On AI & Drug Discovery with Jack Scannell
Dr. Jack Scannell
Etheros Pharmaceuticals

On AI & Drug Discovery with Jack Scannell
Jack Scannell is the much referenced father of Eroom's Law. As part of our research, we read the recent Nature paper he co-authored with Andreas Bender plus a team of AI x R&D veterans: Artificial Intelligence in drug discovery - what it is, where we stand and the path forward, and had asked him for an interview on it to publish it alongside our thesis. Due to his busy schedule and work on his early-stage biotech Etheros, we had to push the publication. We are so incredibly lucky that he always comes through with insightful commentary. The following interview questions reference the recent Nature paper and the responses are like mini-essays themselves. From China’s R&D to PMOS and AlphaFold, he covered a lot of ground. Enjoy!
1. So, will AI “solve” all diseases in the next ten years?
AI will be incredibly helpful in lots of ways and you would be an idiot not to use it where it is helpful. But for what it is worth, I think the rise of good, cheap, and fast drug R&D in China, and perhaps subsequent regulatory competition between China and the US, is going to have a bigger impact on the drug industry in the next ten years than will the rise of AI.
I think a rapid AI-led productivity “revolution” is unlikely for at least two reasons. First, AI works best for the drug R&D tasks that we are already pretty good at. Today’s uncured diseases mainly reflect challenges where there is fundamental ignorance. It is hard to train AI to do a good job when all it has to chew on is fundamental ignorance. Second, AI will initially make parts of a complex process faster and cheaper but won’t change the other parts very soon [Ref 1, Fig. 1a]. I think you can already see something like gold rush economics in certain places, so expect a glut of cheap ligands against genetically validated targets, piled up behind expensive biological or clinical bottlenecks. This may be good for patients, lucrative for the folks who control the bottlenecks, but possibly bad for the people who invested to produce the glut of ligands.
AI works best for the parts of drug R&D we are already good at because to train your AI you need “good” data plus a way of quickly and cheaply testing whether the model outputs are accurate. By “good” data, I mean data that contain the information on whose basis you can map between inputs and outputs, data that are abundant enough to reduce statistical noise and, more importantly, to train the AI model weights. The archetypical example here is protein folding. There were decades of high-quality structural data from experimental X-ray crystallography, a couple of hundred thousand protein structures defined experimentally, plus practical ways of testing the predictions of protein folding models quickly and at low cost.
So structure prediction models, and the protein design tools built on them, are, and will be, great at reducing the cost and increasing the quality of protein design. I can imagine lots of applications of better, cheaper, protein design that create new products and open up new markets, including new kinds of therapeutics. However, because we are relatively good at analysing and manipulating the structure of proteins, and so can train and test folding models, this is rarely the main bottleneck today when it comes to badly treated diseases. I suspect the main benefits from the protein folding models may be “disruptive”, where we use the low cost to design proteins, or sets of proteins, to do things that are uneconomic today.
I think of the application of AI in drug R&D as a bit like an extension of the old and cliched story about a drunk looking for his or her keys under a lamppost. Is that where the keys were lost? Nope, but it is where the light is.
Well, I imagine drug R&D as a dark landscape with scattered lampposts, under which motivated drunkards have been searching very hard for many years. AI unleashes robots with great machine vision. The robots beat the drunks under any given lamppost, but in the short- to medium-term the robots and drunks are stuck with the same illumination. I suspect drug R&D is usually more constrained by the darkness than it is by the sobriety of whoever or whatever is searching each of the illuminated patches.
Of course, there are creative ways that AI can make it economical to scavenge under neglected lampposts, or to efficiently combine information across sets of lampposts, but I think the gains there are likely to be more incremental, at an industry-wide level at least.
2. How do epistemic opacity and conditionality make a lot of biological data problematic for AI applications?
Epistemic opacity has been knocking around for a long time as a scientific concept and it refers to systems where one can run experiments, perturb the system, and observe outputs, but where you don’t know the mechanism that links the input to the output. Most of biology sits in that camp. People do “virtual cells”, an optimistically named form of perturbation model, precisely because they can’t produce a mechanistic model that links the inputs and outputs.
Conditionality refers to systems where the output depends on many variables, most of which you never get a chance to manipulate in your experiment. Many biological data are horribly conditional. Is a drug toxic? Well, it depends on how much you give, for how long, to which cells, from which species, with which concurrent drugs, on how you define “toxic,” and in whose lab the toxicity experiments are conducted [Ref 1, Table 2]. Is a drug effective in mice? Well, it depends on the strain, the sex, the way you caused the mouse “disease,” the temperature at which the mice are housed, what they are eating, and on whether they are handled by male or female lab staff, among other things.
Epistemic opacity and conditionality are related. Because you don’t know the mechanism that links the inputs of your experiment to the outputs, you don’t know a priori which conditions matter, and many important conditions are never explored, so your data labels are incomplete and noisy, and results can change a lot with small changes in experimental conditions. Hence results are not generalisable.
I’ll give you an example. I have done some work on in vitro models of drug toxicity, specifically drug-induced liver injury [Ref 1, Fig. 2a]. It is hard to get well-labelled data on the liver toxicity risk of drugs in humans, not least because we try to avoid giving humans drugs that poison them. You can get rough rankings, from say 1 (very toxic) to 5 (very safe), but the drugs that score 1 are toxic for a bunch of completely different biological reasons. Some are toxic in a small proportion of people with a genetic variation. Some are toxic because they accumulate in elderly people with poor kidney function. Some are toxic because they interact with other common drugs. And arguably, a lot are toxic because they are not very effective, so you need to give a large dose. Even the concept of drug toxicity is conditional on drug efficacy. So the “1” label covers a small and heterogeneous set of compounds whose toxicity is conditional on a whole bunch of factors that are not reflected in the label. That makes it hard to predict drugs that will score 1.
By the way, I can’t help wondering if reductionism, doing studies in simple in vitro systems, makes the conditionality problem worse. Humans have evolved homeostatic mechanisms to try to keep their internal conditions within narrow bounds, so in live humans, you can forget about a lot of those conditions. Lots of homeostatic machinery disappears when you put cells in a dish, so the conditions suddenly become very important. I’ve gotten interested in oxygen levels for in vitro work recently. The amount of oxygen available to cells inside the body, in tissues, is around 4x to 10x lower than the amount of oxygen available to cells in standard cell culture conditions. We know that you can change the results of your cell culture experiment if you vary the oxygen levels to make them more physiological. But hardly anyone systematically runs their in vitro studies at a range of oxygen concentrations to see if it is influencing the result. Folks nearly always forget about oxygen conditions, cross their fingers, and hope that it doesn’t matter for the results. The same neglect is repeated for dozens, perhaps thousands, of other conditions in nearly every in vitro cellular study (e.g., mechanical stimulation, cell density, feeding schedule, circadian rhythms, insulin levels, pH, etc.), all of which we know can substantially change the results. I strongly suspect that this is why in vitro studies so often fail to replicate between laboratories.
3. “Data are not knowledge.” Large volumes of data to answer the question of interest, in effect, can end up resembling noise; the main focus needs to be on the predictivity of data for in vivo outcomes. Can you give an example of that?
I once had an argument with a prior employer, who was instigating a tidy desk policy for the purposes of data security. I tried to sell my boss on an alternative data security technique, called steganography, which was the perfect match for how I kept my desk. Steganography involves hiding the signal in a huge mountain of garbage, such that no one knows the signal is even there. I lost the argument, by the way.
I have been doing quite a lot of work in age-related neurodegenerative diseases over the last few years, which are pathologies with a depressing history of failed drug trials. I have spent a lot of time looking at results from transgenic mouse models because the literature is dominated by results from such models. To be honest, it feels like I have been set a massive steganographic challenge. I hope that somewhere in transgenic mouse results are signals. But the signals are buried in a huge pile of noise; results that are irrelevant, biased, or false when it comes to sick elderly humans. The history of disappointing results from drug trials in age-related neurodegenerative disease tells us that even the best informed among us are bad at distinguishing signal from noise in the neurodegeneration literature.
Of course, I think more could be done in the first place to pick model systems, or patient segments, or trial endpoints, that generate less noise and more signal, and I have written about that elsewhere [3].
By the way, I have found AI to be extremely helpful for this kind of steganography. I suspect that with the right set of priors and prompts around evidential quality and reasoning, and by using AI to cover a lot of ground to find mechanistic triangulations, uncorrelated signals, across more diverse literatures and data sets (e.g., human comparative pathology, natural disease in animals, not just transgenic mice which dominate the literature), one can do a better and faster job. But even if I convinced myself and investors that AI had helped find a new signal, it would still take maybe 10 years and several hundred million dollars to find out if we were right or wrong. Of course, once something works well in people, it becomes much clearer which parts of the data pile are signal and what parts are noise. But until human results make it clear that you have found a signal, you don’t know what the signal looks like.
The time and cost of testing predictions in people is one of the things that makes the application of AI in drug R&D so different from the application of AI in mathematical proofs, or to protein structure. With mathematical proofs, one can brute-force lots of candidate proofs and then test them quickly and at low cost.
4. The paper states that with AI & Drug Discovery, the clinical impact is what matters most, specifically higher rates of success in phase two trials, where efficacy is usually first tested. How do we achieve this?
I always find the “increase Phase II success rates” prescription true but unhelpful. If you simply lower the bar at Phase II, you might well end up failing more in Phase III, which is expensive and helps no one [4].
More helpful, but still difficult to implement, is advice to improve decision quality and candidate quality running into Phase II. You can think of decision quality as the spread between the true positive rate and false positive rate of the progression decisions leading up to Phase II. That in turn depends on lots of things but there are no “magic wands”, to quote a recent essay by Daphne Koller [5]. Human genetic validation helps with the biological true and false positive rates but may harm the commercial true and false positive rates (the “hot” targets have got horribly crowded). More thoughtful disease model design and selection helps, and that is something I have been particularly interested in. Better processes to integrate information from different uncorrelated sources helps. AstraZeneca’s 5Rs framework talks about several of these factors from a practical big pharma perspective.
Also, more informative measures in early human trials, phase 1b, can be a fantastic help. I think an under-appreciated cause of trial failure, among the general public at least, is lousy measures of human disease. I may have a neuroscience bias here, but if your measure is a noisy symptom rating scale, where patients vary a lot day to day, but the scale has been set in stone by regulatory precedent and commercial pressure, then that can make it much harder to detect good drugs. I am optimistic that we are getting better at diagnosing disease in people, and measuring its progress, which makes smaller and cheaper clinical trials much more informative, and which makes it easier to match preclinical signals to the right indications. This all can have a huge impact on R&D productivity.
5. AlphaFold is always talked about as revolutionary in the area of protein structure prediction, but can you tell us that this won’t be the same for other prediction areas because of a lack of a ground truth for model generation and evaluation?
X-ray crystallography is a technique that really does provide ground-truth data on protein folding structure, at least for a large subset of proteins under certain conditions. We also have good ground-truth data on the amino acid sequences that make up the proteins, and on the DNA sequences that create the amino acid sequences. And we can make proteins and test some of their properties quickly and cheaply. If you want a CRO to give you the structure of a protein you supply, it costs around $10k and takes a few weeks. Therefore, for protein structures, we have bright lampposts and the robots are doing a great job.
Contrast this with disease-modifying drugs for sporadic Alzheimer’s or sporadic ALS. There we have the steganography problem. Maybe there is a signal out there in the academic literature, or in the biobanks, but it is swamped by noise. And to find out if your putative Alzheimer’s drug works in people, getting to ground truth, will cost a billion dollars and take ten years; 10^5 times more expensive than a protein structure, and 100 times slower than a protein structure.
Of course, I have picked two extremes here. But there is a general challenge that nearly all of the quick and cheap cycles, cycles that generate AI training data or test AI’s predictions at reasonable cost, involve tests against some presumed correlate of human clinical utility and not tests against real human clinical utility [Ref 1, Fig. 2]. This comes back to my interest in the “Predictive Validity” of model systems [3]. The domains where quick cheap correlates are highly predictive of human outcomes are those domains where the incremental gains from AI are likely to be smaller, since we already have good cheap correlates and are already able to make reasonable predictions of human outcomes. And where we don’t have good cheap correlates, we either lack data, or else are training AI on data that does not do a good job of predicting what happens in people.
So we are back to the problem that in the short- to medium-term, the drunks have already found a lot of what lies under the brightest lampposts. And where it is still dark, the robots are not massively better than the drunks.
6. How do we link models (validation) to the processes they are used in (translation)?
In the paper, we argue that AI models should really be evaluated in the context of the industrial processes they are meant to inform. There is a disease, a target, a dose you expect to give to people, a chemical series you committed to, etc. And there is a decision to be made: which compounds to make next; which to drop; whether to go into the clinic [Ref 1, Fig. 4].
Nearly all AI validation in the public domain ignores that context and answers a much narrower question: How well did the AI model predict a set of parameters? It does not ask whether the project’s decisions got better on the basis of the AI model.
The practical fix is to start from the decision and work backwards, and here you realize that the AI models that have the same headline performance on standard benchmarks can perform very differently. One might be good for picking a few winners from a very large pile, another might be better if the task is to throw out the likely failures. The paper shows two models with the same headline benchmark performance that differ two-fold in a selection setting and two- to three-fold in a deselection setting [Ref 1, Fig. 5]. Neither is “better”; they are good for different jobs. So the first step is simple: write down the R&D decision that the model is meant to help with, choose the metric for that decision [Ref 1, Box 2], and judge the model on that. There is remarkably little of that kind of evaluation in the public domain.
The second step is to test the model in the live process rather than on a historic dataset. A time-split or an “external” test set is still a test on compounds that existed when the model was built [Ref 1, Fig. 3]. The project’s next compounds are, by definition, somewhere the model has not been, so are likely to look different to the training data. The real validation is prospective: make the predictions, run the experiments, see what happens. Drug companies do this, more or less, inside their design-make-test cycles. Academic benchmarks very rarely do, which is one reason the published performance of these models is much better than their real world performance.
The third step is the hard one. Does the preclinical model, whether AI, organoid, or animal, predict what happens in patients? Of course, data here tends to be very sparse, and most of it sits in the large pharma companies [Ref 1, Figure 6b].
7. One of the possible paths proposed to get the right kind of data is creating new research organizations that build purpose-built datasets and model systems. From everything you know about female biology and conditions like PMOS and ovarian aging, where do you think we should start?
Over the years, I have looked hard at a few areas of biology, but never at PMOS or ovarian aging. So treat what follows with caution and suspicion. I also point out that I may be telling people who are experts in those fields things that are either obvious or wrong.
But in very general terms, there are maybe three components here. One is to optimize the quality and then the quantity of the data that describe human pathophysiology. Two is to identify or create, and then evaluate, model systems, almost certainly in vitro or in vivo biological models in the first instance, that embody enough of the right pathophysiology, from the perspective of maximising their “predictive validity”. Three is to train AI on data from such models and human data.
Taking these in turn, it is much harder to treat diseases when the diagnosis is not a coherent pathobiological entity. One sees this a lot in neurodegeneration and psychiatry. Parkinson’s disease is not one thing, which undermines our ability to model it and reduces the average effect size of any given treatment in human trials. A lot of recent progress in oncology has come from the molecular segmentation of tumours.
My guess is that PMOS is not a coherent pathobiological entity. The “PMOS” label covers different combinations of hyperandrogenism, anovulation, and ovarian morphology, and the women it describes range from lean and infertile to obese and insulin resistant. I also understand that there are distinct genetic clusters. Ovarian aging involves at least two processes which might be quasi-independent: the depletion of the follicle pool, and the decline in oocyte quality. I understand again that human genetics is relatively informative, and seems to give a lot of clues (DNA damage repair is important). Also, lots of eggs are collected from women for IVF, women who presumably gave medical histories and then either did, or did not, go on to have successful pregnancies.
For the proxy models, the first thing is to work back from your best guess of the clinically relevant human pathology to define what a good model, or a good assemblage of models, for the purposes of training AI, would look like. “Good” should be pre-defined [Ref 1, Fig. 6a]. If there are various competing pathological hypotheses, there will be different competing visions of “good”. To be frank, some R&D efforts fall at this hurdle. People forget about “good” and start with “available,” “convenient,” or “cheap”.
I don’t want to criticize models in a field that I don’t understand, but I should ask if the models in most common use were optimized for convenience rather than the degree to which they recapitulate the critical causal human biology. The standard PMOS models are rodents given androgens or an aromatase inhibitor. Rodents do not menstruate, are polyovulatory, do not develop PMOS spontaneously, and do not have a human-type menopause, so for ovarian aging a mouse models follicle depletion over a lifespan of two years but not the long post-reproductive period or the slow accumulation of oocyte damage. Prenatally androgenised monkeys and cows might be closer but few people can afford them. On the in vitro side, the commonly used granulosa cell line is tumour-derived, and ovarian organoids and in vitro follicle culture exist, and culture of human follicles has produced mature-looking eggs, but the question is whether or not these systems predict what happens in women. I also wonder about the use of the human material from IVF. I understand that the IVF world already records outcomes and there are national registers in the UK and US. Is there a way to create systematic, consented collection of the biological material that is discarded in the process, under common protocols and linked to the outcomes? That could perhaps create a good new lamppost.
References
[1] Bender, A., Thomas, M. C., Scannell, J. W., Shaywitz, D. A. et al. Artificial intelligence in drug discovery: what it is, where we stand and the path forward. Nat. Rev. Drug Discov. 25, 855–876 (2026). https://doi.org/10.1038/s41573-026-01496-2
[2] Scannell, J. W., Blanckley, A., Boldon, H. & Warrington, B. Diagnosing the decline in pharmaceutical R&D efficiency. Nat. Rev. Drug Discov. 11, 191–200 (2012). https://doi.org/10.1038/nrd3681
[3] Scannell, J. W., Bosley, J., Hickman, J. A. et al. Predictive validity in drug discovery: what it is, why it matters and how to improve it. Nat. Rev. Drug Discov. 21, 915–931 (2022). https://doi.org/10.1038/s41573-022-00552-x
[4] Mellnik, J. & Scannell, J. W. Tripartite models for estimating the value of drug candidates and decision tools. arXiv (2025). https://doi.org/10.48550/arXiv.2503.22117
[5] Koller, D. Drug discovery has no magic wands. Deep Phenotype (Substack), 3 August 2026. https://deepphenotype.substack.com/p/drug-discovery-has-no-magic-wands

Drug hunter and researcher of biomedical R&D productivity from both an economic and a scientific perspective. The term he coined in 2012, “Eroom’s Law,” is now widely referenced by anyone trying to innovate the current paradigm of drug discovery and development.
Jack is currently tackling age-related neurodegeneration at his early-stage biotech called Etheros.