Richard Hamming famously posed a deep question to his colleagues at Bell Labs:

What are the biggest problems in your field? Why aren’t you working on them?1

One can apply Hamming’s question recursively at increasing layers of resolution. What are the most important goals for humankind? What are the most important fields working toward those goals? What are the most important problems in that field?

Why aren’t you working on them?

Here, I outline one such orbit that led me to my own field of therapeutics development, and the key problems that stand between us and inventing an order-of-magnitude more medicines.

Quests of import

Few human endeavours have an impact that persists beyond the scale of a single lifetime2. Progress in science and technology – the accumulation of useful knowledge – is one of the only forces that compounds and enriches human life on the scale of centuries3.

What are the most important scientific & technology problems in our era?

1. Making energy too cheap to meter4

2. Expanding the footprint of humankind beyond a single planet

3. Creating abundant, capable intelligence

4. Increasing the number of happy, healthy years in each human life

There are reasonable arguments for other endeavours to be included on this list, but even this small set captures a large swath of the worthwhile goals.

Creating more healthy time for each individual is perhaps the ultimate goal among these. Even if our species reaches a technological velocity that provides material abundance and the Von Neumann probes are replicating prodigiously among Dyson spheres near each proximal star, each of us will want to live to see it.

Increasing the number of years we have to pursue fulfilling experience and spend with one another will remain the most valuable possible product. Health is an endless frontier.

Health production function

What are the most important problems in the life sciences? How do we create more health?

Our health is roughly the product of (1) the technologies we have to prevent and treat disease in the form of medicines, diagnostics, devices, and sanitation programs and (2) the distribution of these technologies through a healthcare system. If health technology is the dominant variable in the equation, we would expect trends in health and life expectancy to be similar across geographies, despite differing health care systems. We might also expect trends to be monotonic because medicinal technology rarely reverts over time.

By contrast, if distribution is the dominant variable, we might expect that some geographies sharply diverge as a function of superior healthcare systems. We might also expect that these trends are volatile and non-monotonic, improving and declining as the political winds and fiscal vitality shift within a polity.

The data strongly support the notion that therapeutic technology is the dominant factor that determines our health. Life expectancies have increased almost monotonically for the past century5, and this trend is constant across geographies. Despite the dramatically different levels of wealth across the globe, the low marginal cost and rapid diffusion rate of therapeutic technology means that much of the world’s population can benefit from new medicines.

Even the least wealthy geographies are experiencing the same upward trend of progress. The average lifespan worldwide today is nearly a decade longer than the average lifespan of the wealthiest geography in 1950.

Distribution of these technologies is of course an important variable. Therapeutic technology sets the maximum health we can achieve, while distribution sets the minimum.

One way we might further quantify the impact of technology vs. distribution improvements is based on the expected gain in the number of healthy years we might achieve from each. The lifespan gap across geographies due to distribution is on the order of 1 decade. The lifespan gap between the healthiest humans who live to 1106 and the median in the wealthiest geography is 3-4 decades. Most of our latent potential health requires technological improvements to unlock.

Inventing medicines is therefore the most impactful way to increase the number of happy, healthy years in the average human life.

Therapeutic Hamming problems

What are the most important problems in the field of therapeutics? What prevents us from creating new medicines?

I’ll argue that there are three problems with outlier impact.

1. Discovering new therapeutic “targets”

2. Delivering therapies to specific cells & tissues in the body

3. Evaluating more therapeutic hypotheses in humans

Target discovery is critical because in the vast majority of circumstances, we simply don’t know what biological manipulations will be sufficient to preserve health in a human patient. All problems of therapeutic engineering and evaluation are secondary to this fundamental epistemic challenge.

Once targets are known, the largest challenge in building a therapy is delivering a medicine that is sufficiently expressive to the right cells and tissues. Today, our therapeutic approaches each make harsh trade-offs between the axes of penetrance (how many cells are affected), specificity (how many of the right cells vs. the wrong cells), and expressivity (how sophisticated the effect is within the target cells).

Ultimately, both target hypotheses and therapeutic designs must be evaluated for their effect on human health. Our existing preclinical systems (e.g. animal models) suffer from poor predictive validity. What works in these systems rarely works in humans! In order to invent more medicines, we need to collect more data in humans directly. These data will let us both improve our preclinical systems, and test more hypotheses in the most relevant settings.

Others might argue that (1) improving preclinical predictive validity directly, absent more human data, (2) reducing regulatory overhead and development costs, or (3) changing intellectual property and reimbursement incentives are more critical. While there is a case to be made for each of these notions, I think the arguments for our three problems above are far stronger.

Target discovery

Previously, I’ve discussed the target discovery problem at length (see: Creating therapeutic abundance). I believe it’s the most important problem in therapeutics. I’ll refer to this previous post for an in depth treatment of the topic.

tl;dr – The invention of new medicines is rate limited by our knowledge of cells and molecules (”targets”) that we can manipulate to treat disease. The cost of discovering new medicines has increased because the lowest hanging fruit has been picked on the tree of ideas. Emerging technologies at the intersection of artificial intelligence & genomics have the potential to unlock a new era of target abundance, potentially reversing the decades-long decline in R&D productivity. If realized, this will be one of the most important impacts of AI over the coming decades.

At an even more granular resolution, we might ask “What therapeutic targets are the most valuable to discover?” The trivial answer is that the most valuable targets are those that provide the most additional health, for the most people. In practice, this reduces to discovering target biologies for the pathologies of aging that affect every person on the planet.

Effective delivery

Once target biologies are discovered, we need to deliver medicines to the right cells and tissues within the body. This involves building medicines that are penetrant, specific, and expressive.

Penetrant medicines can reach a broad set of cells and tissues. Specific medicines can act primarily on the cells and tissues of interest while avoiding activity elsewhere. Expressive medicines can encode complex logic and interventions, while less expressive, “constrained,” medicines are restricted to blunt modifications. An expressive medicine might activate many genes if and only if a disease-associated gene is also expressed, whereas a constrained medicine might simply deactivate a single gene everywhere at once. Most of the medicines we have today are of the constrained variety.

Penetrance is self-evidently important. If a medicine can’t reach the right cells and tissues, it can’t exert a therapeutic effect! Specificity is critical as well to unlock many therapeutic targets. Biology reuses the same critical molecules across various contexts in the body, so that genes might be more akin to letters or words than sentences in their semantic content [6]. Imagine trying to change the meaning of a book if your only edits were to delete every instance of a given letter. It might be possible, but challenging. Non-specific medicines are a similarly blunt instrument. Specifically acting upon a gene or cell type within a given tissue is much more powerful.

Today, our ability to build medicines that are both penetrant and specific is quite poor. Our ability to create expressive therapeutics is even more limited.

Traditional therapeutic modalities like small molecules, antibodies, and proteins are wonderfully penetrant. They can reach most tissues readily, with a few exceptions like the central nervous system. However, they are mostly non-specific, acting upon their targets across the body without much control. This means that a number of otherwise strong therapeutic targets can’t be drugged effectively with these traditional methods.

Emerging modalities like nucleic acid therapies (RNA and DNA medicines) can often be made specific, but they are rarely penetrant. Most nucleic acid medicines can be delivered only to a handful of cells and tissues today. Addressable cell types for RNA medicines are limited to those where modified RNAs or lipid vehicles like LNPs can travel. Canonically, the liver is the easiest place to target because it’s biologically optimized to filter these types of particles from your circulation. Immune cells and endothelial cells lining your veins and arteries can be targeted with a bit more effort.

The vast majority of our existing medicines are constrained, inhibiting or activating a single molecule or gene without logical gating. Almost all small molecules, protein biologics, and RNA therapies fall into this category. Only recently have the earliest glimpses of expressivity been realized in patients. Multi-specific biologics, combinatorial RNA medicines, and logic-gated cell therapies are now emerging. Nonetheless, we are far from building medicines that match the complexity of the pathologies we hope to treat.

Evaluating hypotheses in humans

The final step in any therapeutic development process is placing a medicine into human patients and measuring if it works. All of the prior steps – in silico simulations, cell culture models, animal studies – are attempting to predict the outcome of this human trial.

All of preclinical development is then a binary classifier implemented with atoms to predict the success or failure of clinical studies. Even clinical studies are binary classifiers to predict success in the real world! Despite this obvious truth, we rarely frame the problem in this fashion or even explicitly measure how well our preclinical systems predict what happens in patients.

Unfortunately, we do know that their performance in aggregate is wanting. ~90% of therapies fail in clinical trials, despite presumably strong ex ante preclinical data. This general phenomenon has been described as a crisis of “predictive validity,” by Jack Scannell and others [Scannell 2022].

Given the poor performance of preclinical models, the value of additional data in humans is tremendous. These measurements can be used not only to directly determine which medicines work, but also to improve our preclinical systems, allowing the returns to compound over time. We can’t hope to improve the predictive validity of our preclinical systems if we don’t even have enough data to measure our performance. Gathering more human data is therefore one of the most important problems in therapeutics.

By the numbers today, our species tests ~3,000 new therapies in humans per year7. Statistically, only ~50% of the new medicines tested in initial safety trials (Phase 1) will succeed and progress to efficacy. This means that only ~1,500 new medicines are tested for efficacy in a given year across all geographies and diseases. There are thousands of recognized pathologies (“indications”) by the US FDA, so we’re effectively testing <1 medicine/pathology/year for efficacy.

It’s difficult for us to improve either our systems of discovery or the absolute number of therapies available given this tight constraint. There are in principle three ways we might collect more human data points:

1. Increasing the number of clinical trials – run more trials of the same form that dominate today

2. Decreasing patients/trial – run smaller trials to test more drugs for similar cost

3. Increasing the number of agents/patient – test more than one medicine per patient

There is a tremendous focus in the industry on increasing the number of trials by cutting costs. Capital is often the limiting reagent for human data generation because most R&D spending occurs in the clinic [Sertkaya 2024]. However, this approach will hit a scaling limit based on other inputs. Clinical trials require not only capital, but patients, clinical centers, and manufacturing capacity8. If there aren’t enough patients to enroll, the marginal cost of a trial isn’t the bottleneck.

We can likely increase the number of clinical trials by 2X through naïve scaling and cost efficiencies, but it seems unlikely we’ll increase by 10X using this approach alone.

Reducing the number of patients per trial would not be beneficial if this resulted in underpowered studies. Rather, technology may enable us to preserve the same statistical power with smaller cohorts. New measurement technologies may allow us to select patients for trials more effectively and provide new endpoints that enable shorter, smaller trials.

As a synoptic example, heart disease trials using a newer biomarker (LDL-C) endpoint are ~10-100X smaller than those using the traditional all cause mortality (“death rate”) endpoint9. If technology can provide superior endpoints for other indications with similar predictive validity, trials become far more scalable.

Least explored among these options is the notion of testing multiple therapeutic agents per patient. In discovery research, pooled screening experiments are often conducted that deliver different perturbations to each cell in the body of an animal. This allows researchers to measure the cell-autonomous effect of many potential therapeutics simultaneously in the same organism10.

As shocking as it may sound, similar studies have already occurred in humans. Lentiviral-based CAR-T cell therapy involves the random integration of a transgenic cassette across millions of sites in the human genome, so each patient in essence receives a mixture of millions of distinct therapies [Biasco 2021]. More directly, CAR- & TCR-T trials have been run where a series of gene edits are introduced at varying efficiencies <100%. The resulting pool of cells then contains all possible combinations of the edits at some frequency [Stadtmauer 2020]. Each cell is challenged to respond to the cancer and grows as a result, so whichever combination of these distinct cell products is most effective has a chance to benefit the patient.

In each of these studies, many assets were effectively tested simultaneously in a single patient.

Cell therapies are a special case where cells are the obvious unit of replication. Nucleic acid medicines like RNA and gene therapies may represent a similar setting. Measuring the effect of multiple small molecules or antibodies in a patient is more challenging because these medicines have systemic effects that can’t be disentangled. There are nonetheless nonclinical settings where pooled screens can be performed in human-like systems regardless of modality [Arap 2002]. Leveraging these approaches could generate as many human data points in a single trial as our entire species generates in a full year, albeit at the cost of less information per asset.

All three of these mechanisms to increase the number of human data points we collect are likely needed. New technology has a role to play in each. I look forward to outlining more thoughts about how to tackle these challenges in a future post.

Coda

We experience but one life. Exceedingly few of our actions will have an impact on the scale of generations, even fewer on the scale of centuries. It’s a gift to contribute toward a goal that will benefit those who follow long after us.

Providing each person with more happy, healthy years is among those rare goals. The beauty of our modern therapeutics industry is that we can awake each day knowing that success is worthwhile, if arduous to achieve.

Medicines are perhaps humankind’s most advanced creations to date. The scientific challenges involved are so great, it’s a wonder that we’ve invented any therapies at all. A few of these challenges – discovering new targets, delivering medicines to the right cells, and measuring the effects in humans – offer an opportunity for impact worth the efforts of a lifetime.

What are the biggest problems in your field? Why aren’t you working on them?

Thanks

Thank you to Stephen Malina, Alex Telford, and Jacob Trefethen for reading a draft of this post and substantially improving the logic.

The invention of new medicines is rate limited by our knowledge of cells and molecules ("targets") that we can manipulate to treat disease. The cost of discovering new medicines has increased because the lowest hanging fruit has been picked on the tree of ideas. Emerging technologies at the intersection of artificial intelligence & genomics have the potential to unlock a new era of target abundance, potentially reversing the decade's long decline in R&D productivity. If realized, this will be one of the most important impacts of AI over the coming decades.

Eroom's law

Gordon Moore famously predicted in 1965 that the number of transistors per integrated circuit would double every two years. The computing industry delivered.

Jack Scannell infamously predicted in 2012 that the number of drugs per billion dollars would decline two-fold every nine years. Unfortunately, our therapeutics industry has largely followed through1.

Why has this happened?

Eroom's law contains within it multiple emerging problems in our industry – rising costs for R&D and declining success rates per drug program.

Rising R&D costs have many sources. A plurality likely trace back to Baumol's cost disease.2 Cost disease applies throughout the economy though, so on the surface, drug development's unique problems might be more directly tied to the high rate of failure for new candidate medicines.

Drug program success rates are equally complex. Failures can be attributed to safety issues, failure of a drug to hit the desired biological target, or improper selection of the target for a given disease.

Ascribing exact values to the frequency of each of these failures is challenging. Most of the knowledge of drug program lifecycles remains locked within drug companies. Nonetheless, we can bucket the failures into a two broad categories of safety and efficacy and make informed estimates.

1. Safety failures – ~20-30% of all candidates
   A molecule was developed, but proved unsafe in patients. These are typically detected as failures in Phase 1 trials.

2. Efficacy failures – 70-80% of all candidates
   The remainder of all drug candidates that fail – 63% of all drugs placed into trials period – fail due to a lack of efficacy. Even though the drugs are safe, they don't provide benefit to the patients by treating their disease.

From these coarse numbers, it's clear that the highest leverage point in our drug development process is increasing the efficacy rate of new candidate medicines.3

This fact shows up clearly in clinical trial results. The plurality of medicines fail in Phase 2 trials, the first time efficacy is measured, the first time we test the hypothesis of whether manipulating a given biological target will actually benefit patients4.

This stands in contrast to some rhetoric in the ecosystem claiming that an undue regulatory burden in the US market (where >50% of revenues arise) is the main challenge holding back drug development. If this were true, you'd expect to see amazing therapies that are available exclusively in ex-US geographies with simpler regulatory schemes. The absence of these medicines suggests that regulatory changes alone are insufficient to fix our therapeutic development challenge, even if they could prove an accelerant.

Rather, our main challenges are scientific. We simply don't know how to make effective drugs that preserve health or reverse disease! If we want more medicines, we need to understand why they don't work and fix it.

Why don't our candidate medicines work?

Efficacy failures can broadly occur for two reasons:

1. Engagement failures: We chose the right biology ("target") to manipulate, but our drug candidate failed to achieve the desired manipulation. This is the closest thing drug development has to an engineering problem.

2. Target failures: The drug candidate manipulated our chosen biology exactly as expected. Unfortunately, the target failed to have the desired effect on the disease. This is a scientific or epistemic failure, rather than an engineering problem. We simply failed to understand the biology well enough to intervene and benefit patients.

It's difficult to know exactly the exact frequency of these two failure modes, but we can infer from a few sources that target failures dominate.

• Success rates for biosimilar drugs hitting known targets are extremely high, >80%5

• Drugs against targets with genetic evidence have a 2-3 fold higher success rate than those against targets lacking this evidence, suggesting that picking good targets is a high source of leverage6

• Among organizations with meaningful internal data, picking the right target is considered the first priority of all programs (e.g. "Right target" is the first tenet of AstraZeneca's "5Rs" framework)7.

The predominance of target failures has likewise led most companies working on new modalities to address a small set of targets with well-validated biology. This has led to dozens of potential medicines "crowding" on the same targets, and this trend is increasing over time8. A recent report from LEK demonstrates just how pronounced this trend has become. As a complement to rigorous academic and market research, simply scanning the pipeline pages of biotechs will convince an interested reader that this phenomenon is very real.

Crowding on known targets is perhaps the strongest integrated signal that target failures are the predominant reason our medicines don't work in the clinic. Many distinct teams of incredibly smart people have aggregated all information available and concluded that target discovery is so fraught, they would prefer to take on myriad market risks to avoid it.

Are targets getting harder to find?

If searching for targets is the limiting reagent in our medicine production function, the difficulty of finding targets must increase over time in order to explain part of Eroom's law. How could this be the case given all the improvements in underlying biomedical science?

In an influential paper "Are ideas getting harder to find?", Nicholas Bloom and colleagues argue that many fields of invention suffer from diminishing returns to investment. Intuitively, the low hanging fruit in a given discipline is picked early and more investment is required merely to reap the same harvest from higher branches on the tree of ideas.

In therapeutics, we can imagine concrete examples to explain how this might be the case. At the beginning of the Eroom's law data series in the 1950s, the most successful new medicines were broad spectrum antibiotics. In the 1960s and 1970s, several new medicines targeted the central dimorphic sexual hormones (estrogen and testosterone agonists and antagonists). The 1980s saw successful antivirals for HIV and early biologics for central signaling hormones (insulin, growth hormone, erythropoeitin).

It's striking from this sort of survey that infectious disease and circulating hormone targets dominated the first several decades of modern drug discovery. These targets are the most obvious examples of low hanging fruit in the industry. Infectious diseases have a small number of genes – making targets relatively easy to find – and their biology is divergent from our own, so they are uniquely straightforward to drug safely. It's easier to find a safe inhibitor of a gene if the gene only exists in a pathogen, and not normal human cells.

Hormones are likewise simple to identify because they circulate in the blood and their levels can be measured longitudinally. They are simple to drug because their structures are comparatively simple and the biology is "designed" for a single molecule to evoke a complex phenotype. Early recombinant DNA companies Genentech and Amgen both chose to develop hormone drugs because the genes were small, and therefore easier to clone and manufacture9.

The common diseases that predominate as ailments today are far more complex. Targets are getting harder to find not because we are getting worse at selection, but because many of the easy and obvious therapeutic hypotheses have already been exploited.

Inventing medicines that match nature's complexity

Accelerating drug discovery will require us to discover "targets" more effectively. Not only will this involve improving our traditional target identification processes, but changing our definition of a target altogether.

Today, we typically conceive of targets as single gene or molecule that we can manipulate to achieve a therapeutic goal. This conception likely needs to be broken to access the metaphorical fruit higher on the tree.

Aging and disease involve the complex interplay of molecular circuits. Outside of infectious and inherited monogenic diseases, there are few health problems that arise as the result of a single molecule that is too high or too low in abundance. Preserving health and enhancing our physiology will require us to match the complexity of our biology with the complexity of our medicines. We need to stop thinking about targets as single molecules and begin to imagine therapeutic hypotheses that rely on combinations of genes, engineered cellular behaviors, and remodeling of tissues.

This point seems obvious. Why haven't we developed medicines like this to date?

The origins of our contemporary targets

Most of our current targets emerged from a stochastic research process. Namely, academic researchers explore the biology of a disease, then eventually identify a molecule that is necessary or sufficient for the pathology to manifest. Each of these molecules are typically proposed through a heuristic process.

Concretely, a scientist sits and thinks hard about the problem, makes a guess at the responsible molecular players based on their intuition, prior art, and their new data, then tests to see if the molecule is causal. The vast majority of these hypotheses are wrong! The few that prove to be correct often become the basis of our modern target-based drug discovery process and several companies quickly launch programs to prosecute them. This approach yielded targets like PD-1, CD19, VEGFR2, and BTK within the sphere of crowded targets today.

Despite its successes, this method has a few key limitations that explain why our current targets are so tightly constrained.

1. The throughput of target:disease pairs tested in this fashion and the efficiency in terms of dollars per target discovered are fairly low10.

2. Given the low throughput, it's nearly impossible to test hypotheses that involve manipulating biology in a manner more complex than dialing a single target all the way up (overexpression, drug-like agonism) or all the way down (genetic knockout, drug-like inhibition). This inherently limits us to discovering targets that are far more reductionist than the actual biology we hope to manipulate.

Distilling natural experiments

The sparsity of target space has been an acknowledged problem in the industry for decades. Shortly after the conclusion of the Human Genome Project, large scale human genetic studies appeared to offer one possible answer to the problem.

Each human genome contains more than a million variants relative to the representative “reference,” genome. These variants serve as a form of natural experiment, one of the only sources of information on the effect of manipulating a given gene in humans.

Given a large number of human genomes paired with medical records, researchers can draw associations between genetic variants and human health. Variants can then be associated to genes, and researchers can discover targets that may exacerbate or prevent a given disease. This approach has successfully yielded some of the now crowded targets in today’s pantheon, including PCSK9.

A whole cohort of companies (Celera, deCODE, Incyte, Millennium, Myriad) was created to leverage this new resource. It might seem surprising at first blush that genetic methods haven’t changed the course of R&D productivity.

While promising, human genetics can only reveal a certain class of targets. The larger the effect size of a genetic variant, the less frequently it appears in the population due to selective pressure. In effect, this means that the largest effects in biology are the least likely to be discovered using human genetics. Many of the best known targets have minimal genetic signal for this reason.

Our current methods are good at discovering individual genes that associate with health, but discovering combinations of genes is nascent at best. Human genetics cannot help us discover the combinatorial medicines or gene circuits to install in a cell therapy.

Sociologically, discovering drug targets with human genetics has become something of a consensus opinion. Most large drug discovery firms have teams dedicated to this approach. This has contributed to the crowding problem, leading many firms to address the same set of targets within the constraints of genetic discovery. These medicines can certainly be impactful, but it seems unlikely that 10+ medicines targeting PCSK9 is the optimal resource allocation for patients.

Building systems of discovery

Is it possible to build a more deterministic, less constrained discovery process? Can we discover target biologies with a complexity matching the origins of disease?

Two technological revolutions argue in the affirmative. Functional genomics methods now enable us to test far more hypotheses than ever before. From the resulting data corpuses, artificial intelligence models can search otherwise intractably large hypothesis spaces, like the space of possible genetic circuits or combinatorial therapies11. By performing most experiments in the world of bits rather than atoms, it’s possible to address questions that were inaccessible to a previous generation of scientists.

Functional genomics use DNA sequencing ("reading") and synthesis ("writing") technologies to parallelize experiments at the level of cells and molecules. Rather than running each experiment in a unique test tube to keep track of the conditions, experimental details are encoded in DNA basepairs within a cell or molecule, then read-out by sequencing.

In practice, this allows researchers to treat the cell as the unit of experimentation, increasing the throughput of many target discovery questions by 100-1000X. These methods aren't applicable to every target discovery problem (e.g. some pathologies only manifest across tissue systems), but they nonetheless unlock a class of putative interventions that were previously too numerous to search effectively.

It's reasonable to think about these methods as a way of making traditional "perturbation" experiments that teach us how biological systems work12 amenable to the multiplexing benefits of DNA sequencing. The cost of DNA sequencing is falling over time, so this provides a tailwind to our ability to discover new target biologies for therapeutics. This is just one way that solving engineering problems can accelerate progress on the distinct and more challenging scientific problems facing our industry.

Even with the best possible experimental methods, some of the most promising target biologies will never be searched exhaustively. There are a nearly infinite number of combinatorial genetic interventions we might drug, synthetic circuits we might engineer into cells, and changes in tissue composition we might engender.

Artificial intelligence models can learn general models from the data generated in functional genomics experiments of many flavors, predicting outcomes for the experiments we haven't yet run. If we manage to construct a performant model for a given class of target biologies, we may be able to increase the efficiency of target discovery by many orders-of-magnitude. The cost of discovering a target could conceivably go from >$1B to <$1M.

There's growing interest in the idea of combining these technologies to build "virtual cells," models that can predict the outcomes of target discovery experiments in silico before they're ever executed in the lab. The grand version of this vision spans all possible target biologies, from gene inhibitions to polypharmaceutical small molecule treatments. In the maximal form, it may take many years to realize.

More limited realizations though are tractable today. The initial versions of these models are already emerging within early Predictive Biology companies. As a few examples, Recursion is building models of genetic perturbations in cancer cells, Tahoe Tx is building models in oncology with a chemical biology approach, and NewLimit has developed models for reprogramming cell age across human cell types13. Focused models like these represent an early demonstration that this general approach can yield therapeutic value.

These technologies have only emerged in the last 5-10 years. This may seem like old news from an academic perspective, but drug discovery cycles are on the order of a decade. We are only now beginning to reap the first harvest from this approach. We've begun to see the first medicines addressing emerging target biologies in the clinic, including complex cell states and combinatorial nucleic acid interventions.

I'm hopeful that our ability to discover these complex target biologies will match our newfound skill in drugging them.

An era of target abundance

The data are quite compelling that target discovery is the limiting reagent in modern drug development. New technologies offer an opportunity to invert the curve of Eroom's law and arc toward progress. We have the potential to enter a future where targets are no longer rate limiting.

How should we allocate resources in light of this opportunity?

Science and therapeutic discovery are driven by pools of public (~$50B/year, US NIH + NSF), philanthropic ($1-2B/year), and private capital (~$5-10B/year, venture + IPOs). Of these, public financing is potentially the largest driver based on shear scale.

Philanthropic academic institutions (Arc, Broad, CZI) have already taken the first steps to pull this possible future forward. Both Arc and CZI have announced major initiatives to build models suitable for large scale target discovery, and the Broad recently launched an AI center that may engender similar progress.

Therapeutic discovery would benefit from public investment following suit. This will require institutions like the NIH to fund larger, team-oriented projects with more integrated support from computer science researchers than the traditional one PI, one R01 scheme that dominates the agency.

Private capital has begun to place the bets on this thesis, but a plurality of resources are still concentrated on prosecuting known targets. Even on the frontier of firms leveraging artificial intelligence (techbio firms, if you'll allow it), much capital is focused on designing new molecules to these old targets more expeditiously.

This likely stems from the fact that while therapeutic engineering has a lower expected value than prosecuting new targets, it likewise has lower volatility, and there are larger pools of capital available for low vol, low EV bets than high vol, high EV bets.

Biotechnology companies often take decades to turn a profit14. If you believe that the future of human health lies outside the narrow universe of known targets, it's rationale to allocate more resources in the direction of that emerging future, even if you believe it will take time to manifest.

Coda

Eroom’s law hangs heavily upon the neck of the biotech industry. Many have internalized it as if a form of gravity — immutable & recalcitrant to a fundamental understanding. In fact, it is neither. The slow down in R&D productivity over the past decades is primarily a limitation of our biological understanding, not the loss of a rare and essential element from the surface of the Earth or an impenetrable barrier of regulation.

Our industry has often reacted to this sense of inevitable decay by attempting to hide from risk. Rather than learning to ask better scientific questions, we’ve too often avoided asking any questions where the answers are not already known. This has resulted in hundreds of distinct therapies attempting to drug the same small group of biologies. It seems self-evident that this is not the allocation of resources that maximizes for the number of healthy years we deliver to the world.

We are entering an epoch of abundant intelligence. With these tools, we have the opportunity to discover & design target biologies at a rate that’s too cheap to meter. The therapies that emerge could serve as the counterexample that downgrades Eroom’s law to a historic conjecture.

If realized, the reignition our therapeutic discovery cadence would represent perhaps the most valuable output of the Intelligence Revolution now being rendered. There is no product more valuable than healthy time.

Describing someone as a biologist tells you surprisingly little about their skills, day-to-day work, or epistemic principles. Do they study the herding patterns of African elephants during the dry season, or the structural basis for regulation of TGF-beta ligand activity in a dark crystallography room?

Over the past century, biology has arborized into subfields that address distinct problems, mirroring physics and chemistry before it. Many of these subfields are distinct enough that they represent their own intellectual disciplines. Not only do they value different questions, but they approach problems using different cognitive tools. If you describe someone as a molecular biologist, it implies both a set of technical skills manipulating nucleic acids and a bottoms-up, reductionist approach to epistemology.

Molecular biology’s historian laureate Horace Freeland Judson captures these cultural and intellectual divisions inimitably:

Molecular biology is no single province, marked off by natural boundaries from the rest of the realm. [...] Molecular biology is [...] a level of analysis, a kit of tools – which is to say it is unified by style as much as content1.

Fields are often born at the confluence of two ancestral disciplines. Molecular Biology emerged from physics and biochemistry. Systems Biology arose at the intersection of genomics and statistical mechanics.

Here, I propose that Predictive Biology is a new field that has emerged in the last five years with roots in molecular biology and machine learning2.

Predictive Biology is focused on inferring the outcomes of future experiments using quantitative models trained on a corpus of past data. Implicitly, Predictive Biologists hypothesize that biological systems contain a large amount of mutual information, so that the present and future state of one system (say, a cell’s shape) can be predicted from a description of another system (say, a cell’s gene expression profile). 

Where Molecular Biology is often reductionist, Predictive Biology is emergent, assuming that many complex biological phenomena cannot be explained absent the interactions of many components. Where Systems Biology argues that mapping the individual interactions within a system will yield understanding, Predictive Biology counters that predicting the future state of a system is understanding. Where Molecular Biology was enabled by nucleic acid biochemistry and Systems Biology by early computers, Predictive Biology is built on artificial intelligence tools that learn to explain biology from data.

Predictive Biology is not superior or inferior to the fields that came before it, but it is distinct. These distinctions have enabled scientists to ask new questions, build new institutions, and found new companies. For potentially the first time in biology’s history, this new frontier may be pioneered largely in for-profit ventures rather than traditional academic institutions.

I believe that these approaches will shape the future of biology, motivating an exploration of Predictive Biology’s origins, interests, and open problems.

Epistemic lineage

Molecular Biology & the beginning of modernity

Modern biomedicine traces its roots to the intersection of chemistry and physiology that birthed biochemistry. Biochemistry might be the first subfield dedicated to the study of living systems as complex but fundamentally physical entities, rather than “vital” elements with a wholly different set of governing principles. Beginning roughly in the 1930’s, the discipline of Molecular Biology emerged from biochemistry as a distinct field. The roots of almost all modern biotechnology firms can be traced back to Molecular Biology in one form or another.

Molecular Biology is famously challenging to define. Francis Crick, the co-discoverer of DNA’s structure, once quipped:

Molecular Biology can be defined as anything that interests molecular biologists.

Alongside his clearer definition:

[Molecular Biology] is concerned with the very large, long-chain biological molecules – the nucleic acids and proteins and their synthesis. Biologically, this means genes and their replication and expression, genes and the gene products.

Molecular Biology is defined by a fundamentally reductionist approach to explaining living systems. Practitioners ask questions about the function of individual molecules and conversely, the molecules that explain a biological process.

Implicit in these questions is an underlying hypothesis – most molecules have a small number of functions, and most functions are controlled by a small number of molecules. For the reductionist approach to yield fruit, this hypothesis must hold true in at least some cases.

While it may seem overly simplistic, it’s amazing how far reductionism was able to take us! The reductionist hypothesis was sufficient to explain the molecular mechanisms of heredity and information propagation that compose the Central Dogma – DNA synthesis, transcription, and translation. Likewise, a large fraction of our knowledge about cell communication, organismal development, and pathobiology arose from picking a molecule, breaking it, and interpreting its role based on what happened.

Molecular Biology favored the reductionist approach as much by necessity as from a desire for epistemic parsimony. The technology available to early Molecular Biologists was still nascent. Fishing even a single protein out of the cytoplasmic soup of life was challenging enough! 

Sequencing a single gene or protein was a years-long effort, worthy of a doctoral thesis. Interrogating the interactions of many genes or their products was intractable. Even if these interactions could be measured, interpreting their meaning would have presented considerable challenges. Biologists typically analyzed their data using the “eyeball test,” to observe binary phenotypes, or manual computation with pen and paper3.

Advances in both measurement and computation allowed a subsequent generation of biologists to begin probing at the phenomena that resist explanation by a handful of molecules.

Systems Biology & the limits of reductionism

Progress depends on the interplay of techniques, discoveries, and ideas, probably in that order of decreasing importance – Sydney Brenner4

Systems Biology is perhaps even more challenging to define than Molecular Biology. Historically, there is considerable tension between the two fields, with Sydney Brenner himself leading some critiques of early systems biologists5.

The largest contrast between the field and its predecessor is that Systems Biology is focused on emergent properties of complex biological systems that can’t be captured with reductionist experimental methods. Human biology provides a motivating example for why this approach is attractive. 

Our bodies are absurdly complex, but there are only ~20,000 human genes. The basic idea of one gene mapping to one function breaks down quickly when you realize that there are far, far more functions than there are discrete genes! Clearly, there are interactions among these molecules that are greater than the sum of their parts.

Until the mid 1990s, biologists had little choice but to ignore these interactions. Even if you wanted to explore the non-linear logic of genes X, Y, and Z as they interact, the tools weren’t available to do so in a practical way. Automated DNA sequencing and synthesis sparked systems biology by providing the first tools to measure many molecules at the same time. Genomic, transcriptomic, and proteomic tools that emerged in this era allowed researchers to measure the sequences and abundance of all the genes in an organism simultaneously.

Systems Biologists try to understand systems by taking these unbiased data and building minimal models of a behavior of interest. If we imagine studying the cell cycle, a systems biologist might try to create a differential equation incorporating the abundances of many cell cycle genes to explain cell behavior. Parsimony and simplicity are often more important goals for these models than predictive performance. Systems Biologists hope to learn the mechanism of a complex process in terms of simple rules that can be written down on a napkin. 

One way to frame the long-term direction of the field is in terms of a causal graph. If we imagine all the nodes in a graph as biological molecules, systems biologists hope to measure and annotate all of the edges between nodes. By quantifying all these connections, Systems Biologists hope that one day we’ll be able to design systems from scratch in a sister field known as synthetic biology.

Predictive Biology & embracing emergence

The tools of systems biology have unfortunately failed to scale beyond the simplest interactions between a few molecules. There are few differential equations that can predict complex cellular behaviors like development, immunity, or drug responses with meaningful fidelity. While noble in articulation, in practice it’s proven difficult for biologists to assemble a stack of simple rules at the micro level that’s large enough to explain dramatic, macroscopic biology.

Predictive Biology defines prediction as the core task of a biological study, rather than cataloging the functions and relationships of molecules. Implicitly, both molecular and systems biology attempt to build from these cataloging primitives to the task of prediction. If we know the function of a gene and its relationships to all others, hopefully we can infer what will happen if I activate or repress the gene. Predictive Biologists are willing to eschew the intermediary catalogs in pursuit of the understanding that arises from predictive power. 

Phrased differently, Predictive Biologists are more concerned with measuring the mutual information between two biological phenomena than they are with measuring direct causality. Where Molecular Biology takes inspiration from the epistemology of classical physics, Predictive Biology borrows the cognitive tools of computer science & information theory.

This approach has only been made possible by the advent of modern machine learning (ML) methods. Until roughly the 1990s, it was practically challenging to learn models from large, complex datasets. Increases in computational power thanks to Moore’s law and algorithmic improvements made performant models more accessible around this time.

This first generation of models allowed researchers to extract more insights from emerging high throughput experiments, but largely could not predict the outcomes of experiments based on their inputs alone. Early DNA sequence models allowed researchers to search for and align similar sequences, but could not predict the effect of a previously unobserved mutation6. Simple models of gene expression could infer cell types or cancer outcomes, but could not predict the effect of inhibiting a gene on cell functions7.

If ML has been around since the 1990s, why has Predictive Biology only arisen in this decade? Computational constraints prevented early models from capturing sufficient biological context, be that a long DNA sequence or high-resolution microscopy image. Absent this context, models were limited to making relatively local predictions, hindering applications to the most complex problems in biology. 

Classical biochemistry offers an analogy. Linus Pauling and Max Perutz solved biochemical structures using precise, physical models of the underlying atoms. These tools were capable of revealing secondary structures like the protein alpha-helix and the double-helix of DNA, but failed to predict the more complex tertiary structures of proteins that required simulation of physical properties at a larger scale8.

Deep representation learning tools enabled by GPU computing broke through this second barrier in roughly the 2010s. It’s now possible for researchers to learn models that capture a rich input context – long sequences of life’s code, thousands of expression profiles and the covariates of paired drug treatments, images capturing hundreds of cells across a half-dozen different phenotypic dimensions. 

By capturing a more detailed portrait of biological systems, a second generation of Predictive Biology models enable in silico hypothesis testing. In addition to extracting more insights from experiments performed in the world of atoms, these models allow researchers to perform many experiments in the world of bits. 

These capabilities change both the questions Predictive Biologists explore and the experimental approaches they use to render new truths from a range of latent possibilities.

Unlocking larger questions

Biology is rife with hypothesis spaces that are too large to ever search exhaustively. Testing all possible 100bp DNA sequences for enhancer activity – the ability to promote expression of a gene – would require 4^100 = ~10^60 experiments. Testing even just all combinations of 2 gene perturbations in a simple cell line would require (20,000 c 2) = ~10^8 experiments.

The traditional tools of molecular and cell biology are insufficient to explore all of these possibilities by many, many orders of magnitude. Simple questions like “What is the strongest possible enhancer for the expression of a gene?” or “What pairs of genes are essential for a cell to divide?” are surprisingly inaccessible.

Molecular Biology and its immediate descendants have made progress in the face of these daunting numbers through local searches. Given that the full space of hypotheses is too large to search, researchers use their intuitions and prior knowledge to guess at which hypotheses are the most fruitful to test. 

Naturally, this leads researchers to explore hypotheses that are in an abstract sense “close,” to our existing knowledge. Perhaps we can’t test every 100bp DNA sequence for enhancer activity, but if we know several strong enhancers at about that size, a clever molecular biologist is likely to try testing mutants initialized from those promising starting points with a reasonable chance of success.

The very best researchers have a taste that allows them to guess correctly which hypotheses will be fruitful further away from our prior knowledge. I was once trained that researchers do not actually improve in their analytical skills beyond the journeyman stage, but merely get better at selecting which hypotheses to test. However, if the space of known strong enhancers is actually quite far from the global optimum, a Molecular Biologist is nonetheless unlikely to find any sequence that comes close to the true strongest enhancer.

Predictive Biology models allow researchers to take a different approach. Rather than using intuitions to navigate a local hypothesis space, researchers can focus on gathering data to train models that enable a global search.

The experiments to do so might look quite different than those a traditional molecular or systems biologist would employ. Speaking loosely, a Predictive Biologist might allocate more of an experimental budget to gather diverse data that spans the range of possibilities within a hypothesis space, in contrast to the Molecular Biologist above that would take a greedy approach and focus on testing hypotheses close to the frontier of current knowledge9.

Picking up our example of the 100bp enhancer sequence, a Predictive Biologist might run an experiment to test the activity of thousands of random sequences to promote gene expression, then train a model to predict the activity from the sequence directly. They might then use this in silico model to search for optimal sequences across the full range of possibilities, predicting the global optimum. Using these tools, it’s quite possible the Predictive Biologist could find new, potent sequences far from the range of those previously known. While this example is stylized, real world experiments to design new proteins have achieved just such results10.

Creating new institutions

Disciplines beget institutions in their image.

Molecular Biology led to the creation of the MRC Laboratory of Molecular Biology11, the Cold Spring Harbor Laboratory, and the original four horsemen of biotech – Genentech, Biogen, Genzyme, and Amgen.

Systems Biology spawned the Broad Institute, UW Genome Sciences12, Illumina, Millennium Pharmaceuticals13, and Myriad Genetics.

Predictive Biology’s institutions are still being rendered. Previous disciplines often germinated in academic centers, only then giving rise to commercial firms. Predictive Biology may be offering an inverse example. 

Few academic organizations are configured to explore this intersection today, but new institutes like Arc and the Schmidt Center offer examples of where the future may blossom. By contrast, a large number of techbio firms have already emerged across diagnostics (Freenome, GRAIL) and therapeutics (BigHat, Dyno, Enveda, Excentia, Generate, Recursion, Xaira). 

Growth in the private sector outpacing traditional academic environments may reflect the distinct resource requirements of Predictive Biology. Unlike Molecular Biology problems that can often be addressed by a single investigator with a modest budget, Predictive Biology is most productive when data can be generated at scale and compute is abundant. 

These conditions are often easier to achieve in a for-profit endeavor. Predictive Biology has the potential to be the first biological discipline truly driven by industrial rather than academic scientists14.

Coda

I feel privileged to be living through a phase transition in my field. From the dawn of early biotech, scientists have dreamed of manipulating biology to craft a better world. We have extended lives & grown wonders once difficult to imagine, but we have yet to tame disease or design our environment.

Even the simplest cell is more complex than our most sophisticated computers. There are far more layers of abstraction than a human mind can conceive. Predictive Biology’s promise is that perhaps we need not be limited by the human mind’s ability to connect nodes on a causal graph, but rather by our ability to observe patterns sufficient to guide our search and our will to do so with vigor.

Five of my favorites, in alphabetical order:

• Altered Fates by Jeffy Lyon & Peter Gorner

• For Blood and Money by Nathan Vardi

• The Founders by Jimmy Soni

• Living Medicine by Frederick Applebaum

• Scaling People by Claire Hughes Johnson

Altered Fates by Jeff Lyon & Peter Gorner

Cell and gene therapies are rapidly changing the practice of medicine, and it seems likely that the prevalence of these modalities will only increase with time.

How did this happen?

I realized earlier this year that even after a decade working adjacent to and within the field, I have never encountered a concise, clear narrative on how the first gene therapies trials came to pass or how the tools of the trade were discovered. There are a fairly small number of delivery vectors and cognate cellular targets in common use — where did they come from? How did the field’s various dogmas about the suitability of a given tool for a given tissue develop? Many of the details seem to have been lost from the community’s collective conscience and pedagogy.

Altered Fates was the history I yearned for. Lyon & Gorner wrote much of their work contemporaneously with the execution of the first FDA approved gene therapy trial, and they were able to perform personal interviews with the majority of players in the field at the time.

It would take a much longer post to encapsulated everything I learned from Fates, but in brief form, the following details of gene therapy history were a surprise to me:

• The first gene therapy trial occurred in 1969 (!) with a leporine virus

• Early gene therapy trials were really cell therapy trials, as all editing was performed ex vivo

• The first FDA-approved gene therapy trial in 1990 actually worked and helped patients, contrary to a popular narrative that much of the early work was premature

• The National Cancer Institute (NCI) was once the world’s most prolific gene therapy center, centralizing many of the practitioners and resources. Legislative changes in 1985 (Gramm-Rudman-Hollings) led to a diaspora of talent and decentralization of expertise into industry and smaller academic settings, setting the stage for our modern industry.

• Regulatory precedent from the first trial in 1990 unlocked a rapid expansion of trials (32 trials in 1992, 59 by 1994 — geometric growth), highlighting the importance of a legible regulatory path for new medicines.

I look forward to writing up a more complete summary soon. Fates is easily in my top 10 books about therapeutics and their development.

For Blood and Money by Nathan Vardi

For Blood and Money belongs alongside Billion Dollar Molecule, Her-2, and Breath from Salt on your drug development bookshelf.

Vardi follows the story of Imbruvica (ibrutinib), an inhibitor for the Bruton’s tyrosine kinase (BTK) protein that serves as a critical signaling axis in B cells of the immune system. Ibrutinib was the first among a class of drugs targeting BTK that have proven effective for treating certain blood cancers. The story is unconventional in a half-dozen ways, and highlights the sheer serendipity that often enables new drug development.

Ibrutinib was originally acquired by Pharmacyclics from Craig Venter’s Celera Genomics for pennies as part of a broader IP deal, then went on to be the centerpiece of an eventual $21B acquisition by AbbVie. Along the way, the company was led by a charismatic CEO who had no biotech background, but among other successful business ventures, created the McDonald’s chocolate chip cookie recipe.

Celera had left the drug on the cutting room floor because it was a covalent inhibitor, going against a common drug development dogma that suggests covalent binders are often toxic. Pharmacyclics found in early trials that imbrutinib radically reduced cancer burden in chronic lymphocytic leukemia (CLL) patients, so much so that blinded clinical trials became challenging because physicians could trivially see the benefits for patients receiving the drug relative to a placebo. At this stage, Pharmacyclics knew that they had a winning medicine, but they still needed to develop it. They went from molecule to drug candidate in an extraordinarily short time.

For Blood is a unique story for exactly this reason. Most of the other tomes in the biotech canon cover the early discovery phases of medicinal invention, but shed less light on the people and patients who make clinical trials and eventual commercialization possible. The Pharmacyclics story provides Vardi a vehicle to “skip to the end” of the development process and explain the fractal complexity of bringing a molecule from the lab to the world.

The Founders by Jimmy Soni

The formation of the Paypal Mafia is one of the founding stories from Silicon Valley’s first internet wave. It’s easy to find a dozen articles outlining how unlikely it is that so many successful entrepreneurs and investors would all work together, purely by chance, on the same payments startup. Surprisingly, it’s hard to find any that go a step deeper and ask why so many members of the early Paypal team went on to succeed in diverse fields.

The Founders is an excellent, rapidly paced answer to this question. The story itself feels like reading a thriller novel. Soni manages to capture the emotional intensity of building a company in lucid prose, even when the real life events he was given as substrate involve moving about an office building and staring at computers. Most of the triumphs and crises occur primarily in the team’s heads.

If I were to summarize the core explanatory argument of Founders in three lines:

1. Everyone at early Paypal learned to exercise outlier levels of agency.

2. Individual exceptionalism was further amplified when the principals collectively found a game where hard work translated directly into impact, rewards, and power with a tight feedback cycle. They learned that agency is rewarded if you find the right place to apply it in a manner that is difficult to teach outside experience.

3. The agency the principals developed through this experience explains much of the success they experienced downstream.

For those curious about early Internet history or the agency production function, Founders is a great read.

Living Medicine by Fredrick Applebaum

Hematopoietic stem cell (HSC) transplants (“bone marrow transplants”) can offer life saving treatment for many forms of blood cancer and inherited disease, treating more than 20,000 patients/year in the US alone. Living Medicine is the story of Don Thomas (Nobel, 1990), the man who invented the technique. It is also the story of the patients who bravely participated in early trials against all odds, and the downstream technologies that have blossomed as a result.

In the early years transplantation, Thomas’ patients were all terminally ill with blood disorders and had no other hope for treatment. At the time, medicine was still naive to the incredibly complex biology of histocompatibility, so Thomas’ patients unfortunately failed to engraft, then passed away time and again. He was widely criticized as a barbarian and accused of promising patients cures that he could not deliver, yet he persevered against conventional wisdom to unravel the mysteries that separate one body from another.

Thomas eventually prevailed and learned to match donors with recipients using clinical diagnostics, eventually leading a specialized transplant ward at Pacific branch of the Public Health Service hospital system in Seattle. His ward and its physicians eventually served as one of the nucleating agents for the Fred Hutchinson Cancer Center (“the Hutch”), one of molecular biology’s most differentiated research organizations.

Living Medicine was a reminder for me that often the best ideas look incorrect, even foolish at first blush.

Scaling People — Claire Hughes Johnson

Johnson’s Scaling is perhaps the most important entry into the management canon since High Output Management. Like Grove before her, Johnson is wonderfully tactical in her guidance, eschewing the high level pseudo-philosophy that too often plagues management advice.

Scaling is all the more valuable because it’s one of the few entries in the management literature that isn’t primarily a restatement of Taylorism. Scientific management principles are often strictly superior to ad-hoc decision making, but there are clearly many cases in modern knowledge work where the management tools developed for manufacturing businesses in the early twentieth century fall short. Scaling provides answers to questions like: How should I instrument a fundamentally creative process like product development or design? How do I measure progress in a non-linear R&D environment?

Highly recommended for anyone building or operating within an ambitious organization.

tl;dr: Techbios manipulate information as much as molecules. They’re defined by building an in silico model of biology, an associated data corpus, and a predict-validate experimental loop that allows them to search otherwise intractably large hypothesis spaces. They use these tools to develop better products, more rapidly. As businesses, they have higher initial capital requirements, but more defensible moats and greater compounding returns to scale.

Etymology of an industry

The word “biotech” brings to mind clean lab coats, perhaps a white-walled laboratory a few floors above the street somewhere in South San Francisco, California or Cambridge, Mass. The actual origins are somewhat…muddier.

Living in 1910’s Hungary, Kroly Erkey developed a new method to raise and fatten hogs for food during a famine. Erkey proposed that any process like his that manipulated biology to solve human problems might best be described as “biotechnologie.” Fifty years later, Herb Boyer and Rob Swanson broke ground on Genentech’s first labs just south of San Francisco’s gleaming hills and inherited the mantle of Erkey’s ambition. Whereas Erkey’s biotech made macroscopic manipulations to the organisms that share our world, the 20th century’s biotech repurposed life’s molecular and cellular constituents to achieve breakthroughs in both medicine and industry.

Our industry’s neologism has more recently been inverted to describe yet another new breed of company — a “techbio.” At first blush it can be hard to distinguish this third generation of life engineering firm from the second, but I’ve recently been convinced that there is indeed a unique approach employed by techbio firms that constitutes a speciation event from the parental biotech strain.

Classifying species of enterprise

What makes a techbio firm different from a biotech, beyond the vintage of the buzzword?

Where biotech firms engineered life for the first time at the molecular level, techbio companies primarily engineer life at the level of information. Biotechs innovate at the scale of atoms, and techbios at the scale of bits.

What classification rules might we employ to make the distinction? To my mind, a true techbio firm:

1. Builds an In silico Model of the biological process sufficient to predict the effect of changes to key engineering parameters

2. Collects & curates a Data Corpus describing a biological system more completely than ever before

3. Generates value from the model by Predicting and Validating useful modifications to a biological process to make it faster, cheaper, or more effective

Learning by observing

Life sciences firms generate value by engineering or measuring a biological systems. Whether designing therapeutics or building new materials with synthetic biology, a life science firm must understand which manipulations or measurements will generate value before they can make a product.

Therein lies the challenge! Biological systems are complex, and there are often many more hypotheses about how to achieve a goal than a firm can readily test. There may be thousands of molecules and millions of interactions at play in a DNA sequence to be engineered, a diseased cell to be treated, or a blood sample to analyzed.

Biotechs navigate this complexity by choosing problems with optimal median outcomes using prior knowledge.

Techbios choose to tackle hypothesis spaces that maximize expected value and employ quantitive models & large scale data to make them tractable.

Biotech: Optimizing median outcomes with prior knowledge

Traditional biotechs often focus on areas of biology that are relatively well-characterized as a means of efficiently searching through the intractably large number of hypotheses that face them. Therapeutics firms might choose targets based on the abundance of academic literature supporting the disease modifying activity of a protein. A synthetic biology company might engineer strains to produce a metabolite that is quite similar to an existing synthetic route.

Another way to frame this is that traditional biotechs search for hypothesis spaces with the greatest median outcome. Each pairing of a biological target and technology to modify or measure it represents an engineering hypothesis. If the risk on the biological target itself is minimized given prior knowledge, the median performance across target:technology pairs is optimized.

How do we know this thesis is more than mere speculation? In therapeutics, there are typically many firms competing to make medicines against the same known targets. This phenomenon is widely acknowledged as “crowding,” or “herding,” and it appears to be increasing with time.

Techbio: Learning to maximize upside

Techbio firms take a different approach. Rather than restricting their search to areas of biology that have already been “derisked,” these firms explore large hypothesis spaces where the best case outcome has the highest impact.

The key to making this approach tractable is that techbio firms build in silico models of their biological system. In silico models can be built in diverse ways, but their defining characteristic is that they can predict the outcome of an experiment given only the recipe of its components.

We might construct a model that predicts the likelihood that a DNA sequence drives gene expression, that a chemical structure inhibits an enzyme, or that a genetic intervention treats a disease. Using these predictions, techbio firms explore most hypotheses in the world of bits, rather than the world of atoms.

While this may sound fanciful, the molecular foundations of modern biology actually emerged from a similar approach. Pioneering scientists discovered the structures of DNA, proteins, and the patterns of heritability using quantitative models, but until recently these quantitative approaches were unable to make useful predictions for more complex biological systems. Recent advances in artificial intelligence broke through this complexity barrier, allowing scientists to learn the rules a biological system from data1.

Techbio firms leverage these new methods to build in silico models of biological problems that were intractable just ten years ago. Even an imperfect model can be used to prioritize hypotheses, allowing a techbio firm to focus on executing experiments that are most likely to yield outcomes in the long-tail of a power law distributed results.

Constructing a Data Corpus

Before a techbio can build an in silico model, they first need to construct a data corpus that captures the fractal complexity of their biological system.

In silico models that learn from experimental data are often limited less by their computational complexity than by the quality and scale of data available to train them. Machine learning scientists have found across various domains that model performance obeys a scaling law. As training dataset scale increases, so does model performance.

This phenomenon appears to govern the behavior of in silico models of biology as well! Increasing data size has led to increased model performance in regulatory DNA sequence prediction2, protein folding3, and cell geometry prediction4.

Unfortunately, large datasets that capture underlying biology of interest do not yet exist for most problem domains. The number of biological problems is so vast that for any given problem — a cell type you’re hoping to treat in a disease, a metabolic pathway you’re trying to engineer, a protein you’re optimizing for a new role — there may only be a few experiments to date that you can access for training.

This paucity of data represents both a challenge and an opportunity. Techbios can rarely focus purely on the world of bits. Instead, they need to span the chasm between bits and atoms and generate the experimental data necessary to train their in silico models. Given how little data is available externally, a focused techbio company can often generate orders-of-magnitude more data in-house than exists in the entire world externally.

Considered as a species of artificial intelligence company, techbios are in the rare position to generate a differentiated data corpus at unprecedented scale5. This data serves as both a moat and a source of compounding returns. As the data corpus grows, the in silico model performance improves, and the rate at which the techbio can generate additional high-value data points increases as well. The construction of a data corpus therefore represents one of the defining features of a techbio and underlies a virtuous flywheel that can take off at the heart of these businesses.

Converting predictions into value

Foundational in silico models are fascinating, but they do not generate business value automatically6. Techbios need to close the loop on value generation by integrating their models into a product development cycle, and the model can’t be purely incidental for branding value. To generate value, the model must either:

1. Accelerate the product development process

2. Reduce the cost of development

3. Improve the quality of the final product

Many Techbio firms achieve these goals by integrating the in silico models into an active learning process using techniques like Bayesian Optimization7. Active learning allows firms to spend a fixed “budget” of experiments more effectively by using models to choose the most promising hypotheses to test in the world of atoms.

Rather than having to guess at which experiment to do next using human intuition, in silico models can quantitatively integrate all the prior experiments a firm has done to make an informed prediction. In the best case, active learning both reduces the time necessary to discover a successful result and increases the magnitude of success achieved8.

We can think about this process as a simple Predict-Validate loop9.

To describe how this process works in practice, a techbio firm might begin a discovery campaign to find a genetic intervention that treats a disease. At the beginning of the campaign, the firm has only a loose prior on which of the countless interventions might be effective, so they start their search by testing a range of interventions to seed initial training data. These seed data serve to initialize an in silico model that then predicts the outcome of future experiments (Predict). The most promising of these predictions are then validated experimentally (Validate), new data is fed back to the model, and the cycle is repeated, iteratively.

Accelerating discovery

The most obvious benefit of these Predict-Validate loops is that they can find effective interventions more quickly, more cheaply. While closely associated, those two benefits are not necessarily the same thing!

Using drug discovery as an example application, an in silico model may allow researchers to generate more reasonable hypotheses to test. If validation experiments can be parallelized, a techbio firm can then reduce the wall-clock time required to find an effective intervention by replacing human decisions in the Predict phase with model decisions. Human predictions may take days to months, while model decisions take seconds to minutes, so the discovery process can be accelerated even if the same number of validation experiments are performed.

Reducing cost

In silico models might similarly accelerate discovery and reduce cost by allowing a techbio firm to test hypotheses with a higher expected value (i.e. each hypothesis tested is more likely to yield a hit). A firm might then be able to perform fewer validation experiments to find an effective intervention, reducing the cost of the discovery process and accelerating the time to completion.

It’s important to note that this cost benefit is primarily realized at the early stages of product development — searching for drug discovery targets or active compounds, or searching for an optimal strain at benchtop scale in synthetic biology. These discovery phases are rate-limiting for the development of new drugs, but they represent only a minority of the expenses involved in a the discovery process10.

Most of the expense of bringing a new medicine to market is incurred in the development phase of the process — scaling up manufacturing and running clinical trials. For an illustrative example, a survey of drug development firms found that only ~15% of total development costs were pre-clinical, with the remaining ~85% related to downstream development. I’m less familiar with the cost breakdown in synthetic biology and diagnostics, but I believe the overall skew is similar.

It’s harder to reduce the costs of these development stages directly using in silico models (though smart teams are trying). However, if in silico models help techbio firms select drug candidates, strains, or diagnostic approaches that have a higher chance of development success, they can likewise reduce costs in aggregate by expending fewer resources on failed programs.

Increasing the efficacy of final products

In silico models can not only reduce the cost of product development, but also improve the quality of the overall product. Imagine we have a fixed budget of experiments we can run to find an ideal drug target or synthetic strain. An effective in silico model has the potential to help us find a higher “global maximum” on the possible product landscape through the active learning process.

In drug discovery, this might equate to a safer, more effective therapeutic due to better target or molecule selection. As one would hope, the better a therapy is along these dimensions, the more value it tends to generate for the developer11. Developing the best product, not just any product, is likely to generate value in other life science domains as well.

Business implications

The features that distinguish a techbio from a biotech matter not just inside the company, influencing how employees work, how goals are set, and who is hired, but also have important implications for the structure of the business.

1. Techbio firms develop natural moats, whereas biotechs struggle to do so

2. Techbios have an abundance of riches at the discovery stage, warranting a more liberal partnership strategy than biotechs

3. Techbios may require more funding than biotechs to deliver the 1st product, but the cost of the N-th product is lower

Techbio firms naturally develop defensible moats

Executed properly, both the data corpus and in silico model that define a techbio firm represented cornered resources. As the data corpus grows, the in silico model makes better predictions that help a firm expand their data corpus more effectively (e.g. by only running experiments that provide non-redundant information). An accumulated data corpus is difficult for new entrants to replicate, and the returns to scale compound over time. Techbio firms therefore have tangible resources that provide a competitive advantage in their area of expertise. Past success enables future success.

By contrast, biotech firms have historically struggled to develop moats that expand beyond a single asset (i.e. a single drug, engineered strain, or diagnostic test). Intellectual property provides meaningful protection for individual assets, but holding the patent for one asset rarely provides a competitive advantage for developing another, even if it’s highly related12. For a traditional biotech, past success in a therapeutic or application area does not increase the likelihood of future success by default, even in that same domain13.

Techbio firms therefore have a more defensible business model than traditional biotechs. Techbios might be analogized to internet businesses with network effects where success is self-propagating. Biotechs are perhaps more akin to entertainment businesses, where each “hit” (e.g. new asset) requires a unique set of inputs to produce. Taking the analogy a step further, techbios may therefore represent a less volatile species of life science business with a differentiated equity product.

Techbios suffer from an embarrassment of early stage riches

The techbio approach improves the productivity of early stage product development, but involves a resourcing trade-off. A techbio therapeutics firm may discover targets or initial drug discovery hits more efficiently than a biotech, leading to a proliferation of early stage opportunities. Building the Predict-Validate loop consumes resources that might otherwise be dedicated to developing a hit into an asset, so techbios are often faced with a opportunity-resource imbalance — there are more early stage opportunities than there is capital to pursue them.

Techbios are therefore a special case of a “platform biotech,”14 and likely benefit from a more liberal partnership strategy. Asset-focused biotechs need to pursue development partnerships with larger peers (e.g. pharma for therapeutics) carefully, since the future value of the asset they partner may represent a non-trivial fraction of the total enterprise value. Techbios by contrast are likely to generate a long-tail of early stage discoveries that they can’t pursue internally, so partnering early and often is a necessary mechanism to capture maximum value from their Predict-Validate loop.

Techbio companies become more efficient with time

Building a data corpus, in silico model, and Predict-Validate loop consumes resources. A traditional asset-focused biotech can skip these steps and jump straight into the development process for their first asset. In the early years of company development, it’s quite likely that a techbio will require more capital than a traditional biotech to generate that initial asset15.

The real value of the techbio platform is realized in the quality of that first asset and in the reduced cost of assets over time. As the data corpus grows and the model improves, techbios have the potential to develop cheaper, more effective assets. Biotechs don’t benefit from the same compounding returns by default.

Coda

Techbio firms as construed here are a young species. Over the coming years, I look forward to seeing these new entrants unlock previously intractable products that help patients, grow the economy, and reveal new biology that promotes human flourishing.

Please get in touch to talk through any contrasting opinions!

• The Power Law — Sebastian Mallaby

• Working Backwards — Colin Bryar, Bill Carr

• Guns, Germs, and Steel — Jared Diamond

• Invention of Nature — Andrea Wulf

• A Shot to Save the World — Gregory Zuckerman

Much delayed, I’m happy to recommend the books below as the best I read in 2022. Last year, I moved into a new role to help start NewLimit. My literary diet shifted along with the contents of my workday, and I enjoyed exploring different organizational designs and funding structures for technological enterprises. I found both The Power Law and Working Backwards below through that focused search and learned a great deal from both. The remainder of my reading hours were spent indulging in a series of science fiction novels, classics I somehow hadn’t had a chance to read, and tales from the annals of science history that left meinspired to press against the boundary of human knowledge.

My top five favorites from the year are outlined below.

If these books seem interesting to you or you’d like to trade notes, please feel free to shoot me an email!

The Power Law — Sebastian Mallaby

The most impactful businesses of the past half-century have a nearly invariant commonality in their origin stories. Whether the business began in a garage, loft, dorm room, or basement laboratory each was nurtured into existence by Venture Capital. Alongside those businesses, impactful technologies that shape our world blossomed — from Intel’s silicon chips to Genentech’s biologic medicines.

Living in San Francisco for my whole adult life, venture feels like a storied, eternal institution — old as the Sequoias. In reality, the modern structure of a venture firm is scarcely older than some of the technology companies most associated with the asset class. In The Power Law, Mallaby tells the story of venture’s inception as “Adventure Capital,” growing out of family offices and a public holding company into the private partnerships that dominate the industry today. Mallaby reprises his formula from More Money than God, using a cast of the industry’s innovative characters to explain the origin of each feature in a modern firm.

While I don’t endorse every opinion it contains, The Power Law taught me a tremendous amount about an asset class with a larger impact per dollar than any other. I can’t recommend it highly enough to anyone interested in technology or finance.

Working Backwards — Colin Bryar, Bill Carr

The nearest grocery store and doctor’s office are both owned by the same company that made my television and the device I read this book on. Amazon is one of the most fascinating businesses in the world, somewhere between a high-technology firm, an old-school conglomerate, and a Sam Walton style discounter.

It seems borderline impossible that each of these diverse business lines can run on the same corporate operating system. And yet. As Bryar and Carr describe in Working Backwards, the entire Amazon empire operates using a shared set of principles and communication mechanisms, even as they differ in nearly every other aspect of their isolated businesses.

The Amazon Way is both a set of abstract leadership principles (including both Customer Obsession and Be Right, A Lot) and concrete management mechanisms (Narratives over slide decks, Press Releases as product plans, Single-threaded decision making). There is no one right way to run a business, and I disagree with some Amazonian principles or mechanisms, but on the whole I find the Amazon operating system incredibly compelling as a baseline for an efficient organization. Bryar and Carr are likely to become canonical references in the school of management, alongside Grove and Horowitz.

Guns, Germs, and Steel — Jeremy Diamond

See full review: Guns, Germs, and Steel

Guns is a classic that was first recommended to me more than 10 (!) years ago. It is a testament to either (1) the growth rate of my book list or (2) my sorting algorithm that I only now got around to reading a book I loved.

Guns asks perhaps the biggest question in contemporary world history — how did a set of societies from a relatively small geographic area in Europe and the Mediterranean come to have such an outsized influence? Diamond reduces this complexity down to a set of highly plausible, if non-falsifiable hypotheses that emphasize the particular influence of geography on human flourishing and the outsized advantages enjoyed by Europe and Asia Minor during the nascent epochs of human development. There are few books that offer such a clarifying lens upon such a large question — a good explanation in the Deutsch-ian sense.

Invention of Nature — Andrea Wulf

Throughout my life, I’ve noticed parks, municipalities, and awards named Humboldt. Never once did I imagine that each was an allusion to one visionary scientist, rather than a collection of references to a common German surname.Such has the star of Alexander von Humboldt faded in the North American consciousness. Invention touches a small spark to the kindling of Humbolt’s work and hopes to reawaken the memory.

Humbodlt was among the last of the old generation of scientists — passionate hobbyists who financed their endeavors with independent wealth or patronage, rather than professionals in an institution funded by government or corporate coffers. He pioneered our modern understanding of ecology, wrote naturalist travelogues that inspired the likes of Charles Darwin and John Muir, kept up correspondence with Thomas Jefferson and the leaders of several European nations — a list so long it is amazing that it fit into a life.

Most striking to me was that his career was built upon a single five year journey through Latin America, climbing the Andes and cataloging one of the world’s most biodiverse regions. These years were the spark of ideas and relationships that he spent the rest of his life expanding, akin to an annulis mirabilis on a grander scale. Invention offers not only the pleasure of following that journey, but an inspiration to venture further along arduous routes, so long as they end in alpine views.

A Shot to Save The World — Gregory Zuckerman

In January of 2020, I began reading news of a flu-like illness spreading in southern China. Until April of 2021, I lived with some degree of anxiety that the flu-like illness would harm me and my loved ones.

Shot offers an explanation for the relatively shocking proximity of those two dates. Prior to the SARS-CoV2 pandemic, the record for the most rapid development of a vaccine stood at four years (see: mumps). Shot recounts how the biopharmaceutical industry beat that record by nearly four-fold in 2020. It’s a story of emerging biotechnologies (see: mRNA, the molecule), young companies turned industry titans (see: MRNA, BioNTech), and countless individuals who worked interminably to render the horse of pestilence quiescent once more.

This is one of the most of the most inspirational stories of technological progress, an Apollo Program for our era. I couldn’t help but swell with pride to know that our species is capable of such feats.

Machine learning approaches are now an important component of the life scientist’s toolkit. From just a cursory review of the evidence, it’s clear that ML tools have enabled us to solve once intractable problems like genetic variant effect prediction¹, protein folding², and unknown perturbation inference³. As this new class of models enters more and more branches of life science, a natural tension has arisen between the empirical mode of inquiry enabled by ML and the traditional, analytical and heuristic approach of molecular biology. This tension is visible in the back-and-forth discourse over the role of ML in biology, with ML practitioners sometimes overstating the capabilities that models provide, and experimental biologists emphasizing the failure modes of ML models while often overlooking their strengths.

Reflecting on the history of molecular biology, it strikes me that the recent rise of ML tools is more of a return to form than a dramatic divergence from biological traditions that some discourse implies.

Molecular biology emerged from the convergence of physics and classical genetics, birthing a discipline that modeled complex biological phenomena from first principles where possible, and experimentally tested reductionist hypotheses where analytical exploration failed. Over time, our questions began to veer into the realm of complex systems that are less amenable to analytical modeling, and molecular biology became more and more of an experimental science.

Machine learning tools are only now enabling us to regain the model-driven mode of inquiry we lost during that inflection of complexity. Framed in the proper historical context, the ongoing convergence of computational and life sciences is a reprise of biology’s foundational epistemic tools, rather than the fall-from-grace too often proclaimed within our discipline.

Physicists & toy computers

Do your own homework. To truly use first principles, don’t rely on experts or previous work. Approach new problems with the mindset of a novice – Richard Feynman

When Linus Pauling began working to resolve the three-dimensional structures of the peptides, he built physical models of the proposed atomic configurations. Most young biology students have seen photos of Pauling beside his models, but their significance is rarely conveyed properly.

Pauling’s models were not merely a visualization tool to help him build intuitions for the molecular configurations of peptides. Rather, his models were precisely machined analog computers that allowed him to empirically evaluate hypotheses at high speed. The dimensions of the model components – bond lengths and angles – matched experimentally determined constants, so that by simply testing if a configuration fit in 3D space, he was able to determine if a particular structure was consistent with known chemistry.

These models “hard coded” known experimental data into a hypothesis testing framework, allowing Pauling to explore hypothesis space while implicitly obeying not only each individual experimental data point, but the emergent properties of their interactions. Famously, encoding the steric hindrance – i.e. “flatness” – of a double bond into his model enabled Pauling to discover the proper structure for the alpha-helix, while Max Perutz’s rival group incorrectly proposed alternative structures because their model hardware failed to account for this rule.

Following Pauling’s lead, Watson and Crick’s models of DNA structure adopted the same empirical hypothesis testing strategy. It’s usually omitted from textbooks that Watson and Crick proposed multiple alternative structures before settling on the double-helix. In their first such proposal, Rosalind Franklin highlighted something akin to a software error – the modelers had failed to encode a chemical rule about the balance of charges along the sugar backbone of DNA and proposed an impossible structure as a result.

Their discovery of the base pairing relationships emerged directly from empirical exploration with their physical model. Watson was originally convinced that bases should form homotypic pairs – A to A, T to T, etc. – across the two strands. Only when they built the model and found that the resulting “bulges” were incompatible with chemical rules did Watson and Crick realize that heterotypic pairs – our well known friends A to T, C to G – not only worked structurally, but confirmed Edwin Chargaff’s experimental ratios⁴.

These essential foundations of molecular biology were laid by empirical exploration of evidence based models, but they’re rarely found in our modern practice. Rather, we largely develop individual hypotheses based on intuitions and heuristics, then test those hypotheses directly in cumbersome experimental systems.

Where did the models go?

Emergent complexity in The Golden Era

The modern life sciences live in the shadow of The Golden Era of molecular biology. The Golden Era’s beginning is perhaps demarcated by Schroedinger’s publication of Max Delbrück’s questions and hypotheses on the nature of living systems in a lecture and pamphlet entitled What is Life?. The end is less clearly defined, but I’ll argue that the latter bookend might be set by the contemporaneous development of recombinant DNA technology by Boyer & Cohen in California ⁵ [1972] and DNA sequencing technology by Fredrick Sanger in the United Kingdom [1977].

In Francis Crick’s words⁶, The Golden Era was

concerned with the very large, long-chain biological molecules – the nucleic acids and proteins and their synthesis. Biologically, this means genes and their replication and expression, genes and the gene products.

Building on the classical biology of genetics, Golden Era biologists investigated biological questions through a reductionist framework. The inductive bias guiding most experiments was that high-level biological phenomena – heredity, differentiation, development, cell division – could be explained by the action of a relatively small number of molecules. From this inductive bias, the gold standard for “mechanism” in the life sciences was defined as a molecule that is necessary and sufficient to cause a biological phenomenon⁷.

Though molecular biology emerged from a model building past, the processes under investigation during the Golden Era were often too complex to model quantitatively with the tools of the day. While Pauling could build a useful, analog computer from first principles to interrogate structural hypotheses, most questions involving more than a single molecular species eluded this form of analytical attack.

The search to discover how genes are turned on and off in a cell offers a compact example of this complexity. Following the revelation of DNA structure and the DNA basis of heredity, Fraçois Jacob and Jacques Monod formulated a hypothesis that the levels of enzymes in individual cells were regulated by how much messenger RNA was produced from corresponding genes. Interrogating a hypothesis of this complexity was intractable through simple analog computers of the Pauling style. How would one even begin to ask which molecular species governed transcription, which DNA sequences conferred regulatory activity, and which products were produced in response to which stimuli using 1960’s methods?

Rather, Jacob and Monod turned to the classical toolkit of molecular biology. They proposed a hypothesis that specific DNA elements controlled the expression of genes in response to stimuli, then directly tested that hypothesis using a complex experimental system⁸. Modeling the underlying biology was so intractable that it was simply more efficient to test hypotheses in the real system than to explore in a simplified version.

The questions posed by molecular biology outpaced the measurement and computational technologies in complexity, beginning a long winter in the era of empirical models.

Learning the rules of life

John von Neumann […] asked, How does one state a theory of pattern vision? And he said, maybe the thing is that you can’t give a theory of pattern vision – but all you can do is to give a prescription for making a device that will see patterns!

In other words, where a science like physics works in terms of laws, or a science like molecular biology, to now, is stated in terms of mechanisms, maybe now what one has to begin to think of is algorithms. Recipes. Procedures. – Sydney Brenner⁹

Biology’s first models followed from the physical science tradition, building “up” from first principles to predict the behavior of more complex systems. As molecular biology entered The Golden Era, the systems of interest crossed a threshold of complexity, no longer amenable to this form of bottom up modeling. This intractability to analysis is the hallmark feature of complex systems.

There’s no general solution to modeling complex systems, but the computational sciences offer a tractable alternative to the analytical approach. Rather than beginning with a set of rules and attempting to predict emergent behavior, we can observe the emergent properties of a complex system and build models that capture the underlying rules. We might imagine this as a “top-down” approach to modeling, in contrast to the “bottom-up” approach of the physical tradition.

Whereas analytical modelers working on early structures had only a few experimental measurements to contend with – often just a few X-ray diffraction images – cellular and tissue systems within a complex organism might require orders of magnitude more data to properly describe. If we want to model how transcriptional regulators define cell types, we might need gene expression profiles of many distinct cell types in an organism. If we want to predict how a given genetic change might effect the morphology of a cell, we might similarly require images of cells with diverse genetic backgrounds. It’s simply not tractable for human-scale heuristics to reason through this sort large scale data and extract useful, quantitative rules of the system.

Machine learning tools address just this problem. By completing some task using these large datasets, we can distill relevant rules of the system into a compact collection of model parameters. These tasks might involve supervision, like predicting the genotype from our cell images above, or be purely unsupervised, like training an autoencoder to compress and decompress the gene expression profiles we mentioned. Given a trained model, machine learning tools then offer us a host of natural approaches for both inference and prediction.

Most of the groundbreaking work at the intersection of ML and biology has taken advantage of a category of methods known as representation learning. Representation learning methods fit parameters to transform raw measurements like images or expression profiles into a new, numeric represenatation that captures useful properties of the inputs. By exploring these representations and model behaviors, we can extract insights similar to those gained from testing atomic configurations with a carefully machined structure. This is a fairly abstract statement, but it becomes clear with a few concrete examples.

If we wish to train a model to predict cell types from gene expression profiles, a representation learning approach to the problem might first reduce the raw expression profiles into a compressed code – say, a 16-dimensional vector of numbers on the real line – that is nonetheless sufficient to distinguish one cell type from another¹⁰. One beautiful aspect of this approach is that the learned representations often reveal relationships between the observations that aren’t explicitly called for during training. For instance, our cell type classifier might naturally learn to group similar cell types near one another, revealing something akin to their lineage structure.

At first blush, learned representations are quite intellectually distant from Pauling’s first principles models of molecular structure. The implementation details and means of specifying the rules couldn’t be more distinct! Yet, the tasks these two classes of models enable are actually quite similar.

If we continue to explore the learned representation of our cell type classifier, we can use it to test hypotheses in much the same way Pauling, Crick, and countless others tested structural hypotheses with mechanical tools.

We might hypothesize that the gene expression program controlled by TF X helps define the identity of cell type A. To investigate this hypothesis, we might synthetically increase or decrease the expression of TF X and its target genes in real cell profiles, then ask how this perturbation changes our model’s prediction. If we find that the cell type prediction score for cell type A is correlated with TF X’s program more so than say, a background set of other TF programs, we might consider it a suggestive piece of evidence for our hypothesis.

This hypothesis exploration strategy is not so dissimilar from Pauling’s first principles models. Both have similar failure modes – if the rules encoded within the model are wrong, then the model might lend support to erroneous hypotheses.

In the analytical models of old, these failures most often arose from erroneous experimental data. ML models can fall prey to erroneous experimental evidence too, but also to spurrious relationships within the data. A learned representation might assume that an observed relationship between variables always holds true, implicitly connecting the variables in a causal graph, when in reality the variables just happened to correlate in the observations.

Regardless of how incorrect rules find their way into either type of model, the remedy is the same. Models are tools for hypothesis exploration and generation, and real-world experiments are still required for validation.

Old is new

Despite the implementation details, ML models are then not so distinct from the analog models of old. They enable researchers to rapidly test biological hypotheses to see if they obey the “rules” of the underlying system. The main distinction is how those rules are encoded.

In the classical, analytical models, rules emerged from individual experiments, were pruned heuristically by researchers, and then a larger working model was built-up from their aggregate. By contrast, machine learning models derive less explicit rules that are consistent with a large amount of experimental data. In both cases, these rules are not necessary correct, and researchers need to be wary of leading themselves astray based on faulty models. You need to be no more and no less cautious, no matter which modeling tool you choose to wield.

This distinction of how rules are derived is then rather small in the grand scheme. Incorporating machine learning models to answer a biological question is not a departure from the intellectual tradition that transformed biology from an observational practice to an explanatory and engineering disipline. Rather, applications of ML to biology are a return to the formal approaches that allowed molecular biology to blossom from the fields that came before it.

Footnotes

1. Researchers have built a series of ML models to interpret the effects of DNA sequence changes, most notably employing convolutional neural networks and multi-headed attention architectures. As one illustrative example, Basenji is a convolutional neural network developed by my colleague David R. Kelley that predicts many functional genomics experimental results from DNA sequence alone. ↩

2. Both DeepMind’s AlphaFold and David Baker lab’s three-track model can predict the 3D-structure of a protein from an amino acid sequence well enough that the community considers the problem “solved.” ↩

3. If we’ve observed the effect of perturbation X in cell type A, can we predict the effect in cell type B? If we’ve seen the effect of perturbations X and Y alone, can we predict the effect of X + Y together? A flurry of work in this field has emerged in the past couple years, summarized wonderfully by Yuge Ji in a recent review. As a few quick examples, conditional variational autoencoders can be used to predict known perturbations in new cell types, and recommender systems can be adapted to predict perturbation interactions. ↩

4. Watson and Crick both knew Chargaff, but didn’t appreciate the relevance of his experimentally measured nucleotide ratios until guided toward that structure by their modeling work. Chargaff famously did not hold Watson and Crick in high regard. Upon learning of Watson and Crick’s structure, he quipped – “That such giant shadows are cast by such [small men] only shows how late in the day it has become.” ↩

5. The history of recombinant DNA technology is beautifully described in Invisible Frontiers by Stephen Hall. ↩

6. Judson, Horace Freeland. The Eighth Day of Creation: Makers of the Revolution in Biology (p. 309). ↩

7. As a single example, Oswald Avery’s classic experiment demonstrating that DNA was the genetic macromolecule proved both points. He demonstrated DNA was necessary to transform bacterial cells, and that DNA alone was sufficient. An elegant, clean-and-shut case. ↩

8. The classical experiment revealed that mutations in the lac operon could control expression of the beta-galactosidase genes, connecting DNA sequence to regulatory activity for the first time. “The Genetic Control and Cytoplasmic Expression of Inducibility in the Synthesis of beta-galactosidase by E. Coli”. ↩

9. Judson, Horace Freeland. The Eighth Day of Creation: Makers of the Revolution in Biology (p. 334). ↩

10. This is just one of many problems at the ML : biology interface, but it’s one I happen to have an affinity for. ↩

Mammalian aging dramatically remodels gene expression in diverse cell identities, as revealed by aging cell cartography studies (Calico Murine Aging Cell Atlas, Tabula Muris Senis). Germline ontogeny is the only process known to reverse features of aging in individual cells, such that adult cells can give rise to young animals (Gurdon 1963). Reprogramming cell identity to a pluripotent state the canonical pluripotency transcription factors (Yamanaka factors Sox2, Oct4, Klf4, Myc) has also been reported to erase many features of aging (Mertens et. al. 2015).

Recent reports have suggested that even short, transient activation of the Yamanaka factors is sufficient to reverse some aspects of cellular aging (Ocampo et. al. 2016, Sarkar et. al. 2020, Lu et. al. 2020, Gill et. al.). These exciting results prompt several questions: What features of aging are reversed? Does partial reprogramming exert similar effects across different cell types? Which aspects of the pluripotency program are required for rejuvenation?

Here, we interrogated these questions by mapping trajectories of partial reprogramming in multiple cell types using single cell genomics. We further measured the effect of partial reprogramming with all possible combinations of the Yamanaka factor set using pooled screening approaches. Inspired by limb regeneration in amphibians, we also explored whether partial multipotent reprogramming could restore youthful expression in myogenic cells.

Partial reprogramming restores youthful expression and suppresses cell identity

We performed partial reprogramming with SOKM in young and aged adipogenic and mesenchymal stem cells. By measuring gene expression across single cells, we captured cells in diverse states across the trajectory of partial reprogramming.

Single cell expression profiles in both adipogenic cells and MSCs revealed a continuous trajectory of cell states induced by partial reprogramming. We also profiled control cells that were not reprogrammed, allowing us to compare the effects of aging and reprogramming in a common measurement space.

We first wondered if partial reprogramming reversed some features of aging. To investigate, we used maximum mean discrepancy (MMD) comparisons between young and aged cells before and after treatment, considering features across the transcriptome. Remarkably, we found that adipogenic cells were more similar to young controls after treatment, with youthful expression levels restored in thousands of genes. In MSCs, we found that fibrotic gene sets and an aging signature derived from bulk RNA-seq were similarly reduced.

Somatic cell identities are transiently suppressed by partial reprogramming

Reprogramming induced unique cell states, unseen in control conditions in both cell types. These unique states suggested to us that reprogramming might be suppressing somatic cell identity programs, despite some prior reports to the contrary. We performed pseudotime analysis to map each cell to a continuous coordinate system spanning the length of the reprogramming trajectories we observed.

We found that somatic cell identity programs were suppressed and pluripotency identity programs were activated in the most reprogrammed cells along these trajectories. In particular, we observed activation of the Nanog transcription factor, previously reported to be a gate-keeper to the induction of full pluripotency.

Pluripotent cells are characteristically neoplastic, forming teratomas in vivo. Our observation that Nanog is activated in a subset of partially reprogrammed cells suggests that even transient activation of pluripotency programs poses a neoplastic risk. Given that we observed only a small Nanog+ cell population, it seems likely that previous reports using bulk measurements were not able to detect this rare cell state.

We next wondered if partially reprogrammed cells would re-acquire their original somatic identities, as suggested by MEF to iPSC reprogramming systems (Samavarchi-Tehrani et. al. 2010).
We turned to RNA velocity analysis to infer changes in cell state and found that most reprogrammed cells in both populations were re-acquiring their original somatic identities.

Pluripotency submodules are sufficient to restore youthful expression

Are all four Yamanaka factors required to restore youthful expression? Are there any sufficient subsets?

We next wondered if alternative reprogramming strategies could also restore youthful expression. The neoplastic risk posed by oncogenes in the Yamanaka Factor set (Klf4, Myc) motivates a search for alternative approaches. We also wondered if the suppression of cell identity we observed was intimately connected to rejuvenation, or if these two phenomena could be decoupled.

To investigate these questions, we developed a screening system that allowed us to perform partial reprogramming interventions in a pooled format with single cell RNA-seq as a read-out. Our approach was inspired by the CellTag lineage-tracing system (Biddy et. al. 2018), taking advantage of expressed barcodes in the 3’ UTR of a constituitive reporter. We used this system to test partial reprogramming in young and aged MSCs with all possible combinations of the Yamanaka factors.

We found that the transcriptional effects of partial reprogramming scaled with the number of unique factors delivered, consistent with known biology for the Yamanaka factors. To determine which combinations had unique effects, we trained a cell identity classification model (scNym) to discriminate different combinations based on transcriptional profiles. We found that effects from combinations of three factors were highly similar to the full Yamanaka factor set, suggesting no single factor is required rejuvenation.

Rejuvenation and identity suppression are not closely entangled

We also scored the expression of an aging gene signature and derived mesenchymal cell identity program scores using a cell classifier trained on a mouse cell atlas (Tabula Muris). We found that almost all combinations significantly reduced the expression of the aging signature, and all significantly suppressed mesenchymal identity. However, the degree of rejuvenation and identity suppression were not significantly correlated, suggesting these effects can be decoupled. The results of our screen suggest that the activation of the full pluripotency program is not required to suppress some features of aging.

Multipotent reprogramming interventions restore myogenic gene expression

Can partial multipotent reprogramming reverse features of aging?

Urodele amphibians have the remarkable ability to regenerate limbs through an endogeneous dedifferentiation process. One key player in this process is the mesodermal transcription factor Msx1. Previous work has shown that Msx1 is sufficient to dedifferentiate synctial myotubes back into proliferating mononuclear progenitor cells, without inducing pluripotency.

We wondered if transient activation of this multipotency factor might also reverse features of aging in myogenic cells, similar to the Yamanaka factors (Sarkar et. al. 2020). We performed a pulse/chase of Msx1 followed by single cell RNA-seq in aged myogenic cells, similar to our other experiments. It has been reported that myogenic differentiation is impaired in aged myogenic cells, and here we found that transient Msx1 treatment improved myogenic gene expression in two independent experiments. This result suggests that transient activation of progenitor factors outside the core pluripotency program may also restore youthful gene expression, similar to the canonical Yamanaka factors.

There are surprisingly few books that tell the story of world changing medicines. Biotechnology has improved the lives of countless patients in the past half-century, but you can’t appreciate that fact scanning the spines at your favorite bookstore. There are books about the early development of most popular websites (e.g. Facebook, Hatching Twitter, No Filter, In The Plex, The Everything Store, etc. etc.), and yet medicines that have cured intolerable diseases outright receive comparatively less attention in our popular canon ¹.

It’s worth celebrating then the few stories of drug development that have been committed to text. The Billion Dollar Molecule and The Antidote by Barry Werth have long been my go-to example for how to tell these stories well. I’m pleased to add Robert Bazell’s Her-2: The Making of Herceptin to the list.

Her-2 recounts the development of Herceptin by Genentech and their academic partners. Herceptin was among the first “targeted” cancer therapies that function by specifically inhibiting cancer cell growth, rather than inhibiting the growth of all cells in the body like traditional chemotherapeutics. It’s difficult to understate the impact Herceptin has had on patient lives and the oncology drug development sphere writ large. Whereas it was once commonly accepted that “targeted antibody therapies don’t work for cancer,” monoclonal antibodies and targeted small molecules have now been developed for several cancer indications against a diverse set of targets ². The success of Herceptin was a catalyzing event for this change in focus for the industry.

How does Herceptin work?

The mechanism-of-action that allows Herceptin to inhibit cancer growth is fairly easy to write on a napkin. Cells in the body proliferate in response to growth factor signals — often hormones or proteins circulating in the blood or permeating tissues. These factors are essential to allow for growth of the body during development. Genentech’s first marketed product was ironically human growth hormone ³.

In some breast and ovarian cancer cells, a receptor for epidermal growth factor encoded by the HER2 gene is expressed at much higher levels than in normal cells (overexpressed in the language of molecular biology). These cells get extra growth signals as a result of this abundant receptor, leading them to proliferate aberrantly. Herceptin is an antibody — a special protein produced by B cells of the immune system to bind to specific targets — that binds specifically to the HER2 receptor. By blocking these extra growth signals, Herceptin can limit the growth of some cancers, shrinking tumors and extending patient’s lives.

Bazzel does a remarkably good job of conveying this mechanism to a lay audience. Too often in biotechnology reporting, technical details are either overbearing or irresponsibly elided. Bazzel manages to strike the proper balance to leave a reader educated, without being bored.

How did we find this target?

The beginning of every drug development story is the identification of target. Target is a special word in drug development, denoting the molecular process you need to modify to treat a disease. For the majority of drugs, targets are specific proteins, and the modification is an inhibition of that protein’s activity.

Bazzel begins his story at this crucial stage — too often left out of historical accounts, even in the biotechnology industry press. The story is filled with classical scientific serendipity. The ortholog of HER2 was originally discovered as an oncogene (a gene that causes cancer when mutated in some way) in chickens and named erb-B.

Robert Weinberg’s team at MIT later discovered a rat ortholog through transfection experiments. His team induced neuro/glioblastomas in rat embryos by injecting a mutagen during development, then transferred DNA from resulting tumors into a set of non-cancerous cells to find genes that might be inducing cancerous growth. Across four separate tumors, they homed in on an oncogene that converted otherwise normal cells to cancerous growth. Based on a hunch, the team performed hybridization (base-pair level binding assays) to erb-B and observed that the rat and chicken genes had some level of shared sequence, known as homology. Perhaps the chicken oncogene had a mammalian ortholog! The original paper describing these experiments is worth a read ⁴.

Axel Ulrich had been the first person to clone the epidermal growth factor (EGF) itself. Famous for his role in cloning human insulin (see Invisible Frontiers: The Race to Synthesize a Human Gene), Ulrich was one of the first scientists at Genentech. Mike Watterfield had a hunch that erb-B was identical to the human EGF receptor gene. Since erb-B was known to cause cancer in chickens, this suggested that EGF receptors in humans might do the same thing!

Watterfield called Ulrich, a known master cloner, for help cloning the human EGF receptor gene to investigate this hypothesis. The collaboration was a profound success, resulting in the first clear connection between growth factor signaling and human cancers. The paper is also worth a read ⁵.

Ulrich used the sequence of the human EGF receptor to search for similar genes, and he pulled out HER2. He was able to show that HER2 was homologous to the neu gene named by Weinberg’s team. By sheer coincidence, Ulrich bumped into Dennis Slamon in the Denver Airport, an oncologist with an extensive collection of human tumors. The two struck up an agreement to search for Ulrich’s HER2 in Slamon’s samples to see if HER2 was driving human cancers. They struck upon samples with 30-fold upregulation of HER2 relative to normal cells — a clear hit ⁶.

Validating the target

These overexpression experiments sure suggested HER2 might play a role in cancers, but how can we know for sure? In a set of follow-up experiments, Ulrich and Slamon showed that HER2 overexpression was sufficient to induce cancers, and that blocking HER2 with an antibody in mice could shrink tumors. In drug development, these critical experiments are known as target validation — drawing the causal graph between nodes connected previously only by correlational edges.

From target to therapy

At this stage, Ulrich’s role at Genentech seems to present a natural path toward translating this discovery into a real medicine. Unfortunately, Genentech had recently made some ill-advised investments in using recombinant interferons as cancer treatments, and wanted to exit oncology altogether after the high profile failure of those programs. Within the company, the HER2 program struggled for resources. Ulrich eventually quit out of frustration.

Despite positive data using a monoclonal antibody to treat human tumors transplanted into mice, there was strong skepticism among senior Genentech management that antibodies would ever be successful for cancer treatment. The thinking at the time was that any protein targeted on a cancer cell would simply be downregulated — the cancer cells would mutate to avoid expressing the targeted protein. While not far-fetched, this thinking failed to appreciate the phenomenon of oncogene addiction, where tumor growth is dependent on a particular mutated gene. Some HER2 driven cancers can’t mutate away from their HER2+ state without severely reducing growth — exactly the reaction you want.

David Botstein and Art Levinson were able to see the promise in HER2 therapy when others were skeptical. Through their leadership, laboratory research continued on HER2 therapies, and additional executives were eventually convinced of the therapeutic potential for monoclonal antibodies in oncology. Their foresight was prescient ⁷.

In order for the mouse antibody to be used in humans, Genentech needed to remove as much of the mouse protein sequence as possible and replace it with human counterparts. The mouse sequence is recognized as foreign by the human body, and attacked by the immune system. The process of swapping out sections of the mouse antibody gene for human counterparts is known as “humanizing” an antibody, and is now standard practice. In the early days of Herceptin though, this was unproven territory and a risky bet. To his credit, Paul Carter at Genentech accomplished this task in only 10 months (!).

How do we know if the therapy works?

After the anti-HER2 antibody (anti-TargetName is a convention for antibody naming) was humanized, it needed to be tested in actual patients. Drug development proceeds through three stages in the USFDA system:

1. Phase I trials establish the safety of a drug, but don’t test efficacy. Outside oncology, these trials are in healthy volunteers.

2. Phase II trials test escalating doses in patients. Increasingly, Phase II trials are used for early efficacy read-outs to dubious effect.

3. Phase III trials are the gold-standard test of effectiveness — large cohorts of patients receive the treatment or an alternative in a randomized controlled trial.

Phase I and II studies are conducted a bit differently in oncology, where drugs are often too toxic to be tested in healthy volunteers. Instead, cancer patients with no alternative treatment options receive experimental therapies as a last resort treatment. Genentech launched their trials in breast cancer patients based on the unmet medical need and high HER2 prevalence.

In the Phase I and II studies, some conducted by Ulrich’s early collaborator Slamon, a handful of patients saw remarkable responses to the drug. These patients had cancers that were recalcitrant to traditional chemotherapy, but nonetheless some with high HER2 expression saw drastic reductions in tumor size and became cancer free for long periods of time. Unlike traditional chemotherapies, Herceptin was largely free of notable side-effects when used alone, so these successful treatments could continue for months to years on end.

Despite these promising early results, the Phase III trials proved incredibly difficult. The Phase III scale is easily 10-100X the scale of Phase II in terms of patient numbers, with a commensurate increase in logistical burden and cost. For Genentech’s Phase III, they originally planned a placebo control arm of the trial that discouraged many patients from participating. Why sit through hours-long infusions of “antibody” if it might just be saline?

The trial struggled to enroll the necessary number of patients for almost a year. In that time, Art Levinson took over as CEO, and Genentech leadership took the risky-but-necessary step of dropping the placebo control arm to increase patient enrollment in the study. After this expensive near-death experience, the trial enrolled on schedule and eventually treated over 450 women. The trials unexpectedly finished early, despite the delays. This was due to the unfortunate discovery that HER2+ breast cancers have a more rapid progression than the general breast cancer population, so that the effects of the treatment were visible earlier than expected.

Those effects were overwhelmingly positive. Even in an arm of the trial that specifically treated patients with the worst, least treatable cancers, more than 10% of patients saw their tumors shrink by >50%. Another 30% of these patients saw their aggressive cancers half their growth, providing them with an average of 9 additional months with their loved ones.

In the larger trial in less serious patients, results were similarly positive. 49% of women saw their tumors decrease by >50% in size, while only 39% of women saw the same effect on standard chemotherapy alone. Added to a then-new microtubule inhibiting agent Taxol, Herceptin increased response rates from 16% to 40%.

Lessons

Herceptin ignited the era of targeted cancer therapy, and encountered strong headwinds along the way.

A few take-aways:

• The results of previous Modality::Indication combinations shouldn’t be overly generalized. The real relationship of interest is the Modality::Target::Indication. Previous antibody based cancer treatments failed because they used the wrong target, not because all antibodies are ineffective for treating all cancer. A similar lesson is currently being relearned in the gene therapy field.

• Internal champions are essential for the progression of drug development programs, even when early results are positive. The hypothesis space for therapeutics is so large that even candidates with positive pre-clinical data don’t always receive investment. Without David Botstein and Art Levinson, Herceptin may have been canceled before reaching Phase III trials.

• More targeted therapies address more targeted populations. Herceptin is so effective and tolerated because of it’s highly specific mechanism. That same specificity means only a subset (~10-30%) of patients see a benefit.

Other drug development programs likely have complementary yet independent lessons to be extracted ⁸. I wish we had more of these stories to learn from.

Do you know of others captured in similar form? Send me an email — jacob@jkimmel.net or a Tweet @jacobkimmel.

Footnotes

1. Why is this true? Is the technical background required for good science writing too high? Is there no market for these stories? ↩

2. https://www.nature.com/articles/nrd3186 ↩

3. Recombinant human insulin (trade name Humulin) was the first drug developed at Genentech, but was marketed in partnership with Eli Lilly. See Genentech: The Beginnings of Biotech, Invisible Frontiers: The Race to Synthesize a Human Gene. ↩

4. https://pubmed.ncbi.nlm.nih.gov/6095109/ ↩

5. https://pubmed.ncbi.nlm.nih.gov/6328312/ ↩

6. https://pubmed.ncbi.nlm.nih.gov/3798106/ ↩

7. Disclaimer: I work at a company founded by David and Art, and I greatly respect them both. ↩

8. This is a joke for NIH grant nerds. A classic line in an NIH grant is that the objectives are “complementary but independent,” because you need to accomplish the insane task of planning 3+ years of research where no action depends on the results of previous actions. ↩

How did the US create one of the most impactful scientific institutions in history?

The National Institutes of Health (NIH) is the world’s pre-eminent biomedical research agency. The annual NIH budget ($40B+) is an order of magnitude larger than peer institutions (CIHR in Canada, MRC in the UK) in nominal terms, and commensurately the NIH is responsible either directly or indirectly for a plurality of the world’s impactful biomedical research each year.

One reductive but instructive data point on the impact of the NIH is the number of Nobel Prize recipients with NIH funding. NIH-funded scientists have received >10% of all Nobel prizes in history. If we subset to the Nobel Prizes for Physiology and Medicine (110 total prizes) or Chemistry (111 prizes) where all but two NIH-funded scientists received their awards, NIH-funded scientists have received a shocking 42% of all prizes. This is especially notable given that the NIH has only existed since 1930 and the Nobel’s began in 1901.

In just the 2010-2016 period, NIH funding can be traced to scientific breakthroughs that supported the development of 210 new drugs. (It’s important to note that NIH funded basic discovery is but one component of the vexing, arduous path to drug discovery.)

From even a cursory glance, it’s apparent that the NIH is responsible for a non-trivial fraction of human progress in both biology and medicine. I’ve long been fascinated by the NIH as an institution: how did it come to be; how does it prioritize abstract, long-term goals; and how might we improve the funding mechanisms of the NIH to accelerate biological discovery.

Given that the NIH funds such a large portion of discovery in one of the most rapidly advancing scientific fields, it seems that we can learn a great deal about scientific progress by investigating the NIH’s political origins and operational decisions.

It strikes me that the NIH’s mandate is much more radical than most presentations of the institutions long history suggest. The NIH fundamentally takes taxpayer dollars, bequeathed by all, and uses that revenue to fund exploratory, high risk basic research. In the language of venture capital, the NIH is black swan farming, but rather than risking the funds of wealthy limited partners, the NIH invests with the public purse.

I believe this arrangement has led to almost unquantifiable good for humanity, but nonetheless, it’s a shocking proposition to include in a political speech.

Imagine the pitch:

“I would like to take tax dollars, disperse them widely on a number of individuals with interesting but inherently difficult to justify ideas, and then we’ll cross our fingers and hope for the best.”

But the pitch worked!
And so did the science!

How did this happen?

Inventing the NIH — A Review

Victoria Harding presents a step-by-step account of the NIH’s political origins in Inventing the NIH, with a strong focus on the role of non-governmental organizations and lobbying groups. She eloquently outlines how the NIH blossomed from much smaller beginnings into a high-growth scientific juggernaut. While insightful, Harding’s text is written for the academic historian and a bit difficult to consume for leisure. I’ve tried to extract some of the main insights below in a briefer form.

The Marine Hospital Service and the Hygiene Laboratory

The NIH was not created anew from whole-cloth in a single legislative text. Rather, it was built upon existing institutional foundations, created for related but distinct purposes.

The deepest origins of the NIH connect back to the Marine Hospital Service, a network of hospitals specifically created to treat ill seamen, funded by a tax on their wages. In a way, we can think of this network as a form of integrated health insurance similar to Kaiser Permanente in modern California. The Service was originally run within the precursor to the US Coast Guard, but was given independent management after the Civil War within the Department of Treasury. This change in management led to the development of distinct class of public health civil servants within Hospital Service.

Crises and external circumstances began to expand the Hospital Service’s initial mission. Beginning with management of quarantines for incoming ships, Congress and the executive branch began asking the Hospital Service to manage and investigate various other public health problems.

It seems like the logic here was roughly: Who has the personnel to deal with problem X? That weird marine worker insurance program? Sure, give it to them.

Germ theory developed in the late nineteenth century, representing one of the great conceptual advances in modern biology. As part of the growing list of demands from Congress, the Hospital Service came to employ a few students of this new doctrine, including a direct trainee of Robert Koch himself, Joseph Kinyoun. Kinyoun was placed in charge of establishing what we would now recognize as a basic research facility, termed the Hygienic Laboratory in keeping with the nomenclature of the time. This laboratory was fairly small by modern standards (< 200 employees), but it was the first time federal funding was used to support ongoing basic health research.

Public health reformers push the Hospital Service to partner with some enterprising chemists

Throughout the early 20th century, a number of private organizations lobbied the US government to become more involved in public health. These groups included labor unions, life insurance companies, social workers, and philanthropic foundations. Several of their campaigns boiled down to advocating a reorganization of existing programs from a divisional organization structure to a functional organization structure. It’s not clear to me this was really a great idea, but it seems like the public health advocates really wanted the government to spend more federal dollars on health overall, and the reorganization demand was a problematic political tactic that allowed them to claim they were seeking efficiencies, while inadvertently alienating the existing civil service.

The Hospital Service was defensive when it came to these possible reforms, as they feared they might be subsumed then eliminated inside some larger department. However, they too wanted some reforms made. It seems they were particularly upset about their poor job security and compensation. These compensation problems stemmed from federal rules that allowed medical doctors to receive federal commissions, but not scientists. To improve their compensation, leaders of the Hospital Service were open to forming political coalitions with reformers, so long as they retained their independence and won pay increases.

These reform campaigns set the stage for Senator Joseph E. Ransdell of Louisiana to partner with members of the American Chemical Society seeking to establish a new research institute for the study of “physiological chemistry.” The ACS members were interested in establishing an institute modeled on Rockefeller University (then, Rockefeller Institute), providing long-term support for basic research from a private endowment to understand the chemical basis of human disease.

After failing for nearly a decade to raise private funds, the ACS members were convinced by Ransdell that the US Government would be a worthy patron. Together, ACS members and Randsell collaborated to develop a proposal for a federal research institute that grew into the National Institute of Health (singular at first!).

In a funny anecdote, it appears Ransdell chose the name at the last minute, crossing out a previous name in the bill text and replacing it with NIH.

Ransdell and the chemists ran through the District of Columbia trying to gather support for their new proposal. After much effort, they received a luke-warm endorsement from the Hospital Service on the grounds that a bill for the new institute also included their desired pay increases. From personal correspondence of Hospital Service leaders, it doesn’t seem like they were all the favorable to the new institute, but really needed political help in the Senate.

In particular, the head of the Hygienic Laboratory viewed a new NIH-like institution as a competitor to his own existing efforts, and he believed it would be impossible to scale a research institution beyond the scope of the Hygienic Laboratory. It strikes me that fear of hypergrowth, and a failure to imagine large scale operation are a common failure mode within otherwise productive organizations like the Hygienic Laboratory.

How did they convince the public?

It took Ransdell and the ACS members 4 years and 2 US presidents to finally pass their NIH legislation. Harden provides an incredibly detailed account of the process. As expected, opposition to increased federal spending was the primary obstruction to the creation of the NIH, but idiosyncratic outcomes and the fickleness of individual legislative personalities also played a role in the lengthy road to acceptance.

The arguments put forward by Ransdell and supporters contained many familiar points. They emphasized the efficiency of preventative treatment for disease, the necessity of basic science for developing new medicines, and they leaned on past successes of federally funded basic research like the creation of a vaccine for Rocky Mountain Fever.

In addition to these familiar arguments, I’ll posit that three additional factors contributed to the NIH’s success:

1. Flexibility in the face of political reality

2. The 1928 influenza pandemic provided political momentum and a demand for action

3. Biomedical science had just entered a phase of exponential growth — successful exemplars were easy to find

Downsizing the ask

NIH proponents’ requested appropriation was based on cost estimates produced by the ACS for their envisioned institute — $10M over five years (~$150M inflation adjusted to 2020). Several Senators viewed this appropriation as exorbitant at a time when the US Government was much smaller in absolute terms than in the modern era (federal net outlays in 1929: $3.1B). After back and forth with the Andrew Mellon’s Treasury Department (yes, that Andrew Mellon), the initial appropriation was dramatically scaled back to $750,000.

While disappointed, Ransdell and supporters were willing to accept a small initial appropriation in exchange for creating the framework for federally funded biomedical research. They felt confident that future legislation would increase the allocation, and that the institution would become a valued part of American life. In these hopes, they proved prescient.

This willingness to scale ambition to political reality seems essential to establishing an inherently high risk endeavor like the NIH. Risk tolerance tends to increase when the downside is well bounded.

A desire for action in the face of tragedy

The contemporary epidemiological context no doubt also played a role. The winter of 1928-1929 saw the deadliest influenza pandemic since the pandemic of 1918. This crisis was entirely new to me, and seems to have faded from the broad public consciousness.

Both President Calvin Coolidge and members of Congress were more receptive to proposals for increased federal expenditures on healthcare and health research in the wake of the proximal tragedy. Coolidge himself vetoed an earlier public health reform bill, but his attitude warmed considerably following the pandemic such that he became one of the stronger political supporters of the legislation.

Coolidge’s reversal stands out to me as a positive example of how local context can influence long-term public policy making. We have an almost perfect counter-factual to consider what would have happened in the absence of the influenza outbreak. The bill had been before Congress already just a year prior, a similar bill had already passed and been vetoed, and yet with few if any changes, the NIH was able to win support once an acute event highlighted the importance of such an institution for long-term health of the public.

Exponential growth in biomedical capability

A key component of Ransdell’s presentation was a set of vignettes highlighting biomedical research advances with everyday impact.

In one portion of the presentation, Ransdell showed short microscopy film of motile cells in a culture dish taken by scientists at Rockefeller in Albert H Ebeling’s group during the hearings. These movies are so entrancing that many scientists (myself included) still work on understanding the biology on display today. I found this aspect of the argument endearing, and wanted to dig a little deeper than Harden’s coverage.

I found what appears to be the exact exchange captured here:

The cause of such diseases as nephritis, arteriosclerosis, cancer [..] must be discovered. [..] This cannot be brought without great advances in the knowledge of fundamental properties of cells. … This is a culture which has been placed in a suitable medium, and is functioning just as it did in a small embryo. […] Now what you are going to see going on before you is a process which in the incubator under the microscope covers a period of 24 hours and you are seeing in 15 or 20 seconds.

(I tried to find the original Ebeling film to no avail. The Wellcome recently restored some microscopy films from the same period, and I imagine the Ebeling film may have looked similar.)

The Rockefeller scientists explained that even though cell culture is artificial and a bit fanciful, these model systems had allowed them to develop a production system for Vaccinia vaccines.

This example is almost a perfect encapsulation of modern biomedical research. The scientists began their study by asking a simple question: What do animal cells need to survive? Can we provide everything a cell needs outside the body? They followed this conclusion through a series of experiments to find the proper culture conditions that allow for ex vivo cell cultures. Though unanticipated at the outset of research, these culture platforms proved useful in later studies of a virulent infectious disease and the production of treatment.

Exploring a fundamental question yielded an unexpected, unpredictable practical benefit.

While this is only one such example, Ransdell’s presentation took place in the midst of long awaited biomedical advances that were making impacts on the lives of everyday Americans. Germ theory provided a framework for understanding and preventing infectious disease, to astonishing effect. Deaths from infectious disease were cut roughly in half (!) between 1900 and 1920 (see a Figure from Armstrong et. al. 1999, JAMA below).

Vaccines had been produced for several, previously ravaging diseases. The Hospital Service itself had identified the source of pellagra as a dietary deficiency, and identified common foodstuffs to prevent it. Just months later, penicillin would be discovered. Ransdell had examples abound of biomedical success and the benefits of research investment, many of which were apparent without being named.

This context of rapid, geometric decay in mortality from disease seems essential to achieving broad public support for a high risk research enterprise.

Acceptance, Passage, and Divisional Structure

Ransdell’s arguments were eventually accepted by both Houses of Congress and signed into law under Herbert Hoover, a rare excited about the application of scientific methods to all aspects of the public sphere (see Hoover: An Extraordinary Life).

Initially, the NIH was only a singular institute in a small building in the District of Columbia, almost exclusively focused on intramural research. It was not until the passage of the National Cancer Institute Act in 1937 that the NIH broadly adopted the practice of extramural research grants. Today, extramural grants to researchers at universities and private institutes makes up ~90% of the NIH budget. The NIH also settled into a “divisional” organizational structure in 1937, where divisions were defined by human diseases (a few exceptions exist in more modern times, the functionally focused National Center for Bio-Informatics being the most prominent).

Harden’s history ends in 1937, but the history of the NIH only blossoms later on. I look forward to exploring the decisions that led to the current system and possible mechanisms for improvement based on other successful funding agencies, like HHMI.

Are there other organizational structures or funding models that could help improve our rate of discovery?