The Anti-Scaling Law in Biology, and Why AI Could Make Crowding Worse Before Making Drug Development Better
Two Trial Wins, One Warning: Why AI Won't Scale Biology the Way It Scaled Tech
In the last two weeks, two clinical trial readouts drew tremendous excitement well beyond the biopharma community.
At the plenary of the world’s largest cancer meeting, a room of oncologists stood and applauded the biggest win in pancreatic cancer history. Revolution Medicines’ daraxonrasib, an oral pan-RAS inhibitor, took median overall survival in previously treated metastatic pancreatic cancer from 6.7 months to 13.2 months, a hazard ratio of 0.40. For my entire scientific career, the efficacy bar in pancreatic cancer did not move, until now.
Days earlier, Lilly’s VERVE-102 (the program Lilly gained when it acquired Verve) showed that a single infusion could edit the DNA inside a living person’s liver and drop PCSK9 by up to 88% and LDL by up to 62%, holding for more than a year. The promise for a “once-and-done” approach to reduce one of the highest risk factor for cardiovascular diseases.
I am thrilled about these successes after decades of hard work in drug discovery. But I also felt deeply unsettled with the excitement from the tech community that “this is just the beginning; imagine what we can achieve with AI in X, Y, and Z diseases in the next 5 years”.
In my view, one of the main reasons for the tech community’s optimism is the scaling-law. Once you demonstrated 0-1, you can do 1-100 much quicker. The internet, social media, and so on.
In biology and drug development, I think there is a mirror image, the anti-scaling law. Because of that, here’s my contrarian view: AI could make crowding in drug development worse, before making it better.
And that’s my perspective as a genuine believer in the transformative power of AI, and an AI practitioner who used $14,000 worths of AI tokens in the past 2 months.
Two of the oldest targets in the book
Nobody needed a model to surface either target. No screen of the literature was going to rank KRAS or PCSK9 any higher than they already sat. The bottleneck was never finding them. It was the decades of biology, failed chemistry, and physical-world groundwork required to drug them. RAS took 40 years and a company betting its existence on chemistry the field had written off. PCSK9 took 6 different modalities stacked on one gene.
RAS was identified as a human oncogene in early 1980s. It is the most common oncogene in all of cancer, mutated in roughly 90% of pancreatic tumors, and for 40 years it sat at the very top of every target list while being the textbook definition of “undruggable.” PCSK9 is probably the cleanest gift human genetics has ever handed medicine, and we have had it for 20 years: a French group tied it to inherited high cholesterol in 2003, Helen Hobbs and Jonathan Cohen found the protective loss-of-function variants in 2005, and a 15-year follow-up showed that humans with the natural loss of PCSK9 had an 88% lower rate of coronary heart disease.
That distinction matters, because the mental model pouring into biology right now assumes the bottleneck is somewhere else.
Tech vs. Biology
In tech, the world runs on a one-to-100 logic. Prove one thing works, then copy, distribute, and scale it across a hundred adjacent cases. More data improves the model, the better model attracts more users, the loop compounds.
Biology runs the mirror image. The first proof of concept does not unlock the next hundred. It usually consumes the single best opportunity in the space, because you never picked your first target at random. You picked it because human biology had already pointed at it with a flashing arrow. The first win is the easiest problem the modality will ever face, not a representative sample of it. The second target is harder, the third harder still. There is no compounding. There is decay. I have called this the anti-scaling law, and RAS and PCSK9 are not exceptions to it. They are the apex, the rare shots so good they were worth 40 and 20 years of siege.
Genetics is the home field, and it is nearly picked over
Where do the good targets actually come from? Human genetics. It is the one place biology runs a natural randomized trial for us: people born with a gene turned up or down, followed for life, telling us for free what happens when you hit that target with a drug. PCSK9 is the canonical case, and it is canonical precisely because it is so rare.
The arithmetic of scarcity is brutal. There are about 20,000 protein-coding genes, maybe 3,000 to 6,000 druggable in any conventional sense, and around 700 with an approved drug against them. Each step compresses by an order of magnitude, and the survivors are not a random draw. They are the ones biology made legible. A 2024 genetic-priority study found the top 0.28% of targets were nearly nine times more likely to make it from Phase 1 to approval. That is not a fat tail you mine with more compute. It is a cliff. The strongest signals are already found, already drugged, and the ones that remain are fainter, smaller, and more likely to be wrong.
What AI changes, and what it does not
Turning a target into a medicine takes many steps, and many of these steps are engineering. Once you have the target, you can find (or “design” in AI’s age) the hit, optimize the molecule, assay the pharmacology, evaluate the DMPK, manufacture the molecule at scale, pick the indication, design the trial, run the operation. AI can be transformative for many of the steps, especially the steps following the scaling law and has fewer dependencies with the physical world at the current moment. We all know the power of Alphafold in predicting protein structure, and now the race to predict an antibody binder for a given target and optimize the ideal developability profile for a drug candidate. The floor is rising fast, and a rising floor is good for patients.
But exactly one layer is not engineering, and it is the foundation layer: choosing the right target for the right disease. That is biology, and the scoreboard has not moved. The place drugs most often die is Phase 2 PoC trial in patients, where the biological hypothesis finally meets reality, and the number that captures the whole gauntlet has barely budged: the likelihood that a drug entering clinical trials ever reaches approval was about 10% in 2014 and closer to 8% by 2020, straight through the entire era of genomics, CRISPR, and machine learning. We got spectacular tools and did not improve the number that decides whether a drug works. AI raises the floor on execution. It has not raised the ceiling on biology.
The crowding gets worse before it gets better
There is a second-order effect that should worry the optimists specifically. If you promise to make the engineering layer radically cheaper/easier, but do not widen the base layer of validated biology, the new horsepower does not spread the bets. It concentrates them.
The logic is a refusal to compound risk. A novel technology platform like AI already carries enormous technical risk, so the rational move is to not also bet on whether the target is real. You aim the new tool at an old, validated target, where a win is legible and the next round is fundable. AI pushes the same way from two sides: it makes building against a known target cheaper, so more teams crowd in, and its training-data gravity pulls toward the targets with the most written about them, which are the validated ones. So the field converges.
We have seen this episode before.
For PCSK9 alone, there are at least 15 antibodies, 10 siRNAs, 4 ASOs, and 5 oral small molecules/cyclic peptides approved or in the clinic.
For CD19, there are more than 300 clinical programs across modalities: autologous CAR-T, allogenic CAR-T, CAR-NK, monoclonal antibodies, T-cell engagers...
When engineering becomes a commodity, as AI promises, and the target shelf stays fixed, the near-term result is a price war over the same validated targets.
The platform scaled. The biology did not.
AI does not democratize originality. It democratizes access to the same obvious ideas.
So how do you find a first-in-class target?
That question deserves its own piece (one I have a work-in progress). For now, here is where it starts. For now I will say only where it starts. The #1 source of first-in-class targets is human genetics, but human genetics discovery is not a virtual exercise.
You can not find the next PCSK9 by reasoning harder over the existing corpus of human knowledge with a SOTA AI model nor through virtual cell perturbations. You find it by going out into the physical world and sequencing enormous numbers of actual human beings, then doing the slow wet-lab biology to figure out what the signal means.
Regeneron is the a poster example of that. To surface GPR75, a gene whose protective variants are associated with lower body weight and 54% lower odds of obesity, they sequenced about 640,000 human exomes. And the protective variants turned up in roughly 4 of every 10,000 of them, a faint signal you could only see at that scale. That was 2021. Five years later, despite three parallel programs, there is still no GPR75 drug in a human yet. The same approach surfaced HSD17B13 for MASH, and it too has yet to deliver an approved drug yet, but there are already 5 clinical-stage programs and many more preclinical ones chasing the same target. The discovery is not the finish line. It is the starting gun for another decade of physical work.
This is the part AI cannot shortcut, because the majority of human first-in-class targets do not live in any training data yet. They live in cohorts, in assays, in many scientists’ dedication in the physical world over time.
Humbled by biology, work on the tough frontiers
So here is the whole argument in one line. In tech, proof of concept means now scale it. In biology, proof of concept often means you found the one place this works, and paid decades to get there.
RAS and PCSK9 are proof that the prize is real and proof of what it costs. AI will keep getting better at the execution. But the work that matters most, finding the next scarce wedge of real biology, still happens out in the physical world, on the timescale of careers, in the part of the problem no model can yet touch.
In my view, the right response to two pieces of great news is not to assume a hundred more are queued up behind them in the next 5-10 years. It is to stay humble enough to keep sequencing, keep looking, and keep funding the unobvious shot before anyone can prove it will work.
And for innovators passionate about using AI to improve drug development and eventually human health, we should have the bravery to focus on solving the toughest problem in biology, not the promise to make the 20th PCSK9 antibody faster.
Great piece. One way I have thought about this is as a feedback problem. In tech you can try and fail fast because you receive almost instanteous feedback at often very little cost. This is not the case in all in drug development. It may be getting faster and cheaper in the pre-clinical setting, but the real challenge is what will work in humans and until you get there you need a lot of time and money.
Excellent piece. I’ve been thinking about this a lot lately talking to my tech-oriented friends starting to dip their toes in biology.
Echoing the feedback problem, I think there is also a lot of disconnect between the research/preclinical vs. clinical teams. the people generating hypotheses are rarely the ones watching them fail in the clinic, and the two rarely cross-communicate as much as they should.
Biopharma could use more of Elon Musk’s approach of putting designers and engineers in the same room, same team, for an immediate feedback loop. Sure, translational research tries to solve this but it’s still a handoff model that builds a bridge between bench and bedside rather than collapsing the distance.