Terence Tao – Kepler, Newton, and the true nature of mathematical discovery

We begin the episode with the absolutely ingenious and surprising way in which Kepler discovered the laws of planetary motion. People sometimes say that AI will make especially fast progress at scientific discovery because of tight verification loops. But the story of how we discovered the shape of our solar system shows how the verification loop for correct ideas can be decades (or even millennia) long. During this time, what we know today as the better theory can actually make worse predictions. And the reasons it survives this epistemic hell is some mixture of judgment and heuristics that we don’t even understand well enough to actually articulate, much less codify into an RL loop. Hope you enjoy! Watch on YouTube https://youtu.be/ztcKyI8_w6k; read the transcript https://www.dwarkesh.com/p/terence-tao. Sponsors - Jane Street https://janestreet.com/dwarkesh loves challenging my audience with different creative puzzles. One of my listeners, Shawn, solved Jane Street’s ResNet challenge and posted a great walk-through on X https://x.com/hynwprk/status/2026376546286711206. If you want to try one of these puzzles yourself, there’s one live now at janestreet.com/dwarkesh https://janestreet.com/dwarkesh. - Labelbox https://labelbox.com/dwarkesh can get you rubric-based evals, no matter your domain. These rubrics allow you to give your model feedback on all the dimensions you care about, so you can train how it thinks, not just what it thinks. Whatever you’re focused on—math, physics, finance, psychology or something else—Labelbox can help. Learn more at labelbox.com/dwarkesh https://labelbox.com/dwarkesh. - Mercury https://mercury.com/insights just released a new feature called Insights. Insights summarizes your money in and out, showing you your biggest transactions and calling out anything worth paying attention to. It’s a super low-friction way to stay on top of your business. Learn more at mercury.com/insights https://mercury.com/insights. Timestamps (00:00:00) – Kepler was a high temperature LLM (00:11:44) – How would we know if there’s a new unifying concept within heaps of AI slop? (00:26:10) – The deductive overhang (00:30:31) – Selection bias in reported AI discoveries (00:46:43) – AI makes papers richer and broader, but not deeper (00:53:00) – If AI solves a problem, can humans get understanding out of it? (00:59:20) – We need a semi-formal language for the way that scientists actually talk to each other (01:09:48) – How Terry uses his time (01:17:05) – Human-AI hybrids will dominate math for a lot longer This is a public episode. If you would like to discuss this with other subscribers or get access to bonus episodes, visit www.dwarkesh.com https://www.dwarkesh.com?utm_medium=podcast&utm_campaign=CTA_1

Speaker names marked ? are inferred from speaking time and the show’s known hosts — they are not voice-verified.

• 0:00Dwarkesh Patel?

  Okay, today I'm chatting with Terence Tao. Who needs an introduction? Terrence, I want to begin by having you retell the story of how Kepler discovered the laws of planetary motion. Because I think this will be a great jumping off point to talk about AI for math.

• 0:15Speaker 01

  Okay, yeah, so I've always had an amateur interest in astronomy. And so I've loved stories of how the early astronomers worked out the nature of the universe. So Kepler was building on the work of Copernicus, who was himself building on the work of Aristarchus. So Copernicus very famously proposed the heliocentric model that instead of the planets and the sun going around the earth, that the sun was at the center of the solar system and the other planets were going around the sun. And Copernicus proposed that the orbits of the planets were perfect circles. And his theory kind of fit the observations that the Greeks and the Arabs and Indians had worked out over centuries.

• 0:56Speaker 01

  I think Kepler got interested, like he learned about these theories in his studies. And he made this observation that the ratios of the size of the orbits that Copernicus predicted seemed to have some geometric meaning. I think he started proposing that, you know, if you take, say, the orbit of, say, the earth and you enclose it in, I think, maybe a cube, the outer sphere of that that encloses the cube almost matched perfectly the orbit of Mars and so forth. And there were six planets, none at the time, five gaps between them. And there were five perfect platonic solids, the cube, the tetrahedron, isosceles octagon, and dodecahedron. And so he had this theory, which he thought was absolutely beautiful,

• 1:38Speaker 01

  that he could inscribe these platonic solids between the spheres of the planets. And it seemed to fit. And it seemed to him like, you know, God's design of the planets was matching this mathematical perfection of the platonic solids. So he needed data to confirm this theory. And at the time, there was only one really high-quality data set. It almost in existence, okay, which was the, so Tycho Brahe, this Danish astronomer, very wealthy eccentric astronomer, had managed to convince the Danish government to fund this extremely expensive observatory, this in fact, an entire island, where he had taken decades of observations of all the planets, Mars, Jupiter, every night, at least every night for which the weather was clear.

• 2:22Speaker 01

  With a naked eye, actually, this is, he was last of the naked eye astronomers. And so he had all this data which Kepler could use to confirm his theory. And so Kepler started working with Tycho, but Tycho was very jealous of the data. He only gave little bits of it at a time. And I think Kepler eventually just stole the data. Actually, he copied it and had to have a fight with Brahe's descendants. But he did work out, he did get the data, and then he worked out to kind of his disappointment that his beautiful theory didn't quite work. Like, the data was sort of off from his platonic solid theory by about 10% or something. And he tried all kinds of fudges, moving the circles around and things. It didn't quite work. But he worked on this problem for years and years.

• 3:05Speaker 01

  And eventually, he figured out how to use the data to work out the actual orbits of the planets. And that was incredibly clever, genius amount of data analysis. And yeah, and then he eventually worked out that the orbits are actually ellipses, not circles, which was shocking for him. And then he worked out, so he worked out the two laws of planetary motion, ellipses, also equal areas, super equal times. And then 10 years later, after collecting a lot of data, the furthest planets like Saturn and Jupiter were the hardest for him to work out. But then he finally worked out this third law also, that the orbits, that the time

• 3:50Speaker 01

  it takes for a planet to lose orbit was proportional to some power of the distance to the sun. And these are the three famous Kepler's laws of motion. And he had no explanation for them. It was just all driven by experiment. And it took Newton a century later to give a theory that explained all three laws at once.

• 4:09Dwarkesh Patel?

  The take I want to try on you is that Kepler was a high-temperature LLM.

• 4:16Dwarkesh Patel?

  Where Newton comes up with this explanation of why the three laws of planetary motion must be true. And of course, the way that Kepler discovers the laws of planetary motion, or figures out the relative orbits of the different planets is, as you say, a work of genius. But then, you know, through his career, he's just trying random relationships. And in fact, in the book in which he writes down the third law of planetary motion, it's sort of an aside on the harmonics of the world, which is this book about, you know, all these different planets have these different harmonies. And the reason there's so much famine and misery on Earth is because the Earth is mi fa mi. That's the note of Earth. And so all this random astrology. But in there is the cube square law, which tells you what relationship the period has to a planet's distance from the sun, which is, as you were detailing,

• 5:03Dwarkesh Patel?

  if you add that to Newton's F equals ma and then the equation for centripetal acceleration, you get the inverse square law. And so Newton works that out. But the reason I think this is an interesting story is, I feel like LLMs can do the kind of thing of like 20 years, let's try random relationships, some of which make no sense, as long as there's a verifiable data bank, like Brahe's dataset, where, okay, I'm going to try out random things about like musical notes. I'm going to try out random things about platonic objects. I'm going to, all these different geometries, I have this bias that there's some important thing about the geometry of these orbits. And then one thing works. And as long as you can verify it, it can then drive, these empirical regularities can then drive actual deep scientific progress.

• 5:44Speaker 01

  Traditionally, when we talk about the history of science, idea generation has always been kind of the prestige part of science. So, I mean, a scientific problem comes with, there's many steps. You know, you have to identify a problem, and then you have to identify a good problem to work on, a fruitful problem. And then you need to collect data. You need to figure out a strategy to analyze the data, to make a hypothesis. And at this point, you need to propose a good hypothesis, and then you need to validate. And then you need to write things up and explain. There's a dozen different components. But yeah, the ones we celebrate are these sort of eureka genius moments of idea generation.

• 6:22Speaker 01

  And yeah, so Kepler certainly had to, as you say, cycle through many ideas and several which didn't work and I bet many that he didn't even publish at all because yeah, they just didn't fit. And that's an important part of the process, trying all kinds of random things and seeing if they worked. But as you say, the, you know, the, it have to be matched by an equal amount of verification, otherwise it's slop. I mean, we celebrate Kepler, but we should also celebrate Brahe for his assiduous data collection with, which was 10 times more precise than any previous observation. And it was, that extra decimal point of accuracy was actually essential for Kepler to get his, his results.

• 7:07Speaker 01

  And, you know, and he was using, you know, Euclidean geometry and like, the most advanced mathematics he could use at the time to match his models of the data. So like, all aspects had to be in play, you know, the data and the theory and the hypothesis generation. I'm not sure nowadays that hypothesis generation is the bottleneck anymore. Sciences has changed in the century since. So classically, sort of the two big paradigms for science were theory and experiment. Then in the 20th century, numerical simulation came along.

• 7:48Speaker 01

  And so you can also do computer simulations of, to test theories. But then finally, in late 20th century, we had big data. We had the era of data analysis. And so a lot of new progress is actually driven now by analyzing massive data sets first, collecting large data sets, and then drawing the patterns from them to deduce laws, which is a little bit different from how science used to work, where you make a few observations or you just have one out of the blue idea. And then you collect data to test your idea. That's a classic scientific method. Now it's almost reverse. You collect big data first and then you try to get hypotheses from it. I mean Kepler was maybe one of the first early data scientists,

• 8:28Speaker 01

  but even he didn't start with Tycho's dataset and analyze it. He had some preconceived theories first. But it seems like this is less and less the way we make progress in just because the data is just so much more massive. It's just so much more useful.

• 8:48Dwarkesh Patel?

  Oh, interesting. I actually feel like the more the 20th century science that you're describing is actually very well describes what happened in Kepler, where he did have these ideas. 1595 and 96 is where he comes up with the first polygons and then platonic objects theory, but they were wrong. And then a few years later, he gets Brahe's data. And it's only after 20 years of just trying random things that he gets this empirical regularity. And so it actually feels closer to Brahe's data is analogous to some massive data bank of simulations. And then now that you've got the data, you can keep trying random things. But if it wasn't, Kepler would be out there just writing books about harmonics and platonic objects.

• 9:32Dwarkesh Patel?

  And there would be nothing to actually verify against.

• 9:35Speaker 01

  Yeah, yeah, yeah. So the data was extremely important. But the distinction I was trying to make was that sort of traditionally you make a hypothesis and then you test it against data.

• 9:45Dwarkesh Patel?

  Yeah.

• 9:47Speaker 01

  But now with machine learning and data analysis and statistics and so on, you can start with data and through, say, statistics, work out laws that were not present before. And so Kepler's third law is a little bit like this, except that for the third law, instead of having the thousand data points that Brahe had, Kepler had like six data points, like every planet. He knew the length of the orbit and the distance to the sun. And there was like five or six data points. And he did what we would now call regression. You know, he could fit a curve to these six data points. And he got a square coupler, which was amazing. But actually, he was quite lucky. I mean, that these six data points gave him the right conclusion.

• 10:30Speaker 01

  You know, that's not enough data to be really reliable. There was a later astronomer, Johannes Bode, who took the same data, actually, the distances to the planets. And inspired by Kepler, I think, he had a prediction that the distances to the planets formed basically a shifted geometric progression. He also fit a curve, except there was one point missing. So there's a big gap between Mars and Jupiter. His law predicted that there was a missing planet. So it was a kind of a crank theory, except when Uranus was discovered by Herschel, the distant Uranus fit exactly this pattern. And then Ceres was discovered, this asteroid between, I think, in the asteroid belt, and it also fit the pattern.

• 11:11Speaker 01

  So people got really excited that the board had discovered this amazing new law of nature. But then Neptune was discovered, and it was completely way off. And, you know, and basically it was just a numerical fluke. You know, there were six data points. Yeah, so maybe one reason why Kepler didn't highlight his third law as much as the first two laws is that maybe instinctively, even though he didn't have modern statistics, he kind of knew that with six data points, he had to be somewhat tentative with the conclusions.

• 11:44Dwarkesh Patel?

  But maybe to ask the question about the analogy more explicitly. Does this analogy make sense to if we have, you know, in the future we'll have smarter and smarter AIs, and we'll have millions of them, and then they can go out and hunt for all these empirical regularities? It sounds like you don't think the bottleneck in science is finding more things that are for each given field, their equivalent of the third law of planetary motion, so that then later on, somebody can say, oh, we need a way to explain this, let's work out the math, here's the inverse square law of gravity.

• 12:16Speaker 01

  Right, so I think AI has basically driven the cost of idea generation down to almost zero. In a very similar way to how the internet drove the cost of communication down to almost zero. Which is an amazing thing, but it doesn't make, it doesn't create abundance by itself. Yeah, so now the bottleneck is different. So we're now in a situation where suddenly people can generate thousands of theories for a given scientific problem. And now we have to verify them, evaluate them. And this is something which we have to change our structures of science to actually sort this out. So, you know, in fact, traditionally, we build walls, you know, so in the past, you know, before we had AI slop, you know, we had sort of amateur scientists, you know,

• 13:00Speaker 01

  have their own theories of universe, many of which were basically of very little value.

• 13:07Speaker 01

  And so we've built these peer review publication systems and things to kind of filter out and try to isolate the high signal ideas to test. But now that we can generate these possible explanations at massive scale, and some of them are good and a lot are terrible. I mean, human reviewers, they're already being overwhelmed, actually. Many, many journals are reporting AI. Journal submissions are just flooding their submissions. So it's great that we can generate all kinds of things now with AI, but it means that we have to, the rest of the aspects of science have to catch up.

• 13:45Speaker 01

  So verification, validation, and assessing what ideas actually move the subject forward and which ones are dead ends or red herrings. And that's not something we know how to do at scale. For each individual paper, we can discuss it, have a debate among scientists and get to a consensus in a few years, but when we're generating a thousand of these every day, this doesn't work.

• 14:12Dwarkesh Patel?

  So I think there is this incredibly interesting question of you have billions of AI scientists. Not only how do you gauge which ones are real progress, but how do you, I mean, this is actually a question that human scientists had to face and we've solved somehow. And I'm, I actually am not sure how we solved this, but in any given field, let's say in the 1940s, and if you're at Bell Labs, or if you're just generally trying to, there's these new technologies coming out, pulse code modulation, basically how do you transfer signals, how do you digitize signals, how do you transfer them over analog wires? But there's like all these papers about the engineering constraints there and the details. And then there's one which is like, comes up with the idea of the bit, which has implications across many different fields. And you need some system which can then look at that and say, okay, we need to apply this

• 14:55Dwarkesh Patel?

  to probability, we need to apply this to computer science, et cetera. And in the future, the AIs are coming up with the next version of this kind of unifying concept. And how would you identify it among millions of papers, which might actually constitute progress, but which have much less general unifying ideas?

• 15:13Speaker 01

  So a lot of it's the test of time. So many great ideas. Didn't actually get a great reception at the time that they were first proposed. It was only after some other scientists realized that they could take it further and apply them to their own. You know, deep learning itself was actually a niche area of AI for a long time. The idea of getting answers entirely through training on data and not through first principles, you know, reasoning was very controversial and it just took a long time before it actually started bearing fruit. You know, you mentioned the bit, you know, I mean, there are other proposals for computer architectures than the zero one that is universal today. I think there were trits, you know, zero one, three valued logic. And, you know, in an alternate universe, maybe a different paradigm would have showed up.

• 16:00Speaker 01

  People have argued that, you know, the transformer, for example, is the foundation of all modern large language models. And it was the first deep learning architecture that really was sophisticated enough to capture language. But it didn't have to be that way. There could have been some other architecture that was the first to do it. And once that was adopted, it would become the standard. So I think one reason why it's hard to assess whether a given idea is going to be fruitful is that it depends on the future. It depends on, and it depends also on the culture and society, like which ones get adopted, which ones don't. You know, the base ten, neural system in mathematics, extremely useful, much better than the Roman neural system, for instance.

• 16:45Speaker 01

  But again, there's nothing special about ten. It's a system that we, it's useful for us because everyone else uses it. And we've standardized it and we've built all our computers and our number of representation systems around it. And so we're stuck with it now, actually. You know, some people occasionally push for other systems than decimal, but it's, this is no, this is no, there's too much inertia.

• 17:09Speaker 01

  So.

• 17:11Speaker 01

  You can't look at any given scientific achievement purely in isolation and give it an objective grade without being aware of the context, both in the past and the future. And so it may never be something that you can just reinforce and learn the same way that you can for much more localized problems.

• 17:30Dwarkesh Patel?

  Yeah. It seems often in the history of science, when a new theory comes up that in retrospect we realize is correct, it seems to make implications that just either make no sense because they're wrong and we realize later on why they're wrong, or they're correct but seem wildly implausible at the time. So, as you talked about, Aristarchus had heliocentrism in the third century B.C. and then the ancient Athenians were like, this can't be, because if the earth is going around the sun, we should see the relative position of the stars change as we're going around the sun. And the only way that wouldn't be the case is if they're so far away that you don't notice any parallax, which is actually the correct implication.

• 18:14Dwarkesh Patel?

  But there's times when actually the implication is incorrect and we just need to graduate to a better level of understanding. So Leibniz would chide Newton and disagree with Newton's theory of gravity on the basis that it implied action at a distance, and then we don't know the mechanism. And Newton himself was stunned that inertial mass and gravitational mass were the same quantity. So all these things, the literature was resolved by Einstein.

• 18:36Speaker 01

  Yes, yes.

• 18:37Dwarkesh Patel?

  But it was still progress. And so the question for a system of pure Euclideanian would be, even if you can falsify a theory, how would you notice that it still constitutes progress, relative to the thing before?

• 18:49Speaker 01

  Yeah, so often, actually, the ultimately correct theory initially is worse in many ways. Yeah, so Copernicus's theory of the planets, it was less accurate than Tomlin's theory. So heliocentrism had been developed for a millennium by that point, and they had many, many tweaks and very increasingly complicated ad hoc fixes to make it more and more accurate. And Copernicus's theory was a lot simpler, but much less accurate. There was only Kepler that made it more accurate than Tomlin's theory. I mean, science is always a work in progress. So when you only get part of the solution, it looks worse than a theory which is incorrect,

• 19:30Speaker 01

  but somehow has been completed to the point where it kind of answers all the questions. As you say, Newton's theory had big mysteries, the equivalence of mass and action at distance, which were only resolved with a very conceptually different approach centuries afterwards.

• 19:54Speaker 01

  Often, progress has been made not by adding more theories, but by deleting some assumptions that you have in your mind. So, you know, one reason why geocentrism held on for so long is we had this idea that objects naturally want to stay at rest. This is the Aristotelian notion of physics. And so the idea that the Earth was moving, how come we weren't all falling over? Once you have Newton's motion, object in motion remains in motion and so forth, then it makes sense. But you had to, so conceptually, it's a very big conceptual leap to realize that the Earth is in motion. It doesn't feel like it's in motion.

• 20:33Speaker 01

  And the biggest advances, Darwin's theory of evolution,

• 20:39Speaker 01

  the idea that species are not static. But this is not obvious because you don't see evolution in your lifetime. Well, now we actually can, but it seems permanent and static.

• 20:57Speaker 01

  Right now, we're going through

• 21:00Speaker 01

  a cognitive version of the Copernican revolution, where we used to think that human intelligence is the center of the universe. And now we're actually seeing that there's very different types of intelligence that are out there with very different strengths and weaknesses. And so our assessment of which tasks require intelligence, which ones don't, has to be reworked quite a bit.

• 21:22Speaker 01

  And so, you know, trying to fit AI into our theories of scientific progress and what is hard and what is easy, we're struggling quite a lot. We have to ask questions that we've never really had to ask before. Or maybe the philosophers had, but now we all have to deal with it.

• 21:37Dwarkesh Patel?

  Brings up a topic I've been very curious about. So you mentioned Darwin's theory of evolution. There's this book, The Clockwork Universe by Edward Dolnick, which covers a lot of this era of history we're talking about. And he has this interesting observation in there that The Origin of Species is published in 1859. The Principia Mathematica is published in 1687. So The Origin of Species comes out basically two centuries after the Principia. And conceptually, it seems like Darwin's theory is simpler. There's a contemporaneous biologist to Darwin who reads The Origin of Species, Thomas Huxley, and he says, "How stupid not to have thought of that." And nobody ever says that about Principia. They're shiding themselves for not having beaten Newton to gravity. And so there's a question of, well, why did it take longer? It seems like a big part of the reason is that the evidence for natural selection

• 22:22Dwarkesh Patel?

  is cumulative and retrospective, whereas Newton can just like, "Here's my equations, let me see the moon's orbital period and its distance. And if it lines up, then we've made progress." And so Lucretius actually had the idea, this idea that species adapted their environment in the first century B.C., but nobody ever really talks about it until Darwin, because Lucretius can't run some experiment and people are forced to pay attention. And so I wonder if we'll, in retrospect, end up seeing much more progress in domains, which have this kind of tight data loop, where you can verify them quite easily, even though they're conceptually much more difficult.

• 23:01Speaker 01

  I think one aspect of science is it's not just creating a new theory and validating it, but communicating it to others. So Darwin was actually an amazing science communicator. He wrote in English, in natural language, I'm speaking like that.

• 23:18Dwarkesh Patel?

  No lean.

• 23:20Speaker 01

  Okay, I have to sort of get out of my technical mindset. He spoke in plain English. You know, didn't use equations. And he synthesized a lot of disparate factors. So, you know, little pieces of evolution had been worked out in the past, but he had this very compelling vision. And again, still missing things like he didn't know the mechanism for hereditary DNA.

• 23:49Speaker 01

  Yeah, but his writing style was persuasive and that helped a lot. Newton wrote in Latin. He invented entire new areas of mathematics just to explain what he was doing. He was also from an era which was where scientists were much more secretive and competitive. So academia is still competitive, but it was even worse back in Newton's day. So he held back some of his best insights because he didn't want his rivals to get any advantage. He was also, okay, somewhat unfusen person from what I gather, actually. So it was actually only a couple of decades after Newton where other scientists explained his work in much simpler terms that they became widespread.

• 24:33Speaker 01

  So, yeah, the art of exposition and making a case and creating a narrative is also a very important part of science. And if you have the data, it helps, but people need to be convinced. Otherwise, they will not push it further or they won't take initial investment to learn your theory and really explore it.

• 24:57Speaker 01

  And that's another thing which is really hard to reinforce and learn on. How can you score how persuasive you are? Okay, well, okay, there's the entire marketing departments who are trying to do this. So maybe it's good that AI are not yet optimized to be persuasive. So, yeah, there's a social aspect to science. Even though we pride ourselves on having an objective side to it where there's data and there's experiment and validation, we still have to tell stories and convince fellow scientists. And that's a soft, squishy thing. Like it's a combination of data and.

• 25:38Speaker 01

  Yeah, and painting a narrative and it's been out of gaps. You know, I mean, as you know, so even Darwin, as I said, there are pieces of his theory he cannot explain, but he could still make a case that, you know, in the future, people would would would find transitional forms, that they would find the mechanism of inheritance. And they did. Yeah, I don't know how you can quantify that in such a precise way that you can start to reinforce some learning. Maybe that was to be forever the human side of science.

• 26:09Dwarkesh Patel?

  One takeaway I had from reading and watching your stuff on the cosmic distance ladder. By the way, I highly, highly, highly recommend people watch your series with Through the One Round on the Cosmic Distance Ladder. But one takeaway was that the deductive overhang in many fields could be so much bigger than people realize, where if you just had the right insight about how to study a problem, you might be surprised at how much more you could learn about the world. And I wonder if you think that's sort of a product of astronomy at the particular times in history that you're studying, or is this that based on the data that is incident on the earth right now, we could actually divine a lot more than we happen to know?

• 26:51Speaker 01

  Right, so astronomy was one of the first sciences to really embrace data analysis and squeezing every last possible drop of information out of the information they had because because data was the bottleneck. I mean, it still is a bottleneck. I mean, it's really hard to to collect astronomical data. So astronomers are the best, you know, almost world class in extracting, you know, almost like Sherlock, you know, like extracting all kinds of conclusions from little traces of data. I hear that a lot of quant hedge funds, they preferred hires in astronomy PhD. They also are very interested for other reasons in extracting signals from various random bits of data.

• 27:35Dwarkesh Patel?

  Okay, speaking of clever ideas, one of my listeners, Sean, solved the puzzle that Jane Street made for my audience and posted a great walkthrough on X. For context, Jane Street trained a ResNet and then shuffled all 96 layers and then challenged people to put them back in the right order using only the model's outputs and training data. You can't brute force this. There's more possible orderings than atoms in the universe. So Sean broke the problem into two different parts. First, pair the layers into 48 different blocks. And second, put those blocks in the right order. For pairing, Sean realized that in a well-trained ResNet, the product of two weight matrices in a residual block should have a distinctive negative diagonal pattern. And this arises as a way for the model to keep the residual stream from growing out of control.

• 28:20Dwarkesh Patel?

  From this insight, he was able to recover the right pairings. For ordering, Sean noticed that the model seemed to improve if he sorted the blocks by the size of their residual contributions. Starting with that rough approximation, he combined a clever ranking heuristic with local swaps to recover the exact right order. His full walkthrough is linked in the description. Don't worry if you didn't get to this puzzle in time, though. There's still one up about backdoor LLMs that even Jane Street doesn't know how to solve. You can find it at janestreet.com/thawcash. All right, back to Terrence.

• 28:49Speaker 01

  We do under-explore how to extract extra information from various signals. Like, I just to pick one random study. I remember reading once that people had discovered, we're trying to measure how often scientists actually read the citations that the papers cite. So how do you measure this? Okay, you could try to survey different scientists, but they had some clever trick. So many citations have little typos, like a number is wrong or punctuation symbol is wrong. And they measured how often a typo got copied from one reference to the next, and they

• 29:33Speaker 01

  could infer whether an author was actually just copying, cutting and pasting a reference without actually checking it. And so from that, they were able to infer some measure of how much attention people were paying. So there are also clever tricks to extract. You know, so these questions you posed earlier of, you know, how can we assess whether a scientific development is fruitful or interesting or represents real progress, you know? Maybe there are really useful metrics and or footprints of this phenomenon in data, so we can examine citations and like how often something is mentioned in a conference or something.

• 30:17Speaker 01

  And maybe there's a lot of sociology of science research to be done and that could actually detect these things. Yeah, maybe we usually get astronomers on the case, actually.

• 30:31Dwarkesh Patel?

  Okay, so I think this brings us nicely to the progress that from the outside, it seems like AI for math is making. And I think you had a post recently where you pointed out that over the last few months, AI programs have solved 50 out of the 1100 odd Burdo's problems, but then I think, I don't know if it's still correct, but as of a month ago, you said that there had been a pause because the low hanging fruit had been picked. First of all, I'm curious if actually that is still the case, that we have picked the low hanging fruit and now we're at this plateau currently.

• 31:02Speaker 01

  It does seem so. I mean, there's still activity at the early, yeah. So 50 odd problems have been solved with AI systems, which is great, but there's like 600 to go. And people are still chipping away at one or two of these right now. We're seeing a lot fewer sort of pure AI solutions now where the AI just one shots the problem. So there was a month where that happened and that has stopped. Not for lack of trying. I know three separate attempts to get frontier model AI to just attack every single one of the problems simultaneously. And they picked up some minor observations or maybe they found that some problems are already solved in the literature, but there hasn't been any further AI purely powered solution yet.

• 31:47Speaker 01

  People are using AI a lot currently. So someone might use AI to generate a possible proof strategy. And then another person will use a separate AI tool to critique it or rewrite it or generate some numerical data for it or do a literature survey.

• 32:04Speaker 01

  And and some problems have been solved by a ongoing conversation between lots of humans and lots of AI tools. But it it it does seem like it it was this this one off thing. So maybe one analogy to for these problems is like, imagine like, there's there's all these that you're in some sort of mountain range with all kinds of of cliffs and walls. And and maybe there's a there's a there's a little wall, which is maybe like three feet high and one this six feet high and then this fifteen feet high and then this there's there's some mile high cliffs. And you're trying to climb as many of these cliffs as possible, but it's in the dark. We don't know which ones are tall, which ones are short.

• 32:45Speaker 01

  And so, you know, we try to light some candles and make some maps and and slowly we kind of figure out some of them are are climbable, some of them we can identify some some partial track in the wall that you can reach first. And then these these AI tools, they're kind of like these jumping machines that can kind of jump, you know, two meters in the air, you know, higher than than any human. And sometimes they jump in the wrong direction and sometimes they they crash, but sometimes they they they can reach the tops of of of the lowest, you know, walls that we we couldn't reach before. And so we basically set them loose in this mountain range, hopping around. And, you know, and then there's this exciting period where they they could actually find all the all the low ones and that they could reach them.

• 33:29Speaker 01

  But then there's been no, you know, I mean, maybe if the next time there's a big advance in the models, then they will try it again and maybe a few more will be will be will be breached. But it it it's a different style of doing mathematics than sort of the, you know, so normally we would hill climb and, you know, we would we would make little markers and and and try to identify partial things. And, you know, the these tools, they either succeed or they fail. And they they've been really bad at creating sort of partial progress or identifying intermediate. Um, stages that you should you should focus on first. Again, going back to this previous discussion, you know, we don't have a way of evaluating partial progress.

• 34:13Dwarkesh Patel?

  Yeah.

• 34:14Speaker 01

  The same way we could, you can evaluate a one-shot success or failure of solving a problem.

• 34:19Dwarkesh Patel?

  So there's two different ways to think through what you've just said, and one of them is more bearish on AI progress, and one of them is more bullish and bearish on being, oh, they're only getting to a certain height of wall, which is not as high as humans are reaching.

• 34:33Dwarkesh Patel?

  And the second is that, well, they have this powerful property that once they achieve a certain waterline, they can fill every single problem that is available at that waterline, which we simply can't do with humans, where we can't make a million copies of you and give each of them a million dollars of inference compute and have you do a hundred years of subjective time research on a hundred different problems at the same time, or a million different problems at the same time. But once AIs reach Terran's Tower level, they could do that. And then once they reach intermediate levels, they could do, they could do the intermediate version of that. So the same reason that we should be bearish now is the reason we should be especially bullish, not even when they achieve superhuman intelligence, but just when they achieve human level intelligence, because their human level intelligence is qualitatively wider

• 35:18Dwarkesh Patel?

  and more powerful than our human level intelligence.

• 35:21Speaker 01

  I, I, I agree. Yeah, so they excel at breadth and humans excel at depth, like human experts at least. Yeah, so I think they're very complementary. But our current way of doing math and science is focused on depth, because that's where the human expertise is, because humans can't do breadth. But, uh, yeah, so we, we have to redesign the way we do science to take full advantage of, of this breadth capability that we now have. So as I said, we, we should have a lot more effort in creating very broad classes of problems to work on, rather than, than one or two really deep, important problems. I mean, we should still have the deep, important problems, and humans should still be working on them.

• 36:03Speaker 01

  But now we have this other way of doing of doing science. You know, I mean, we can explore entire new fields of science by first getting the these broad moderately competent AIs to sort of map it out and clear out all the easy, make all the easy observations, okay, and then identify certain islands of difficulty, which, you know, then human experts can come and and and work on. So I see very much a future of complementary science. Eventually, you would hope to get both breadth and depth, you know, and somehow get the best of both worlds. But I think we need practice with the breadth side, because it's too new.

• 36:46Speaker 01

  We don't even have the paradigms really to to to make full advantage of it, but we will. And then science will be unrecognizable after that.

• 36:55Dwarkesh Patel?

  To this point about complementarity, programmers have noticed that they're way more productive as a result of these AIs. And I don't know if you, as a mathematician, feel the same way, but it does seem like one big difference between vibe coding and vibe researching is that with software, the whole point of the thing is to have some effect on the world through your work. And if it leads to you better understanding a problem or you coming up with some clean abstraction to embody in your code, that is instrumental to the end goal. Whereas maybe with research, the reason we care about solving the millennium problems is presumably that in the process of solving them, we discover new mathematical objects

• 37:39Dwarkesh Patel?

  or better new techniques and those who understand our civilizations' understanding of mathematics. And so the proof is sort of instrumental to the intermediate work. I don't know if you agree with that dichotomy or if that in any way will explain the relative uplift we'll see in software versus research.

• 37:58Speaker 01

  Right. Yeah, so certainly in math, the process is often more important than the problem itself. The problem is kind of a proxy for for measuring the progress. And I think even in software, there's there's different types of software tasks. I mean, you know, like if you just kind of create a webpage that does the same thing that a thousand other webpages do, there's there's sort of no skill to be learned. Well, there's there's still some skill maybe that the individual programmer could pick up, but you know, for for kind of boilerplate type code, definitely, you know, it's it's something that you should definitely offload offload to AI. But you know, sometimes, once you make the code, you know, you still have to maintain it and there's issues with upgrading it and making it compatible with other things.

• 38:42Speaker 01

  And that, I think, I've heard that programmers are reporting, you know, that even if an AI can create the first prototype of a tool, making it mesh with everything else and making it interact with the real world in the way they want, I mean, that's an ongoing process. And if you didn't have the skills that you pick up from writing the code, that may impact your ability to maintain it down the road. So certainly, mathematicians, we've used problems to build intuition and to train people to have a good idea as what's true, what to expect, what is provable, what is difficult.

• 39:25Speaker 01

  And so, yeah, just getting the answers right away may actually inhibit that process. I mean, so I made this distinction between theory and experiment before. So in most sciences, there's an equal division between, there's a theoretical side and experimental side. But in math, it's been almost unique, it's almost entirely theoretical. We place a premium on sort of trying to have coherent, clean theories of why things are true and false. And we haven't done much experiments as to like, you know, maybe we have two different ways to solve a problem, which one is more effective? We have some intuition, but we haven't done large-scale studies where we take a thousand problems and we just test them.

• 40:10Speaker 01

  But we can do that now. So I think AI-type tools, we really will actually revolutionize the experimental side of math, where you don't care so much about individual problems and the process of solving them, but you want to gather just large-scale data about what things work, what things don't. Same way that if you want to, if you're a software company and you want to roll out a thousand pieces of software, you know, you don't really want to handcraft each one and learn lessons from each, you just want to find what are the workflows that let you scale. So we don't yet, the idea of doing mathematics at scale is at its infancy, but that's where AI is really going to revolutionize the subject.

• 40:52Dwarkesh Patel?

  Interesting. I feel like a big crux in these conversations about how much, how good AI will be for science is, I think you said this, it's like, oh, they're using existing techniques and modifying them. And it would be interesting to understand how much progress one can make simply from using existing techniques, like how much of, if I looked at the top math journals, how many of them are, how many of the papers are coming up with, whatever coming up with a new technique means, doing that versus using existing techniques in new problems and what the overhang is, where if you just applied every known technique to every open problem, would that just constitute a humongous uplift in our civilization's knowledge? Or would that not be that impressive and useful?

• 41:34Speaker 01

  It's, this is a great question.

• 41:38Speaker 01

  We don't have the data to fully answer it yet.

• 41:42Speaker 01

  Certainly, a lot of work that human mathematicians do, you know, when you, when you take a new problem, one of the first things we do is we just find, we, we look at all the standard techniques that have worked on similar problems in the past, and we try them one by one. And sometimes that works. And that's still worth publishing sometimes because the question was important. Sometimes they almost work and you have to add one more wrinkle to it, and that's also interesting. But then, you know, the papers that go into the top journals are usually ones where you, you know, the existing methods can kind of solve, you know, 80% of the problem, but then there's this 20%, which is resistant. And a new technique has to be invented to fill in the gaps. It's, it's very, very rare now that a problem gets solved with sort of no reliance on past literature,

• 42:26Speaker 01

  where all the ideas come out of, of, of nowhere. You know, that was more common in the past, but math is so mature now that it's, it would, it's just so much of a handicap to, to, to, to not use the literature first.

• 42:43Speaker 01

  So, yeah, AI tools are really good at, are getting really good at the first part of that, just trying all the standard techniques on a problem. Often now actually making fewer mistakes in employing them than, than, than humans. They still make mistakes, but, but I've, I've tested these tools, you know, on, on, on like little tasks that I can do. And, and sometimes they pick up errors that I make, sometimes I pick up errors that they make. It's about a tie right now.

• 43:11Speaker 01

  But.

• 43:13Speaker 01

  Yeah, I haven't yet seen them take the next step. You know, so when there are holes in the argument where none of the things are working, then what do you do? And then they can kind of suggest random things. And it but it often I find that trying to chase them down and make them work and finding they don't work, it wastes more time than it saves. Yeah.

• 43:37Speaker 01

  Now, so I think some fraction of problems that we currently think are hard will fall from this this method. I mean, especially the ones that haven't received enough attention. So like with the Erdem problems, you know, like almost all of the fifty problems that were solved by AIs were ones for which basically there was no literature. I mean, Erdem posed problems once or twice. I think maybe some people tried it casually and they couldn't do it, but they never wrote up anything. But it turned out that there was a solution and it was just, you know, maybe combining this one obscure technique that that not many people know about with some other result in the literature. And that's the kind of the median level of what AIs can accomplish. And that's really great. It clears out fifty of these problems.

• 44:20Speaker 01

  So I think you'll see some isolated successes. But the six but what we found, so people have to have done large scale sweeps of these Erdem problems. And like if you only focus on the success stories, the ones that get broadcast on social media, it looks amazing. You know, like all these problems that haven't been solved before for decades, now that now they're falling. But whenever we do a systematic study, any given problem, an AI tool has a success rate of maybe one or two percent. It's just that it's just that they can buy a scale and if you just pick the winners, it looks great. So I think there'll be a similar thing happening with, you know, there are hundreds of really prestigious, difficult math problems out there. A couple may make, you know, some AI may get lucky and actually solve them.

• 45:03Speaker 01

  And there was there was some some backdoor to solve the problem that everyone else missed. And that will get a lot of publicity. But then people will try these fancy tools on their own favorite problem and they will again experience the one to two percent success rate. Right. So there'll be a lot of noise amongst the signal of sort of when they're working, when they're not.

• 45:26Speaker 01

  We have to do, it's increasingly, it will be increasingly important to collect these really standardized data sets. You know, there are efforts now to create a standard set of challenge problems for, for AI to solve. And not just rely on the AI companies to only publish their wins and, and, and not disclose their, the negative results. So that will maybe give more clarity as to where, where we're actually at.

• 45:48Dwarkesh Patel?

  Well, I think it's worth emphasizing how much progress in AI constitutes already to have models that are capable of applying some technique that nobody

• 45:56Speaker 01

  Yeah.

• 45:57Dwarkesh Patel?

  had written down is applicable to this particular problem.

• 46:00Speaker 01

  The progress is simultaneously amazing and disappointing. It is, it is a very strange feeling to, to, to see these tools in action and, and, you know, but also be acclimatized really quickly. You know, I remember when, when, when Google's Web Search came out 20 years ago and it just blew all the others, all the searches out of the water. Like you're just getting relevant hits on the front page like perfectly, almost, you know, exactly what you wanted. And it was amazing. And then after a few years, you just took for granted that, that you could, you could just Google anything. And yeah, so a lot of, yeah, I mean, 2026 level AI would be stunning in 2021. And a lot of it, you know, face recognition, natural speech, yeah, doing, you know, college level math problems, we just take for granted now.

• 46:42Dwarkesh Patel?

  Right.

• 46:43Speaker 01

  Yeah.

• 46:43Dwarkesh Patel?

  Okay. So speaking of 2026, yeah, you made a prediction in 2023 that I think by 2026, what was it? That it would be like a colleague in mathematics or?

• 46:52Speaker 01

  Yeah, a trustworthy co-author if used correctly.

• 46:55Dwarkesh Patel?

  Which is looking pretty good in retrospect.

• 46:57Speaker 01

  Yeah, I'm, I'm pretty pleased. Yeah.

• 46:59Dwarkesh Patel?

  So, you know, let's see if you can continue the streak. You personally are 2X more productive as a result of AI. What year would you say that?

• 47:11Speaker 01

  Yeah. So productivity, I think, is not quite a one dimensional quantity. Like, I'm definitely noticing that the style in which I do mathematics is changing quite a bit and the type of things I do. So for example, my papers now have a lot more code, a lot more pictures.

• 47:28Speaker 01

  Because it's so easy to generate these things now. So some plot which have taken me hours to do now, I can, I can do in minutes. But in the past, I just wouldn't have put the plot in my paper in the first place. I would, I would just talk about it in words. So it's hard to measure, to measure what 2X means.

• 47:46Speaker 01

  So, yeah, on the one hand, you know, I think the type of papers that I would write today, if I had to do them without AI assistance, they would definitely take five times longer.

• 47:55Dwarkesh Patel?

  Interesting.

• 47:56Speaker 01

  But I would not write my papers that way.

• 47:58Dwarkesh Patel?

  Five X, so.

• 48:00Speaker 01

  Yeah, but it's because, but these are sort of auxiliary, I mean, you know, the, you know, so things, you know, things like doing a much deeper literature search, supplying a lot more numerics.

• 48:13Dwarkesh Patel?

  Yeah.

• 48:13Speaker 01

  I mean, they enrich the paper. So, yeah, the core of what I do, like actually solving the most difficult part of a math problem, that hasn't changed too much. I still use pen and paper for that. But, you know, there's lots of silly things. I use an AI agent now to reformat. Like sometimes all my parentheses are not quite the right size. You know, I usually manually change my hand and I can get an AI agent to sort of do all that quite nicely now in the background.

• 48:45Speaker 01

  So, yeah, they really sped up lots of secondary tasks. They haven't yet sort of sped up the core thing that I do, but it's allowed me to sort of add more things to my papers.

• 48:59Speaker 01

  Yeah, but by the same token, like if I were to write a paper I wrote in 2020 again and not add all these extra features, but just have something of the same sort of level functionality, yeah, then that actually doesn't, I haven't saved that that much, to be honest. Yeah, so it's made the papers sort of richer and broader, but not necessarily deeper.

• 49:19Dwarkesh Patel?

  You made this distinction between artificial cleverness and artificial intelligence. And I would like to better understand those concepts. What is an example of intelligence that is not just cleverness?

• 49:35Speaker 01

  Yeah, so.

• 49:39Speaker 01

  Intelligence is famously hard to define. It's one of these things that you can't know it when you see it. But when I talk to someone, and we're trying to collaboratively solve a math problem together, there's this conversation where neither of us knows how to solve the problem initially, but one of us has some idea and it looks promising. And so then we have some sort of prototype strategy. And then we test it and then it doesn't work, but then we modify it. And there's some adaptivity and continual improvement of the idea over time. And eventually, we've sort of, we've systematically mapped out what doesn't work, what does work,

• 50:23Speaker 01

  and we can kind of see a path forward, but it's evolving with our discussion. And this isn't not quite what the AI is. The AI can kind of mimic this a little bit. So to go back to this analogy of these jumping robots, they can jump and fail and jump and fail and jump and fail. But what they can't do is they kind of jump a little bit and they reach some handhold, but then they sort of stay there and then they pull other people up. And then they try to jump from there.

• 50:54Dwarkesh Patel?

  Right.

• 50:55Speaker 01

  There isn't this cumulative process which is sort of built up interactively. It seems to be a lot more trial and error and just repetition through force, which it scales and it can work amazingly well in certain contexts. But yeah, this idea is sort of building up cumulatively from partial progress is kind of what's still not quite there yet.

• 51:23Dwarkesh Patel?

  Interesting. You were saying if Gemini 3 or Claude 4.5 whatever solves a problem, it is not the case that its own understanding of math has progressed. Or even if it works on a problem without solving it, it's not that its own understanding of math has progressed.

• 51:36Speaker 01

  Yeah, you run a new session and it's forgotten what it just did. It has no new skills to attach to, to build on related problems. Maybe what you just did is part of 0.01% of the training data for the next generation. So maybe eventually some of it gets absorbed, but yeah.

• 51:54Dwarkesh Patel?

  So Terrence talks about the importance of decomposing particularly gnarly problems into a series of easier chunks. Even if this doesn't result in the full solution. Approaching problems in this way helps you build up the intuitions and practice the techniques that you'll need to keep making progress. But models today tend to struggle with these kinds of problem solving techniques. That's where Labelbox comes in. Labelbox helps you train models not just to get the right answer, but to think the right way. They've operationalized these reasoning behaviors into rubrics, giving you the ability to evaluate every important dimension of a model's output. These rubrics go beyond simple correctness. Did the model have reached for the right tools? Did it check its own work and explore alternative paths? How clear was its response?

• 52:35Dwarkesh Patel?

  These skills are useful across domains: math, physics, finance, psychology, and more. And they're becoming increasingly important as models take on harder, open-ended problems, some of which have multiple solutions and some of which we don't even know the solutions to. Labelbox can get your rubrics tailored to your domain, helping you systematically measure and shape how your models think. Learn more at labelbox.com/dwarakash.

• 53:00Dwarkesh Patel?

  One big question I have is, how plausible is it that if we just keep training AIs that get better and better at solving problems in Lean, that they will continue to solve more and more impressive problems? And then we will, in retrospect, be surprised at how little insight we got from some Lean solution to proving the rebound hypothesis or something? Or do you think it is a necessary condition of solving the rebound hypothesis even by an AI that is totally doing it in Lean? The constructions which are made, the definitions which are created, even in the Lean program, have to advance our understanding of mathematics? Or do you think it could just be assembly code googledigook?

• 53:39Speaker 01

  Yeah, we don't know. I mean, some problems have been basically solved by pure brute force. The four-color theorem is a famous example. We have still not found a conceptually elegant proof of this theorem. It basically... And maybe we never will. I mean, some problems may only be solvable by just splitting into some enormous number of cases and doing brute force. And insightful computer analysis on each case. I mean, part of the reason we phrase problems like the hypothesis is that we're pretty sure that that something amazing has to, a new type of mathematics has to be created or a new connection between two previously unconnected areas of mathematics has to be discovered to make this work.

• 54:21Speaker 01

  We don't even know what the shape of the solution is, but it doesn't feel like a problem that will be solved just by exhaustively checking cases or something. I mean, it could be false, actually. So we could actually, again, there is an unlikely scenario that the hypothesis is false and there's this, this, this, you can just compute, oh, here's a zero off the line and a massive computer calculation verifies it. That would be very disappointing.

• 54:49Speaker 01

  I don't know. I do feel that, you know, fully autonomous, one-shot approaches are not the right approach for these problems. I mean, I think you will get a lot more mileage out of the interplay between, between humans collaborating with these tools. And I can see one of these problems being solved by, by some smart humans assisted by some extremely powerful AI tools, but the exact dynamic may be very different from what we envisioned right now. I mean, it could be a collaboration of a type that we just, doesn't exist yet.

• 55:29Speaker 01

  Yeah, I mean, there may be a way to, to generate, you know, a million variants of the human data function and do some data analysis, AI assisted data analysis, and we, we discover some pattern between connecting them, which, which we didn't know about before. And this lets you transform the problem into, into a different area of mathematics. I mean, there could be all kinds of, of scenarios.

• 55:52Dwarkesh Patel?

  The AI figures it out and latent in the Lean is some brand-new construction, which, you know, if you realize the significance, we would be able to apply it in all these different situations. How would we even recognize it, right? Like, if you just, again, a very naive question, but if you come up with the equivalent of like, Descartes comes up with this idea, oh, you can have this coordinate system where you can unify algebra and geometry. But in Lean code, it would just look like R to R, and it wouldn't look that significant or something. Or similarly, I'm sure there's other constructions which have this kind of property.

• 56:25Speaker 01

  Well, the beauty of formalizing a proof in something like Lean is that you can take any piece of it and study it atomically. So, you know, so when I read a paper with my humans with, which solves some difficult problem, you know, there's often some big sequence of lemmas and theorems and things. And so ideally, the author will talk their way through, you know, what's important, what's not. But sometimes they don't reveal what steps were the important ones and which ones are just kind of boilerplate standard steps. But you can study each lemo in isolation, and some of them I can see, oh, this looks fairly standard. This resembles something I'm familiar with. I'm pretty sure there's nothing interesting going on here. But this lemo, oh, that's something I haven't seen before.

• 57:08Speaker 01

  And I could see why if you could, if you had this result, that would really help prove the main result. Like, you could, you know, you can assess whether some things are really key to your, to your argument or not. And Lean really facilitates that, you know, you can, you can, you can, you know, the individual steps are defined really precisely. I think in the future, there'll be, you know, there'll be entire professions of mathematicians. If I take a giant Lean generated proof and maybe do some ablation on it or something, I'll try to remove parts of it and try to find more elegant ways, you know, maybe some other AIs to sort of do some reinforcement learning. How can you make the proof more elegant? And maybe other AIs will grade whether this proof looks better or not.

• 57:56Speaker 01

  One thing that will change quite a bit in the near future is that until recently, writing papers was the most time-consuming and expensive part of the job. And so you did it very rarely. You only wrote up your results once everything was, all the other parts of your argument were checked out and things. Because just rewriting it again, refactoring was just a total pain. But that's one thing that's become a lot easier now with modern AI tools. So you don't have to have just one version of your paper. You can, once you have one, people can generate hundreds more. So yeah, one giant messy lean proof may not be very meaningful or understandable on its own, but other people can refactor it and do all kinds of things with it.

• 58:39Speaker 01

  We have seen with the Erdem problem website, you know, that people will, an AI will generate a proof and then here's 3,000 lines of code that verify the proof. But then people got other AIs to summarize the proof and they will write their own proofs. There's actually, post-processing, once you actually have one proof, we actually have a lot of tools now to deconstruct it and interpret it. It's a very nascent area of science or mathematics, but I'm not as worried about, so some people are concerned, what if the real hypothesis is proof of a completely incomprehensible proof? I think once you have the artifact of a proof, we can do a lot of analysis on it.

• 59:19Dwarkesh Patel?

  You posted recently that it would be helpful to have a formal or semi-formal language for mathematical strategies as opposed to just mathematical proofs, which is what lean specializes in. I would love to learn more about what that would involve or look like.

• 59:34Speaker 01

  We don't really know. I mean, we've been very lucky in mathematics that we have worked out the laws of logic and mathematics, but this is actually a fairly recent accomplishment. I mean, it was started by Euclid, you know, millennia ago, but only in like the early 20th century did we finally list up, here are the axioms of mathematics, or to the standard axioms of what we call ZFC and the axioms of first order logic. And this is what a proof is, and this we've managed to automate and have a formal language for. There could be some way to assess plausibility of certain, you know, so you have a conjecture that something is true. You test a few examples and it works out.

• 1:00:16Speaker 01

  Like, how does this increase your confidence that the conjecture is true? We have a few sort of mathematical ways to model this, Bayesian probability, for example. But they're not, but you often have to, they're often, you have to set certain base assumptions and it's, there's a lot of subjectivity still in these tasks. So it is, it's not clear. I mean, it's, this is more of a wish than a plan to develop these languages. But just seeing how successful having a formal framework in place like Lean

• 1:00:55Speaker 01

  has made deductive proofs so much easier to automate and train AI on. If there was some similar framework, so the bottleneck for using AI to create strategies and make conjectures is we have to rely on human experts to, and the test of time to validate whether something's plausible or not. If there was some semi-formal framework where this could be done semi-automatically in a way that isn't sort of easily hackable to, you know. So of course, yeah, it's really important with these formal proof assistants that there are just no, there's no backdoors or exploits that you can do

• 1:01:39Speaker 01

  to somehow get your certified proof without actually proving it. Because reinforcement learning is just so, so good at finding these backdoors. But yeah, if it's a framework that sort of mimics how scientists talk to each other in a semi-formal way, you know, using data and argument, but also, you know, constructing narratives and there's some subjective aspect of science that we don't know how to capture in a way that we can insert AI into them in any useful way. Interesting. So yeah, this is a, this is a future problem.

• 1:02:20Speaker 01

  I mean, there are research efforts to, you know, to try to create automated conjectures and and and and maybe there are ways to benchmark these and and get some some way to simulate this, but this is it's all very, very new science.

• 1:02:35Dwarkesh Patel?

  Can you help me get some intuition for I have two sub questions.

• 1:02:43Dwarkesh Patel?

  One, it would be very helpful to have a tangible sense of it would be helpful to have a specific example of what something like this would look like that the way scientists communicate that we can't formalize yet. And two, it seems almost definitionally paradoxical to say, building up some narrative or building up some natural language explanation and then also having something which you could have formalized. And I'm sure there's some intuition behind where that overlap is, and I'd love to understand that better.

• 1:03:19Speaker 01

  All right. So so an example of of conjecture. So Gauss was interested in the prime numbers and he computed, he created one of the first mathematical data sets. He just computed the first hundred thousand prime numbers or so, hoping to find patterns. And he did find a pattern, but maybe not the pattern he was expecting. He found a statistical pattern in the primes that if you count how many primes there are up to one hundred, one thousand, one million and so forth, they get sparser and sparser, but the the the the drop off in in in the density was inversely proportional to the natural logarithm of of of of of the range of numbers. So he conjectured what we know for the prime number theorem. The number of primes up to X is like X divided by the natural log of X.

• 1:04:04Speaker 01

  And he had no way to prove this. It was it was data driven. So this this was a conjecture. It was revolutionary for its time because it was maybe the first really important conjecture of of mathematical statistical nature, you know. So normally you you talk about pattern like maybe the spacing between the primes has a certain regularity or something, but yeah, but this was really something which it didn't tell you exactly how many primes there were in any given range. It just gave you an approximate approximation that got better and better as you went further and further out. But it.

• 1:04:41Speaker 01

  It helped, so it started the field of what we call analytic number theory. But it was the first in many conjectures like this, many of which got proved, which sort of started consolidating the idea that the prime numbers actually didn't really have a pattern, that they behave like random, random sets of numbers with a certain density. I mean, they had some patterns, like they're almost all odd, okay, so there was something, and they're not actually random, they're what's called pseudorandom, I mean, there's no random number generation involved in creating the prime numbers. But over time, it became more and more productive to think of the primes as if they were just generated by some god rolling dice all the time and just creating this random set.

• 1:05:25Speaker 01

  And this allowed us to make all these other predictions. So there's still open conjecture in number theory, called the twin prime conjecture, that there should be infinitely many pairs of primes that are twins, distant to a part, like 11 and 13. We can't prove that, and there's actually good reasons why we can't prove it, but because of this statistical random model of the primes, we are absolutely convinced it's true. We know that if the primes were sort of generated by flipping coins or something, that we would, just by random chance, just like infinite monkeys at a typewriter, we would see twin primes appear over and over again. And we have, over time, developed this very accurate conceptual model of what the primes should behave like, based on statistics and probability, but it's all mostly heuristic and non-rigorous, but extremely accurate.

• 1:06:08Speaker 01

  So the few times where we actually can prove things about the primes, it has matched up with the predictions of this, what we call the random model of the primes. So we have this conjectural conceptual framework for understanding the primes that we, everyone believes in, and you know, it's the same reason why we believe the Riemann hypothesis is true, why we believe that cryptography based on the primes is basically, is mathematically secure, things like that. It's all part of this belief.

• 1:06:39Speaker 01

  In fact, one reason why we care about the Riemann hypothesis is that if the Riemann hypothesis failed, we knew it was false, it means it would be a serious blow to this model, that this, it would mean there's a secret pattern to the primes that we were not aware of. And I think we would very rapidly abandon any cryptography based on the primes, because if there was one pattern that we didn't know about, there's probably more. And these patterns can lead to exploits in crypto, and it's gonna be, it would be a big, big shock. So we really want to make sure that doesn't happen. So, yeah, it's, so we've been convinced of things like the Riemann hypothesis and things over time, but some of it is experimental evidence, some is the few times we've been

• 1:07:23Speaker 01

  able to make theoretical results that have always aligned. You know, it is possible that the consensus is wrong, and we've all just missed something very basic. You know, there have been paradigm shifts in the past in scientific history. Yeah, but we don't really have a way of measuring this, I think partly because we don't have enough data on how math or science develops. We have one timeline of history, and you know, we have like, you know, a hundred stories of turning points in history. If we had access to a million alien civilizations, and each of the different development of history and of science in different orders, then maybe we actually have a decent shot

• 1:08:04Speaker 01

  at understanding of how do we measure what is progress and what is a good strategy. And we could maybe start formalizing it and actually having a framework. Maybe if what we need to do is actually start creating lots of mini universes or simulations of AI solving very basic problems, you know, in arithmetic or whatever, but coming up with their own strategies for doing these things and having these little laboratories to test. I mean, there are people who investigate, like trying to, what's the smallest, you know, neural network that can do Tendijam application and things like that. I think, I think we could actually learn a lot just from evolving small AIs on simple problems, we could learn a lot.

• 1:08:49Dwarkesh Patel?

  I was super excited when Mercury reached out about sponsoring the podcast because I've been banking with them for years. I think I opened my first account with them in 2023. Something I've come to appreciate over the last few years is that Mercury is constantly updating things and adding new features. Take their newest feature, Insights. Insights summarizes your money in and out, showing you your biggest transactions and calling out anything that deserves extra attention. Like, maybe your revenue from a particular partner has gone down, or you've got a big uncategorized purchase that needs to be investigated. It's a super low-friction way for me to keep tabs on my business and make quick decisions. For example, I try to invest any cash that I don't need on hand to keep running the business. With Insights, with just a couple of clicks, I was able to see exactly how much money I spent in each month of 2025. And that lets me know exactly how much cash I'll need for the next year or so of operations, and then I can go invest the rest.

• 1:09:34Dwarkesh Patel?

  Mercury just keeps adding new features like this. Go to mercury.com to check it out. Mercury is a fintech company, not an FDIC insured bank. Banking services provided through Choice Financial Group and Column NA, members FDIC. You have to learn about new fields, not only very rapidly, but deeply enough to contribute to the frontier. So in some sense, you're also one of the world's greatest autodidacts. What is your process of learning about a new subfield in math? What does that look like?

• 1:10:06Speaker 01

  Yeah, so I certainly identify with kind of the, yes, we talked about depth and breadth before, and it's not purely human-AI distinction. I mean, humans also split, I think it was Hervin who split them into hedgehogs and foxes. And the hedgehog knows one thing very, very well, and a fox knows a little bit about everything. So I definitely, I think of myself as a fox. You know, I work with hedgehogs a lot, and sometimes I can be a hedgehog if need be. But yeah, so.

• 1:10:40Speaker 01

  I've always had a little bit of an obsessive streak. If there's something which I read about, which I feel like I should understand. I have the capability to understand this, but I don't understand why it works. There's some magic in it that, you know, so someone was able to use a type of mathematics I'm not familiar with and get a result which I would like to prove, and I can't do it by myself, but they could do it by their method. Then I wanted to find out what was their trick. It bugs me that someone else can do something which I think I can do, but I can't. So I've always had that kind of obsessive completionist type streak. I've had to weed myself off computer games because I start a game, I want to play it to completion, so all the levels.

• 1:11:22Speaker 01

  So that's one way in which I learn new fields. I collaborate with a lot of people who have taught me other types of mathematics. I just make friends with a mathematician who's working on another area of mathematics, and I find their problems interesting, but they have to teach me some of the basic tricks, and what's known, what's not known, and I learn a lot from that.

• 1:11:47Speaker 01

  I found that writing about what I've learned, I have a blog where I sometimes

• 1:11:54Speaker 01

  record things that I've learned, because in the past, when I was younger, I would learn something and do this cool trick, and I'd say, "Okay, I'm gonna remember this." And then six months later, I'd forgotten. I remember remembering it, but I can't reconstruct my arguments. And the first few times, it was so frustrating to have understood something and then lost it. I sort of resolved I should always write down anything cool that I've learned. And this is part of how this blog came about. How long does it take you to write a blog post?

• 1:12:26Speaker 01

  It's something I often do when I don't want to do other work. You know, like there's some referee report or something. There's something that feels slightly unpleasant for me to do at the time. And so writing a blog, it feels creative and fun. Like, it's something that I do for myself. So maybe, depending on the topic, it could be a quick, you know, half an hour or several hours. But I, it doesn't, because it's something that I do sort of voluntarily, it doesn't feel like it, it doesn't feel...

• 1:12:56Speaker 01

  Time flies whenever I write these things, as opposed to sort of doing something which I have to do for administrative reasons, but it's just that it's drudgery. Okay, those are tasks where AI is really helping with nowadays, actually.

• 1:13:06Dwarkesh Patel?

  Is it, if civilization could from first principles decide how to use Terry Tao's time? You know, it's like a limited resource. What is the biggest diff between, if the veil of ignorance got to decide how to use Terry Tao's time versus what it does now?

• 1:13:24Speaker 01

  Okay.

• 1:13:25Dwarkesh Patel?

  So this podcast wouldn't be happening.

• 1:13:28Speaker 01

  Yeah, so as much as I complain about certain tasks that I don't want to do, but I have to do, so as you get more senior in academia, you get more and more responsibilities, like it's more committees and whatever. But I have also found that a lot of events that I kind of reluctantly went to because I was obliged to for one reason or another, because it's outside my comfort zone, I often find interactions with people who I wouldn't normally talk to, like you for instance, and I would learn interesting things and have interesting experiences. And I would have opportunities to then network with other people that I would never have done before. So I do believe a lot in serendipity.

• 1:14:10Speaker 01

  I mean, I do optimize my time when I, so there are some portions of my day where I do schedule very carefully. But I have been willing to sort of leave some portions just, okay, I'm going to do something which is not my usual thing, and maybe it'll be a waste of my time, but maybe I will learn something. And more often than not, it's, I feel like I've gotten a positive experience, which is not something I would have planned for. And yeah, so I believe a lot in serendipity. And maybe there's a danger actually that, you know, in the modern societies, it's not just AI, but we've become really good at optimizing everything.

• 1:14:52Speaker 01

  And maybe we are optimizing, we're not optimizing, I love optimization. That, you know, with COVID, for example, we switched, like, we switched a lot to remote meetings, and so everything was scheduled now. And so we kept busy, at least in academia, you know, we met almost the same number of people that we met in person, but everything had to be planned. You had to schedule things in advance. And what we lost out on was sort of the casual, like, you know, knocking on a hallway, just meeting someone, you know, while getting a coffee.

• 1:15:27Speaker 01

  And this, you know, serendipitous interactions that you may think are not optimal, but actually are really important. You know, when I was a grad student, I would go down to the library to look, I had to look for a journal article. Yeah, I'd physically go in the library, check out the journal and read your article. And sometimes the next article, you know, you can just browse through and the next article is also interesting. Sometimes it wasn't, but, but you could accidentally find interesting things, which is something which has basically been lost now because you can just type in, you know, if you, if you want to access an article now, you just type it into a search engine or even an AI and you can get instantly what you want. But you don't get so the accidental things that you might have have gotten if you'd

• 1:16:12Speaker 01

  done it more inefficiently.

• 1:16:15Speaker 01

  So, yeah, there've been times when I mean, I spent a year once at the Institute for Advanced Study, which is a great place to, you know, there's no distractions. You're there to just do research. And like the first few weeks you're there, like, it's great. You're getting all these papers written up that you've been wanting to do for a long time. You've been thinking about problems for blocks of hours at a time. But I find if I'd stay there for more than several months, like I'd, I run out of inspiration somehow. Like I get bored, actually, you know, surf the internet a lot more. You actually do need a certain level of distraction in your life. It somehow adds enough randomness and, and that, and temperature, high temperature, if you need, yeah.

• 1:16:58Speaker 01

  So, yeah, I don't know the, the optimal way to schedule my life. It just seems to work.

• 1:17:05Dwarkesh Patel?

  I'm very curious when you expect AIs that can like actually do frontier math better than the, at least as good, well as the best human mathematician.

• 1:17:15Speaker 01

  I mean, in some ways, they're, they're already doing frontier math that is super intelligent that humans can't do, but it's a different frontier from what we're used to.

• 1:17:23Dwarkesh Patel?

  Right.

• 1:17:24Speaker 01

  I mean, you could argue that calculators were doing frontier math that, that humans could not accomplish, but it was, but it wasn't, you know, number crunching. But.

• 1:17:33Dwarkesh Patel?

  But replacing Terry Tao completely.

• 1:17:38Speaker 01

  I mean, what do you want me for?

• 1:17:43Dwarkesh Patel?

  You'll just go on other podcasts after.

• 1:17:48Speaker 01

  I'm not sure we've. It might not be the right question to ask.

• 1:17:57Speaker 01

  I think within a decade, a lot of things that mathematicians currently do, where we spend a lot of the bulk of our time doing it and a lot of stuff we put in our papers today can be done by AI. But we will find that that actually wasn't the most important part of what we do.

• 1:18:16Speaker 01

  You know, a hundred years ago, a lot of mathematicians were just solving differential equations.

• 1:18:23Speaker 01

  People needed, physicists needed some exact solution to some system. And they were just, they hired a mathematician to laboriously go through the calculus and work out the solution to this fluid equation, whatever. A lot of what 19th century mathematician would do, you could make a call to Mathematica or WolframAlpha or a computer algebra package or now more recently an AI, and it would just solve the problem in a few minutes. But we moved on. We worked on different types of problems after that.

• 1:18:56Speaker 01

  You know, once computers came along, you know, computers used to be human, right? People used to laboriously create log tables and work out primes as Gauss did. And that has all been outsourced to computers, but we moved on.

• 1:19:10Speaker 01

  In genetics, you know, to sequence the genome of a single organism, that was an entire PhD of a geneticist, you know, so carefully separating all the chromosomes and whatever. And now you can just spend a thousand dollars and send it to a sequencer and get it done. But genetics is not dead as a subject. You move to a different scale. You know, maybe you study whole ecosystems rather than individuals.

• 1:19:34Dwarkesh Patel?

  I take your point, but on the question of, well, when is most mathematical progress or almost all mathematical progress happening by AI? So that if you find out, oh, this year a millennium prize problem has been solved, you would put, you know, a 95% odds that an AI did it autonomously. Surely there will be such a year.

• 1:19:53Speaker 01

  I guess, I mean, I do believe that that hybrid human plus AIs will dominate mathematics for a lot longer. It will depend, it will require some additional breakthroughs beyond what we already have. So it's going to be sarcastic. You know, I think AIs currently are very good at certain things, but really terrible at others. And while you can sort of add more and more frameworks on top to kind of reduce the error rates and make them work with each other a bit more and so forth.

• 1:20:27Speaker 01

  It feels like we don't have all the ingredients to like really have a truly satisfactory sort of replacement for all intellectual tasks. It is complimentary currently. It's not, it is not a replacement.

• 1:20:45Speaker 01

  But maybe, I mean, because current level AIs will accelerate science in so many ways,

• 1:20:54Speaker 01

  hopefully, I mean, new discoveries, new breakthroughs will happen more quickly. I mean, it's possible that also by somehow destroying serendipity, we actually inhibit certain types of progress. Anything is possible really at this point. I think the world is very, very unpredictable at this point in time.

• 1:21:13Dwarkesh Patel?

  What is your advice to somebody who would consider a career in math or is early in a career in math, especially in light of AI progress? How should they be thinking about their career differently, if at all, as a result of AI progress?

• 1:21:28Speaker 01

  Yeah, so we live in a time of change. It is, as I said, we live in a particularly unpredictable era.

• 1:21:37Speaker 01

  And I think like, things that we've taken for granted for centuries may not hold anymore. So, yeah, the way we do everything, and not just mathematics, will change.

• 1:21:56Speaker 01

  You know, so I think, which is, you know, I mean, in many ways, I would prefer the much more boring, quiet era where things are much the same as they were 10 years ago, 20 years ago. But so I think one just has to embrace that this, there's going to be a lot of change. And that, you know, the things that you study, some of them may become obsolete or revolutionized. But but some things will be retained. And so you somehow always have to keep an eye on, like, there'll be a lot of opportunities for things that you wouldn't be able to do before. So, I mean, in math, you know, you previously had to basically go through years and years

• 1:22:41Speaker 01

  of education to be a math PhD before you could contribute to the frontier of math research. But now it's quite possible at the high school level or whatever that you could get involved in math project and actually make a real contribution because of all these AI tools and Lean and everything else. So there'll be a lot of non-traditional opportunities to to learn. So you need a very adaptable mindset. You know, there'll be pursuing things just for curiosity, for playing, playing around. And I mean, you still need to get your credentials for, I mean, for a while, it would still be important to to sort of still go through traditional education and and and learn math and science and so forth, the old fashioned way for a while.

• 1:23:24Speaker 01

  But, yeah, but you should also be open to to very, very different ways of of doing science, some of which don't exist yet. Yeah, so it's it's a scary time, but also very exciting. Yeah.

• 1:23:40Dwarkesh Patel?

  Awesome. That's a great note to close on. Terence, thanks so much.

• 1:23:43Speaker 01

  Yeah, it's a pleasure.