Today, I'm chatting with Terence  Tao, who needs no 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. 

I've always had an amateur interest in astronomy. 

I've loved stories of how the early astronomers  worked out the nature of the universe. 

Kepler was building on the work of Copernicus, who  was himself building on the work of Aristarchus. 

Copernicus very famously proposed the  heliocentric model, that instead of the  

planets and the Sun going around the Earth, the  Sun was at the center of the solar system and the  

other planets were going around the Sun. Copernicus proposed that the orbits of  

the planets were perfect circles. His theory fit the observations  

that the Greeks, the Arabs, and the  Indians had worked out over centuries. 

Kepler 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. 

He started proposing that if you take the orbit  of the Earth and you enclose it in a cube,  

the outer sphere that encloses the cube almost  perfectly matched the orbit of Mars, and so forth. 

There were six planets known at the time and five  gaps between them, and there were five perfect  

Platonic solids: the cube, the tetrahedron,  icosahedron, octahedron, and dodecahedron. 

So he had this theory, which he  thought was absolutely beautiful,  

that you could inscribe these Platonic  solids between the spheres of the planets. 

It seemed to fit, and it seemed to him that  God's design of the planets was matching this  

mathematical perfection of the Platonic solids. He needed data to confirm this theory. 

At the time, there was only one really  high-quality dataset in existence. 

Tycho Brahe, this very wealthy,  eccentric Danish astronomer,  

had managed to convince the Danish government  to fund this extremely expensive observatory. 

In fact, it was an entire island where he had  taken decades of observations of all the planets,  

like Mars and Jupiter, at least every night for  which the weather was clear, with the naked eye. 

He was the last of the naked-eye astronomers. He had all this data which Kepler  

could use to confirm his theory. Kepler started working with Tycho,  

but Tycho was very jealous of the data. He only gave him little bits of it at a time. 

Kepler eventually just stole the data. He copied it and had to have a fight with  

Brahe's descendants. He did get the data,  

and then he worked out, to his disappointment,  that his beautiful theory didn't quite work. 

The data was off from his Platonic  solid theory by 10% or something. 

He tried all kinds of fudges, moving the  circles around, and it didn't quite work. 

But he worked on this problem for years and years,  and eventually, he figured out how to use the data  

to work out the actual orbits of the planets. That was an incredibly clever,  

genius amount of data analysis. And then he worked out that the  

orbits were actually ellipses, not  circles, which was shocking for him. 

So he worked out the two laws of planetary  motion: the ellipses, and also that equal  

areas sweep out equal times. Then ten years later, after  

collecting a lot of data—the furthest planets  like Saturn and Jupiter were the hardest for  

him to work out—he finally worked out this  third law, that the time it takes for a  

planet to complete its orbit was proportional  to some power of the distance to the Sun. 

These are the three famous  Kepler's laws of motion. 

He had no explanation for them. It was all driven by experiment,  

and it took Newton a century later to give a  theory that explained all three laws at once. 

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

Newton comes up with this explanation of why  the three laws of planetary motion must be true. 

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 through his career, he's  just trying random relationships. 

In fact, in the book in which he writes  down the third law of planetary motion,  

it's an aside on The Harmonics of the World,  which is just a book about how 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. 

It's 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. 

As you were detailing, if you add that to  Newton's F=ma and 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 that I feel LLMs can do the kind of  

thing of trying random relationships for  twenty years, some of which make no sense,  

as long as there's a verifiable data bank like  Brahe's dataset. "Ok, I'm going to try out random  

things about musical notes, Platonic objects,  or different geometries, I have this bias that  

there's some important thing about the geometry  of these orbits." Then one thing works. As long  

as you can verify it, these empirical regularities  can then drive actual deep scientific progress. 

Traditionally, when we talk about the  history of science, idea generation has  

always been the prestige part of science. A scientific problem comes with many steps. 

You have to identify a problem, and then you have  to identify a good, fruitful problem to work on. 

Then you need to collect data,  figure out a strategy to analyze  

the data, and make a hypothesis. At this point, you need to propose a  

good hypothesis, and then you need to validate. Then you need to write things up and explain. 

There are a dozen different components. The ones we celebrate are these eureka  

genius moments of idea generation. Kepler certainly had to cycle through  

many ideas, several of which didn't work. I bet there were many that he didn't even  

publish at all because they just didn't fit. That's an important part of the process,  

trying all kinds of random  things and seeing if they worked. 

But as you say, it has to be matched by an equal  amount of verification, otherwise it's slop. 

We celebrate Kepler, but we should also  celebrate Brahe for his assiduous data  

collection, which was ten times more  precise than any previous observation. 

That extra decimal point of accuracy was  essential for Kepler to get his results. 

He was using Euclidean geometry and the  most advanced mathematics he could use at  

the time to match his models with the data. All aspects had to be in play: the data,  

the theory, and the hypothesis generation. I'm not sure nowadays that hypothesis  

generation is the bottleneck anymore. Science has changed in the century since. 

Classically, the two big paradigms for  science were theory and experiment. 

Then in the 20th century, numerical  simulation came along, so you can do  

computer simulations to test theories. Finally, in the late 20th century,  

we had big data. We had the era of data analysis. 

A lot of new progress is actually driven  now by analyzing massive datasets first. 

You collect large datasets and then draw  patterns from them to deduce thoughts. 

This is a little bit different from how  science used to work, where you make a  

few observations or have one out-of-the-blue  idea, and then collect data to test your idea.  

That's the classic scientific method. Now it's  almost reversed. You collect big data first,  

and then you try to get hypotheses from it. Kepler was maybe one of the first early  

data scientists, but even he didn't start  with Tycho's dataset and then analyze it. 

He had some preconceived theories first. It seems like this is less and less the  

way we make progress, just because the  data is so much more massive and useful. 

Oh, interesting. I feel like the 20th-century  science that you're describing actually very  

well describes what happened with Kepler. He did have these ideas—1595 and '96 is where  

he comes up with the polygons and then the  Platonic objects theory—but they were wrong. 

Then a few years later, he gets Brahe's data,  and it's only after twenty years of trying random  

things that he gets this empirical regularity. It actually feels a bit closer to Brahe's data  

being analogous to some massive data bank of  simulations, and now that you've got the data,  

you can keep trying random things. If it wasn't for that, Kepler would be  

out there just writing books about harmonics  and Platonic objects, and there would be  

nothing to actually verify against. The data was extremely important. The  

distinction I was trying to make was that  traditionally, you make a hypothesis and  

then you test it against data. But now with machine learning,  

data analysis, and statistics, you can  start with data and through statistics  

work out laws that were not present before. Kepler's third law is a little bit like this,  

except that instead of having the thousand data  points that Brahe had, Kepler had six data points. 

For every planet, he knew the length of  the orbit and the distance to the Sun. 

There were five or six data points, and  he did what we would now call regression. 

He fit a curve to these six data points and  got a square-cube law, which was amazing. 

But he was quite lucky that these six  data points gave him the right conclusion. 

That's not enough data to be really reliable. There was a later astronomer, Johann Bode,  

who took the same data—the distances  to the planets—and inspired by Kepler,  

he had a prediction that the distances to the  planets formed a shifted geometric progression. 

He also fit a curve, except  there was one point missing. 

There was a big gap between Mars and Jupiter. His law predicted that there was a missing planet. 

It was kind of a crank theory, except  when Uranus was discovered by Herschel,  

the distance to Uranus fit exactly this pattern. Then Ceres was discovered in the asteroid belt,  

and it also fit the pattern. People got really excited that Bode had  

discovered this amazing new law of nature. But then Neptune was discovered,  

and it was way off. Basically it was just a numerical fluke.  

There were six data points. Maybe one reason  why Kepler didn't highlight his third law as  

much as the first two laws is that 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. 

To ask the question about the analogy more  explicitly, does this analogy make sense if  

in the future we have smarter and smarter AIs? We'll have millions of them, and they can go out  

and hunt for all these empirical irregularities. It sounds like you don't think the bottleneck  

in science is finding more things that  are the equivalent of the third law of  

planetary motion for each given field,  so that 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." 

I think AI has 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. 

It’s an amazing thing, but it doesn't create  abundance by itself. Now the bottleneck is  

different. We're now in a situation where  suddenly people can generate thousands of  

theories for a given scientific problem. Now we have to verify them, evaluate them. 

This is something which we have to change our  structures of science to actually sort this  

out. Traditionally, we build walls. In the past,  before we had AI slop, we had amateur scientists  

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

We built these peer review publication  systems to 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,  

human reviewers are already being overwhelmed. Many journals are reporting that AI-generated  

submissions are just flooding their submissions. 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. That's not something we know how to do at scale. 

For each individual paper, we can  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. There's this incredibly interesting  

question. If you have billions of AI  scientists, not only how do you gauge  

which ones are real progress, but how do you... This is actually a question that human science  

has had to face and we've solved somehow,  and I’m actually not sure how we solved this. 

Let's say in the 1940s, if you're at Bell Labs  and there are these new technologies coming out. 

Pulse-code modulation, how do you transfer  signals? How do you digitize signals?  

How do you transfer them over analog wires? There are all these papers about the engineering  

constraints and the details, and then there's one  which comes up with the idea of the bit, which has  

implications across many different fields. You need some system which can then look  

at that and say, "Okay, we need  to apply this to probability. 

We need to apply this to  computer science," et cetera. 

In the future, the AIs are coming up with  the next version of this unifying concept. 

How would you identify it among millions of papers  that might actually constitute progress, but which  

have much less in terms of general unifying ideas? A lot of it's the test of time. 

Many great ideas didn't actually get a great  reception at the time they were first proposed. 

It was only after some other scientists  realized that they could take it further  

and apply them to their own... Deep learning itself was a  

niche area of AI for a long time. The idea of getting answers entirely  

through training on data and not through first  principles reasoning was very controversial,  

and it just took a long time before it started  bearing fruit. You mentioned the bit. There were  

other proposals for computer architectures  than the zero-one that is universal today. 

I think there were trits, three-valued logic. In an alternate universe,  

maybe a different paradigm would have shown up. 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've been some other architecture that  was the first to do it and once that was adopted,  

it would become the standard. 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 also on the culture and society,  which ones get adopted, which ones don't. 

The base ten numeral system in mathematics  is extremely useful, much better than  

the Roman numeral system, for instance. But again, there's nothing special about ten. 

It's a system that is useful for us  because everyone else uses it. We've  

standardized it. We've built all our  computers and our number representation  

systems around it, so we're stuck with it now. Some people occasionally push for other systems  

than decimal, but there's just too much inertia. It's not something where you can 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. So it may never be something that you can  

just reinforcement learn the same way that  you can for much more localized problems. 

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 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. 

As you talked about, Aristarchus had  heliocentrism in the third century BC. 

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. But there's times when the implication is  

incorrect and we just need to graduate  to a better level of understanding. 

Leibniz would chide Newton and disagree with  Newton's theory of gravity on the basis that  

it implied action at a distance, and they  didn't know the mechanism, and Newton himself  

was sort of stunned that inertial mass and  gravitational mass were the same quantity. 

All these things later were resolved by  Einstein. But it was still progress. 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? 

Often, the ultimately correct theory  initially is worse in many ways. 

Copernicus's theory of the planets was  less accurate than Ptolemy's theory. 

Geocentrism had been developed for a  millennium by that point, and they had  

made many tweaks and increasingly complicated  ad hoc fixes to make it more and more accurate. 

Copernicus's theory was a lot  simpler but much less accurate. 

It was only Kepler that made it  more accurate than Ptolemy's theory. 

Science is always a work in progress. When you only get part of the solution,  

it looks worse than a theory which is incorrect  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. 

They had the equivalence of mass  and action at a distance, which  

were only resolved with a very conceptually  different approach centuries afterwards. 

Often progress has to be made not by  adding more theories, but by deleting  

some assumptions that you have in your mind. 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 laws of motion—an  

object in motion remains in motion  and so forth—then it makes sense. 

Conceptually, it's a very big leap to  realize that the Earth is in motion. 

It doesn't feel like it's in motion. The biggest advances, like Darwin's  

theory of evolution, is the idea  that species are not static. 

This is not obvious because you  don't see evolution in your lifetime. 

Well, now we actually can, but  it seems permanent and static. 

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 seeing that there are  

very different types of intelligence out there  with very different strengths and weaknesses. 

Our assessment of which tasks require  intelligence, which ones don't,  

has to be reordered quite a bit. 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. 

This brings up a topic I've  been very curious about. 

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. 

He has this interesting observation in there. The Origin of Species was published in 1859. 

Principia Mathematica was published in 1687. So The Origin of Species comes out two centuries  

after Principia. Conceptually,  

it seems like Darwin's theory is simpler. There's a contemporaneous biologist to Darwin,  

Thomas Huxley, who reads The Origin of Species and  he says, "How stupid not to have thought of that." 

Nobody ever says that about  Principia, chiding themselves  

for not having beaten Newton to gravity. So there's a question of why did it take longer? 

It seems like a big part of the  reason is what you were saying. 

The evidence for natural selection is overwhelming  in a certain sense, but it's cumulative and  

retrospective, whereas Newton can  just say, "Here are my equations. 

Let me see the moon's orbital  period and its distance,  

and if it lines up, then we've made progress." Lucretius actually had this idea that species  

adapted to their environment in the first  century BC but nobody really talks about it  

until Darwin because Lucretius couldn't run some  experiment and force people to pay attention. 

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. I think one aspect of science is that it's not  

just creating a new theory and validating  it, but communicating it to others. 

Darwin was an amazing science communicator. He wrote in English, in natural language. I'm  

speaking like a— No Lean. 

I have to get out of my technical mindset. He spoke in plain English, didn't use equations,  

and he synthesized a lot of disparate facts. Little pieces of evolution had been worked out in  

the past, but he had this very compelling vision. Again, he was still missing things. 

He didn't know the mechanism for  heredity, he didn't have DNA. 

But his writing style was persuasive, and  that helped a lot. Newton wrote in Latin.  

He had invented entire new areas of  mathematics just to explain what he was doing. 

He was also from an era where scientists  were much more secretive and competitive. 

Academia is still competitive, but it  was even worse back in Newton's day. 

He held back some of his best insights because  he didn't want his rivals to get any advantage. 

He was also a somewhat unpleasant  person from what I gather. 

It was only a couple of decades after Newton  when other scientists explained his work in  

much simpler terms that they became widespread. The art of exposition and making a case and  

creating a narrative is also a  very important part of science. 

If you have the data, it helps, but people need  to be convinced, otherwise they will not push  

it further or take the initial investment  to learn your theory and really explore it. 

That's another thing which is really  hard to reinforcement learn on. 

How can you score how persuasive you are? Well, there are entire marketing  

departments trying to do this. Maybe it's good that AI is not  

yet optimized to be persuasive. There's a social aspect to science. 

Even though we pride ourselves on having an  objective side to it, where there's data and  

experiment and validation, we still have  to tell stories and convince our fellow  

scientists. That's a soft, squishy thing. It's  a combination of data and painting a narrative,  

and it's a narrative of gaps. Even with Darwin, as I said, there  

were pieces of his theory he could not explain. But he could still make a case that in the future,  

people would find transitional  forms, that they would find the  

mechanism of inheritance, and they did. I don't know how you can quantify that  

in such a precise way that you can  start doing reinforcement learning. 

Maybe that will be forever  the human side of science. 

One takeaway I had from reading and watching your  stuff on the cosmic distance ladder… By the way,  

I highly recommend people watch your series  with 3Blue1Brown on the cosmic distance ladder. 

One takeaway was that the deductive  overhang in many fields could be  

so much bigger than people realize. 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. 

I wonder if you think that's a product  of astronomy at the particular times  

in history that you're studying. Or is it just 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? 

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 data was  

the bottleneck. It still is the bottleneck.  It's really hard to collect astronomical data. 

Astronomers are world-class in  extracting all kinds of conclusions  

from little traces of data, almost like Sherlock. I hear that for a lot of quant hedge funds, their  

preferred hire is an astronomy PhD, actually. They are also very interested for other reasons  

in extracting signals from  various random bits of data. 

Okay, speaking of clever ideas,  one of my listeners, Shawn,  

solved the puzzle that Jane Street made for my  audience and posted a great walkthrough on X. 

For context, Jane Street trained a ResNet,  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 Shawn 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, Shawn realized that in  a well-trained ResNet, the product of  

two weight matrices in a residual block should  have a distinctive negative diagonal pattern. 

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, Shawn 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 backdoored LLMs that  even Jane Street doesn't know how to solve. 

You can find it at janestreet.com/dwarkesh. Alright, back to Terence! 

We do under-explore how to extract  extra information from various signals. 

Just to pick one random study, I remember reading  once that people were trying to measure how often  

scientists actually read the papers  that they cite. How do you measure  

this? You could try to survey different  scientists, but they had a clever trick. 

Many citations have little typos, like a  number is wrong or punctuation is almost wrong. 

They measured how often a typo got copied  from one reference to the next, and they  

could infer whether an author was just copying and  pasting a reference without actually checking it. 

From that, they were able to infer some measure  of how much attention people were paying. 

So there are some clever tricks to extract… These questions you posed earlier of how  

we can assess whether a scientific development  is fruitful, interesting, or represents real  

progress… Maybe there are really useful metrics  or footprints of this phenomenon in data. 

We can examine citations and how often  something is mentioned in a conference. 

Maybe there's a lot of sociology of science  research to be done that could actually  

detect these things. Maybe we should get  

some astronomers on the case, actually. That brings us nicely to the progress that, from  

the outside, it seems like AI for math is making. You had a post recently where you pointed out  

that over the last few months,  AI programs have solved fifty  

out of the eleven hundred odd Erdős problems. 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 that is still the  case, that we have picked the low-hanging fruit  

and now we're at this plateau currently. It does seem so. Fifty-odd problems have  

been solved with AI assistance, which is  great, but there's like six hundred to go. 

People are still chipping away  at one or two of these right now. 

We're seeing a lot fewer pure AI solutions  now where the AI just one-shots the problem. 

There was a month where that happened and  that has stopped, not for lack of trying. 

I know of three separate attempts to get  frontier model AIs to just attack every  

single one of the problems simultaneously. They pick out some minor observations,  

or maybe they find that some problem was already  solved in the literature, but there hasn't been  

any further purely AI-powered solution yet. People are using AI a lot currently. 

Someone might use AI to generate a possible  proof strategy, and then another person will  

use a separate AI tool to critique it, rewrite  it, generate some numerical data for it,  

or do a literature survey. Some problems have been solved  

by an ongoing conversation between  lots of humans and lots of AI tools. 

But it does seem like it was this one-off thing. Maybe one analogy for these problems is  

that you're in some sort of mountain  range with all kinds of cliffs and walls. 

Maybe there's a little wall which is three  feet high, and one that's six feet high,  

and then there's fifteen feet high, and  then there are some mile-high cliffs. 

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. 

So we try to light some candles  and make some maps, and slowly we  

figure out some of them are climbable. Some of them we can identify a partial  

track in the wall that you can reach first. These AI tools, they're like jumping  

machines that can jump two meters  in the air, higher than any human. 

Sometimes they jump in the wrong  direction, and sometimes they crash,  

but sometimes they can reach the tops of the  lowest walls that we couldn't reach before. 

We've just set them loose in this  mountain range, hopping around. 

There was this exciting period where they could  actually find all the low ones and reach them. 

Maybe the next time there's a big  advance in the models, they will  

try it again, and a few more will be breached. But it's a different style of doing mathematics. 

Normally we would hill climb, make little  markers, and try to identify partial things. 

These tools either succeed or they fail. They've been really bad at creating partial  

progress or identifying intermediate  stages that you should focus on first. 

Going back to this previous discussion, we  don't have a way of evaluating partial progress  

the same way we can evaluate a one-shot  success or failure of solving a problem. 

There's two different ways to think  through what you've just said. 

One of them is more bearish on AI  progress, and one of them is more bullish. 

The bearish one being, "Oh, they're only  getting to a certain height of wall,  

which is not as high as humans are reaching." The second is that 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. 

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 million  

different problems at the same time. But once AIs reach Terence Tao-level,  

they could do that. Once they reach intermediate levels,  

they could do the intermediate version of that. 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. I agree. They excel at breadth,  

and humans excel at depth, human experts at  least. I think they're very complementary.  

But our current way of doing math and science  is focused on depth because that's where human  

expertise is, because humans can't do breadth. We have to redesign the way we do science to take  

full advantage of this breadth  capability that we now have. 

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. 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 entirely new fields of  science by first getting these broad,  

moderately competent AIs to map it out  and make all the easy observations. 

And then identify certain islands of difficulty,  which human experts can then come and work on. 

I see very much a future of  very complementary science. 

Eventually, you would hope to get both breadth  and depth and somehow get the best of both worlds. 

But we need practice with the breadth side.  It's too new. We don't even have the paradigms  

to really take full advantage of it. But we will, and then science will be  

unrecognizable after that, I think. To this point about complementarity,  

programmers have noticed that they're way  more productive as a result of these AI tools. 

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 is to have some  effect on the world through your work. 

If it leads to you better understanding  a problem or coming up with some clean  

abstraction to embody in your code,  that is instrumental to the end goal. 

Whereas with research, the reason we care  about solving the Millennium Prize Problems  

is that presumably that in the process of  solving them, we discover new mathematical  

objects or new techniques that advance our  civilization's understanding of mathematics. 

So the proof is 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. Certainly in math, the process is often more  

important than the problem itself. The problem is kind of a proxy  

for measuring progress. I think even in software,  

there are different types of software tasks. If you just create a webpage that does the same  

thing that a thousand other webpages  do, there's no skill to be learned. 

Well, there is still some skill maybe that  the individual programmer could pick up. 

But for boilerplate-type code, it's something  that you should definitely offload to AI. 

Sometimes once you make the code,  you still have to maintain it. 

There are issues with upgrading it and  making it compatible with other things. 

I've heard programmers report 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 is an ongoing process. If you don't have the skills that you pick up from  

writing the code, that may impact your  ability to maintain it down the road. 

So yes, certainly mathematicians, we've used  problems to build intuition and to train people  

to have a good idea of what's true, what to  expect, what is provable, and what is difficult. 

Just getting the answers right away  may actually inhibit that process. 

I made a distinction between  theory and experiment before. 

In most sciences, there's an equal  division between the theoretical side  

and the experimental side. Math has been unique in  

that it's almost entirely theoretical. We place a premium on trying to have coherent,  

clean theories of why things are true and false. We haven't done many experiments as to,  

if we have two different ways to solve  a problem, which is more effective. 

We have some intuition, but we haven't done  large-scale studies where we take a thousand  

problems and just test them. But we can do that now. 

I think AI-type tools 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 large-scale data  about what things work and what things don't. 

The 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  workflows let you scale. 

The idea of doing mathematics  at scale is at its infancy. 

But that's where AI is really  going to revolutionize the subject. 

I feel like a big crux in these conversations  about how good AI will be for science is,  

I think you said this, that they're using  existing techniques and modifying them. 

It would be interesting to  understand how much progress one  

can make simply from using existing techniques. If I looked at the top math journals, how many of  

the papers are coming up with a new technique,  whatever that means, versus using existing  

techniques on new problems? What is the overhang?  If you just applied every known technique to every  

open problem, would that constitute a humongous  uplift in our civilization's knowledge, or would  

that not be that impressive and useful? This is a great question, and we don't  

have the data to fully answer it yet. Certainly, a lot of work that human  

mathematicians do… When you take a new problem,  one of the first things we do is we look at all  

the standard things that have worked on similar  problems in the past, and we try them one by one. 

Sometimes that works, and that's still worth  publishing 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 the papers that go into the top journals  

are usually ones where the existing methods  can kind of solve 80% of the problem, but then  

there is this 20% which is resistant and a new  technique has to be invented to fill in the gaps. 

It's very rare now that a problem gets  solved with no reliance on past literature,  

where all the ideas come out of nowhere. That was more common in the past,  

but math is so mature now that it's just so much  of a handicap to not use the literature first. 

AI tools are getting really good at the  first part of that, just trying all the  

standard techniques on a problem, often making  fewer mistakes in applying them than humans. 

They still make mistakes, but I've tested  these tools on little tasks that I can do,  

and sometimes they pick up errors that I make. Sometimes I pick up errors that they make. 

It's about a tie right now. But I haven't yet seen them take the next step. 

When there are holes in the argument where none  of the things are working, then what do you do? 

They can suggest random things, but often  I find that trying to chase them down to  

make them work, and finding they don't  work, wastes more time than it saves. 

I think some fraction of problems that  we currently think are hard will fall  

from this method, especially the ones  that haven't received enough attention. 

With the Erdős problems, almost all of the 50  problems that were solved by AIs were ones for  

which there was basically no literature. Erdős posed the problem once or twice. 

Maybe some people tried it casually and couldn't  do it, but they never wrote up anything. 

But it turned out that there was a solution,  and it was just combining this one obscure  

technique that not many people know about  with some other result in the literature. 

That's 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… Some people have done  large-scale sweeps of these Erdős problems. 

If you only focus on the success  stories, the ones that get broadcast  

on social media, it looks amazing. All these problems that haven't been  

solved for decades, now they're falling. But whenever we do a systematic study,  

on any given problem an AI tool has  a success rate of maybe 1% or 2%. 

It's just that they can buy scale, and you  just pick the winners. It looks great. I  

think there'll be a similar thing happening  with the hundreds of really prestigious,  

difficult math problems out there. Some AI may get lucky and actually solve them,  

and there will be some backdoor to solve  the problem that everyone else missed. 

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 1% to 2% success rate. 

There'll be a lot of noise amongst the signal  of when they're working and when they're not. 

It will be increasingly important to  collect these really standardized datasets. 

There are efforts now to create a standard set of  challenge problems for AIs to solve, and not just  

rely on the AI companies to only publish their  wins and not disclose their negative results. 

That will maybe give more clarity  as to where we're actually at. 

Although I think it's worth emphasizing how  much progress in AI it constitutes already,  

to have models that are capable of applying  some technique that nobody had written down  

as applicable to this particular problem. The progress is simultaneously amazing  

and disappointing. It is a very strange  

feeling to see these tools in action. But people also acclimatize really quickly. 

I remember when Google's web  search came out 20 years ago. 

It just blew all the other  searches out of the water. 

You're getting relevant hits on the  front page, exactly what you wanted. 

It was amazing, and then after  a few years, you just took for  

granted that you could Google anything. 2026-level AI would be stunning in 2021. 

A lot of it—face recognition, natural speech,  doing college-level math problems—we just  

take for granted now. Speaking of 2026 AI,  

you made a prediction in 2023 that by 2026  it would be like a colleague in mathematics? 

A trustworthy co-author if used correctly. Which is looking pretty good in retrospect. 

Yeah, I'm pretty pleased. So let's see if you can continue this streak. 

You personally are 2x more  productive as a result of AI. 

What year would you say that? 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. 

For example, my papers now have a  lot more code, a lot more pictures,  

because it's so easy to generate these things now. Some plot which would 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. On the one hand, I think the type of  

papers that I would write today, if I  had to do them without AI assistance,  

would definitely take five times longer. But I would not write my papers that way. 

5x? Yeah, but these are auxiliary tasks. 

Things like doing a much deeper literature  search or supplying a lot more numerics.  

They enrich the paper. The core of what I do,  actually solving the most difficult part of a  

math problem, hasn't changed too much. I still use pen and paper for that. 

But there's lots of silly things. I use an AI agent now to reformat. 

Sometimes if all my parentheses are not quite  the right size, I used to manually change them  

by hand, and now I can get an AI agent to  do all that quite nicely in the background. 

They've really sped up lots of secondary tasks. They haven't yet sped up the core thing that I do,  

but it's allowed me to add  more things to my papers. 

By the same token, 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 level of functionality—it actually  

hasn't saved that much time, to be honest. It's made the papers richer and broader,  

but not necessarily deeper. You made this distinction between  

artificial cleverness and artificial intelligence. I would like to better understand those concepts. 

What is an example of intelligence  that is not just cleverness? 

Intelligence is famously hard to define. 

It's one of these things that  you know 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. 

One of us has some idea and it looks promising,  so then we have some sort of prototype strategy. 

We test it, and it doesn't  work, but then we modify it. 

There's adaptivity and continual  improvement of the idea over time. 

Eventually, we've systematically mapped  out what doesn't work and what does work,  

and we can see a path forward, but  it's evolving with our discussion. 

This isn't quite what the AIs do. The AIs can mimic this a little bit. 

To go back to this analogy of these jumping  robots, they can jump and fail, and jump and fail. 

But what they can't do is jump a little bit, reach  some handhold, stay there, pull other people up,  

and then try to jump from there. There isn't this cumulative process  

which is built up interactively. It seems to be a lot more trial and  

error and just repetition: brute force. It scales, and it can work amazingly  

well in certain contexts. But this idea of building  

up cumulatively from partial progress  is what's still not quite there yet. 

Interesting. You're 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. 

No. Or even if it works  

on a problem without solving it, it's not that  its own understanding of math has progressed. 

Yeah. You run a new session and  it's forgotten what it just did. 

It has no new skills to build on related problems. Maybe what you just did is 0.001% of the  

training data for the next generation. So maybe eventually some of it gets absorbed. 

So Terence 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 reach for the right tools? Did it check its own work and  

explore alternative paths? How clear was its response? 

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 you rubrics tailored to  your domain, helping you systematically  

measure and shape how your models think. Learn more at labelbox.com/dwarkesh. 

One big question I have is how plausible is it  that if we just keep training AIs—they get better  

and better at solving problems in Lean—that they  will continue to solve more and more impressive  

problems, and then we will be surprised at how  little insight we got from some Lean solution  

to proving the Riemann hypothesis or something. Or do you think it is a necessary condition of  

solving the Riemann hypothesis, even by  an AI that is doing it entirely in Lean,  

that the constructions and definitions  created in the Lean program have to  

advance our understanding of mathematics? Or could it just be assembly code gobbledygook? 

We don't know. 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, and maybe we never will. Some problems may only be solvable by splitting  

into an enormous number of  cases and doing brute force,  

uninsightful computer analysis on each case. Part of the reason we prize problems like  

the Riemann hypothesis is that we're  pretty sure 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 it could be false actually. Okay, there is an unlikely scenario  

that the hypothesis is false, and you  can just compute a zero off the line,  

and a massive computer calculation verifies  it. That would be very disappointing. I do  

feel that fully autonomous, one-shot approaches  are not the right approach for these problems. 

You'll get a lot more mileage out of the interplay  of humans collaborating with these tools. 

I can see one of these problems  being solved by smart humans  

assisted by extremely powerful AI tools. But the exact dynamic may be very different  

from what we envision right now. It could be a collaboration of  

a type that just doesn't exist yet. There may be a way to generate a million variants  

of the Riemann zeta function and do AI-assisted  data analysis to discover some pattern connecting  

them that we didn't know about before. This lets you transform the problem  

into a different area of mathematics. There could be all kinds of scenarios. 

Suppose the AI figures it out, and latent in  the Lean is some brand-new construction which,  

if we realized its significance, we would be  able to apply in all these different situations. 

How would we even recognize it? Again, a very naive question, but if you come  

up with the equivalent of Descartes' idea that  you can have a coordinate system unifying algebra  

and geometry, in Lean code it would just look  like R→R, and it wouldn't look that significant. 

I'm sure there are other constructions  which have this kind of property. 

The beauty of formalizing a proof in  something like Lean is that you can take  

any piece of it and study it atomically. When I read a paper which solves some  

difficult problem, there's often a  big sequence of lemmas and theorems. 

Ideally, the author will talk their way  through what's important and what's not. 

But sometimes they don't reveal what steps  were the important ones and which ones  

were just boilerplate, standard steps. You can study each lemma in isolation. 

Some of them I can see look fairly standard  and resemble something I'm familiar with. 

I'm pretty sure there's nothing  interesting going on there. 

But this other lemma, that's something I haven't  seen before, and I can see why having this result  

would really help prove the main result. You can assess whether a step is really key  

to your argument or not, and  Lean really facilitates that. 

The individual steps are  identified really precisely. 

I think in the future, there will be entire  professions of mathematicians who might take  

a giant Lean-generated proof and do some  ablation on it, trying to remove parts of  

it and find more elegant ways. They might get other AIs to do  

some reinforcement learning to 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 how we write papers. Until recently, writing papers was the most  

time-consuming and expensive part of the job. So you did it very rarely. 

You only wrote up your results once all the other  parts of your argument were checked out, because  

rewriting and refactoring was just a total pain. That's become a lot easier now  

with modern AI tools. You don't have to have just  

one version of your paper. Once you have one,  

people can generate hundreds more. 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've seen this with the Erdős problem website. 

An AI will generate a proof, and here are  3,000 lines of code that verify the proof. 

Then people got other AIs to summarize  the proof, and people write their own  

proofs. There's actually post-processing.  Once you have one proof, we have a lot of  

tools now to deconstruct and interpret it. It's a very nascent area of mathematics,  

but I'm not as worried about it. Some people are concerned about what happens if  

the Riemann 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. 

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. We don't really know. We've been very  

lucky in mathematics that we have worked  out the laws of logic and mathematics,  

but this is a fairly recent accomplishment. It was started by Euclid two millennia ago,  

but only in the early 20th century did we  finally list out the axioms of mathematics,  

the standard axioms of what we call ZFC, the  axioms of first-order logic, and what a proof is. 

This we've managed to automate  and have a formal language for. 

There could be some way to assess plausibility. You have a conjecture that something is true,  

you test a few examples, and it works out. How does this increase your  

confidence that the conjecture is true? We have a few sort of mathematical ways to model  

this, like Bayesian probability, for example. But you often have to set certain base  

assumptions, and there's a lot of  subjectivity still in these tasks. 

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, has  made deductive proofs so much easier to automate  

and train AI on… 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 is plausible or not. 

If there was some semi-formal framework  where this could be done semi-automatically  

in a way that isn't easily hackable... It's really important with these formal  

proof assistants that there are no backdoors  or exploits you can use to somehow get your  

certified proof without actually proving  it, because reinforcement learning is  

just so good at finding these backdoors. If there's some framework that mimics how  

scientists talk to each other in a  semi-formal way, using data and argument,  

but also constructing narratives... There's some subjective aspect of  

science that we don't know how to capture in a way  that we can insert AI into it in any useful way.  

This is a future problem. There are research  efforts to try to create automated conjectures,  

and maybe there are ways to benchmark these and  simulate this, but it's all very new science. 

Can you help me get some intuition? I have two  sub-questions. One, it would be very helpful  

to have a specific example of what something  like this would look like, the way scientists  

communicate that we can't formalize yet. Two, it seems almost definitionally paradoxical  

to say you're building up some narrative or  natural language explanation and then also having  

something which you could have formalized. I'm sure there's some intuition behind  

where that overlap is, and I'd  love to understand that better. 

An example of a conjecture: Gauss was  interested in the prime numbers and  

created one of the first mathematical datasets. He just computed the first 100,000 prime numbers  

or so, hoping to find patterns. 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, 1,000, one 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 X divided by the natural log of X. 

He had no way to prove this. It was  data-driven. 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. Normally you're talking about a pattern,  

like maybe the spacing between the  primes has a certain regularity. 

But this 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. 

It started the field of what  we call analytic number theory. 

It was the first in many conjectures  like this, many of which got proved,  

which started consolidating the idea that the  prime numbers didn't really have a pattern,  

that they behaved like random sets  of numbers with a certain density. 

They had some patterns,  like they're almost all odd. 

They're also not actually random,  they're what's called pseudo-random. 

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 creating this random set. 

This allowed us to make all  these other predictions. 

There's a still-open conjecture in number  theory called the twin prime conjecture, that  

there should be infinitely many pairs of primes  that are twins just two apart, like 11 and 13. 

We can't prove that, and there are  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 generated by  flipping coins, we would just—by random chance  

like infinite monkeys at a typewriter—see  twin primes appear over and over again. 

We have over time developed this very accurate  conceptual model of what the primes should behave  

like based on statistics and probability. It's mostly heuristic and non-rigorous,  

but extremely accurate. The few times when we actually  

can prove things about the primes, it has  matched up with the predictions of what we  

call the random model of the primes. We have this conjectural concept  

framework for understanding the  primes that everyone believes in. 

It's the same reason why we believe the  Riemann hypothesis is true, and why we  

believe that cryptography based on  the primes is mathematically secure. 

It's all part of this belief. In fact, one reason why we care  

about the Riemann hypothesis is that  if the Riemann hypothesis failed,  

if we knew it was false, it would  be a serious blow to this model. 

It would mean there's a secret pattern  to the primes that we were not aware of. 

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 are probably more, and these  

patterns can lead to exploits in crypto. It would be a big shock. 

So we really want to make  sure that doesn't happen. 

We've been convinced of things like  the Riemann hypothesis over time. 

Some of it is experimental evidence, and some  is that the few times we've been able to make  

theoretical results, they've always aligned. It is possible that the consensus is wrong and  

we've all just missed something very basic. There have been paradigm shifts in  

the past in scientific history. But we don't really have a way of  

measuring this, partly because we don't have  enough data on how math or science develops. 

We have one timeline of history, and we have  maybe 100 stories of turning points in history. 

If we had access to a million alien  civilizations, each with a different  

development of history and science in different  orders, then maybe we'd actually have a decent  

shot at understanding how we measure what  progress is and what is a good strategy. 

We could maybe start formalizing  it and actually having a framework. 

Maybe what we need to do is start creating  lots of mini-universes or simulations of AI  

solving very basic problems in arithmetic  or whatever, but coming up with their  

own strategies for doing these things and  having these little laboratories to test. 

There are people who investigate what's  the smallest neural network that can do  

10-digit multiplication and things like that. I think we could learn a lot just from evolving  

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It's a super low-friction way for me to keep  tabs on my business and make quick decisions. 

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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? We talked about depth and breadth before. 

It's not a purely human-AI distinction. Humans also, I think it was Berlin who  

split them into hedgehogs and foxes. The hedgehog knows one thing very well,  

and a fox knows a little bit about everything. I definitely think of myself as a fox. 

I work with hedgehogs a lot, and  sometimes I can be a hedgehog if need be. 

I've always had a little  bit of an obsessive streak. 

If there's something I read about which I  feel like I have the capability to understand,  

but I don't understand why it works and  there's some magic in it… Someone was able  

to use a type of mathematics I'm not familiar  with and get a result I would like to prove. 

I can't do it myself, but they  could do it by their method,  

and I want to find out what their trick was. It bugs me that someone else can do something  

I think I can do, but I can't. I've always had that obsessive,  

completionist streak. I've had to wean myself off  

computer games because if I start a game, I want  to play it to completion, through all the levels. 

That's one way 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  

working on another area of mathematics. I find their problems interesting,  

but they have to teach me some of the basic  tricks, what's known, and what's not known. 

I learn a lot from that. I found that writing about  

what I've learned helps. I have a blog where I sometimes  

record things I've learned. In the past when I was younger,  

I would learn something, do this cool trick,  and say, "Okay, I'm going to remember this." 

Then six months later, I'd forgotten it. I remember remembering it,  

but I can't reconstruct my arguments. The first few times, it was so frustrating  

to have understood something and then lost it. I resolved I should always write down  

anything cool that I've learned. That's part of how this blog came about. 

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. There's some referee  

report or something that feels slightly  unpleasant for me to do at the time. 

Writing a blog feels creative and fun. It's something I do for myself. 

Depending on the topic, it could be a  quick half an hour or several hours. 

Because it's something I do voluntarily,  time flies when I write these things down, as  

opposed to doing something I have to do for  administrative reasons that is just drudgery. 

Those are tasks, by the way, that  AI is really helping with nowadays. 

If civilization could from first principles  decide how to use Terry Tao's time, as a  

limited resource, what is the biggest difference? What if the veil of ignorance got to decide how to  

use Terry Tao's time versus what it does  now? This podcast wouldn't be happening. 

As much as I complain about certain tasks that  I don't want to do, but have to do… As you get  

more senior in academia, you get more and more  responsibilities, more committees, and whatever. 

I have also found that a lot of events  I reluctantly went to because I was  

obliged to for one reason or another…  Because it's outside my comfort zone,  

it often results in interactions with people I  wouldn't normally talk to, like you for instance. 

I would learn interesting things  and have interesting experiences. 

I would have opportunities to then network with  other people that I never would have before. 

So I do believe a lot in serendipity. I do optimize portions of my day  

where I schedule very carefully. But I am willing to leave some portions just  

to do something that is not my usual thing. Maybe it'll be a waste of my time,  

but maybe I will learn something. More often than not, I get a positive  

experience that I wouldn't have planned for. So I believe a lot in serendipity. 

Maybe there's a danger in modern  societies, not just with AI, that we've  

become really good at optimizing everything. We’re not optimizing our own optimization. 

With COVID, for example, we switched a lot to  remote meetings, so everything was scheduled.  

We kept busy in academia. We met almost  the same number of people we met in person,  

but everything had to be planned in advance. What we lost out on was the casual knocking  

on a hallway door, just meeting  someone while getting a coffee. 

Those serendipitous interactions may not seem  optimal, but they are actually really important. 

When I was a grad student, I would go to  the library to look for a journal article. 

You had to physically check out  the journal and read the article. 

You could browse through and sometimes  the next article was also interesting. 

Sometimes it wasn’t, but you could  accidentally find interesting things. 

That has basically been lost now. If you want to access an article,  

you just type it into a search engine or an AI,  and you get exactly what you want instantly. 

But you don't get the accidental things you might  have found if you'd done it more inefficiently. 

I spent a year once at the Institute  for Advanced Study, which is  

a great place with no distractions. You're there just to do research. 

The first few weeks you're there, it's great. You're getting all these papers written up that  

you've been wanting to do for a long time. You think about problems for  

blocks of hours at a time. But I find if I stay there for more  

than several months, I run out of inspiration.  I get bored. I surf the internet a lot more. 

You actually do need a certain  level of distraction in your life. 

It adds enough randomness and high temperature. I don't know the optimal way to schedule  

my life. It just seems to work. I'm very curious when you expect AIs  

that can actually do frontier math at least  as well as the best human mathematicians. 

In some ways, 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. 

You could argue that calculators were doing  frontier math that humans could not accomplish,  

but it was number crunching. But replacing Terry Tao completely. 

I mean, what do you want me for? You'll just go on all the podcasts after. 

It might not be the right question to ask. I think within a decade, a lot of things that  

math students currently do—what we spend the  bulk of our time doing 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. A hundred years ago, a lot of mathematicians  

were just solving differential equations. Physicists needed some exact solution to  

some system, and they hired a mathematician to  laboriously go through the calculus and work out  

the solution to this fluid equation, whatever. A lot of what a 19th-century mathematician would  

do, you could make a call to Mathematica, Wolfram  Alpha, a computer algebra package, or now more  

recently to 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. Once computers came along—computers  

used to be human. 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. In genetics,  to sequence the genome of a single organism,  

that was an entire PhD of a geneticist, carefully  separating all the chromosomes and whatever. 

Now you can just spend $1,000 and send  it to a sequencer and get it done. 

But genetics is not dead as a subject. You move to a different scale. 

Maybe you study whole ecosystems  rather than individuals. 

I take your point but when is most  mathematical progress, or almost  

all mathematical progress, happening by AI? If you find out this year a Millennium Prize  

Problem has been solved, you would put  95% odds that an AI did it autonomously. 

Surely there will be such a year. I guess I do believe 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 stochastic. 

I think AIs currently are very good at  certain things, but really terrible at others. 

While you can add more and more frameworks on top  to reduce the error rates and make them work with  

each other a bit more, it feels like we don't  have all the ingredients to really have a truly  

satisfactory replacement for all intellectual  tasks. It is complementary currently. It's not  

a replacement. Because current level AIs  will accelerate science in so many ways,  

hopefully new discoveries and new  breakthroughs will happen more quickly. 

It's also possible that by destroying serendipity  we actually inhibit certain types of progress. 

Anything is possible at this point. I think the world is very,  

very unpredictable at this point in time. 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? We live in a time of change. 

As I said, we live in a  particularly unpredictable era. 

Things that we've taken for granted  for centuries may not hold anymore. 

The way we do everything, and not  just mathematics, will change. 

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 I think one just has to embrace that  

there's going to be a lot of change. The things that you study, some of them  

may become obsolete or revolutionized,  but some things will be retained. 

You always have to keep an eye on opportunities  for things that you wouldn't be able to do before. 

In math, you previously had to go through  years and years of education and 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, Lean, and everything else. There will be a lot of non-traditional  

opportunities to learn, so you  need a very adaptable mindset. 

There will be room for pursuing things  just for curiosity and for playing around. 

You still need to get your credentials. For a while it will still be important to  

go through traditional education and learn  math and science the old-fashioned way. 

But you should also be open to very different ways  of doing science, some of which don't exist yet. 

It's a scary time, but also very exciting. That's a great note to close on. Terence,  

thanks so much. Pleasure.