AI is a powerful tool, but we barely understand human biology. A powerful weapon pointed randomly hits nothing.
AI’s magic is standard equipment on the keynote stage: build a sufficiently powerful intelligence and disease becomes a solved problem.
The logic goes something like this: The body is a system we can read from and write to. Disease is therefore an information problem, and enough intelligence trained on an information problem yields an answer.
This is Wrong
AI cures disease only if the cures already are within a set we have measured, waiting for a better approach. One problem – they do not. Most of human biology has never been observed with detail and understanding sufficient to target a therapy.
No amount of inference recovers data that was never collected.
The need for AI in life sciences and drug discovery is indisputable. Of roughly ten thousand known human diseases, the large majority have no approved therapy at all; among rare diseases, the figure approaches ninety-five percent. Most approved drugs slow a disease rather than stop it.
For the bulk of human illness, medicine offers management or nothing.
AI will eventually transform human health. The capital now flowing toward that conviction is aimed at the wrong stage of the problem.
Perfect Marksmanship and Bad Aim
Drug discovery decomposes into three stages, and confusing them is the source of nearly every bad forecast.
- Disease to mechanism. Identify a pathway, target, or molecular interaction where intervention alters the course of disease in a human being.
- Mechanism to drug. Build a molecule — small molecule, antibody, siRNA, gene therapy — that produces the intended mechanistic effect with tolerable safety and pharmacology.
- Drug to patient. Design a development program that finds the right patients and measures what the molecule actually does to them.
Nearly all AI investment has landed on stage two. That is understandable because computational protein structure prediction was a genuine scientific achievement, and it seeded an explosion of tools that design proteins, small molecules, oligonucleotides, and delivery systems. Given a mechanism worth hitting, we can now design something to hit it faster and more precisely than at any point in the history of the field.
Which raises the question: does better molecular design enable cures for otherwise intractable diseases?
Consider the undruggable targets — mechanisms we trust but historically could not reach. KRAS, SHP2, transcription, and new protein factors and interactions finally yielded to decades of structural biology and medicinal chemistry, not to AI.
There is no case in which an AI-derived insight has cracked a target that resisted conventional approaches. More telling, the historical step changes came not from better design tools but from new therapeutic modalities: biologics, then antisense and siRNA, then gene editing.
Each opened a class of targets that no amount of cleverness could have reached with the prior toolkit.
We don’t know – and that’s a bad data set for AI.
Set that aside, because it understates the problem. Validated-but-undruggable targets are a rounding error against unmet medical need. For the overwhelming majority of untreatable disease, we do not know the mechanism at all.
More than ninety percent of drugs entering clinical trials fail, a figure essentially unchanged in three decades. In most of those failures, the molecule performed as designed. The mechanism was wrong. We have built extraordinary precision into the act of firing and almost none into the act of choosing the target.
The binding constraint in medicine is identifying a mechanism whose modification changes what happens to a patient.
Molecular design is not where drug discovery succeeds or fails. It never was.
Crowding Is the Symptom, and It Cures Nothing
Mechanistic conviction is scarce.
The global R&D pipeline nearly doubled over the past decade, from roughly eleven thousand active programs in the mid-2010s to about twenty-one thousand by the end of 2024. Early-stage venture funding compounded at roughly eighteen percent annually across the same period: more capital, more programs, more shots.
Now the other side of the ledger. Novel biological targets entering the pipeline fell from about 100 per year before the pandemic to 30 in 2024. Thirty-eight targets — roughly two percent of all targets under investigation — absorb about a quarter of the entire pipeline.
The industry doubled its activity and cut its new ideas by seventy percent.
This is what rational actors do when failure is punished, and conviction is rare. Nobody is fired for the fiftieth program against a validated mechanism. Ask how many variations on GLP-1 biology the world requires, and the honest answer is that the number was passed some time ago. The capital misallocation is expensive.
The opportunity cost is worse: hundreds of millions of patients whose diseases have no mechanism under investigation by anyone.
Measuring What Matters
Don’t worry, the LLMs are here.
Language models will read the whole of published biology and reason their way to new mechanisms. Connect enough dots and the hypothesis appears.
The dots don’t exist.
Human biology spans interlocking layers — genome, protein, cell, tissue, organism — where components respond dynamically to modest changes in neighboring components and in the environment.
It was not engineered.
It is the residue of billions of years of stochastic evolution, which produced variation without regard for legibility: countless genes, cell types, cell states, and contexts, each behaving on its own terms. There is too much of it, and it is too idiosyncratic, to derive from first principles like an engineering project. It has to be measured.
The largest cell atlases now span hundreds of millions of cells and remain orders of magnitude short of covering them all. Worse, until recently they contained almost no measurements of how a system responds when you intervene. A drug is an intervention. Descriptive maps of biology cannot tell you what happens when you push on it.
Several groups have launched serious efforts to build a virtual cell, pairing large-scale experiments with models that extrapolate beyond that virtual cell. This is the right instinct. It is also, at present, a vanishing fraction of the possible, executed almost entirely in a narrow set of immortalized cell lines that resemble human tissue the way a wind tunnel resembles weather.
It’s the System
Humans are systems, and the hardest diseases are within human systems and unsolved.
Even a perfect cell model addresses half the equation. Most human disease is systems-level dysfunction — a temporal interaction across multiple biologies and diverse cell types. Characterizing that requires measurements that scale badly and often require a living organism.
The lack of useful data sets becomes structural rather than merely misguided and expensive.
Some biology is conserved across all life. Protein folding is nearly self-contained and closer to physics than to biology, which is why models trained on sequences from thousands of species work. Metabolism involves at least a dozen cell types and holds reasonably well across mammals. Brain function involves dozens of cellular identities and is exquisitely human: rodents do not develop Alzheimer’s disease, and non-human primates do not reproduce ALS.
This is unforgiving. The diseases where we have made the least progress are precisely the ones most specific to humans – and therefore the ones where data is costliest, scarcest, and most constrained by ethics. They are also the most important and critical to solve. Scaling AI compute does not touch this.
The constraint is not intelligence. It is understanding the system.
Agents Need Weights. Biology Doesn’t.
Swarms of models running closed loops with automated laboratories, generating hypotheses, directing robots, reading results, and iterating without sleep have produced results. Automated systems have optimized cell-free protein synthesis and designed antibodies against known targets with genuine efficiency.
Agents thrive wherever the scorecard is fast, cheap, and accurate.
Give a capable model an instant feedback signal, and it will grind against that benchmark until it wins. Coding assistants improved at extraordinary speed because a compiler adjudicates correctness in seconds and a developer adjudicates intent in minutes. The closed-loop flywheel is concise, cheap, and objective.
Drug development is the inverse. The only conclusive scorecard is whether a molecule helps a patient. Computational approximation and high-throughput assays are not very good at assessing this. Human clinical trials are the only reliable test, and these run for years, cost millions (approaching billions), and are subject to the pace of living biology and ethics.
No quantity of compute compresses it.
The agentic laboratory successes are the ones that look like software: quantitative objectives inside constrained search spaces. This is valuable work, and largely orthogonal to whether a drug works in people. Human translation cannot be solved by optimizing the wrong objective function more efficiently. This industrializes the production of well-designed failures.
Agentic AI becomes transformative in this field the moment we possess an objective function that is a proxy for human clinical benefit and still permits rapid experimentation. We do not have one.
Compress Everything!
It doesn’t work.
Target the clinic: shrink the cost and duration of trials, and everything accelerates.
Accelerate a pipeline aimed at the wrong mechanisms, and you get failure sooner. Not what we should be going for…
The narrower version of the claim is sound, and worth pursuing. Predictive toxicology and AI-drafted regulatory filings compress IND-enabling work. Patient identification from electronic health records, better site selection, and automated data management reduce operational drag. These are real gains against real waste.
But there are limits. IND-enabling work and operational overhead together account for roughly half of development time. In vivo biological observation accounts for the other half, and it is governed by how fast disease progresses in a human body. Compress everything AI can touch, comprehensively and optimistically, and total development time falls by about 10%. The majority of the process is structurally untouched.
It’s the Design
Deep mechanistic understanding of a disease serves three purposes: selecting patients likely to respond, confirming target engagement, and detecting early evidence that disease biology is actually impacted. Trials that enroll correctly, read out sooner, and kill failures earlier are not an operational improvement. They are a different trial design.
Better trials are inseparable from better biology, enabling a more complete understanding of the mechanism of action.
It’s the Mechanism
Molecules can be generated faster. Literature can be scoured at amazing speed and scale. Laboratory work can be automated. Trial operations can be tightened. These are critical but only point solutions. But they will produce real opportunities.
None of them relieves the binding constraint. Value is at the bottleneck, and the bottleneck is not molecular design, literature synthesis, laboratory throughput, or trial logistics.
It is the identification of mechanisms whose modification changes disease in humans.
The uncomfortable truth is that this is the hardest problem and the one with the worst track record. The only conclusive validation is a clinical trial. Adjacent paths offer shorter timelines, cleaner benchmarks, and clearer near-term proof points, and they are shorter precisely because the problems are more tractable.
A shorter path to a smaller destination is still a smaller destination. Much of what is described today as an AI-and-biology thesis is process improvement on problems we already knew how to solve.
Data at scale, in human systems, generated deliberately from quality data sets specific to human function is capital-intensive, slow to validate, and unglamorous, which is why it remains underfunded relative to its importance. It is also the only input that makes the rest of the stack worth anything.
For the hundreds of millions of people with no meaningful treatment, the distance between a wrong mechanism and a right one is the distance between another expensive failure and a life-changing treatment. Intelligence was never the scarce resource. Understanding mechanisms and human biological systems is.
