What Today’s Best Models Still Can’t Do in Math

The goal of mathematics is not to produce mathematics papers. It's to produce some kind of understanding. Maybe some of that understanding resides in model weights. To me, that's like pretty unsatisfying.

They definitely are not good at it autonomously, but with some hints, you can kind of get them to do something interesting. A lot of progress in mathematics comes from like letting a thousand different flowers bloom and people pursue their own curiosity and then the boundaries of knowledge expand in some fairly uniform way.

My favorite fully autonomous result by an AI so far is the solution to the Irish unit distance problem. There was some lemma I wanted to prove, none of the frontier models could do it. So I like worked out a ton of examples on my own and I realized, oh well, maybe like here's some reason why it could be true. Once I had that statement, the models were able to very quickly prove that sort of better statement.

Um.

I have a lot of opinions.

Yeah. So okay, so there have, you know, now been a lot of results, some of them produced autonomously, some produced like semi-autonomously, some whose like where the AI contribution is just not at all clear. Um, they're in a lot of different areas, so anything I say is kind of, you know, I can only really comment on things that I, you know, have some expertise on. So it's quite possible that if you talk to a different mathematician, you'll get like different answers here. Uh, so my favorite, uh, like fully autonomous result by an AI so far is the solution to the Irish unit distance problem, which I think was announced in mid-May. Um, so at least what I liked about that is it seemed to me that like it was in some ways a little bit creative. So, uh, I think some of the results, uh, we've seen have had kind of the flavor of like, you know, you kind of take some known techniques and apply them in maybe a clever way, or you, uh, I don't know, they have kind of been some kind of results I would characterize as like last mile, like where some recent work was done, like quite deep work done by a group of human mathematicians, and then the AI kind of took the final step.

Yeah. Um, but yeah, with the sort of, you know, distance problem, I I think it was something where the result was like a little unexpected. So first of all, my sense was like that people working in the area thought it was true, and then there was a counterexample found. But then also it like brought in some techniques from from another area. I think those techniques were like not especially, uh, you know, like deep or new. They were sort of classical ideas from the 60s, but they were new to this area of studying, um, you know, point configurations in the plane. And so that was pretty cool. And then afterwards we got to see like it was kind of fruitful. So a bunch of mathematicians took those ideas and used them to find counterexamples to a bunch of other interesting open questions. So for example, like the sum-product conjecture over the real numbers. Um, so that's at least what way I like to think about how cool a result is, like you look at it post hoc and you see like, oh well, you know, whatever new ideas that were introduced, if any, like kind of useful to do other things, like did they improve our understanding of something? And I think that's maybe so far the the the main example I know of of a of a result of that form.

Yeah. Okay. So, first of all, I mean, you you kind of characterized it as like inhuman in some way. I actually think the argument was very human. Like, you know, I'd love to judge or sorry, OpenAI like released some chain of thought. It was very recognizable. It was like kind of, you know, if if I tried to imagine like my chain of thought, uh, in trying to solve a problem, like it might look kind of like that.

Um, you know, we haven't seen the raw chain of thoughts, maybe that...

Yeah. Or maybe, you know, maybe the model liked to swear a lot in the middle of the chain of thought and they cleaned that up or something. We don't know. But like at least the summary seemed pretty plausible. And I would say that's actually like kind of typical of, uh, most of the results that I've studied. Like they don't seem inhuman at all. They seem absolutely like something a human mathematician could produce. Um, and, uh, they're like typically understandable if like not so well written if you just like look at raw model output. It's not like there's some, you know, move 37 or whatever. Um, it's like a human mathematician doing math. It's like a human mathematician doing certain types of math. So like they're definitely the models are still like not very good at some mathematical activities. And here I don't mean like by field, but just like certain things you do when you try to solve a problem the models don't seem to be doing, but certain things they're very good at. So, um, the ways they might be a little bit inhuman is like they don't get tired. They know a lot. Um, but if you have to just read the final output, it doesn't seem kind of inhuman.

Okay. So so first of all, I really like your point by the way that that they're mostly doing natural language reasoning rather than Lean. Like I think that that suggests to me that like these, you know, you hear a lot of people say like math is a verifiable domain, like that explains these the progress whatever. Like my sense is that because they're, you know, primarily scaling in formal reasoning, like probably the techniques are going to generalize to other domains pretty well. That's just my guess.

Um, my sense is that they're pretty similar in terms of capabilities. I've played a lot around a lot more with ChatGPT than than Claude, but you know, I it seems like there's a lot of cases where, you know, uh, OpenAI will drop a solution to some problem and Anthropic will say, 'Oh, you know, too.' Exactly. So it actually seems like they're they're solving a very similar collection of problems, and it's like kind of a small, you know, uh, it's like a relatively small portion of what human mathematicians do. Um, so yeah, one thing, um, that is interesting is like we see the solutions have a certain flavor, right? There'll be things that this isn't surprising, like there'll be things that rely on the model strengths, like their ability to like grind out long computation or like, you know, pull together kind of technical ideas for many areas, um, or like many maybe many papers that, you know, a human mathematician might not have read. But they're not like they seem like weaker in things like intuition or like having some big picture point of view. Like a lot of what I do as a mathematician is like I have some kind of philosophy that's like very non-rigorous. Like maybe I think this thing is kind of analogous to thing, and then like a lot of what I'm working out is like figuring out how to make that precise and like, you know, trying to measure the extent to which I've succeeded in understanding that by like can I solve a problem or whatever, like can I find an interesting phenomenon which I don't understand and then now I understand it. And like so far, um, I haven't, you know, you can even the best results the models are producing, you don't see, um, that much of this kind of reasoning. It's more like they're very very good at applying some known techniques, um, which is to be clear that's like a a very powerful thing to do, to be very good at applying like all known techniques. Uh, there are mathematicians who have had great careers, uh, doing very high quality work of that flavor, and I think a lot of what the models are producing it's high quality in that way, but it's it's like some kind of fairly narrow band of what mathematicians care about, um, so far. Um, I do think there's like signs of both, um, you know, all the frontier models starting to be able to do more fuzzy things. Um, so like I've I've tried to get, uh, both both Claude and, um, ChatGPT 5.6, I guess, to do some kind of theory building. And it's like they're not good. They definitely are not good at it autonomously, at least with like whatever scaffolding I've set up. But with some hints, you can kind of get them to do something interesting. Um, you know, when you do when you give the models hints, it's always a little hard to tell like what part is from the model and what part is from you. But my experience is that like if they can do it with like a hundred bits of hints or whatever in six months, maybe they can do it without hints. Yeah, you know, I do think there's signs that they're also kind of somehow picking up some of this like implicit and unwritten mathematical knowledge.

Well, why is I don't know. I mean I just I think it's just inertia. Like I have pretty sure of it. Um, it got one thing is that ChatGPT got better at math earlier. So like for a long time, um, the Claude models were just like not useful for research math, and then I think maybe around Opus 4.5 or Opus 4.6 they like more or less caught up. Yeah. Uh, but you know some experimentation suggests to me they're pretty neck and neck, and so for my own work, you know, except when I'm just experimenting, I mostly just stick with one and sort of random.

I'm not I find they're both pretty bad at theory.

Yeah. So so I I mean I think there are a lot of different kinds of mathematicians. Um, there's like a lot of different, uh, you know, spectra on which one can put a mathematician. Um, so, uh, definitely a lot of mathematicians like solving open problems. Uh, and then I think I'm one of those like I like to solve an open problem. That's, uh, I think of myself as a problem solver as opposed to like one, you know, one other taxonomy you could you could have is a problem solver versus a theory builder. Um, at least for me, uh, the point of an open problem is it's like supposed to measure your failure to understand something. So it's kind of like a benchmark. Um, right, like, uh, you know, one problem I really like is the Gross-Zagier conjecture, whatever that is. It's it measures something about our our failure to understand differential equations. So it's like there's some very basic object we would like to understand. If we can't answer this conjecture, we know we don't understand it. Okay. So in practice like how do you get at a problem which is supposed to be measuring something you don't understand? Well like of course you try to understand the thing better. Um, and and in practice what that means is like well you try to find the smallest situation where you can't understand something and and and fiddle around with it, and then you stare at like what once you win you stare at like what you develop to win and try to turn that into some theory. Um, so that's one thing you might do. You might try to like solve a problem and in so doing develop some kind of new understanding of the situation. Uh, you might also just like have some feeling that like this thing is related to this other thing. Um, and you know you might start building a table like oh this property A is related to property A prime, property B is related to property B prime, and so on so forth. So, uh, for example, uh, in in my work a lot of it is motivated by some analogy between homology of algebraic varieties and representations of fundamental groups. Okay, so that's some some fancy stuff. Uh, but it's that this analogy is like very very fruitful and like really any phenomenon that appears on one side, you can find an analog on the other side. And so you know trying to, uh, to realize that dream has led led to a lot of beautiful mathematics of the last like 30 or 40 years, um, by people like Carlos Simpson and and Takuro Mochizuki and others. Um, and so here it's really just like someone noticed like here's an analogy, and then that analogy has like led to a huge amount of developments. There's not really like an open problem at the end, although of course like as you develop this you come up with lots of open problems. There's just like a philosophy that you're trying to, uh, you know, you're trying to realize, and that philosophy is like super not rigorous actually. It's not like symbol pushing at all. Um, yeah, so that's another kind of activity that I like. Um, yeah, beyond that, uh, you know, a lot of, uh, what you do when you try to, you know, a lot of the activities you like, you're actually trying to figure out what the right question is. Even like here you're you have some object you feel like you don't understand it, and like figuring out what you don't know is like actually a very challenging thing to do. So, so, um, you know there's like a list of, you know, you can go online and list open conjectures or whatever, and this like doesn't really capture in a lot of ways what we don't know. Like often finding the conjecture is like really really hard. Uh, so I don't know, a good example of this is like the Birch and Swinnerton-Dyer conjecture, which is one of Millennium problems. Uh, is this like beautiful relationship between L-functions of elliptic curves and, uh, the the set of solutions to the corresponding equations of the rank of the of the group of solutions, sort of what that means. Um, it was discovered by like it was like the first big data conjecture. So Birch and Swinnerton-Dyer had like found all these statistics on elliptic curves in the 60s, like this one of the first ever computer-aided bits of mathematics, and they like graphed these statistics and they noticed that you know some the slope of some line on a graph was related to some other algebraic invariant they knew, and that was the source of this conjecture. So a lot of the time you're just like working out examples and like trying to like you're doing kind of science like you run an experiment and you try to figure out an explanation for that, um, experiment. And so I mean I think going back to AI, I think like these are things where AI seems so far to, you know, help a lot more in some things than other things. So like, uh, you know I think the the more vague, uh, uh, a phenomenon is or like the the less you have a precise question in mind, the less useful it happens to be. And so you were asking like how I use it in my daily life, like actually what I found is that the projects that I have that kind of predate AI, like the projects I've been thinking about for three or four or five years, um, it's just not that useful. Like it's primarily kind of a substitute for Google or something. Like I might use it to like learn about some related topic or like something where I would have earlier Googled something and then like read a paper, like maybe I'll discuss it with AI instead. So it saves some time for sure. It's like not really doing deep intellectual work for me. But then you know because I, you know, I'm now like well I I suck at coding, and so now I have, you know, my good friend who's really good at coding, and now I have all these coding projects because like suddenly well I if I had a question where coding would have been really useful, I would have procrastinated on it for six months until I...

Exactly. Yeah. So, so yeah, now I picked up all these projects where yeah, coding is really useful. Like the models are like very good for kind of massively parallel things. Like if you want to find an example of something, you can just ask it to find, you know, work through a thousand examples in parallel or maybe 10 examples at a time, you know, 10 different sub-agents, and like that's really useful. But these are like kind of different activities, uh, which are like I don't know on top of what I was doing before.

So yeah, it's Yeah, go.

Yeah. I mean, so definitely some people are like motivated by like beauty or or kind of aesthetic considerations. I try not to be motivated by that. I think that's a bad way like Well, one thing like that sort of limits you, right? Like one thing kind of a failure mode I see among young mathematicians sometimes is like you you have something and you kind of think you know how to prove it, and then like the proof feels really ugly and you decide but like okay I mean what if you're wrong and it's not ugly like you why limit yourself you should...

I I don't really know. I I don't really have aesthetic feelings, but people people sometimes feel this way like maybe it involves a lot of grinding calculation that's not illuminating or... but you should like win by any means necessary in my opinion. Like I I like to think of what I'm doing like doing kind of physics except with concepts. So, um, you know, I instead of beauty I try to think about maybe like what is kind of fundamental, what's going to open up further understanding most. Will you know am I introducing a new idea that will be like broadly useful to understand this object? And I guess you know in some sense there's there's like some aesthetic consideration there, but it's I try to I think the the orientation of like trying to do good science rather than trying to do art is what I prefer. Uh, but there's a huge I mean there's a huge variety of of opinions here and like lots of mathematicians think of themselves as being like closer to poets or something. Um, yeah, what I what I do think is broadly true is that like progress comes from people like it seems to come in mathematics from people sort of pursuing their personal curiosity. Um, and that it's sort of been crucial historically that there's like a lot of different people with different views of what's interesting, and then the frontier of knowledge expands and expands, and then suddenly you know you have these opportunistic situations where a new idea has been introduced and you can kind of now find you now can suddenly like cascade through a bunch of other things that we didn't understand before.

Yeah, so in some cases I mean the the some cases there is like a well-stated problem here like you know you know I said I've been thinking about things for se you know maybe 10 years now at this point for certain problems sometimes there is just like a conjecture that I would like to prove that that is is there. Um, I think one reason the models might not be useful for some of these things is like the conjectures are true. Um, so like, uh, I think that certain you know for for example, um, you know this unit distance conjecture problem like the the general belief, uh, in the community was that it was true and then it turned out to be false. And so what that means is that there's like a specific construction you can do to to, um, uh, to to refute it. Um, on the other hand I think a lot of the things I I think about like I know okay maybe I'm about to, you know, that someone will come up with a counterexample to the curvature conjecture hypothesis tomorrow and like, uh, I'll look like a fool. Uh, but that in general like these conjectures fit into some very broad theoretical framework which means that like we actually have a lot of evidence that they're true. Um, and so, uh, you know yeah so that's part of it like there's not like a construction you can do to refute it. Um, you need to somehow kind of, uh, you know there's we have this giant framework where certain certain pieces of it are only conjecturable and you probably need a to resolve some of those conjectures to win. Um, we also have like a pretty good sense I think that like very serious new ideas are needed to resolve those conjectures. So like, um, of course you can't be sure like maybe there's some very clever construction that will let you I don't know, uh, avoid having a big new idea. Um, I don't know. Uh, uh, maybe you know it's quite possible we'll find this out, but my sense is that for at least a lot of the things I've been thinking about, um, there are they're just not accessible to, um, you know, applying known techniques very very techn in a very technically strong way. Um, so you need to develop a new technique. Just be clear like I'm not saying the models won't be able to do this, it's just like so far they seem not to.