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Terence Tao – Kepler, Newton, and the True Nature of Mathematical Discovery

Dwarkesh Podcast

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  • How Kepler Turned Bad Guesses Into Real Laws
    • Kepler spent years testing beautiful but wrong ideas before extracting the actual laws of planetary motion from Tycho Brahe’s unusually precise observations.
    • His Platonic-solid model failed; only Brahe’s decade-scale naked-eye dataset had enough accuracy for Kepler to infer ellipses and equal areas. Transcript: Dwarkesh Patel Okay, today I’m chatting with Terence Tao, who needs an introduction. Terence, 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. Terence Tao 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. 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 Croninco predicted seem To have some geometric meaning. I think he started proposing that if you take, say, the orbit of the Earth and you enclose it in, I think, maybe a cube, the outer sphere 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, isochedron, octahedron, and dodecaedron. And so he had this theory, which he thought was absolutely beautiful, that he could inscribe these platonic solids between the spheres of the planets, and it seemed to fit and it seemed To be to him like you know god’s design of the planets was 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 almost in existence okay which was the so Tycho Brahe this Danish astronomer very wealthy 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, with the naked eye, actually. He was the last of 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 him little bits of it at a time. And I think Kepler eventually just stole the data. He copied it and had to have a fight with Brahi’s descendants. But he did work out, he did get the data um and then he worked out to kind of his disappointment that um his beautiful theory didn’t quite work like the data was sort of off from his platonic Solid theory by you know about 10 or something and he had all kinds of fudges moving the circles around and things it didn’t quite work but he worked on this problem for for years years And eventually he figured out how to use the data to work out the actual orbits of um of the planets um and that was incredibly clever genius amount of data analysis and um yeah and then He eventually worked out that the uh the also actually ellipses not circles which was shocking for him and then he worked out so he worked out the two laws of planetary two laws of planetary Motion ellipses also equal areas sweep out equal times and then 10 years later after collecting a lot of data that the the the furthest planets like um like saturn and jupiter were the Hardest for him to to work out but then he finally worked out this third law also that uh um that the uh the orbits the the the time it takes for a planet to commit its orbit was proportional To some power of of the distance to the sun and these are the three famous couples of laws of motion um and he had no explanation for them it it it it was just all driven by by experiment and It took Newton a century later to give a theory that explained all three laws at once. (Time 0:00:00)
  • AI Makes Verification The New Scientific Bottleneck
    • AI makes idea generation cheap, so science’s bottleneck shifts from proposing hypotheses to verifying and ranking them.
    • Terence Tao compares this to the internet making communication cheap; journals already face floods of AI-generated submissions while validation still scales badly. Transcript: Terence Tao 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, 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. And yeah, so Kepler certainly had to to as you say cycle through many ideas and and several which didn’t work and and i bet many that he didn’t even um publish at all um because yeah they Just didn’t fit and that’s an important part of the process um trying all kinds of random things and seeing if they worked um but as you say the um you know the uh it had to be matched by an Equal amount of verification otherwise it’s it’s slow you know i mean um we celebrate kepler but we should also celebrate brahi for for his his assiduous data collection with which Was ten times more precise than any previous observation and it was um that extra decimal point of accuracy was actually essential for Kepler to get his results. And he was using Euclidean geometry and the most advanced mathematics he could use at the time to match his models with the data. So all aspects had to be in play. The data and the theory and the hypothesis generation. I’m not sure nowadays that hypothesis generation is the bottleneck anymore. Science has changed in the centuries since. So classically, sort of the two big paradigms for science were theory and experiment. Then in the 20th century, numerical simulation came along. And so you can also do computer simulations to test theories. But then finally, in the 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 the 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, but even he didn’t start with Tycho’s data set and analyze it. He had some preconceived theories first. But it seems like this is less and less the way we make progress just because the data is just so much more massive. (Time 0:05:44)
  • Six Data Points Can Fool A Civilization
    • Tiny datasets can make false laws look profound, so even striking empirical fits may be numerical flukes.
    • Kepler’s third law came from roughly six planetary datapoints; Bode later fit a planet-spacing rule that looked brilliant until Neptune broke it. Transcript: Terence Tao Yeah, yeah. So the data was extremely important. But the distinction I was trying to make was that sort of traditionally, make a hypothesis and then you test it against data yeah um but um now with um machine learning and data analysis And statistics and something you can you can start with data and um through say statistics work out um um laws that um were not present before and so kepler so kepler’s third law is a little Bit like this except that uh for the third law, instead of having the thousand data points that Brahe had, Kepler had like six data points. Like every planet, you knew the length of the orbit and the distance of 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 couplau which was amazing but actually he was quite lucky I mean that these six data points gave him the right conclusion You know it’s that’s not enough data to be really reliable there was a later astronomer Johannes Bordet who took the same the same data actually the the distances to to the planets and Inspired by Kepler I think he had a prediction that the the the distances to the planets formed basically a shift to geometric progression. He also fit a curve. Except there was one point missing. So there was 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 distance 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. 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 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 but (Time 0:09:35)
  • Great Ideas Need A Future To Prove They Matter
    • Potentially transformative ideas often cannot be recognized on contact because their value depends on future adoption, extensions, and standards.
    • Terence Tao points to deep learning, the bit, and the transformer as paths that only looked inevitable after culture and follow-on work locked them in. Transcript: Dwarkesh Patel 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, they’re 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. Terence Tao 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, have their own theories of the universe, many of which were basically of very little Value. And so we brought 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 general 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 the rest of the aspects of science have to catch up. 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. (Time 0:11:46)
  • Better Theories Often Start Out Looking Worse
    • Correct theories often begin by looking worse than entrenched wrong ones because old frameworks have accumulated patches and explanatory completeness.
    • Copernicus predicted planets less accurately than Ptolemy; Newton left action-at-a-distance and mass equivalence mysterious for centuries. Transcript: Dwarkesh Patel Yeah it seems often in the history of science when what 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 impossible at the time so as you’ve talked about aristarchus uh had heliocentrism In the third century uh bc and then um the ancient athenians were like this can’t be because it would 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 um that you don’t notice any parallax which is actually the correct implication But there’s times when actually the implication isn’t correct and we just need to graduate to a better level of understanding so leibnitz would you know chide newton and disagree with New and sea of gravity on the basis that it implied action at a distance um and then there’s we don’t know the mechanism and um newton himself was sort of stunned that inertial mass and Gravitational mass were the same quantity so all these things which were resolved by einstein yes yes but it was still progress and so the question for a system of peer review for ai would Be even if you can falsify a theory, how would you notice that it still constitutes progress relative to the thing before? Yeah. Terence Tao 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 Tomli’s theory. So geocentrism had been developed for a millennium by that point, and they had made many, many tweaks and very increasingly complicated ad hoc fixes to make it more and more accurate. And Copernicus’ theory was a lot simpler, but much less accurate. It 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, but somehow it 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. Often progress has been made not by adding more theories, but by deleting some assumptions that you have in your mind. So 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 sort of falling over? You know, once you have neutrons in motion, you know, 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 to realize that that the earth is in motion it doesn’t feel like it’s in motion and like the biggest advances you know Darwin’s theory of evolution you know is the the idea that that species are not static but you know it’s not obvious because you don’t see evolution in your lifetime. Well, now we actually can, but, you know, it seems permanent and static. You know, right now we’re going through 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 reordered quite a bit. And so, you know, trying to fit AI into sort of our theories of scientific progress and what is hard and what is easy, we’re struggling 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. (Time 0:17:30)
  • Science Advances Through Persuasion Not Just Proof
    • Scientific progress depends not just on truth and data but on narrative, exposition, and persuading others to invest attention.
    • Darwin’s plain-English synthesis spread faster than Newton’s Latin technical work; Tao says this social layer is hard to formalize or reinforce-learn. Transcript: Terence Tao Conceptually much more difficult. I think one aspect of science is 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. No lean. Okay. I have to sort of get out of my technical mindset. He spoke in plain English, didn’t use equations, and he synthesized a lot of disparate facts. So 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 for for for um hereditary uh uh he didn’t have dna okay and um yeah but uh his writing style was persuasive and that That helped a lot um newton wrote in latin um he had invented you know entire new areas of mathematics just to explain what he was doing um he was also from an era which was where scientists Were much more secretive and competitive. So, you know, academia is still competitive. 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 actually a somewhat unpleasant person from what I gather, actually. So it was actually only a couple decades after newton where other scientists explained his work in much simpler terms that they became um widespread um so um yeah the the the art of exposition And making a case and creating a narrative um is uh is also a very important part of science um and um you have the data, it helps, but people need to be convinced. Otherwise, they will not push it further. Or they will not take initial investment to learn your theory and really explore it. 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 there’s a social Aspect to science um they you um even though we pride us also having an objective um side to it where there’s data and there’s experiment and validation we still have to tell stories and Convince our fellow scientists and that’s a soft squishy thing like it’s you know it’s it’s a combination of data and yeah and painting a narrative and it’s a narrative of gaps you know I mean as you know so so even darwin as 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 uh would would find transitional Forms that they would find the mechanism of inheritance and they did um yeah um i don’t know how you can quantify that in such a precise way that you can start to reinforce some learning. Maybe that will be forever the human side of science. (Time 0:23:00)
  • Astronomers Learned To Extract Signal From Almost Nothing
    • Astronomy became exceptionally good at inference because scarce data forced astronomers to squeeze signal from tiny traces.
    • Terence Tao compares them to Sherlock Holmes and notes even citation typos can reveal whether scientists actually read the papers they cite. Transcript: Dwarkesh Patel 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 Thru Luan Brown 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? Terence Tao Right. So astronomy was one of the first sciences to really embrace data analysis and, and, and squeezing every last possible drop of information out of the information they had, because, Because data was the bottleneck. I mean, still is a bottle i mean it’s it’s really hard to to collect astronomical data so astronomers are the best uh you know um almost uh world class in in extracting you know almost like Sherlock you know it’s like extracting all kinds of conclusions from little traces of data um i hear that uh that a lot of quant hedge funds, they’re preferred hires in astronomy PhD. They also are very interested for other reasons in extracting signals from various random bits of data. Dwarkesh 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 resonant, 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. 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 jainestreet.com/dworkash. All right, back to Terrence. Terence Tao We do underexplore sort of how to extract extra information from various signals. Like, just to pick one random study, I remember reading once that people had discovered, were trying to measure how often scientists actually read these citations, the papers that They cite. So how do you measure this? You could try to survey different scientists, but they had some clever tricks. So many citations have little typos, like 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 could infer whether an author was actually just copying it, cutting and pasting a reference without actually checking it. And so from that, they were able to infer some measure of sort of how much attention people were paying. So there are also clever tricks to extract. So these questions you posed earlier of 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 a data survey. We can examine citations and how often something is mentioned in a conference or something. And maybe there’s a lot of sociology of science research to be done and that could actually detect these things. (Time 0:26:11)
  • Math AIs Jump Walls But Rarely Build Scaffolding
    • Current math AIs clear many low walls at scale but contribute little partial progress on harder problems.
    • After quickly solving about 50 Erdős problems, pure one-shot successes stalled; Tao says models jump or crash rather than establish reusable intermediate footholds. Transcript: Dwarkesh 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 ERDOs 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. Terence Tao It does seem so. I mean, there’s so 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 and that has stopped. An awful 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 already solved in the literature, but there hasn’t been any further AI purely powered solution yet. 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. And and some problems have been solved by a ongoing conversation between lots of humans and lots of ai tools um but uh it it does seem like it it was this this one-off thing um so maybe one Analogy to for these problems is like um imagine like um there’s this there’s all these that you’re in some sort of mountain range with all kinds of of cliffs and walls and and uh maybe There’s a little wall, which is maybe like three feet high and one that’s six feet high and then there’s 15 feet high. And then 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 and um so you know we try to light some candles and make some maps and and slowly we kind of figure out uh some of them are climbable some Of them we can identify some some partial um track in the wall that you can reach first um 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 any human. And sometimes they jump in the wrong direction and sometimes they crash. But sometimes they can reach the tops of the lowest, you know, walls that 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 could actually find all the um all the low ones um and they could reach them um but then uh there’s been no you know i mean Maybe if the next time there’s a big advance in the models then they’ll try it again and maybe a few more will be will be uh will be breached um but 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 make little markers and try to identify partial things. And, you know, these tools, they either succeed or they fail. And they’ve been really bad at creating sort of partial progress or identifying intermediate stages that you should focus on first. Again, going back to this previous discussion, we don’t have a way of evaluating partial progress. The same way you can evaluate a one-shot success or failure of solving a problem. (Time 0:30:31)
  • Breadth Is AI’s Edge While Depth Stays Human
    • AI’s near-term scientific advantage is breadth, while humans still dominate depth, so research will be reorganized around their complementarity.
    • Tao imagines AIs mapping whole fields, clearing easy observations, and marking islands of difficulty for human experts to attack. Transcript: Dwarkesh Patel 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. 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 100 years of subjective time research On 100 different problems at the same time or a million different problems at the same time. But once AIs reach Terence Tower level, they could do that. And once they reach intermediate levels, 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 and more powerful than our human level intelligence. Terence Tao I agree. Yeah. So they excel at breadth and humans excel at depth um like human experts at least yeah so um i think they’re very complementary um but our current uh way of doing math and science is focused On depth because that’s where the human uh expertise is because humans can’t do breadth um but uh yeah so we have to redesign the way we do science to take full advantage of this breadth Capability that we now have. So, as I said, we should have a lot more effort in creating very broad classes of problems to work on rather 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. But now we have this other way of doing science. We can explore entire new fields of science by first getting these broad, moderately competent AIs to sort of map it out and clear out all the easy, make all the easy observations and Then identify certain islands of difficulty uh which you know then human experts can come and and and work on so i i see very much uh a future of very complementary um um science eventually You would hope to get both breadth and depth you know and and um somehow get the both best best of both worlds um but i think we need practice with the breadth side it It’s too new. We don’t even have the paradigms really to make full advantage of it, but we will. And then science will be unrecognizable after that. (Time 0:34:19)
  • AI Will Make Math Broader Before It Makes It Deeper
    • In math, solving a problem matters less than the process because the process builds intuition, techniques, and transferable understanding.
    • Tao expects AI to revolutionize the experimental side of mathematics by testing workflows across thousands of problems rather than handcrafting each proof. Transcript: Terence Tao So certainly in math, the process is often more important than the problem itself. The problem is kind of a proxy for measuring the progress. And I think even in software, there’s different types of software tasks. I mean, you know, like if you just kind of create a web page that does the same thing that a thousand other web pages do, there’s sort of no skill to be learned. Well, there is still some skill maybe that the individual programmer could pick up. But, you know, for kind of a boilerplate type code, definitely, you know, it’s something that you should definitely 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. 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. And so just getting the answers right away may actually yeah inhibit that process um i mean so as um i made this thing between theory and experiment before um so um in most sciences there’s An equal division between there’s a theoretical side and experimental side um but in math has been almost unique is that it’s almost entirely theoretical uh we we uh um we pay a premium On sort of trying to to to have coherent clean theories of 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. 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’re a software company and you want to roll out a thousand pieces of software, 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. (Time 0:38:00)
  • Selection Bias Makes AI Math Look Deeper Than It Is
    • Most apparent AI math breakthroughs reflect selective reporting from broad low-probability sweeps rather than consistently high competence.
    • Tao says a model may solve only 1 to 2 percent of problems in systematic studies, even though social media highlights the rare wins. Transcript: Dwarkesh Patel Interesting. I feel like a big crux in these conversations about how good AI will be for science is, I think you said this, 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 any technique means doing that versus using Existing techniques and, um, and 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? This is a great question. We don’t have the data to fully answer it yet. Terence Tao 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 things that Have worked on similar problems in the past and we try them one by one um and sometimes that works um and that’s still worth publishing sometimes because the question was important um Sometimes they almost work and you have to add one more wrinkle um to it and that’s also interesting um 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 this is 20%, which is resistant. And a new technique has to be invented to fill in the gaps. It’s very, very rare now that a problem gets solved with sort of no reliance on past literature where all the ideas come out of nowhere you know that was more common in the past but 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 so yeah AI tools are really good at getting really good at the first part of that Just trying all the standard techniques on a problem um often now actually making fewer mistakes in implementing them than than humans they still make mistakes but but um i’ve i’ve Tested these tools you know on on on um 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 it’s about a tie right Now uh for um but um yeah i i haven’t yet seen them take the next step you know so so when there are holes in in in the argument where none of the things are working to to how then what do you do Um and then they can kind of suggest random things and it but it it um often i find that trying to chase them down and make them work and finally they don’t work it wastes more time than it Saves yeah so um now so i think some fraction of problems that we currently think are hard will will fall from this this method um i mean especially the ones that haven’t received enough Attention. So with the Erdős problems, almost all of the 50 problems that were solved by AIs were ones for which basically there was no literature. I mean, Erdős posed the problem 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 not many people know about with some other result in the literature. And that’s the kind of love, the median level of what AI can accomplish. And that’s really great. It clears out 50 of these problems. So I think you will see some isolated successes. But what we found, so people have done large-scale sweeps of these early problems. If you only focus on the success stories, the ones that get broadcast on social media, that looks amazing. All these problems that haven’t been solved before for decades, now they’re falling. But whenever we do a systematic study, any given problem, an AI tool has a success rate of maybe 1% or 2%. It’s just that they can buy a scale. And 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, you know, some AI may get lucky and actually could solve them and there was there was some some back door to solve the problem that everyone else missed um and that would get A lot of publicity um 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 um there’ll be A lot of noise amongst the signal of sort of when they’re working, when they’re not. We have to do, yeah, it’s increasingly important to collect these really standardized data sets. You know, there are efforts now to create a standard set of challenge problems for AI to solve and not just rely on the AI companies to only publish their wins and not disclose their negative Results. (Time 0:40:52)
  • Terence Tao Uses AI To Enrich Papers Not Solve Them
    • AI has made Terence Tao’s papers richer and faster to produce, mainly by accelerating secondary tasks rather than core problem solving.
    • He now adds more code, plots, literature search, and formatting help; the hardest mathematical step still happens with pen and paper. Transcript: Dwarkesh Patel Okay. So speaking of 2026 AI, you made a prediction in 2023. I think by 2026, what was it? It would be like a colleague in mathematics or? Terence Tao Yeah, a trustworthy co-author if used correctly. Got it. Dwarkesh Patel Which is looking pretty good in retrospect. Terence Tao Yeah, I’m pretty pleased. Dwarkesh Patel So, you know, let’s see if we can continue the streak. You personally are 2x more productive as a result of AI. What year would you say that? Terence Tao Yeah, so productivity, I think, is not quite a one-dimensional quantity. 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 because it’s so easy to generate these things now. So some plot, which have taken me hours to do now, 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 just talk about it in words. So it’s hard to measure what 2x means. 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. Interesting. But I would not write my papers that way. Dwarkesh Patel 5x? Terence Tao Yeah, but it’s because these are sort of auxiliary types. I mean, you know, so things like doing a much deeper literature search, supplying a lot more numerics. Yeah. 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. 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. 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 of functionality, Then that doesn’t save that much, to be honest. So it’s made the papers sort of richer and broader, but not necessarily deeper. (Time 0:46:43)
  • Artificial Cleverness Still Lacks Cumulative Understanding
    • Cleverness is not the same as intelligence; real mathematical intelligence accumulates partial progress, adapts strategy, and retains what it learned.
    • Tao says current models can mimic discussion but forget each session and fail to build durable understanding from failed attempts. Transcript: Dwarkesh Patel And I would like to better understand those concepts. What is an example of intelligence that is not just cleverness? Yeah. Terence Tao So intelligence is famously hard to define. It’s one of these things that you kind of 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, you know, 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, you know, we’ve systematically mapped out what doesn’t work, what does work, 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, of these jumping robots, you know, so, you know, 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. 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 brute force, you know, 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. Interesting. Dwarkesh Patel You’re saying if Gemini 3 or Cloud 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. Terence Tao 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 0.001% of the training data for the next generation. So maybe eventually some of it gets absorbed. (Time 0:49:25)
  • Unreadable Proofs Can Still Yield Human Understanding
    • Even if AI proves a theorem in unreadable Lean code, mathematicians can still inspect lemmas, isolate key steps, and refactor the result into understanding.
    • Tao compares this to studying atomic subclaims in human papers and expects future experts to ablate and simplify giant machine proofs. Transcript: Dwarkesh 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? It is a necessary condition of solving the rebound hypothesis, even by an AI that is like totally doing it in Lean, that 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 googly gook? Yeah, we don’t know. Terence Tao I mean, some problems have been basically solved by pure brute force. A full-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 a brute force, uninsightable computer analysis on each case. I mean, part of the reason we prize problems like a hypothesis is that we’re pretty sure 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. 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. We could actually… There is an unlikely scenario that the hypothesis is false and there’s this compute, oh, here’s a zero off the line and a massive computer calculation verifies it. That would be very disappointing. I don’t know. I do feel that fully autonomous one-shot approaches are not the right approach for these problems. I mean, I think you’ll get a lot more mileage out of the interplay between humans collaborating with these tools. And I can see one of these problems being solved by some smart humans assisted by some extremely powerful AI tools. But the exact dynamic may be very different from what we envision right now. I mean, it could be a collaboration of a type that we just doesn’t exist yet um yeah i mean we there may be a way to to generate you know a million variants of the human’s 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 a different area of mathematics. I mean, there could be all kinds of scenarios. Dwarkesh Patel So suppose 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 do you even recognize it, right? Um if you just again a very naive question but you if you if you come up with the equivalent of like Descartes comes 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 well the beauty of formalizing a proof in something like Lean is that you can take any piece of it and study it atomically. Terence Tao So when I read a paper with my humans, which solves some difficult problem, there’s often some big sequence of lemmas and theorems and things. And so ideally, the author will talk their way through 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 lemma in isolation. And some of them I can say, 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 lemma, oh, that’s something I haven’t seen before. And I could see why if you had this result, that would really help prove the main result. Like you can assess whether some things are really sort of key to your argument or not. And Lean really facilitates that. You can do the individual steps that I identify really precisely. I think in the future, there’ll be entire professions of mathematicians who might take a giant Lean-generated proof and maybe do some ablation on it or something, try to remove parts Of it and try to find more elegant ways. 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. 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 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. 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. We have seen with the Erdős problem website, 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 people 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, you know, so some people are concerned, you know, what if the real hypothesis is proven with a completely Incomprehensible proof? I think once you have the artifact of a proof, we can do a lot of analysis on it. (Time 0:53:00)
  • Math Still Lacks A Lean For Research Strategy
    • Mathematics has formal languages for proofs but lacks a semi-formal language for strategies, plausibility, and the narratives scientists actually use.
    • Tao wants something like Lean for conjectures and research judgment, but warns RL would exploit any backdoor in such a framework. Transcript: Dwarkesh Patel 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 Terence Tao In. I would love to learn more about what that would involve or look like. 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, like here are the axioms of mathematics, or 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 formal language for. But there could be some way to assess plausibility of certain, so you have a conjecture that something is true, you test a few examples and it works out, 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 you often have to set certain base assumptions, and there’s a lot of subjectivity still in these tasks. So it’s not clear. I mean, this is more of a wish than um than than than a plan to to uh develop these languages but just seeing how successful having a formal framework in place like lean has made deductive Proofs so much um easier to automate and and train ai on if there was some similar framework yeah so the bottleneck for using AI to create strategies and make conjectures is we have to Rely on human experts 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. So, of course, it’s really important with these formal proof assistants that there’s no backdoors or exploits that you can do to somehow get your certified proof without actually Proving it. Because reinforcement learning is just so so good at finding these these these backdoors um but um yeah if a strong framework that sort of mimics how scientists talk to each other in A semi-formal way you know using data and an argument but but also um you know constructing narratives and and and 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 future problem. I mean, there are research efforts to try to create automated conjectures, and maybe there are ways to benchmark these and get some way to simulate this. But it’s all very, very new science. (Time 0:59:20)
  • Math Runs On Heuristics Long Before Proof Arrives
    • Mathematicians often trust conjectures through a web of statistical evidence, heuristic models, and repeated theoretical alignment long before proof arrives.
    • Tao uses Gauss and the primes: the random model predicts twin primes and underwrites confidence in the Riemann hypothesis and prime-based cryptography. Transcript: Dwarkesh Patel Have two step questions. 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, the way scientists communicate that We can’t formalize yet. 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 all right so so an example of of a conjecture so um was interested in the prime numbers, Terence Tao And he computed, he created one of the first mathematical data sets. He just computed the first 100,000 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 100, 1, 1 million and so forth, they get sparser and sparser, but the drop-off in the density Was inversely proportional to the natural logarithm of the range of numbers. So he conjectured what we now call the prime number theorem. The number of primes up to x is like x divided by the natural log of x. And he had no way to prove this. It was data-driven. So this was a conjecture. It was revolutionary for its time because it was maybe the first really important conjecture of math that was statistical in nature. So normally you talk about patterns like maybe the spacing between the primes has a certain regularity or something, but this was really something which didn’t tell you exactly how Many primes there were in any given range. It just gave you an approximation that got better and better as you went further and further out. But 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 behaved like random sets of numbers with a certain density. I mean, they had some patterns, like they’re almost all odd. And they’re not actually random. They’re what’s called pseudo-random. 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. And this allowed us to make all these other predictions. So there’s a still open conjecture in number three called the twin prime conjecture that there should be infinitely many pairs of primes that are twins, distance two apart, 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 charts, 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 so the few times when 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 we have this conjectural concept framework for understanding the primes that we everyone believes in and you know it’s the same reason why we believe the real hypothesis is true Why we believe that cryptography based on the primes is basically um is mathematically secure things like that it’s it’s all part of this this belief um in fact one reason why we care About the human hypothesis is that if the real hypothesis failed um knew it was false. It means it would be a serious blow to this model that 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 yeah, it’s going to 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 agreement hypothesis and things over time, but some of it is experimental evidence. Some is the few times we’ve been able to make theoretical results, they’ve 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 enough data on how math or science develops. We have one timeline of history and we have like 100 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’d actually have a decent shot at An 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 what we need to do is actually start creating lots of mini universes or simulations AI solving very basic problems, you know, in arithmetic or whatever, but coming over their Own strategies for doing these things and having these little laboratories to test. I mean, there are people who investigate, like, what’s the smallest, you know, neural network that can do 10-digit application and things like that. I think we could actually learn a lot just from evolving small AIs on simple problems. (Time 1:02:40)
  • Why Terence Tao Writes Blog Posts To Remember Math
    • Terence Tao learns new fields through obsessive gaps in understanding, collaboration, and writing down whatever he finally grasps.
    • Forgetting hard-won insights pushed him to blog; he treats posts as a creative way to preserve tricks he might otherwise lose in six months. Transcript: Dwarkesh Patel 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? Yeah, so I certainly identify with kind of the, yeah, we talked about depth and breadth before. Terence Tao And it’s not purely human AI distinction. I mean, humans also split. So I think it was Irving who split them into hedgehogs and foxes. And a hedgehog knows one thing very, well and a fox knows a little bit about everything so i definitely i didn’t you know i i think of myself as a fox um you know i i work with hedgehogs a lot And sometimes i can be a hedgehog if need be but um yeah so um i’ve always had a little bit of an uh obsessive. 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 wean myself off computer games because I start a game, I want to play it to completion, so both the levels. 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 another 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. I found that writing about what I’ve learned, I have a blog where I sometimes record things that I’ve learned. Because in the past, when I was younger, I would learn something and do this cold trick and say, okay, I’m going to remember this. And then six months later, I’ve forgotten. I remember remembering it, but I can’t reconstruct my arguments. It the first few times it was so frustrating to have understood something and then lost it um that i sort of resolved i should always write down anything cool that i’ve learned um and that’s This is part of why how this blog came about um how long does it take you to write a blog post? 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, time flies when I write these things, you know, as opposed to sort of doing something which I have to do for administrative reasons, but it’s just that it’s drudgery. Those are tasks that AI is really helping with nowadays, actually. (Time 1:09:54)
  • Serendipity Is An Input To Great Research
    • Over-optimizing schedules can destroy the randomness that generates good ideas, collaborations, and intellectual renewal.
    • Tao says remote meetings preserved planned contact but killed hallway encounters; even inefficient library browsing once surfaced valuable accidental discoveries. Transcript: Dwarkesh Patel First principles, decide how to use Terry Tau’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 Tau’s time versus what it does now? This podcast wouldn’t be happening. Yeah. Terence Tao 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. I get some 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 semantivity. I mean, I do optimize my time when I – so there are some portions of a 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, I feel like I’ve gotten a positive experience, which is not something I would have planned for. And so I believe a lot in serendipity. And maybe there’s a danger actually that uh you know in the modern society it’s not just ai but we’ve become really good at optimizing everything um and and and maybe we are optimizing We’re not optimizing a lot of optimization um that uh you know with with with covert for example um we we switched like we switched a lot to remote meetings um and so everything was scheduled Now. And so we kept busy, at least in academia, 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, knocking, you know, knocking on the hallway, just meeting someone, you know, while getting a coffee. And there’s 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 into 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 you could accidentally find interesting things, which is something which has basically been lost now because you can just type in, 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 the accidental things that you might have gotten if you’d done it more inefficiently. So, yeah. There have been times when 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 of a time. But I find if I stay there for more than several months, I run out of inspiration somehow. I get bored. I actually surf the internet a lot more. You actually do need a certain level of distraction in your life. Somehow uh adds enough randomness um and and that uh and temperature high temperature if you need yeah um so yeah i don’t (Time 1:13:09)
  • Stay Flexible If You Want A Career In Math
    • Embrace an adaptable mindset if you pursue math now, because AI will change both the path into research and the shape of useful work.
    • Tao says students should still learn the old-fashioned fundamentals while staying open to nontraditional projects enabled by AI and Lean. Transcript: Dwarkesh Patel 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? Terence Tao Yeah, so we live in a time of change. It is, as I said, we live in a particularly unpredictable era. And I think things that we’ve taken for granted for centuries may not hold anymore. So, yeah, the way we do everything, not just mathematics, will change. And, 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 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 some Things will be retained. So you somehow always have to keep an eye on, there’ll be a lot of opportunities for things that you wouldn’t be able to do before. So I mean, in math, you previously had to basically go through years and years of education, 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 a 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 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 I think For a while it will still be important 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. But you should also be open to very, very different ways of doing science, some of which don’t exist yet. Yeah, so it’s a scary time, but also very exciting. (Time 1:21:13)