Can AI revolutionize materials discovery?

Cubuk starts by establishing how much of materials history was luck. Tungsten became usable as a light bulb filament around 1905 after it was dropped into liquid mercury by mistake and came out ductile. Lithium-ion storage fell out of work at Exxon that was aimed at superconductivity. Bardeen’s transistor notebooks show one of the best solid-state physicists who ever lived trying material after material, with silicon failing, germanium working, then trouble with the glue and the metal electrode. He is careful that none of this was purely random, since Bardeen knew the semiconductor would be something like silicon or germanium. But the pattern sets up the structural problem.

That problem is a contradiction he applies to science and to machine learning equally: the better you know a system, the more you can keep optimizing it, and that knowledge does not help you find something different. Expertise in material A does not get you to C, or even B. Machine learning has the same bias in sharper form, because accuracy falls off as you move away from the training distribution, and the materials worth predicting are precisely the ones furthest from what we already know. His asymmetry is that humans have at least demonstrated paradigm shifts and AI has not; today’s best models are strong on textbook-level work and weak on the creative jump. So the honest near-term claim is about exploitation rather than exploration, and he argues that is still worth a lot. Nobody knows, forty or fifty years on, why high-temperature superconductivity happens in cuprates. That did not stop researchers who had LBCO from swapping in a similar element to get YBCO, which was the first superconductor above liquid nitrogen temperature. Machine learning can plausibly accelerate that substitution search. It is not positioned to make the leap that put cuprates on the table in the first place, and Cubuk notes that even the human leap was made on reasoning about conventional superconductivity that turned out not to transfer well.

The constraint underneath all of this is data. The Inorganic Crystal Structure Database holds a bit more than 200,000 inorganic crystals, which is nothing beside internet scale. Simulation can manufacture more, and does: the GNoME work trained on several million computed points and other groups are now at tens of millions, with returns that appear to follow a predictable power law in the amount of data. The trouble is that a crystal structure is not a property. For most of those 200,000 entries nobody has measured the band gap or the electronic conductivity, so the labeled set for a given property can fall to a thousand or two thousand points. The hoped-for path is the one large language models took, pre-training on abundant low-quality data and fine-tuning on a smaller set of real measurements, but Cubuk offers that as a maybe rather than a result. Worse for the near term, he makes a point that is easy to miss: experimental uncertainty in materials science is usually at the same level as computational error. That means the labels are too noisy to improve simulations against, which is a ceiling that no amount of model work removes. It is also why he cannot imagine eliminating lab work. When Kann suggests the chicken-and-egg version, that you might need much more lab work up front to train the thing meant to replace lab work, Cubuk agrees and points to efforts building experimental synthesis datasets for exactly that reason.

Where the field lands first therefore depends less on AI than on which physics the underlying simulation handles well. Density functional theory predicts structural stability better than it predicts electronic properties such as band gap, which makes optical applications a poor early bet and batteries a good one, since stability and how fast lithium moves through an electrolyte are the kinds of question it answers. Catalysis is attractive but the reacting surface is messy and changes during use. Superconductivity involves quantum interactions the method may simply not reach. A second filter comes from the product rather than the physics, and Kann and Cubuk build it together: the problems that fit are self-contained ones. A solid electrolyte is not a battery and has to work with the cathode, the anode, the interfaces and the manufacturing line, whereas a carbon-capture sorbent is closer to being a product by itself, which is Cubuk’s speculation about why so many startups pitch metal-organic frameworks. He adds that MOFs are not currently very commercially impactful, so those startups are betting on the future. And there is no AlphaFold moment in sight, because AlphaFold had a problem the community cared about and an objective, shared benchmark to be measured on. Materials science does not have one yet, and building one runs into the noise problem again, which is why the missing ingredient on his account is clean experimental data at least as much as better models.