Look, Mom, I pressed a button!

Posted on September 5, 2026 by Persiflage

I have recently heard a few extraordinary opinions about how mathematicians should use AI. One I would paraphrase as “professional mathematicians should never use AI for any problem not in their narrowly defined (by whom?) research program”, which seems ridiculous — one great advantage of AI is that it allows us to precisely broaden our own research (and mathematics more generally). But that is not what this post is about. Generally, my plan on this blog is neither to make predictions about the future nor to make any ethical pronouncements about its usage, but rather to understand its implications for mathematics as a discipline. (I always remind myself that my one prediction about AI was that computers would never beat humans at chess, and I’m not that old!)

The question is:

Question: What is the value of a result obtained by someone pressing a button in a context where they themselves contribute no insight?

There are a number of subtle things that may count as insight, including which problems to ask in the first place. It seems pretty clear, however, that suitably interpreted, the answer to this question is “no value at all”. If someone else was interested in the question, they could press the same button.

If a result can be obtained on demand by anyone merely by pressing a button, and the particular person who obtains it supplies no insight, then the production and announcement of that result have no mathematical value. In particular, I’m not only saying that the button-presser deserves no credit (which is obvious). I’m talking about what counts as a valuable mathematical result once answers themselves become freely reproducible commodities. In that setting, the first person to print the machine’s answer has not added anything to mathematics. The proposition may be true, and knowing it may have consequences, and the argument may be interesting, but this particular result — the act of generating and circulating the answer — is mathematically of marginal value.

There are many people right now burning through tokens asking LLMs about famous or not-so-famous conjectures. One reason is pure intellectual curiosity or a desire to explore the limits and capabilities of these models; the opportunity for everyone^* to have access to such powerful models is amazing. But if the motivation is some sort of personal glory for having been the first person to “prove” or to “know” some particular fact, then this seems misplaced, to put it politely. If you don’t do anything besides press a button and you don’t understand what comes out or whether it is correct, what is the point? Even assuming it is 100% correct (and Lean-certified!), it still takes an expert to determine if the proof contains anything original or interesting to mathematics as a discipline.

The theorems we prove often serve as a proxy for what is more important, namely, the creation of new methods and new ideas. I am not saying that results are not important. I would like to know that \(\zeta(5)\) is irrational as well as knowing why it is irrational. But that knowledge is less important than some people seem to think. The problem of whether \(\zeta(5)\) is irrational is an obvious enough question to ask that the first person who “presses a button” and gets a proof seems more or less irrelevant if they added no intellectual content of their own. What AI obviously changes is that novelty of theorem statement no longer reliably signals novelty, competence, effort, or understanding.

What I have said so far seems to be somewhere between tautological and self-evident, but I was reminded of it in the past few weeks by being forwarded not one but three proofs that \(\zeta_5(3) \in \mathbf{Q}_5\) is irrational. Let me give a quick and selective history of this type of problem (omitting the work of many people):

In 2005, I proved that \(\zeta_2(3)\) and \(\zeta_3(3)\) were irrational, as well as \(L_2(2,\chi_{-4})\), the \(2\)-adic Catalan’s constant. The insight here was to understand how Fritz Beukers’ modular version of Apéry’s proof had a \(p\)-adic analogue, where the “overconvergence” which in the complex case was coming from the functional equation and Eichler integrals — which saw the period \(\zeta(3)\) — was replaced by \(p\)-adic overconvergence of (non)-classical Eisenstein series, which see the period \(\zeta_p(3)\).

My collaboration with Dimitrov and Tang (around 2020) more or less started when Vesselin discovered a holonomy bound (following André) and noted that it could be used (by using the same overconvergent template I had used in my paper) to show that \(\zeta_2(5)\) was irrational, something that was not possible using my original method. Using our later, more refined bounds, we included a proof of this result in our ICM paper.

In 2025, Lai, Sprang, and Zudilin independently proved that \(\zeta_2(5)\) was irrational. Their proof used a more direct Apéry-like construction.

So what, then, are my thoughts on these proofs that \(\zeta_5(3)\) is irrational? First, among the (proper subset of) proofs that are probably correct, they contain essentially no original ideas whatsoever — they are simply applying the best holonomy bounds from [CDT] to the template constructed in [C2005]. Who knows how many other people have pressed the same button to prove the same result! If these had been written up well by a graduate student, then to me their value would be “this graduate student has understood how to apply [CDT] correctly”, and such a paper could plausibly appear in a journal. If we want this to continue, we have to be very clear and conscious of what the other added value is beyond the result itself.

What was interesting about the irrationality of \(\zeta_2(5)\) was not only the result, per se, but the completely new method used to obtain it. At the same time, the proof by Lai-Sprang-Zudilin of the irrationality of \(\zeta_2(5)\) [A known result!] is much more interesting than these proofs that \(\zeta_5(3)\) is irrational [A new result!], because in the former case the argument required the construction of a new series of approximations related to higher-dimensional families of Calabi-Yaus rather than families of elliptic curves, and in the latter case, you just take the currently available arguments and apply them in the obvious way to the obvious constructions.

The proofs vary both in quality and in the extent to which the respective “authors” made the effort to ensure that the argument was correct. Two of the proofs seem more or less plausible, more or less the same, and more or less obvious. But I could hardly recommend that anyone spend time reading them, let alone reviewing either paper for a journal. They have no value. The third proof, however, is more amusing. It claims to prove that \(\zeta_2(2k+1)\) is irrational for a set of positive integers \(k\) of density one. That would be a more substantial result. The proof even passes, with caveats, an initial examination by ChatGPT 5.6. So now one feels compelled to make at least some effort to consider what is going on. What one quickly realizes is that the same argument would apply not only to the constant term of the \(2\)-adic Eisenstein series \(E_{-2k}(q)\), but would also “show” that (as \(k\) varies), for a positive proportion of positive integers \(k\), the constant terms of the Eisenstein series \(E_{-2k}(q) – E_{-2k}(q^2)\) are also irrational. That last result, if true, would indeed be impressive.

The last example is also interesting to consider on several levels: it’s bad for OpenAI because the cost of that computation is more than what they charged for it; it’s bad for the amateur who produced that proof because they are throwing away money to produce slop and also (potentially) suffering the embarrassment of proudly posting slop (though I have never found amateurs to worry much about that); it’s bad for me because I felt compelled to waste some time thinking about it; and it’s bad for anyone else who looks at the argument (whether they know anything about mathematics or not) because, well, it is AI slop. So this is a situation where everybody loses! I think that is far from a unique case right now.

I don’t think the implications of what I have said for amateurs are that interesting (though with ChatGPT 6 just released, the volume of button pressing is only going to increase.) What I think is more interesting is the implication for mathematicians and the results that they prove, whether they are using AI or not. But I shall return to this in a later post.

^* everyone who can afford it.

Posted in AI, Mathematics | Tagged , , , , , , , | 2 Comments

OpenAI, updated

Posted on August 23, 2026 by Persiflage

An update on this post, from my inside sources:

word on the math streets of SF is that the OpenAI team tried something like 500 problems to get their 10 solutions.

I don’t know how much of an insider this source is (or this sources sources, etc), but (allowing for the possibility of confirmation bias) this is within the expected range.

Posted in Mathematics | Tagged , , | 5 Comments

Google Alert!

Posted on August 20, 2026 by Persiflage

I have my google alert set for the phrase “Galois Representations”. Every six months or so it pops up with a suggestion, and I can’t quite work out what algorithm is using. Here was today’s breaking news: On the conductors of mod \(\ell\) Galois representations coming from modular forms.

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The inverse Galois challenge, part II

Posted on August 16, 2026 by Persiflage

This is a sequence to this post. The SAIR competition (Round I) has been completed! 98.4% of the possible signatures were obtained, with only 39 non-solvable cases missing.

Some thoughts.

First, my timing in the last post of dissing the problem of realizing \(M_{23}\) as a Galois group was not so great. It seems to me that the delightful paper does an excellent job of combining human and AI thoughts but also clearly and concisely explaining the ideas, especially distinguishing between what is known, what is clever, and what is lucky. Nicely done!

Moving on to the competition. I thought that it would be better to get a precise sense of the difficulty by trying it myself. The approach I used was purely to tell CODEX to do 6 obvious things, but not to either look at any literature myself, not to write any code, and just to come back and complain when it failed. This quickly produced around 40,000 pairs, but then stalled. One approach that wasn’t successful at all was as follows. There were around 80,000 pairs or so could be realized as coming from the Galois closure of degree 12 extensions of quadratic fields. But alas, my suggestions for how to construct these were not taken up sensibly, and I didn’t pursue it.

Certainly my personal explorations produced no meaning mathematical content at all. The only mathematical idea I had that was not completely obvious was one I learnt entirely from David Roberts. In situations where one has a Galois extension \(L/K/\mathbf{Q}\) where \(K\) has Galois group \(G\) and \(L\) has Galois group a central extension of \(G\) of degree \(2\), then one can write \(L\) as the splitting field of a polynomial of the form \(f(x^2)\) where \(f(x)\) has splitting field \(K\) and one root of \(f(x)\) generates a field \(E\). But now, given \(g(x)\) with \(E \simeq \mathbf{Q}[x]/g(x)\), how does one find \(f(x)\)? The observation is that one can often find \(f(x)\) by applying \(\texttt{polred}\) to \(g(x)\).

That said, having done some of these experiments, it did help me appreciate what type of problem this was. It certainly seemed to be the case that real skill and knowledge working with explicit polynomials and explicit Galois theory would be genuinely useful, and simply a purely theoretical knowledge of (say) the general solvable case is not sufficient. It is no surprise then that Klüners and Malle (the leading team) were so successful.

But where does it lead us? I don’t think the conclusion is so far from my original prediction. I think there might be a new second round coming, and after that is done, it really could be the case that the only pairs remaining are \((G,r)\) where \(G = \mathrm{PSL}_2(\mathbf{F}_{23})\) and also \(G = \mathrm{PGL}_2(\mathbf{F}_{23})\) with \(r=0\) (which are hard for the same reasons), and then possibly some cases of \(M_{24}\) (say with \(r=0\)) as well. We shall see!

Posted in Mathematics | Tagged , , , , , , , , , , , , | 2 Comments

Putting ChatGPT through its paces

Posted on August 11, 2026 by Persiflage

We are all aware of what ChatGPT can do. I think we would be better informed if we also learn what it cannot do (at least right now!). In order to better understand the current capability of the latest publicly available AI models, I decided to curate a set of problems and test how well ChatGPT (running 5.6 sol ultra) could do. While this certainly is not a scientific experiment, I had some rules I set for myself in advance:

  1. The problems should be, as far as I know, generally be open problems.
  2. I should have at least some original thought or idea on how to approach the problem which I can suggest to the model, however stupid it might be.
  3. I will limit myself to one ChatGPT pro subscription and the time between the ICM and the Emerton-Kisin conference (a bit under two weeks) to address all of these questions.

The strategy I employed was as follows. I gave ChatGPT one to two hours on each problem (ultra think in the chat window). If it made no progress at all, then I didn’t pursue the problem any further. If it did make progress, then I used codex on goal mode to push towards the problem, or at least towards some interesting intermediate goal, with a maximum run of two days.

The goal of this project is not to test the limits of what can be done by these models, but a much more practical test of how it might be to use these models as a working mathematician. If you take this experiment, scale up the amount of compute, and the amount of mathematicians giving (limited) direction to the machines, the result is (to my mind) broadly consistent with what OpenAI achieved, of course assuming that there were a significant number of problems on which they made no progress and then abandoned.

This quarter at Chicago I will be running a “ChatGPT seminar” precisely to explore these questions. The scope of that seminar will be somewhat broader than pure problem solving, and also include typesetting, coming up with interesting conjectures, and many other things. That said, it will certainly involve tests such as these.

So how well did it do? Let us see.

  1. Compute the slopes of all finite slope overconvergent modular forms with \(p=2\), level \(N=1\), and integral weight \(k\).

    2. This is a special case of the Ghost Conjecture of Bergdall and Pollack, which has now been solved by Liu-Truong-Xiao-Zhao (see also this post. Note, however, that that proof excludes this particular case when \(p=2\). I specifically pointed the model towards Conjecture 2 of this paper. In this very special case, the problem reduces to computing the Newton Polygon of a very explicit matrix where one can take \(k\) to be a non-negative integer. Our paper answer the case when \(k=0\). We also worked out the case \(k=-12\) and \(k=-72\) (the latter in part for proof of concept of the approach we were using).

    Level of interest: Kevin and I certainly spent some time trying to prove it! This special case probably now mostly of historical interest in light of more recent approaches.

    Level of difficulty: I would not be surprised if it could be solved by some elementary arguments.

    Result: No progress in the initial time period; not pursued. I was a little surprised, but with the time constraints this did not seem worth devoting extra time to this question. Time spent: about 90 minutes. I’m going to get on a plane in a few hours, I’m going to give it another go for 6 hours or so this evening, then update tomorrow if anything changes. (Update: my flight is delayed and I’m waiting at the airport, but I’m stopping it after looking what it has done so far.)

  2. Prove that there exists a constant \(N\) such that, if \(G\) is a finite group with \(H^i(G,\mathbf{Z})=0\) for \(i=1,2,\ldots,N\), then \(G\) is trivial.

    3. This perhaps the one problem I felt I had the least insight. I think I learnt it from a mathoverflow question in the long past (yes, I looked it up and found it here).

    Level of interest: Hard for me to say. One imagines this problem should be more or less a computation plus a literature search for the case of finite simple groups (assuming CFSG), and then it becomes some inductive problem which may or may not be about facts concerning the cohomology of almost simple groups. But this is not my area.

    Level of difficulty: I have no idea.

    Result: Partial progress. It knows enough to answer the case of finite simple groups, which is the first step in the obvious induction argument. It does cover quite a few non-trivial cases, but then gets bogged down, and comes up against what it calls difficult problems. Time spent: about 48 hours.

  3. Determine the slopes of all periodic billiard paths in the regular heptagon.

    An equivalent formulation is to take the \((2,7,\infty)\) triangle group and ask for a classification of its cusps in \(\mathbf{P}^1(K)\) where \(K = \mathbf{Q}(\zeta_7)^{+}\). This is a thin group inside \(\mathrm{SL}_2(\mathcal{O}_K)\). I heard about this problem from Curt McMullen, who also gave a possible answer (who he attributed to someone else, but since this was just a conversation I apologize that I did not remember at the time).

    Level of interest: I think if you answered this question then Curt would be impressed. What more could you ask for?

    Level of difficulty: One reason I considered this problem is that I had a sense that the answer should involve some mix of algebraic number theory and or Arakelov theory, and at the same time some complex analysis in the form of Hodge Theory. This could exactly be the type of situation where there might be a simple answer just by combining ideas from different fields.

    Result: ChatGPT had sloppy thoughts on this one! My first reading is that it did not have any crucial insights beyond fleshing out a little what I had suggested. It certainly diligently tried to push things as far as it could, but I think it is still missing a (or the) key idea. Time spent: around 48 hours.

  4. Let \(M\) and \(N\) be two finite volume hyperbolic \(3\)-manifolds with isomorphic pro-finite completions. Prove that \(M \simeq N\).

    5. I first learnt about this problem from Martin Bridson and Alan Reid in Ventotene in 2015. At the time, I had some idea about approaching this via the representation variety, but it was sufficiently far from things I knew that I didn’t pursue it.

    Level of interest: Definitely there are people interested in this problem.

    Level of difficulty: Too difficult for me to say, but it’s a well–known problem,
    and (as I learnt during this process) significant progress has been made over the past few years.

    Result: Claimed Solution. This perhaps might be the most interesting positive case. ChatGPT informed me of a recent paper of Liu in which he proved that, for closed hyperbolic \(3\)-manifolds, the profinite completion determined the volume modulo a conjecture about the injectivity of a certain regulator map. I suggested that one could bypass this using the mod-\(p\) Chern class maps discussed in Calegari-Garoufalidis-Zagier. With that, ChatGPT was very quickly able to write a \(5\)-page paper using Liu’s result giving an unconditional proof (in this class of manifolds) that volume was determined by the pro-finite completion. I think that this could have lead to a nice short note that I could reasonably post under my name with suitable AI assistance disclaimers. But then I learnt from Alan Reid and Martin Bridson (who I sent a draft to) that the full result had recently been proved by Xu! At this point, I “pressed another button” and asked ChatGPT to prove the full result, which it did. In particular, the notes below were produced completely independently from the work of Xu, now available here, but they were produced with knowledge that such a paper existed. This surely (?) would have influenced the strategy that ChatGPT decided to pursue. In fact, while there are similarities in the argument they are certainly not the same; After Xu’s paper was posted on the arXiV, I asked ChatGPT to compare the proofs, and it came up with the following: When it was first done, I asked ChatGPT to referee and revise its own work back and forth in until it claimed it was ready to be submitted. It modestly suggested that it should be submitted to the Annals of Mathematics. Now it is not the main point of this post, but obviously the question of how we evaluate work going forward is going to be an extremely important one. While the paper posted above does contain at least one idea of mine, I certainly do not intend to publish it, nor am I willing to take responsibility for its contents. Time spent: about 12 hours. Added: I was asked for my estimate of the chances that this proof is correct, and my response was “over 75% … Perhaps higher”.

  5. Let \(\Delta = \langle x,y | x^p, y^q, (xy)^r \rangle \) be a hyperbolic triangle group, and let \(B/K\) be the associated quaternion algebra over the invariant trace field. Let \(g(p,q,r)\) be the density of real places such that \(B\) is non-split. Prove that either \(g(p,q,r)=0\) or \(g(p,q,r) \ge 1/12\).

    6. Level of interest: This is a question of Curt McMullen raised in this paper.

    Level of difficulty: Note that in this paper here we prove that \(g(p,q,r)=0\) for precisely \(14\) explicit hyperbolic triangle groups, also answering a conjecture of Curt from that same paper. It was definitely clear to me during the writing of this paper that it could certainly be possible to prove this result. I actually started a project with University of Chicago undergrads towards it, but none of the people who signed up seemed actually willing to do any work so it petered out. The one difficulty that was certainly possible was that some eventual argument might be effective, but not effectively effective. Two improvements were needed from the previous paper; the first was to optimize the Fourier analysis aspect. The second one was to replace the Jacobsthal function argument which produced a single interesting conjugate to something more flexible that could produce a positive density of interesting conjugates.

    Result: Solved. Here ChatGPT did a number of things I expected, which was to choose a much more elaborate test function in the Fourier argument than we used, since it would obviously be much better handling much more complicated expressions. This was the first problem I asked, and for some time I actually was going to get ChatGPT to formalize the proof in Lean, which it felt completely capable of doing. But the time frame was going to be several weeks, and I didn’t want to waste the tokens. But this might possibly be worth doing. Time spent: about 6 hours.

  6. All the problems listed in my current NSF proposal draft.

    7. They are all ChatGPT hard, right now!

  7. Construct a new finite sporadic simple group not in the current classification.

    8. Level of interest: A lot. This sounds like a trolling question, but I do actually have one not entirely stupid idea, which should hopefully at least produce some interesting mathematics.

    Level of difficulty: Probably quite hard.

    Result: We are now 10 days into various computations that are making progress on something. But it didn’t come under budget, so I will talk about it later instead.

Posted in Mathematics | Tagged , , , , , , , , , , , , , | 5 Comments

Observations from the ICM, Part 1

Posted on August 7, 2026 by Persiflage

My recent post generated a surprising amount of personal emails defending of Philadelphia. I can happily report that, although I didn’t really get a chance to explore the city in any depth, it has at least one excellent cafe. “Thank You, Thank You” is one of the best cafes I have been to in the US; I wish there were something half as decent near Hyde Park. (Hat tip to Toby Gee for finding this in his research.)

Returning to the conference, Terry Tao made the point in his public talk — as others have made elsewhere — that, more than ever, we should insist on rewarding aspects of mathematics beyond simply proof, in particular good exposition, particularly of the deepest and most difficult ideas.

It was interesting, in this light, to see Dennis Gaitsgory’s plenary talk^*. The fundamental problem with the ICM is that there is a contradiction behind the entire concept of an invited talk, particularly a plenary talk. It is simultaneously supposed to be an honor for great work and an opportunity to communicate those ideas. On the one hand, there is no question that Dennis deserves the first honor. On the other hand, the talk was, shall we say, somewhat challenging for a mainstream mathematical audience. I don’t blame Dennis; he has his style of giving talks^**, and this one went more or less exactly as anticipated. But it seems to me that a very simple solution would have been to have asked David Ben-Zvi to talk about the work of Dennis (and his collaborators). I hope for the next ICM the struture committee will consider more radical changes than what they have done so far. Would inviting someone to talk on the work of X be any less of an honour for X than asking X to talk? If they did that with *every* plenary talk, and at the same time made an effort to choose the right speakers (who could even collaborate with X), I think that would be a great improvement.

As the community moves ever so slightly towards demanding better exposition, it is interesting to look back on the Mochizuki circus. If we are going to be honest now, we should also be honest about the past. “Inter-universal Teichmüller theory” is nonsense, and that was more or less obvious to everyone at the time I wrote that post (which was five years after the announcement). The saving grace of those papers is that they were written in “Mochislop,” an almost comically embarrassing STYLE that screams “I am a crackpot.” Were it not for Mochizuki’s reputation, they would have been immediately dismissed. I am glad that, at the time, there were people (Scholze and Stix) willing to donate their time in a heroic effort to actually engage with the mathematics. In today’s world of AI slop, I think people would feel more comfortable not even bothering, and this is a good thing.

^*: The reason I single Dennis out here is not because his talk was in any way particularly exceptional compared to some other plenary talks, but simply because I know him well enough to be able to criticize his talk and feel confident that he will be OK.

^**: A student onced asked Dennis whether, given two correspondences \(X \leftarrow Z \rightarrow Y\) and \(Y \leftarrow W \rightarrow X\), if the fixed point groupoids of \(W \circ Z\) and \(Z \circ W\) are canonically equivalent. Dennis immediately gave the correct answer and said the proof was simple. The student replies “amazing! Most people end up struggling through the technical aspects of \((2,\infty)\)-categories”. Dennis replied “is there any another way?”. OK, well this might not have happened.

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Look at everything that OpenAI failed to prove!

Posted on August 2, 2026 by Persiflage

I was heartened to see a recent list of results proved by OpenAI here. Heartened because we are now clearly in an age in which AI can truly contribute to serious research mathematics. But also heartened because one can only imagine how many thousand of open problems OpenAI tried and failed to solve, assuming these are the ones they consider the most impressive. It would be vastly more informative to see the list of problems they tried to solve and didn’t, as well as possible partial progress that was made on other problems.

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Xena on Counterexamples

Posted on July 22, 2026 by Persiflage

There is an interesting post here on Xena’s blog.

I don’t centre “proof” in mathematics to anywhere near the extent that Kevin does, but I think emphasizing that distinction obscures the fact that our opinions about mathematics, mathematicians, and, I suspect, AI are quite similar.

It is fascinating to observe the progress of AI in mathematics (other people might use different adjectives). The result that a finite group scheme of order \(n\) need not be annihilated by \(n\) is the first AI-assisted result that I actually “care about.” I most closely associate this problem with a remark Hendrik Lenstra (the human equivalent of an LLM in the 90s) once made to me in the elevators of Evans Hall: namely, that there is a weaker result asserting that every finite flat group scheme \(G\) of order \(n\) is annihilated by \(n^{c(n)}\), for some integer \(c(n)\) independent of \(G\). The point is that there is, in an appropriate sense, a universal family of group schemes of order \(n\) over a finite-type base \(S\), where \(S\) is more or less the parameter space required to write down all the necessary Hopf-algebra data.

I absolutely agree with Kevin’s reaction to reading LLM-generated mathematics. Reading mathematics is already extremely hard; we are used to the fact that we might have to spend weeks understanding a few lines in a difficult paper. But what gives us the spirit to persevere is that we have been trained to give the author the benefit of the doubt: it is we who are missing the idea, and if only we think a little more about it, we will work it out. For better or worse, this is a cultural truth of mathematics. Once that is taken away (and it absolutely should be, for now, when reading LLM-generated mathematics) it becomes almost impossible to read mathematics. If there is one thing that LLMs have mastered, it is writing with the confidence and airs of someone possessing great authority.

Low-Hanging Fruit:

Some people have dismissed the recent AI-assisted breakthroughs because they were “obvious in retrospect” or because “not enough people tried to do them.” The first criticism seems clearly ridiculous, since “obvious in retrospect” is very far from “obvious.”

The second criticism reflects, in part, the way humans solve conjectures. In my experience, the process goes as follows. First, you learn about the conjecture and why it might be interesting. Second, you learn a little about why it is hard. You might think about it for a while and fail, and then file it away in the back of your mind. Later, when you encounter new ideas, you perform some pattern recognition and ask whether those ideas have any relation to previous problems you care about. If you are lucky, you “see a connection,” and then you can begin. Sometimes the first inspirational connection is most of the work; sometimes it is only the beginning, and there is much more work to do. In either case, that initial step is crucial.

An LLM, on the other hand (to anthropomorphize), can conduct an extremely thorough literature search and then throw a thousand different ideas at the problem to see whether anything sticks. If one of those ideas does seem relevant, and if the journey from that realization to the end of the proof is not a long one, then the LLM can solve the entire problem. As it becomes possible to chain together longer and longer stretches of reasoning, the only problems that can resist attack are those requiring a genuinely new idea (whatever that means).

Finally, there is the observation that these results are all counterexamples to conjectures that, as far as I know, were generally regarded as true. This phenomenon has a clear diagnosis, given by Deligne: “All problems in mathematics are psychological.” Well, to be precise, that quote was ascribed to Deligne* by Kisin in a lecture at Luminy, but it captures the essence of something clearly true. And the good news is that AI is an insane psychofreak with no hangups.

Addressing the more interesting—and controversial—question of what we, as a profession, are to do about all of this will have to wait until later. This week, I will be attending my first ICM in person. It is a much-maligned conference whose most exciting moment has already been blown by incompetent website design and which is being held in a city with slightly less appeal to me personally than St. Petersburg; but we shall see!

* Since I always check the original source, here is a slightly more nuanced version of that quote:


Dear Calegari,

I don’t remember the exact words, but I expect it is roughly accurate. Of course, it is not always true. The meaning was that we often have blocks which prevent us from seeing things which later will seem obvious to us.

Best,
Pierre Deligne

Posted in Mathematics | Tagged , , , , , , , , , , | 3 Comments

The inverse Galois challenge

Posted on June 19, 2026 by Persiflage

I learnt a few days ago about the following AI challenge: find polynomials with Galois group \(G\) for each of the transitive subgroups of \(S_{24}\), with each of the possible signatures \((r_1,r_2)\) with \(r_1 + 2r_2 = 24\) where \(r_1\) is the number of fixed points for some (possibly trivial) involution \(c \in G\). (See the remark at the end about the formulation of this problem.)

I first heard about it at afternoon tea at SMRI. I had an interesting discussion (with Raymond van Bommel and others) on the merits of such a challenge. I was a bit confused to be honest. It seems as though the challenge has been “gamified” to some extent by awarding \(1\) point for each possible group and signature (with some additional points for small discriminants). The scoring system seems peculiar to me as well. I was challenged to commit to paper my thoughts on what the result would be, what examples I imagined were challenging and what would be easy.

The problem itself breaks up naturally into two subproblems: existence and construction. Now these are certainly different problems, and while the former is more interesting to me, the second can certainly also be challenging even when one has a positive answer to the first question. But that is also colouring my response here.

The case of solvable groups is more or less trivial and not so interesting. Certainly
existence is known, and the existence proof is more or less constructive, although there
is (potentially) going to be some issue of computational feasibility. That’s the aspect
of the problem on which I am the least informed. But I certainly don’t think the solvable
case is that interesting here from a theoretical point of view, unless one takes into account the additional problem of finding fields with small discriminants. From a computational point of view, I think one of the issues is identifying the most practical way of choosing the filtration of \(G\) in order to constructively set up the most efficient algorithm. As an example of what I mean, the efficient way to construct \(S_4\)-extensions is not to start with a quadratic extension! Of course, from a computational point of view, even constructing cyclic extensions of sufficiently high degree explicitly (say with some Galois structure to avoid trivialities with cyclotomic extensions) which might theoretically be trivial using class field theory becomes quite tricky, and Henri Cohen has written books about how to do this sort of thing. Perhaps these sort of questions are more to the heart of what this challenge is about. Another type of problem is to construct the \(S_n\) extension of \(\mathbf{Q}\) with smallest discriminant; obviously this is a much more subtle computational question than constructing a single example! Since John Jones (half of the team behind the database of local fields and the database of global fields now folded into the LMFDB) is one of the people behind this challenge this may indeed be more the spirit of this problem. That starts to touch on problems of Malle’s conjecture in very small ranges of discriminants which is definitely interesting, and certainly this blog post addresses quite different aspects of the problem related purely to the vanilla inverse Galois problem.

There are 25,000 transitive subgroups; 24193 are solvable and 807 are not.
In the remaining cases, you can bucket the groups by their (simple) composition
factors to get the following:

Non-solvable buckets by non-abelian composition factors:
{A_12}: 8
{A_12, A_12}: 4
{A_24}: 2
{A_5}: 267
{A_5, A_5}: 55
{A_5, A_5, A_5, A_5}: 45
{A_6}: 204
{A_6, A_6}: 64
{A_6, A_6, A_6, A_6}: 45
{A_8}: 20
{A_8, A_8, A_8}: 10
{LieA(1,11)}: 10
{LieA(1,11), LieA(1,11)}: 4
{LieA(1,23)}: 2
{LieA(1,7)}: 44
{LieA(1,7), LieA(1,7), LieA(1,7)}: 12
{M_11}: 3
{M_11, M_11}: 1
{M_12}: 5
{M_12, M_12}: 1
{M_24}: 1

While there may be subtleties, the examples involving \(A_n\) do not strike me as ones which would theoretically present that much difficulty. The general shape of these groups is presumably going to be something like \(A \subset H \subset G\), where \(\Gamma = H/A\) is the (direct product) of the non-simple groups in the bucket, and \(A\) and \(G/H\) will be solvable and quite small. So you are constructing \(\Gamma\) extensions over some small solvable field \(K\) with compatible \(\mathrm{Gal}(K/\mathbf{Q})\) action in a way that one can then solve some central extension problems, which is going to be a question of ensuring that the ramification in your \(\Gamma\) extensions is liftable. When you have an easy source of such \(\Gamma\) extensions, say when \(\Gamma = A_n\), this seems very manageable. When \(\Gamma\) is a product of some \(A_n\) then it is probably actually coming from \(A_n \wr C\) for some small group \(C\) which is equally easy.

That leaves the 83 remaining groups.

The group that first came to mind immediately upon hearing about this challenge as something that would be difficult was a totally real extension with Galois group \(G = \mathrm{PSL}_2(\mathbf{F}_{23})\). If I was to put money on one pair (group and involution) which would still be missing after this project, then this would be one. Moreover, I don’t really see how having every single other possible pair in the table computed would be helpful in understanding this last case. For example, if you choose the other conjugacy class in this case, even the computational problem is reduced to finding explicit Galois representations coming from mod \(p\) representations of modular forms.

Apparently the case of \(M_{23}\) as an explicit Galois group has been touted as a possible “super hard” problem for AIs to work on. I’m not super excited by this problem, since there are a number of places one could look and then randomly get lucky; my version of this problem would be \(\mathrm{SL}_2(\mathbf{F}_p)\) for all primes \(p\) (the case \(p=23\) related to the example above). The advantage of this example is that one clearly cannot “accidentally” find a solution for all \(p\) at once. (I’ve mentioned this example before at this blog.)

As for other difficult cases, it’s possible that some of the cases related to \(\mathrm{PSL}_2(\mathbf{F}_{11})\) could cause similar issues with difficult choices of involution. My impression is that one knows that \(M_{24}\) occurs as a regular extension, but I’m not sure which involutions one sees over this family, and that could also cause issues (e.g. my guess might be that the rigidity method produces/forces a particular choice of \(c\)).

Remark: Actually I’m not sure if the challenge requires one to find all pairs \((G,c)\) where \(c\) is a conjugacy class of involutions (which would be the most sensible choice) or all \(G\) with a possible pair \((r_1,r_2)\); while the former determines the latter the converse is not true.

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The moral panic over AI

Posted on May 26, 2026 by Persiflage

A number of journals appear to have frothed themselves into a moral panic over AI. There is certainly a lot of AI-generated crap appearing in multiple places, and the arXiv moderators are no doubt playing whack-a-mole trying to keep it down. On the other hand, other aspects of the profession continue on, unchanged.

I submitted a paper in January 2025 to TAMS. A number of my papers are long and technical, and I am not surprised that they take a long time to review. This paper, however, is both short and elementary. So it was somewhat surprising to me that it took over 16 months to receive a referee report. Out of curiosity, I also asked ChatGPT to produce a referee report. That took 30 minutes, and produced a far more substantial report than the one I had received. In addition to all of the more or less cosmetic issues addressed by the (presumably) human referee, ChatGPT also found non-trivial mathematical points that required addressing.

The most interesting correction, in my mind, was the following. At one point, we considered a lattice \(\Phi\) of rank \(d\) and chose successive minimal vectors \(\mathbf{v}_1, \ldots, \mathbf{v}_d\); that is, \(\mathbf{v}_1\) is a nonzero vector of shortest length, \(\mathbf{v}_2\) is a vector of shortest length not in the span of \(\mathbf{v}_1\), and so on. Then something happened in the paper which could be taken straight out of Serre’s talk on how “not to do mathematics”. Specifically, at some point it was assumed that these vectors generated the lattice \(\Phi\), but this was never stated. Instead; a claim was subsequently made that depended on this fact implicitly. The great thing about never mentioning something that you use is that you don’t have to prove it either, and in this case, when you are forced to actually think about it, it is easy to see that it is false! For example, \(\Phi\) could be the lattice \(\mathbf{Z}^n\) together with the vector \((1/2,1/2,\ldots,1/2)\). Such arguments are exactly a good way to slip something past a reviewer. To compound the issue, this was part of a section giving an alternate argument and was not used elsewhere in the paper. So the referee completely missed it, but ChatGPT did not.

As far as I understand the policy of TAMS, it would have been against the rules for the reviewer even to ask ChatGPT to look at the paper, let alone ask it to generate the report. But at least in this case — and I do stress this particular case — it would have been not only more time efficient by a factor of over 20,000, but also much more accurate and precise. I believe that literally the only comment made by the referee that was not made by ChatGPT was the recommendation to use the construction: Let \(k\) be an integer satisfying \((k,n)=1\) over the alternate Let \((k,n)=1\) be an integer.

There are many things in our profession which work quite well, and which AI threatens to make, if it hasn’t already, significantly worse. But there are many things in mathematics that are clearly broken as well. We should at the very least take the changes that will be forced on our profession by AI as a chance to finally address some of these lingering issues, many of which relate to what we publish and how we publish it, head on.

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