capital than FROs in many cases — some might even be bootstrapped.

The downside is that this introduces a level of ongoing financial risk that is not present in FROs. Founding a BBN is not advisable if you can successfully fundraise for an FRO or have an offer to run a team at the Arc Institute. Those are more stable options. BBN founders may need to be a bit scrappy or creative in their revenue strategies to survive and expand. They might have grand ambitions on the scale of FROs or the Arc Institute, but they must begin with plans that, in the beginning, operate on the scale of an NIH grant, philanthropic grant, or DARPA contract. But if done well, as with FROs, the BBN model can enable a “critical mass of scientists, researchers, and managers” to assemble and pursue ambitious R&D agendas outside of the university.

BBNs offer ambitious field strategists a chance. With BBNs, the chance offered by some contracts and a bright team can be leveraged to world-changing effect. While BBNs might even compete for the same contracts as groups like Raytheon, what differentiates the two is that BBNs are steered in ways that prioritize an ambitious technical agenda over revenue-maximization. This can be tough, but it can be done. The early career of the original BBN’s first computing field strategist, J.C.R. Licklider, demonstrates this. His steering of the BBN computing portfolio provides a clear example of how the BBN approach — with the right field strategist, team, and contracts — can drive an exceptionally ambitious R&D agenda.

BBN’s Computing Agenda: A Mix of Grants, Contracts, Talent, and Vision

BBN was founded in the 1940s. It began as a psychoacoustics R&D firm spun out of MIT by two professors. The firm began as a way for the professors to take on large contracts that were cutting-edge, but too involved to pursue in their own labs — concert hall design for the UN, cockpit design R&D for the Navy, etc. Over the next decade, the firm opportunistically expanded. Hiring for their firm as if they were staffing an academic department, the rule of thumb was to only make hires that would “raise the average level of competence of the firm.” In the late 1950s, the BBN partners looked to expand into computing. They believed J.C.R. Licklider was the best person to lead this effort. Licklider had a clear vision for the near future of computing. It was a vision that might have been too engineering-heavy to be optimally pursued at MIT.

BBN offered an interesting alternative. The firm had carved out a useful niche for itself, with a comparative advantage in projects that required both:

1. Cutting-edge academic knowledge

2. Professional engineering work or contract management

Licklider, a man of impressive vision, saw the administrative scaffolding BBN provided and believed it could be used to pursue his technical vision of real-time personal computing. This technical agenda — quite different from the batch-processing paradigm then in vogue — would require substantial engineering improvements in computing interfaces and real-time computing technology. Licklider left his tenured position at MIT to join BBN. Under his leadership, BBN’s computing efforts would go on to earn BBN praise from many former MIT researchers, later being described as “the third great university of Cambridge,” “the cognac of the research business,” and the true “middle ground between academia and the commercial world.”

A field strategist with an infectious sales pitch, Lick would gradually convince many MIT, Harvard, and Lincoln Labs researchers to defect and join BBN. This included a core of rare real-time computing experts, many of whom came from Lincoln Labs. While MIT and Lincoln Labs were great research environments, many who defected to BBN felt the nature of academia forced them to leave their best ideas as under-developed prototypes or “applied” ideas in papers. Many of these individuals — more engineers than pure researchers — would have felt their minds were wasted at a large firm like Honeywell. But BBN offered an interesting alternative to them as well. They could simultaneously work on the hardest problems and build useful technology.

Licklider convinced BBN to provide funds for computers that were relatively generous by the firm’s standards, but quite small given the scope of his ambition. The work began with a $30,000 Royal McBee ($300,000 today). Licklider soon convinced the BBN partners to buy another, more powerful machine that he felt would be more useful. After this second purchase, Licklider immediately proved the partners’ confidence in him was well-placed. One BBN founder described how seamlessly contracts fell into place following the second purchase, writing:

Lick and I took off for Washington D.C. to seek research contracts that would make use of this machine, which carried a price tag of $150,000 (~$1.5 million today). Our visits to the Department of Education, National Institutes of Health, National Science Foundation, NASA, and the Department of Defense proved Lick’s convictions correct, and we soon secured several important contracts.

Licklider’s computing group routinely found creative ways to offset the costs of investigations aligned with their technical agenda. Some of the group’s revenue came from relatively typical academic funding sources — federal research grants, a NASA contract to use the group’s computer to produce a textbook, etc. But BBN also took on much more applied contracts, well-suited to the group’s embrace of engineering and project management tasks. I’ll briefly describe two of these applied projects that took advantage of BBN’s comparative advantages. Both helped lay the groundwork for now-famous technical breakthroughs.

The first of these projects was BBN's Libraries of the Future Project. The project, indirectly funded by the Ford Foundation, sought to understand how computing might impact libraries moving forward. It was a contract for a philanthropy that, today, might go to a consulting firm like the Bridgespan Group. But in this unassuming contract, Lick saw an opportunity. The BBN team won the contract and used it as an excuse to explore seemingly futurist technology and make practical engineering improvements. As one example, the second half of the group’s book-length report for this unassuming contract contains technical explorations that attempt to emulate a future in which users interact with the library as a store of knowledge with a question-answering front-end, not as a way to find books. The final report also contained early work related to PC file systems, improved information retrieval methods, mathematical representations of information, and associated hardware improvements — all paid for by this unassuming contract. The opportunities to further explore and translate academic ideas via this contract proved attractive to other researchers in Cambridge. On this project alone, Marvin Minsky, John McCarthy, and Fischer Black all spent time working with the BBN group.

The second of these projects was built on a contract to develop a usable real-time computing system in a presciently chosen application area: hospital administration. The contract came about because a BBN partner made a compelling pitch to the NIH Clinical Center’s Director that hospital administration would be done using computers at some point. The director was convinced and had the partner write up a proposal for BBN to begin developing and building a computing system to pilot with a research hospital. The BBN hospital time-sharing computer project provided the firm with three years of funding, worth ~$10 million in total today. The contracting relationship would continue for several additional years, growing into an actual system deployed in the operations of Massachusetts General Hospital. With the contract, BBN was able to fund years of work a bit too far along for academia but not close to private-market-readiness. The contract required far more contract management and engineering work than would have been reasonable for a university team — they had to continually reduce machine error rates, install and maintain terminals at the hospital, coordinate with hospital staff, train doctors, provide customer service, make UX changes, etc. But with this applied work came a sizable budget. BBN’s small team of real-time computing experts used it to push the engineering frontier forward.

By the time Larry Roberts began putting out feelers for the ARPAnet contract in the late-1960s, BBN had been solving all sorts of related problems for years — similar to the ones that had stumped Roberts while he was at MIT. BBN won the contract. The first four nodes of the ARPAnet would be delivered within a year, on time and on budget. But it was BBN’s years of work on related contracts that paved the way for this overnight success.

Nonprofit BBNs: The Case of CMU's Early Autonomous Vehicle Teams

The BBN model can also be operated with a nonprofit structure. The early CMU autonomous vehicle teams — which helped pave the way for the autonomous vehicle revolution — demonstrate this. In another world, these teams probably could have operated with an FRO structure. But in practice, they operated using a model more similar to BBN’s contract research model.

The CMU Robotics Institute was primarily established to build ambitious, practical computing systems. While housed at a university, these CMU teams are more aptly compared to a group like BBN than a group like Marvin Minsky's computer science department at MIT. Contracts were a large part of the Institute’s plans from its inception. The Institute’s early autonomous vehicle group successfully deployed a BBN-style approach on DARPA’s 1980s autonomous vehicle contracts, achieving clear counterfactual impact and developing systems DARPA’s primes and academic labs under contract would not.2

The CMU group had an operational structure and incentives that enabled it to excel on these ambitious, applied contracts. As one example, the Robotics Institute created suitable tracks through which engineering and project management-focused individuals could be hired and tenured just as CMU's best professors would be. Instead of researching and teaching classes, these individuals would research and operate projects. A CMU Ph.D. and one-time project manager for the group’s early autonomous vehicle projects, Chuck Thorpe described the incentives of his role, recounting:

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

The CMU teams also found ways to effectively use the grad students as both project staff and researchers. Requiring dissertation problems of their own they could “sole author,” grad students were assigned components of the system for their dissertation to improve upon. Each project had to easily plug into the larger system. High-risk, high-reward projects still had a place in this structure. If projects were high-risk, project managers like Chuck Thorpe might simply assign more grad students to improve a component to ensure at least one succeeded. A good project might reduce the processing time for data from some sensor 10X. The best grad student project would prove to be world-changing.

In 1988, a sharp grad student named Dean Pommerleau combined his knowledge of CMU’s systolic array machine and neural nets to build a neural net-based steering system for the vehicle — ALVINN. In the following years, the team built this neural net steering system into a new vehicle system. In 1995, with this new system, the CMU vehicle would drive cross-country 98.5% autonomously on its “No Hands Across America” tour.

Getting BBNs Off The Ground

Attempting to found and operate a BBN is not easy. You might fail to raise a required seed grant or win contracts to get off the ground. You might sell a contract funder on your idea but need a partnership with an existing org or philanthropy to get the deal over the finish line. You might win an initial batch of revenue and still have to shut down after a year due to a lack of funds. You might even succeed in raising funds, but raise them from misaligned funders and become a myopic R&D contractor. This is a failure mode all the same; becoming Battelle or Raytheon is not the goal of a BBN. But great field strategists can use the BBN model to turn revenue, people, and vision into what Patrick Collison recently called a “great scene of discovery.” This is what BBN made itself into for real-time computing and CMU for autonomous vehicles.

Building a BBN is a viable, alternative path for those field strategists and scientific entrepreneurs eager to do work in the cracks of the R&D ecosystem. Done well, BBNs can be a force multiplier to investments made by scientific funders, enabling them to undertake projects that are cheaper, better, or different than they would otherwise. This “create the performer” approach still has its uses in the context of modern philanthropy.3 As Jacob Trefethen recently discussed on his blog, the Gates Foundation funds “half or more” of many global health product development partnerships (PDP) budgets because they usefully fill cracks vital to Gate’s global health mission.

But founding BBNs can require overcoming a somewhat delicate coordination problem. While some BBNs can be bootstrapped, many BBNs will require some combination of a low-seven-figure seed grant to get started, contracts, and (maybe) NSF/NIH grants to optimally pursue their research agenda. It takes a bit of talent to overcome the associated chicken-and-egg problems that might arise. Philanthropies might want to provide seed funds to spin up a BBN, but only if they can be assured contracts for R&D projects will materialize. A contract funder like DARPA might require the org actually exist before engaging in some negotiations. OpenPhil might happily provide 60% of the budget for ~2 years for some BBN useful to its mission but require the group to source additional funds and contracts to cover the rest. The list goes on. It’s not an easy path. But if the crack is big enough and a field strategist is proactive enough, these challenges can be overcome.4

But none of this can happen without an ambitious, open-minded contract funder. Funders with the level of vision and ambition of ARIA are ideal. I would encourage funders reading this to ask themselves the question, “Could I take my portfolio to another level if I was able to create a single performer to work in a targeted area?” If the answer is “yes” or “maybe,” you might benefit from a BBN.

BBNs might apply to many areas. Some areas in which BBNs might have natural comparative advantages include:

• Development of new instruments

• Producing bespoke hardware

• Engineering new pipelines to serve a group of researchers

• Building and maintaining research software or datasets

• Pilot-plant style work with the intention to:

  • Scale promising lab bench ideas in manufacturable processes

  • Produce a key research material for labs

• Translation of academic ideas to non-venture markets.

  • One example could be a CivTech BBN that wins city government contracts to both translate the best social science insights into practice and conducts research projects on the org’s internal data.

It’s hard to predict how many areas might benefit from a BBN, but the model offers opportunities for the ideas of special individuals to surprise you. Progress studies funder and Stripe CEO Patrick Collison recently spoke of a similar phenomenon regarding a new Stripe product, tweeting:

We launched Stripe Issuing a few years ago. I wasn't sure how many use-cases there would be — like, issuing a card is surely a pretty niche thing to do. As usual, developer platforms surprise, and customers have now issued a cumulative 200 million cards.

BBN’s idea to bid on the Libraries of the Future project is one example of this cleverness at work. The BBN model has the potential to not just plug obvious cracks in the R&D ecosystem, but create great scenes of discovery in their place. In which cracks these scenes will take hold is hard to predict.

The fact that FROs now exist and are a fixture of the new science lexicon makes the task of coming up with ideas for BBNs easier for field strategists. A good FRO problem is, in many cases, rather similar to a problem for a BBN. Adam Marblestone recently shared one example, explaining that an FRO might arise from a problem like neuroscientists requiring a different kind of microchip. One complex chip solving many life sciences problems is a great example of an FRO problem. But what if many neuroscience applications required many, simpler microchips? That’s a problem well-suited to a BBN.5

Tyler Cowen points to the history of Hollywood as proof that exciting young people can find ways to create exceptional things if given an opportunity to take charge and figure things out. FROs, with their time-bound nature, remind him of Hollywood movies. BBNs, with the scrappy nature of their origins, have the chance to become a vehicle for unproven R&D entrepreneurs to prove they are masters of their craft — just as Tyler believes Paul McCartney did with the Beatles.

It is an exciting proposition. But founders and funders with vision are required to make it a reality.

Thanks for reading.

Please reach out if…

I am already working with a few field strategists who believe they might have ideas for BBNs in areas like automated material discovery, bespoke semiconductor production as test bed hardware for certain areas of semiconductor design, and modifying instruments to enable a wider range of life science experiments. I will release those pieces in the coming weeks. Please reach out if you are a funder or interested field strategist to discuss ideas (egillia3@alumni.stanford.edu or on Twitter). I’d love to help!

I am setting aside as much time as necessary to assist would-be BBN founders and funders. I believe we have J.C.R. Lickliders sitting on the shelf with vision, philanthropists with exciting ideas that are best served by a new contractor, and outside funders who might happily provide the seed funding to catalyze this change. BBNs can be a vehicle to turn this potential energy into action.

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Various ideas and details included in this piece have been explored in FreakTakes pieces on BBN, DARPA’s Autonomous Land Vehicle and NavLab projects, an interview with CMU’s Chuck Thorpe, and how BBNs might apply to new era semiconductor research.

I’d also like to mention that Adam Marblestone listed OtherLab as an org that does great work with a BBN-type model.