Ideas for Biotechnology BBNs

Three projects that might not make sense for venture capital or academia.

Biotechnology is filled with promising young scientists who want to work on big problems, but whose ideas do not neatly fit within academia, venture capital, or even large-scale philanthropy. Academics tend to work within individual laboratories, rather than big teams. And they usually work toward publishable results instead of scalable technologies. (Most papers stop at the proof-of-concept stage.) Venture capital expects large returns within a ten-year period. Focused research organizations take tens of millions of dollars to get off the ground.

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.

Lilly staff packaging insulin in 1923. Thanks to Jake Wintermute for the pointer to the photo.

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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.

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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.