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I had the pleasure of speaking with Pushmeet Kohli, VP of Science and Strategic Initiatives at Google DeepMind, where he leads the unit behind some of the most consequential AI-for-science work of the past decade: AlphaFold, AlphaGenome, AlphaProof, AlphaEvolve, and AI Co-Scientist, alongside work spanning fusion, materials science, weather, and quantum computing. Before DeepMind, he spent over a decade at Microsoft Research working on computer vision and machine learning.

DeepMind pursues problems the field agrees are transformative and inevitable but believes are decades away; betting that they can be solved in a third of the time. Pushmeet is leading one of the most ambitious AI for Science teams in the world, tackling important problems. I was keen to understand how he and his team select those problems, and how he sees science advancing in the near future.

In this interview we discuss:

• The four-condition framework DeepMind uses to select problems, and why the unit only takes on roughly two new ones per year.
• Why the distinction between “predictive” and “visionary” AI may be a category error.
• The bottlenecks on virtual cells (and virtual organisms) and scaling laws in biology.
• The three forms of intelligence and why fixating on the AlphaFold-style cases underrates how the other two will reshape research.

This was a live interview and the transcript has been edited for readability.

Pablo Lubroth: Tell us about your role at DeepMind and your background.

Pushmeet Kohli: I lead the Science and Strategic Initiatives unit at DeepMind. The whole purpose of the unit is to go after problems that can have transformative impact. There is a very simple algorithm we follow to isolate problems the unit works on:

• The first step is to find problems where there is complete consensus in the community that, if solved, will be transformative; it will completely change the way something is done.
• The second requirement is that there should also be consensus that this problem is inevitable; we don’t want to work on infeasible things.
• The third requirement is that there should be almost a consensus that, even though it’s inevitable and transformative, it’s not going to be solved in the next five to ten years.
• The fourth condition is that we believe the community consensus is correct on the first two points and incorrect on the third: that we can solve the problem in half or one third of the time the community believes will be needed.

If those four conditions are met, then we take on those problems. We started with key problems in biology, materials science, and quantum chemistry, and over the last eight to nine years really expanded across fusion, mathematics, algorithmic discovery, quantum computing, weather, geospatial understanding, and many other projects.

You span mathematics, machine learning, computer vision, drug discovery, quantum computing. Most scientists go deep in one area. How do you actually develop enough domain competence to make original contributions across fields, and what’s your strategy?

When you’re looking at any problem, you really need to have an understanding of why this problem is interesting, and how you measure progress on the problem. There’s the what and the how of the problem. The what cannot be short-circuited. You really need to understand the problem deeply, including what metrics will quantify progress. So we don’t start these projects ten at a time. We only do it one at a time. Over the last eight, nine years, we’ve only done roughly two each year, because there is a lot of work needed to define the problem crisply.