🔬 Why AlphaFold Didn't Solve Protein Folding — Pushmeet Kohli, Google DeepMind & Sal Candido, Biohub

The moderator opens by reframing the “bitter lesson”—the idea that methods that scale eventually win—as a question about data. Sal Candido agrees that scaling can work, but warns against assuming scaling laws exist everywhere automatically. The difficult step is finding situations in which adding compute or data reliably improves the result; once that relationship is found, the work can become an engineering exercise of “turning the crank.” Sal emphasizes that architecture and data are inseparable. A model can only extract information from the data it has and generalize beyond it, so data must contain the relevant statistics for the desired capability. When asked whether modelers tend to choose problems simply because usable data already exists, Sal jokes that he is “lazy” and often works with what is available. He gives protein language models trained on metagenomic sequences as an example: much of that material may not even represent complete, real proteins, yet including it improves the design of functional proteins and the understanding of known proteins. He also warns that this success can encourage people to scale whatever data is easiest to generate rather than determining what data the scientific problem actually requires. The Biohub effort is valuable, he says, because it brings modelers, data generators, and the wider community together to identify the needed data and discover the relevant scaling law in an open way.

Pushmeet Kohli gives a more conceptual interpretation of the bitter lesson. His takeaway from Rich Sutton’s original argument is not simply that more data or compute always wins, but that researchers should avoid becoming “religious” about their role as modelers or data generators. The problem comes first, and the team should search flexibly across modeling, data collection, compute, and scientific expertise. He says older machine-learning practice often treated the dataset as fixed—training data on one side, test data on the other—while researchers optimized only the model. That approach is broken when the goal is to solve a real scientific problem. Kohli contrasts AlphaFold with work on “cell genomics” and the ambition to build a virtual cell. For AlphaFold, the existing Protein Data Bank represented an enormous investment by scientists worldwide, and DeepMind lacked both the resources and the expertise to expand it by orders of magnitude, so improving the modeling approach offered the best return. For the virtual-cell problem, however, the team concluded after substantial investigation that the necessary data did not yet exist. The correct response was therefore to bring people together around data generation rather than apply the AlphaFold strategy automatically. Kohli’s advice to newcomers is to become multidisciplinary, understand why the problem matters, identify the required combination of modeling, compute, and data, respect practical constraints, and “fail fast” on approaches that cannot reach the desired impact.

The moderator asks whether AlphaFold 2’s carefully designed, handcrafted features represent an older style of modeling that should give way to general, scalable strategies. Kohli argues that AlphaFold 2’s design was not arbitrary “arts and crafts.” The architecture incorporated scientific intuition from biophysics and biochemistry—especially the fact that amino-acid residues influence one another rather than acting independently. Encoding that knowledge gave the model an advantage and made it more data-efficient. Kohli adds that curating good data is itself an intellectual task. Simply replicating more examples does not necessarily help; researchers must understand the coverage required by the problem and determine what kinds of data are missing. Sal agrees that inductive bias is especially valuable when data is limited. As datasets grow, however, an incorrect or overly restrictive bias can prevent a model from discovering patterns that researchers did not anticipate. Sal also rejects the idea that scaling is devoid of craft. Making models larger and training them on more data requires algorithmic and infrastructure work, including faster inference and architectures adapted to their intended use. He says the field is not “post-transformer,” but researchers are modifying transformer-based systems and exploring more bespoke architectures even at internet-scale data. At every stage, progress involves both selecting the next useful information and choosing the architecture that can extract the most from it.

The moderator notes that public accounts often say protein structure prediction has been solved, while scientists continue to describe function, dynamics, and design as open problems. Kohli explains that the claim is true only in a narrowly defined sense. Proteins are not static building blocks: they can be disordered, change shape with context, and occupy distributions of structures. AlphaFold 2 was trained and evaluated largely on the practical task of reproducing structures that had already been experimentally determined and deposited in the Protein Data Bank. Kohli says that DeepMind did not know the “true ground state” of proteins or the full distribution of structures they take. AlphaFold 2’s ability to reproduce deposited structures nevertheless proved useful, but it did not amount to a complete understanding of protein dynamics. He argues that the community should celebrate the advance without using it as a reason to stop funding research into structure, dynamics, function, and design. Asked what he would create with a magic wand to accelerate one of those areas, Kohli chooses cryo-electron-microscopy micrographs. His computer-vision background makes him want to work directly from the raw images rather than only from structures already extracted into the PDB. Models that could scale over cryo-EM data while recovering dynamic and distributional information would be powerful, although he says his own attempts still require more work.

Sal says current models are useful but often solve a narrower problem than scientists ultimately care about. He compares modeling a single bicycle spoke with understanding the whole bicycle: researchers may need to move from models of individual parts to models of wheels and eventually complete bicycles. He adds that people sometimes use a model built for one component to design a part for something as different as a pickup truck, which illustrates the limits of taking a specialized model out of context. For protein science, Sal believes progress will come from placing increasingly capable models into the broader biological contexts in which proteins operate. Better structure models remain worthwhile, but understanding interactions among proteins and larger systems is necessary for the questions researchers actually want answered. This complements Kohli’s argument that biological understanding cannot be reduced to a single static structure. The panel then turns to whether useful design requires human-understandable models. Sal notes that scientists and engineers used “magical black boxes” to design things long before AI, so a system does not have to be fully interpretable to be useful. Still, he thinks understanding matters because models may contain far more information than researchers realize. Work on interpretability in protein language models has revealed representations associated not only with structure, but also with function and motion. Since these models compress information from evolution, examining their internal knowledge may teach scientists how biology works, not merely produce a successful protein.

Kohli distinguishes between understanding what a model can reliably do and understanding exactly how it produced every answer. He uses AlphaFold 2’s performance and confidence estimates to make the point: even if the model achieved a very high accuracy score, an uncalibrated confidence measure would make it unsafe to trust. A prediction that appears highly certain but is wrong could send scientists down an unproductive year-long path. He says AlphaFold 2 became more interpretable at a behavioral level after its release. Once the weights were made available, researchers discovered that it could predict disordered regions even though that was not the headline capability for which it had been built. For Kohli, this demonstrates that the model generalizes in ways that were not fully anticipated. He also questions what “interpretable” means and for whom. AlphaFold 2 is not interpretable to a human in the sense of exposing a simple cognitive explanation for every operation. A much larger and more sophisticated model might be able to inspect its activations and infer how it works. Regardless, users need a careful characterization of a model’s strengths, limitations, uncertainty, and failure modes. Kohli agrees with the moderator’s paraphrase: strict mechanistic interpretability may not be essential, but evidence that enables humans to make trustworthy, actionable decisions is essential.

In the final exchange, the moderator asks for a quantitative prediction of when AI will begin producing results in the clinic. Kohli says the question is ill-posed because AI is already used across drug discovery and is already affecting work that leads toward clinical development. The more meaningful question is when AI will create a tenfold or hundredfold acceleration, but that depends on which stage is being accelerated—target discovery, lead optimization, preclinical work, toxicology, or something else. Kohli argues that the larger breakthroughs will require solving hard biological problems and building better biological models. The effort announced at the event matters, he says, because it is aimed at those foundational challenges. Sal is similarly reluctant to name a date for a drug made entirely by AI, but expects rapid progress because the tools are already being used throughout the field. Sal returns to a lesson from his earlier career at Google: seeking a 10x improvement can be more productive than seeking a 10% improvement, not because it is easier, but because it forces researchers to reconsider the problem from first principles and notice approaches they would otherwise miss. He says both incremental and transformational work are needed. Biohub’s mission to “cure all disease,” in his phrasing, makes the search for a genuinely 10x path especially appropriate.