For the sake of anyone who might read this blog post in the distant future (a month from now, say), let me mention that I am writing it a few days after OpenAI announced that it had solved ten major problems in mathematics and theoretical computer science, including the first construction of a non-sofic group, and a proof that the multicolour Ramsey number (where there are 3’s) grows superexponentially in . The first was, to judge from various talks I have been to, one of the most important unsolved problems in group theory, and the second was a major open problem in Ramsey theory that I didn’t necessarily expect to see solved in my lifetime, though of course such expectations now have to be revised. The reason I want to be clear about the timing is that I shall be discussing the current capabilities of LLMs in the full expectation that those will continue to change rapidly. So it is likely that in not too long from now, if there is anything interesting in what I write, it will be interesting mainly as a record of what the situation looked like in early August 2026.

These results, and the other eight on the list, are extraordinarily impressive, but it still doesn’t seem to be the case that LLMs are better than all humans at all aspects of mathematics. If they were, then their big speed advantage over us would mean that there would be much more of a flood of results. So it is natural to wonder about what kinds of problems LLMs are good at, and about where there is still room for improvement. I don’t pretend to have a good answer to this question, where a good answer would be a crisp classification that would fit the current examples well, but it is an interesting exercise to try to rule out some bad answers, and to try to identify potential answers that aren’t obviously contradicted by the evidence.

Are LLMs particularly good at finding counterexamples?

A first remark here is that LLMs are not just good at finding counterexamples: they can find proofs of difficult statements as well. However, it is notable that the most famous problems they have solved have almost all been with counterexamples rather than proofs. That is true of the two problems mentioned above, and also of the Jacobian conjecture and the unit distance conjecture.

If one wants to theorize that LLMs are particularly good at finding counterexamples, then there are two things it would be good to do to make the theory more convincing. The first may sound unproblematic: it is to decide when solving a problem counts as finding a counterexample. Once that is sorted out, the second is to come up with a potential explanation of why LLMs would be particularly well suited to solving problems of that particular kind.

What does it mean to find a counterexample?

Why am I suggesting that it is not completely obvious what it means to find a counterexample? Surely, one might suggest, all it means is that you have a statement of the form “Every object of such and such a type has such and such a property,” and you exhibit an object of the given type that does not have the given property.

However, this doesn’t always work. Consider a famous result of Vinogradov, which states that every sufficiently large positive integer is a sum of three primes. The negation of this statement is (or is equivalent to) the statement that for every positive integer there exists an integer such that is not a sum of three primes. In other words, it states that every positive integer has a certain property. Seen in this light, Vinogradov found an example of a positive integer that does not have the given property. Do we want to say that Vinogradov found a counterexample? Clearly not — the result should obviously be classified as a theorem and not a counterexample.

Thus, we cannot just naively say that LLMs are particularly good at negating universally quantified statements: there has to be something about the nature of the universal quantification. With the three-primes example, it is clear that Vinogradov did not think, “How am I going to find with this property?” Rather, what he thought would have been more like, “I’ve got an integer that is very large. How am I going to show that it is a sum of three primes?” In other words, all his focus would have been on the universally quantified , with the existentially quantified being a sort of afterthought once the details of the proof have been worked out.

In general, many interesting results, when they are stated formally, begin with an alternation of two or three (or more) quantifiers. The question then becomes to determine which is the first “interesting” quantified variable in some sense. Here’s another example to illustrate the point, from the theory of finite-dimensional normed spaces. I’ll give a few mathematical details for those curious, but if you don’t care about those, then you can skip the next three paragraphs and should get the gist of what I am saying about this example.

Let and be two -dimensional normed spaces and let be a linear map from to . We say that is a –isomorphism if there exists such that for every . By rescaling we can always take to be 1, in which case we have that for every . If , then this tells us that is an isometry. In general, the Banach-Mazur distance between and is defined to be the smallest such that there exists a -isomorphism from to . It is easy to see that the logarithm of the Banach-Mazur distance is a metric on the set of isometry classes of -dimensional normed spaces. A less easy fact, but still not too hard, is that the resulting metric space is compact: in fact, it is known as the Banach-Mazur compactum.

It is natural to wonder what the diameter of the Banach-Mazur compactum is, and here things get interesting. A result of Fritz John states that every -dimensional space has distance at most from . (The idea of the proof is as follows: pick inside the unit ball of an -dimensional ellipsoid of maximal volume; that is the unit ball of a normed space that is isometric to ; it can be shown that the identity map is a -isomorphism between and .) From Fritz John’s theorem and the (multiplicative) triangle inequality, it follows that for any two -dimensional normed spaces. That is, the diameter of the Banach-Mazur compactum is at most . But might it be substantially less than that?

An indication that the answer is not obvious comes from looking at the spaces and . The identity map between these two spaces is an -isomorphism, but one can do much better by mapping the standard basis vectors not to themselves but to vertices of the unit cube, with the vertices chosen to be as orthogonal as possible. In particular, if there exists an Hadamard matrix, then the corresponding linear map is a -isomorphism. One can push this observation and deduce that for any the Banach-Mazur distance between and is . It is also easy to show that , so -spaces hardly improve on the easy lower bound, and do not improve on it at all in dimensions for which an Hadamard matrix exists.

In 1981, Gluskin famously solved the problem by determining the correct asymptotics for the diameter of the Banach-Mazur compactum. Informally, what he showed was that the diameter is within a constant of the upper bound that follows immediately from Fritz John’s theorem. If we make the quantification explicit, then the statement we end up with is

,

where I have written for the set of all -dimensional normed spaces. (If you want to argue that it is not a set, then let me specify in addition that the underlying vector space is .) In words, there is a positive constant such that for every positive integer there are -dimensional normed spaces and such that the Banach-Mazur distance between and is at least .

I can’t continue without very briefly describing the beautiful and highly influential idea Gluskin had for solving this problem. He took and to be normed spaces whose unit balls were random symmetric convex sets defined as follows: take the standard basis vectors and a handful of other random unit vectors, as well as the negatives of all these vectors, and take the convex hull. Gluskin then showed that if two normed spaces are chosen from this distribution, then with high probability their Banach-Mazur distance is at least .

But back to the main point, which is that the logical form of the above statement is very similar to the logical form of Vinogradov’s theorem, which is

where I have written for the set of primes. And yet, Vinogradov’s result is unquestionably a theorem, while Gluskin’s result is unquestionably a counterexample, or at least an example.

What is the important difference between the two statements? It seems to be that in Vinogradov’s three-primes theorem the number plays a more essential role in the statement that is to be proved about the various quantified variables. In Vinogradov’s theorem, that statement is , whereas for Gluskin’s theorem the statement to be proved is

and ,

which we can write equivalently as

and .

In the case of Vinogradov’s theorem, the whole challenge is to get those three primes to add up to , whereas for Gluskin it is not remotely challenging to get the dimensions of and to equal : the challenge is to get and to be very far from each other, relative to their common dimension.

There is a further complication to bear in mind here, which is that via the process known as Skolemization, a universally quantified statement of the form can be converted into an existentially quantifed statement . (For this to be an equivalence one needs the axiom of choice, but it is certainly a sufficient condition.) This is not just a piece of logical trickery, but it often reflects quite accurately how we think about some problems. For instance, it is more natural to think of Gluskin’s example as a recipe for constructing (or at least proving the existence of) a pair of suitable normed spaces for any given dimension , or in other words to construct a suitable function from to pairs of normed spaces by giving its value at each , than it is to think of it as a statement that says that every positive integer has a certain complicated property.

Yet another complication is that some universally quantified statements follow naturally from existentially quantified statements, or may even be equivalent to them. For example, the theorem that a 2-dimensional torus is not homeomorphic to a 2-dimensional sphere is a universally quantified statement (every map from the torus to the sphere fails to be a homeomorphism), but the natural way to prove it is to prove the existential statement that there is an invariant that distinguishes the two spaces. For an example of where a universal statement is equivalent to an existential statement, consider a statement of the form that a vector does not belong to the convex hull of a certain compact set . The statement that no convex combination of elements of is equal to is equivalent to the existence of a linear functional and a such that and for every . In both these cases it feels natural to regard the result as a theorem that is proved via an existential statement, perhaps because it is the theorem that is ultimately what interests us. But using “what interests us” as a criterion to determine what counts as a counterexample seems a little vague, and is a difficult criterion to use if we want to explain convincingly why AI should be good at finding counterexamples.

A more general argument against the notion that there is something about existential statements that is particularly suited to AI is that the need to establish existential statements pervades almost all of mathematical research, regardless of the nature of the headline result being aimed for. For example, if I want to prove a statement by induction, I may well look for a strengthening of the statement that serves better as an inductive hypothesis. Or if I want to prove that every object of type with property also has property , then I may well look for a property that follows from and can be used to prove . These are more metamathematical existence problems, but the distinction can be somewhat blurred, and more importantly, when trying to prove a statement , it is often the case that the main question in our minds is less, “Why is true?” and more, “What could a proof of be like?” To give an example, I feel I understand pretty well why Goldbach’s conjecture is true — a highly plausible probabilistic model of the primes implies it and agrees closely with computational data — but if I were making a serious attempt to prove it, that understanding, which many mathematicians have had for a century or so, would be of limited help. Rather, my main task would be to try to find proof techniques that were powerful enough to make those heuristic ideas rigorous.

What is the difference between an example and a counterexample?

Logically, every statement of the form is a counterexample to the universally quantified statement . However, we do not describe all existential statements as counterexamples. For example, if I were to say, “The -spaces with are all separable, as is , but is not separable,” I would not describe the second part of that assertion as a counterexample to the claim that all Banach spaces are separable. Rather, I would present it as probably the most basic example of a non-separable space. The important point seems to be that there was no particular reason to think that all Banach spaces would be separable, and finding an example of a non-separable space is not very difficult.

I think the first point is more important here: we are more inclined to call an object a counterexample if the existence of that object disproves a statement that we had quite good reason to believe. It often happens that after repeated unsuccessful attempts to prove a statement, mathematicians begin to feel that it has no particular reason to be true, even if it seems to be hard to come up with a counterexample to it. In such a situation, if a counterexample is eventually found, it may have lost something of its “counter” feel. My impression is that the construction of a non-sofic group comes into this category. There have been several proposals in the literature for how one might construct such a group, and I don’t think there were many (or even any?) experts who strongly believed that all groups were sofic. So it feels more natural to say, “OpenAI came up with the first example of a non-sofic group” than to say, “OpenAI found a counterexample to the soficity conjecture” (despite the fact that that section of their paper is entitled “A counterexample to the soficity conjecture”).

Likewise, it seems to me that the new lower bound for multicolour Ramsey numbers is more of an example than a counterexample. I think quite a lot of people believed that the bound should be exponential, so for them it was a counterexample, but others, myself included, were more neutral about it. As a matter of fact, I have worked on the problem in the past (a long time ago) in an equivalent formulation, which asks how many triangle-free graphs on vertices you need if you want their union to be the complete graph . If you take bipartite graphs, then it’s easy to see that you need of them, but that bound can be improved if instead you observe that a complete 5-partite graph can be written as a union of two triangle-free subgraphs, and therefore it is possible to write the complete graph as a union of triangle-free graphs. It is then tempting to try to do better, with triangle-free graphs that are less dense but that make up for it with unbounded chromatic number — a necessary condition if one wishes to use a sublogarithmic number of graphs, which is equivalent to showing a superexponential lower bound for . All this is to say that when I worked on the problem, my efforts were concentrated on what turned out to be the right direction, so for me OpenAI found an example of what I (weakly) expected, rather than a counterexample.

Where does this leave us?

I would like to find a coherent explanation of the conjunction of the following facts.

1. The most notable mathematical results proved by LLMs have tended to be ones that we would classify as examples or counterexamples, where counterexamples are, broadly speaking, existence statements that disprove statements that we expected to be true.
2. Many statements can be formulated as existence statements when we would usually think of them as universal statements, and vice versa, so what we consider to be an example depends on the mathematical context of a statement as well as its logical form.
3. LLMs are pretty good at proving universal statements as well: it’s just that the strongest statements they have proved that we would think of as theorems have mainly not been at the level of the strongest statements that we would think of as counterexamples.

Given these facts, it seems likely that what LLMs are good at is something else, which happens to have as a consequence that they are good at the kind of existence problem that we would normally classify as asking to find a non-trivial example.

Let us consider two things that we can be confident that LLMs are good at. One of them is knowing a lot of mathematics: if a problem can be solved by means of a relatively standard argument, it is highly likely that an LLM will be able to find and use that argument. The other is the ability that an LLM has simply by virtue of being a computer: it can work at huge speed (compared with humans at least) and can therefore afford to make a large number of unsuccessful attempts at a problem before it finds a solution.

Without even looking at what LLMs have actually managed to solve, one might guess that these two features would lead to their having a somewhat different style from human mathematicians. Very roughly, LLMs would have the edge when there is more of a probabilistic element to the proof-finding process: they would be good at problems for which the best method is to try a lot of ideas, not necessarily particularly novel, until at some point you get lucky. Humans on the other hand would be better (for the moment) at finding more “surprising” and “conceptual” arguments, where the appropriate method is to dig deeper and deeper into a problem until the solution reveals itself. (It is hard to say exactly what this means, but I hope that any experienced researcher reading this will know what I am talking about.)

This raises two questions: does the guess above correspond at all to the reality that we are observing, and is there any reason to suppose that what I have tentatively described as the “LLM style” of doing mathematics would lead naturally to LLMs discovering several counterexamples (or just examples) to long-standing conjectures, even if that was by no means all they could do?

I don’t pretend to have a scientific answer to either question, but the reactions of experts to several of the remarkable solutions that ChatGPT has found do lend some support to the idea that LLMs work in more of a try-lots-of-things-till-you-get-lucky way. People often seem to react by saying something like, “Initially I was amazed that the problem had been solved, but on closer inspection I realized that the approach was actually not all that novel, and one that with the right small hint a suitably expert human could have found quite easily.”

For the second question — whether the LLM style is well suited to finding (counter)examples — I think matters are less clear, because there are many ways of searching for a counterexample, and some of them fit better than others the style I have described. Here are a few general methods. (I don’t claim that the list is exhaustive.)

1. Look for an off-the-shelf example. Here one has a stock of fairly standard examples and one simply tries them out one after another to see whether any of them fails to satisfy the given statement. For example, Ryan O’Donnell ends his wonderful book on the analysis of Boolean functions with some tips, one of which is, “If you have a conjecture about Boolean functions, test it on dictators, majority, parity, tribes (and maybe recursive majority of 3). If it’s true for these functions, it’s probably true.”
2. Build an example from basic examples and standard construction methods. For an algebraic problem, for instance, one might start with some standard examples, but then take products or quotients or limits.
3. Make heavy use of metavariables. The word “metavariable” comes from computer science, and in particular from automatic theorem proving, and refers to the practice that in mathematics would correspond to writing, “where is to be chosen later,” (in which case is the metavariable). In a paper we usually do this only in fairly simple situations such as when we need to choose a number that is small enough for later arguments to work. But when we search for an example of an object that satisfies some property (which may well be a conjunction of simpler properties ), it is often not a good strategy to specify completely and only then to check whether it satisfies . Instead, it can be more fruitful to do almost the opposite: we start by saying virtually nothing about and simply launch into proving that it satisfies . In the course of doing so, we find that we need to satisfy a property . If we are lucky we can describe in a nice way a very general class of objects that satisfy . For instance, we may be able to find a parametrized class: we identify some function and show that satisfies for every of a certain type. The problem is then reduced to finding such that $Q(f(y))$ holds, which is a more specific version of the original problem. There may be many iterations of this process, or a mixture of this process and other processes, before an example is eventually found.
4. Try to prove the opposite. If one wishes to find such that , it can be surprisingly helpful to start by attempting to prove the statement . The reason this can be helpful is that using our standard methods of attempting to prove something, we may end up identifying a key lemma that would suffice: that is, we may find an intermediate property that implies in a non-trivial way and thus reduce the problem to . Turning things round again, it may well then be that finding a counterexample to is easier than finding a counterexample to (that is, an example that satisfies ). Of course, there is no guarantee that a counterexample to will be an example of , but sometimes we are lucky and it is. More often, we can use the idea of the previous method, noting that it is at least a necessary condition of an example of that it should not be an example of , so one can try to describe a general class of objects that fail and in that way reduce the problem.
5. Successive approximation. Sometimes, when we are searching for an example of such that , we write down a moderately plausible guess not because we think it has a chance of working (if we did, then we would be using the first strategy), but because we hope that if does not satisfy , then we will be able to diagnose what went wrong and specify a new guess that does not have that defect. Again, this strategy can either be iterated or combined with one or more of the other strategies.
6. Just-do-it proofs. Sometimes we need to satisfy infinitely many properties , each of which is, individually, quite easy to satisfy. In such situations, we often “build” inductively bit by bit, ensuring at the th stage of the process that however the building process continues, will satisfy .
7. Pick a random example. Often it is very hard to give an explicit example of an that satisfies , but there is a natural probability distribution for which one can show that if one chooses randomly from that distribution, then with high probability (or at least non-zero probability) it will satisfy .
8. Pick a generic example. In more infinite contexts, it may again be quite hard to give an explicit example of an that satisfies , but one may be able to show that the set of that fail is or measure zero, or is a meagre set, or is small in some other way.

There is no particular reason to suppose that LLMs would be equally good at each of the methods above. So perhaps what we are observing is not quite that LLMs have a particular ability to find examples, but more that they are particularly good at finding examples (and proofs) in a certain way. Looking at the above techniques, one might imagine that they would be very well suited to checking off-the-shelf examples, finding just-do-it proofs (since that is a rather standard method with lots of instances in their training data), using the probabilistic method (unless, as often happens, significant new ideas are needed to show that the probabilities work out), and picking generic examples. The other three methods described above — use of metavariables, trying to prove the opposite, and using successive approximation — require more of an ability to judge whether the approach one is taking is likely to be fruitful. Here it seems at least possible that humans will sometimes have an advantage, but the conditions that a problem would need to satisfy are quite stringent. One would need an example to be one that lies at a leaf of a very large search tree — too large to be searched for by a combination of moderate mathematical ability and brute force — but that can be found by a mathematician with a sufficiently good nose for when they are making progress that they can prune the search tree very substantially.

Why wouldn’t LLMs also have that “nose”? I don’t rule out that “nose” is an emergent property of the way LLMs are trained, and that within a year or two they will have it to the same extent that we have it. But for now, in my interactions with ChatGPT, I do have a distinct impression that they haven’t got there quite yet. When I discuss an open problem with 5.6 Pro, I am often presented with approaches that sound promising until I think about them carefully, and then seem quite a lot less promising. And they will also often end a response by saying, “I have not managed to answer the question you asked, but have managed to reduce it to the following much narrower and more precise question,” which sounds very promising until it has happened five times without any obvious progress having been made. It isn’t completely obvious how they will get better at this, since their training data will not be full of examples of fruitful and less fruitful directions to pursue when trying to solve problems: all they will typically see is tidied up proofs that hide the thought processes of their discoverers. Of course, human mathematicians also don’t get to learn much about how to do research from the experience of other mathematicians, and yet we somehow manage to pick it up. But the situation is a little different for us, in that a lot of what we learn is by doing rather than emulating.

Another reason it is not obvious that “nose” is a property that emerges naturally when LLMs are scaled up is that if LLMs make heavy use of their broad knowledge and can afford to do a lot more brute-force search than humans can, then they will lack the incentive that humans have to prune the search tree ruthlessly. It could conceivably be that their successes so far are achieved using methods that for a human would be considered extremely inefficient, but that because of their superior speed and knowledge, the combinatorial explosion these methods will lead to has not yet become apparent.

It would be very interesting to try to test this experimentally, but it is also difficult, because if an LLM has what looks like the kind of idea that could only be the result of “deep thought” about a problem, we can never be sure that it has actually carried out that deep thought, as opposed to finding a model argument already in the literature, or in other words exploiting the deep thought of a human mathematician. It would probably be easier (but still not easy) to test it by using models that are less powerful than the latest ones and that have been to some extent shielded from the mathematical literature: one could give them a carefully designed suite of problems and see whether the ones that the LLMs solve have particular characteristics.

It may seem as though I am desperately clinging to the hope that humans will continue to be able to make meaningful contributions to mathematical discovery for a while yet, but while I do indeed hope that, I am not making any assertions of the form “LLMs will never be able to do X”. I think it is likely that they will, and given the pace of progress over the last three years it will probably happen quite soon. But I do think that there may be a hurdle for LLMs to clear and it seems at least possible that it won’t be cleared as straightforwardly as some of the previous hurdles.

In that connection, it would also be interesting to see whether a different reward structure leads to LLMs being able to solve different kinds of problems. For example, if during training an LLM (or machine-learning system of some other kind) is not just rewarded if it ends up with a solution, but also penalized if it explores too many dead ends or if it “cheats” by getting the answer from the literature, perhaps it would be incentivized to go about the research process in a more human way and thereby achieve better results for classes of problems where it is yet to make a big impact.

If the hurdle is cleared, either by pure scaling up or by some more thoughtful method, it will be quite difficult to know when that has happened, since, as just mentioned, an idea that seems very original and surprising may just be lurking somewhere in an LLM’s training data. But I would be confident that it had been cleared if an LLM were to come up with a proof that was as surprising to me as the solution of the cap-set problem was in 2016: the previous best known bounds were completely eclipsed, the method was utterly different from anything I had thought about trying, and afterwards there was a flurry of activity as people came to understand what this wonderful new technique was capable of.

Conclusion

I wasn’t quite sure where I would end up when I started this post, and now that I’ve got to the end, I feel that my main conclusions are not particularly new or surprising, but I hope that the route to them is of some interest. The main points I have made are the following.

1. “Finding an example” is in practice not the same thing as proving a statement that begins with an existential quantifier.
2. If it is true that current models are particularly good at finding examples, that is probably not because they have a particular affinity for existential statements, but more because the proof-discovery methods that are appropriate for finding certain kinds of examples play to the obvious strengths of LLMs: wide knowledge and the ability to explore many paths of the search tree that humans would judge to have a low probability of success.
3. It seems likely that LLMs will carry on improving very quickly. However, if, contrary to expectations (mine at least), there turns out to be some residual class of problems (or other mathematical activities) for which humans continue to have the edge for a while, it is likely that those will be problems for which the mysterious human ability to prune the proof-discovery search tree is particularly advantageous: that is to say, problems where the search tree is deep and has a large amount of branching, so that without rigorous pruning a search is not feasible even for a computer.
4. A good sign that LLMs have reached human level for a much wider class of problems will be if they start proving theorems using methods that, like much of the very best human mathematics, are new and surprising but that with hindsight come to seem beautiful and natural. They should also be methods that are difficult to stumble on by accident. It is hard to say precisely what would count as such a proof, but I think we’ll recognise it when we see it.

Last September I went to a workshop at the Lorentz Centre in Leiden to discuss mathematics and AI with historians, philosophers, computer scientists, AI researchers, and mathematicians of several different flavours (though there was a surprising preponderance of algebraic geometers). The whole event was extremely stimulating, with some talks but also a lot of time set aside for discussion. One of the concrete outcomes of the workshop was the Leiden Declaration, which has now been signed by over 3000 people. Given that I was part of the workshop, it might seem a bit strange that I am not one of the signatories of the resulting declaration. The reason is not so much that I disagree with it in any concrete way, but more that in several places it makes confident assertions and recommendations that I feel somewhat uncertain about. So instead I prefer to try to articulate my views about the issues raised by the declaration and put them in this blog post. Before I do that, I would like to make clear that I am very glad that the Leiden Declaration exists and I think that it has done a lot of good in focusing people’s minds on the issues that AI is forcing the mathematical community to grapple with, which are more acute now than they were last September.

Let me begin by quoting a passage from the declaration that sets out “what we take to be characteristic values of mathematical research that we have a joint interest in preserving”.

1. There are many reasons to pursue mathematical research, ranging from intellectual curiosity to a desire to solve practical and societal problems. Underlying much of mathematics is the activity of proof. Mathematical proofs are regarded as conferring the highest degree of certainty to their conclusions, as well as imparting understanding of why their conclusions are true. These characteristics of proof support the scientific integrity of mathematics.
2. Results are attributable to specific authors who take credit for their discovery and assume responsibility for their correctness. These principles ground the merit-based standards to which we aspire in mathematical research.
3. Mathematical arguments are regarded as transparent and subject to independent verification. They may be extremely long or difficult, but in principle no proprietary knowledge or equipment should be required to understand them.
4. Mathematicians share a concern for proper evaluation of mathematical work relative to shared standards of depth, difficulty, and significance.
5. Mathematics produces not only a body of results, but also understanding, clarity, and judgment among the communities of mathematicians who have shaped them, often in the context of their own autonomously guided research. This expert knowledge is essential, both to effectively use mathematics, and to continue to articulate new and significant research questions. A key source of strength of the discipline has long been the autonomous shaping of the direction of research and the methods used to pursue it.

The first thing I would say about these values is that they are undoubtedly values that are widely held by mathematicians, including, with some qualifications, me. The main qualification I have concerns point 4: I find the notion of “proper evaluation” somewhat problematic, given that different mathematicians can have very different judgments without either of them being clearly wrong, especially when it comes to the significance of a piece of mathematics. Also, these judgments are used for purposes such as the acceptance of papers in journals, hiring and promotion decisions, the awarding of prizes, and so on, that are part of a system that copiously rewards a few people — I myself have hugely benefited from it — but doesn’t necessarily adequately reward a lot of people who are doing less visible work that is essential to keeping the whole enterprise going.

But the more important point is whether these values are ones that we should fight for in the future, as the Leiden Declaration suggests. I find that clearer for some of them than others. For example, it seems to me that the importance of rigorous proof will be even greater in an AI age than it was before — if the output of AI is not underpinned by rigorous proof, then the kinds of difficulties one already hears about with certain areas of human mathematics (see for example many talks by Kevin Buzzard arguing for the value of formalization) would be hugely magnified. But what about the attribution of results to specific authors, who take both credit and responsibility for them? Suppose that at some point in the future AI becomes more autonomous, reading the literature and solving many problems that it finds. Suppose also that its solutions are autoformalized, so there is no serious doubt about their correctness. In such a situation, there would be nothing for a human to take credit for or responsibility for. Does that mean that we should declare such results undesirable and threatening to mathematical values?

Of course, something could well be missing in such a situation: perhaps the proofs would be badly written and hard to follow, which would mean that they lacked something we all very much value. So let me extend the thought experiment slightly. What if by that stage one could take one of these outputs and ask an LLM to explain the ideas, and what if LLMs did a very good job at that? That is not particularly hypothetical, since they are often pretty good at this job already, but I am imagining a world in which they are much better than they are now, as they will presumably become.

So now we would have a world in which a lot of problems had been solved, we were sure that the solutions were correct, and we had an LLM ready to explain those solutions in as much or as little detail as we wanted. Is that a future we should resist, and if so, why?

One obvious reason is that it would take a huge part of the fun out of the subject. It is extremely satisfying to struggle with a mathematical problem for months or even years and eventually solve it. But I worry about that argument, because it seems to be saying that we should resist doing mathematics the easy way because a tiny fraction of the world’s population gets huge pleasure from taking orders of magnitude longer to do it. That is not to say that I wouldn’t be sad that a way of life that has sustained me for the last forty years was not available any more — of course I would. I just find it hard to use it as a reason to argue that we should try to preserve the “ownership structure” of mathematical results. If we arrive at a world where mathematical theorems are no longer associated with mathematicians, maybe that won’t be any more problematic than the fact that stars aren’t named after astronomers and most aren’t named at all. I’m not necessarily in a hurry for that world to exist, but maybe once the transition had happened, people would be OK with it.

The third value I share in an uncomplicated way, and I have already discussed the fourth. The fifth value is one that I hold very strongly, though I’m not so keen on the idea of experts consciously “shaping the direction of research”, something that I see as happening more organically. Obviously there are some notable examples of mathematicians who have created wonderful programmes of research, but even there I would like to credit other mathematicians with understanding what is wonderful about those programmes and contributing to them enthusiastically as a result, rather than being told what direction to pursue and meekly doing so (which is probably not what the declaration is actually trying to suggest, but it has a slight flavour of that for me).

But that’s a minor quibble when set against my main worry about the effect of AI on mathematics, which is the possible destruction of mathematical culture. There is at the moment an extraordinary body of knowledge and expertise that exists not just in the mathematical literature but in the heads of mathematicians all round the world. Imagine if AI didn’t exist and a pandemic broke out that for some reason wiped out all mathematicians and nobody else. All the literature would still be there, but nobody would have the faintest idea what to do with it. To revive a mathematical tradition under those circumstances would be extremely difficult and take decades. Now imagine a slight variant of that, where AI does exist and because of it people are no longer motivated to put in the years of effort it takes to reach the level of expertise that a typical research mathematician has now. After a decade or two, we might arrive at a situation where the mathematical literature has, in some form, been vastly expanded, but there is no corresponding community of human experts who have a shared understanding of parts of it. Almost all of mathematics would be like the areas that we have more or less forgotten about today, areas that exist in papers written many decades ago that nobody reads any more. (I won’t name any such area because I don’t want accidentally to suggest an area that many people still love and work on.)

This, it seems to me, is a possibility that we should try very hard to resist, but I agree with many other commentators who say that in order to resist it, we will need to give less priority to some of our current values — and I would include ownership of mathematical results in that list — and more to others. For example, if Person A gets an LLM to one-shot a solution of an important open problem (which is formalized, possibly automatically, so there is no doubt about its correctness) but Person B makes the effort to digest the solution and explain it in a way that other mathematicians can understand and learn from, then I think we will want Person B to get the lion’s share of the credit. The credit would be of a slightly different from what it is now, which could be described as admiration for somebody’s talent, insight, speed (I mean here the purely factual statement that speed is often admired — I would prefer that to be less the case) and hard work. It would be more like the gratitude that one feels already for somebody who writes a beautiful textbook that makes a whole area of mathematics coherent and accessible.

Maybe that is what the “research mathematicians” of the future should do: make a selection from a vast sea of AI-generated mathematics and write a book about it in such a way that other mathematicians can read the book and feel the kind of enrichment that we feel when we get to grips with an area of mathematics.

At this point I have to admit that there’s a pessimistic side of me that asks the following general question whenever anyone says anything about what the role for humans might be in the future: why do you think that AI wouldn’t be able to do it? For example, with the suggestion I’ve just made, what reason is there to suppose that ChatGPT 8.2 wouldn’t be able to have a short interaction with you about your mathematical tastes and background and then write the ideal textbook just for you? Humans are likely to be better at this kind of curating for a little while yet, but is it a fundamentally human ability that AI could never hope to emulate?

In a world where AI wrote bespoke textbooks (or more likely, just taught people in some more direct way), something would be lost that feels important: mathematics as a collective endeavour. If we all just learnt cool bits of maths for our own private satisfaction, we would miss the considerable pleasure that comes from discussing mathematics with others, though even that could in principle be restored by a benign LLM that deliberately taught many people the same cool bits of the subject, though an LLM that could do that sort of social engineering would raise all sorts of safety issues.

Let me now turn to the section of the declaration about potential threats. I’ll put my comments on each one in square brackets.

1. Current automated techniques can produce plausible but unreliable (or even incorrect) arguments which are difficult to distinguish from correct mathematical proofs. This applies not only to informal arguments, but also to formalizations, where the difficulty lies in the translation between computer-encoded and human presentations of concepts. These fast-moving developments put our present system of review under increasing pressure, jeopardizing our ability to implement traditional standards for the correctness, transparency, and independent verifiability of proof. [This feels like less of a problem now than it did last September, partly because the best LLMs hallucinate a lot less than before, and partly because autoformalization is improving all the time — I have just used harmonic.fun’s Aristotle system to formalize a complicated paper in Lean and I didn’t need to know any Lean to do it.]
2. Technologies that draw extensively on the published mathematical commons undermine the traditional system of attribution. Models trained on published works frequently return outputs that do not properly cite the human works they synthesize. Many current models are also built on data obtained by systematically exploiting licenses and access arrangements that were not made with artificial intelligence in mind, or indeed by simply violating copyright protections. [This is a problem at the moment, when ownership of results is important, and I am very much in favour of people making an effort to give appropriate credit for mathematical ideas that AI may have used. However, in the longer term, as I have already discussed, I think this ownership structure will break down and the issue will become less important. It also seems possible that LLMs will become better at revealing their sources.]
3. Technologies which affect the way in which mathematics is practiced may disturb the current system of incentives. The use of artificial intelligence — and thus also the sort of problems which it can address — may become incentivized for its own sake, disrupting our mechanisms for hiring, funding, and recognition. This disadvantages researchers who do not have access to the technologies or decision-making related to them, or who are unwilling to use technologies controlled by organizations whose values they do not share. [These seem to me to be genuine problems. I think there is simply no point in hoping that our current system of incentives will not be disturbed — it obviously will. I am not necessarily too worried if our mechanisms for hiring, funding and recognition are disrupted, as I don’t find those mechanisms unproblematic as they are, but disadvantaging researchers who do not have access to good LLMs is something I certainly think we should worry about.]
4. Proper evaluation is endangered if results are communicated through informal channels such as press releases or blog posts, often without any research paper or other disclosure of information necessary for scientific evaluation. This practice seeks publicity for new results on market timelines before the accepted processes of community evaluation in mathematics can take place. In many cases this leads to simplifications in reporting, such as overemphasizing the significance of automated tools and undervaluing the prior human contributions which have made those tools possible. Such oversimplification risks influencing public opinion in a way that not only damages perceptions of mathematics, but also misleadingly uses specific mathematical tasks as metrics for the general reasoning capacities of commercial products. [I think this can be a problem, but I think it is not as serious a problem as some of the others, since when results get overhyped, there seems to be no shortage of people publicly (and rightly) pointing that out.]
5. These developments put the autonomy of mathematics under threat. The increasing involvement of technology companies in mathematical research raises the risk that research questions may come to be prioritized because of their amenability to automated mathematics, rather than expert judgment of their deeper significance. Indeed, broader understanding of the field may be permanently lost in the process of automation. With university budgets under pressure, this reshaping also changes professional incentives in a manner which encourages the collaboration of researchers with technology companies on asymmetric terms. If left unchecked, these trends go beyond threatening researchers’ autonomy, affecting the scope and depth of mathematical research itself. [I think this could be a problem, but it also seems to me that mathematicians have a lot of power here. For instance, if a technology company were to produce a lot of research that mathematicians did not find all that interesting or important, I don’t think they would be able to use their financial and other resources to persuade us to change our minds. Rather, what seems to happen is that mathematicians say, “Yes that does X but it doesn’t do Y,” and the tech companies then feel challenged to do Y.]

There follow eleven recommendations for individual mathematicians. I agree with almost all of them. The one that I’m not so sure about, for reasons I’ve basically already gone into, is this.

Affirm the humanity of authorship. Credit and responsibility continue to belong to humans within the mathematical community and should not be given to automated systems. Artificial intelligence may obscure, but does not replace, the collective human labor behind a result.

I’m not sure what that really means. For example, should we affirm the humanity of authorship in the case of the solution to the unit-distance problem? Some humans did a wonderful job of explaining the proof that OpenAI’s model came up with, and the model made use of some highly non-trivial mathematics produced by humans, but the solution itself has not been credited to any human, and nor should it be in my view.

Under recommendations for mathematical organizations and not-for-profit research funders I again agree with several of them but have my doubts about some. An interesting case is the following.

Protect the rights of authors. Automated mathematics presents new challenges to the rights of authors, and societies should be proactive in the development of sample licensing agreements to protect these rights. In particular, material should not be used as training data without consent, and publishing agreements should allow authors to opt-out [sic] of the use of their work in this way.

This recommendation seems to belong to a world in which journal articles are the main means of dissemination of mathematics. But that has long since ceased to be the case: almost all dissemination now takes place via arXiv preprints, with journals limited to providing a little extra mark of prestige. Once an article is on arXiv, it is on the internet and one can hardly ask for it not to be used as training data. So this recommendation, if it applies at all, will apply to a tiny fraction of articles that are published without first appearing on arXiv. More generally, what right of an author is being compromised when an article is used as training data? We don’t object if human mathematicians use our articles to help train themselves to become better mathematicians — indeed, we will typically be delighted that somebody else thought our articles worthy of their attention. So the objection to a machine doing the same would have to be that for some reason one did not want machines to get better at mathematics in a similar way. I can imagine grounds for such a wish: perhaps somebody is worried about the threat that LLMs pose to traditional mathematical practice, or perhaps they worry that mathematical ability of LLMs will transfer to much more dangerous reasoning ability. But there’s a more complicated discussion to be had here than one might think from reading the recommendation.

The next recommendation is this.

Insist on appropriate publication outlets. Demand that mathematical results continue to be published in peer-reviewed venues such as journals, proceedings, and books. Informal mechanisms such as press releases or blog posts can provide a valuable supporting role, but they cannot replace peer-review or community scrutiny.

For reasons that I’ve gone into many times, I am not too fond of the current publication system, so I can’t get behind this recommendation. Indeed, if the current system becomes unsustainable because of a flood of AI-generated and AI-aided content, I would regard that as a beneficial consequence of AI. However, that doesn’t mean that I would advocate a total free-for-all. I’ve already said that one of my worries is that if mathematical content is not sufficiently organized, then the traditions that we all value could die. I just think that what we will want to do to preserve those traditions is likely to be a lot more innovative than clinging on to the peer-reviewed journal system.

I have highlighted in this post the parts of the declaration that I have doubts about, either because I disagree with them or, more typically, because I sort of half agree with them but want to add many qualifications. That may make the post come across as rather negative, but that is not my intention. The parts I disagree with are in the minority, and I think it is important that a declaration such as this should be made. I should also make clear that my views are evolving all the time, largely because the speed of progress of LLMs has taken me by surprise, but also as a result of conversations I have had or opinions that other mathematicians have expressed online.

I’ll end with two further clarifications. The first is that it may seem as though I am taking it for granted that LLMs will soon be better than humans at all aspects of mathematical problem solving, and maybe also problem posing, theory building, formulation of definitions, etc. I do think all that will happen at some point, but whereas some people say that it will obviously happen within the next two to three years, I would say that it might happen as soon as that, but I don’t rule out that we’ll get lucky and find that we can do interesting AI-assisted maths for quite a bit longer than that before AI doesn’t need us any more.

The second is that I think I have acquired a reputation as somebody who celebrates what is going on. But if, for example, I post on Twitter saying that such-and-such an AI solution is a remarkable development, the word “remarkable” is meant to indicate no more nor less than that I found it very surprising. My feelings about the possibility of AI solving all sorts of problems that interest me are much more mixed. I’ve had the experience twice now of seeing GPT 5.6 Pro one-shot a solution to a problem that I very much liked and had thought about hard (in both cases with much younger collaborators, who, with my approval, were the ones who prompted the LLM). It felt very strange and not particularly pleasant to have the rug pulled out from under my feet like that. On the other hand, I was quite pleased to see the problems solved. It’s actually a similar feeling to the one I have had many times when a problem I am fond of and have thought about gets solved by another human mathematician.

Another factor for me is that I have invested a lot of thought into automatic theorem proving of a more traditional kind. One of my main motivations for that was the hope that the work I put into it would extend the state of the art, measured by which problems a computer can solve. That ship has sailed now, and that saddens me. I still think that there is value in the work that I and my group are doing, but it has become a tougher sell.

So I personally have already found AI quite disruptive, and this is just the beginning. I would have preferred the developments to happen at a slower pace. But I don’t see any practical way to slow them down, so the best we can do is probably to face up to the changes that are being thrust upon us and do what we can to maximize the benefits and minimize the damage. The Leiden Declaration may not be perfect, but it makes an important and positive contribution to that effort.

We are all having to keep revising upwards our assessments of the mathematical capabilities of large language models. I have just made a fairly large revision as a result of ChatGPT 5.5 Pro, to which I am fortunate to have been given access, producing a piece of PhD-level research in an hour or so, with no serious mathematical input from me.

The background is that, as has been widely reported, LLMs are now capable of solving research-level problems, and have managed to solve several of the Erdős problems listed on Thomas Bloom’s wonderful website. Initially it was possible to laugh this off: many of the “solutions” consisted in the LLM noticing that the problem had an answer sitting there in the literature already, or could be very easily deduced from known results. But little by little the laughter has become quieter. The message I am getting from what other mathematicians more involved in this enterprise have been saying is that LLMs have got to the point where if a problem has an easy argument that for one reason or another human mathematicians have missed (that reason sometimes, but not always, being that the problem has not received all that much attention), then there is a good chance that the LLMs will spot it. Conversely, for problems where one’s initial reaction is to be impressed that an LLM has come up with a clever argument, it often turns out on closer inspection that there are precedents for those arguments, so it is still just about possible to comfort oneself that LLMs are merely putting together existing knowledge rather than having truly original ideas. How much of a comfort that is I will not discuss here, other than to note that quite a lot of perfectly good human mathematics consists in putting together existing knowledge and proof techniques.

I decided to try something a little bit different. At least in combinatorics, there are quite a lot of papers that investigate some relatively new combinatorial parameter that leads naturally to several questions. Because of the sheer number of questions one can ask, the authors of such papers will not necessarily have the time to spend a week or two thinking about each one, so there is a decent probability that at least some of them will not be all that hard. This makes such papers very valuable as sources of problems for mathematicians who are doing research for the first time and who will be hugely encouraged by solving a problem that was officially open. Or rather, it used to make them valuable in that way, but it looks as though the bar has just been raised. It is no longer enough that somebody asks a problem: it needs to be hard enough for an LLM not to be able to solve it.

In any case, a little over a week ago I decided to see how ChatGPT 5.5 Pro would fare with a selection of problems asked by Mel Nathanson in a paper entitled Diversity, Equity and Inclusion for Problems in Additive Number Theory. Nathanson has a remarkable record of being interested in problems and theorems that have later become extremely fashionable, which has led him to write a series of extremely well timed and therefore highly influential textbooks. In this paper, he argues for the interest of several other problems, some of which I will now briefly describe.

If is a set of integers, then its sumset is defined to be . For a positive integer , the –fold sumset, denoted , is defined to be . Nathanson is interested in the possible sizes of given the size of . To that end one can define a set to be the set of all such that there exists a set with and .

An obvious first question to ask is simply “What is ?” When , the answer is the set of all integers between and . It is an easy exercise to show that if , then , so this result is saying that all sizes in between can be realized. However, it is not true in general that can take every size between its minimum and maximum possibilities, and we do not currently have a complete description of .

Another natural question one can ask, and this is where ChatGPT came in, is how large a diameter you need if you want a set with and having prescribed sizes. (Of course, the size of must belong to .) Nathanson showed that for every there is a subset of with and , and asked whether the bound could be improved. ChatGPT 5.5 Pro thought for 17 minutes and 5 seconds before providing a construction that yielded a quadratic upper bound, which is clearly best possible. It wrote up its argument in a slightly rambling LLM-ish style, so I asked if it could write the argument up as a LaTeX file in the style of a typical mathematical preprint. After two minutes and 23 seconds it gave me that, after which I spent some time convincing myself that the argument was correct.

The basic idea behind both Nathanson’s argument and ChatGPT’s was that in order to obtain a set of a given size with a sumset of a given size, it is useful to build it out of a Sidon set, which means a set with sumset of maximal size (that is not quite the usual definition but it is the simplest to use in this discussion), and an arithmetic progression. Also, for a bit of fine tuning one can take an additional point near the arithmetic progression. Then if one plays around with the various parameters, one finds that one can obtain sets of all the sizes one wants. Nathanson doesn’t express his argument this way (it is Theorem 5 of this paper), instead giving an inductive argument, but I think, without having checked too carefully, that if one unravels his argument, one finds that effectively that is what he ends up with, and the Sidon set in question consists of powers of 2. ChatGPT obtained its improvement by simply using a more efficient Sidon set — it is well known that one can find Sidon sets of quadratic diameter. (One might ask why Nathanson didn’t do that in the first place: I think it is because the obvious idea of using a more efficient Sidon set becomes obvious only after one has redescribed his inductive construction. Is that what ChatGPT did? It is very hard to say.)

Next, I asked ChatGPT to see whether it could do the same for a closely related question, where instead of looking at the size of the sumset, one looks at the size of the restricted sumset, which is defined to be . Unsurprisingly, it was able to do that with no trouble at all. I got it to write both results up in a single note, to avoid a certain amount of duplication. If you are curious, you can see the note here.

I then asked what it could do for general . I was much less optimistic that it would manage to do anything interesting, because the proof for makes fundamental use of the fact (due to Erdős and Szemerédi) that we know exactly which sizes we need to create. If we don’t know what the set is, then it seems that we are forced to start with a hypothetical set with and and build out of it a set of small diameter with the same property. As it happens, I still don’t know how to get round that difficulty (I’m mentioning that just to demonstrate that my mathematical input was zero, and I didn’t even do anything clever with the prompts), but Nathanson mentioned in his paper a remarkable paper of Isaac Rajagopal, a student at MIT, who must have got round the difficulty somehow, because he had managed to prove an exponential dependence of on for each fixed .

I’ll leave the previous paragraph there, but Isaac has subsequently explained to me that that isn’t really the difficulty. His argument gives a complete description of when is sufficiently large, and if one wants to prove a polynomial dependence for fixed , then assuming that is sufficiently large is clearly permitted. The real difficulty is that constructing the sets with given sumset sizes was significantly more complicated, and necessarily so because the degree of the polynomial grows with , and one therefore needs more and more parameters to define the sets.

In any case, the task faced by ChatGPT was not to solve the problem from scratch, but to see whether it was possible to tighten up Isaac Rajagopal’s argument. Here’s what happened.

1. After 16 minutes and 41 seconds, it came back with an argument that claimed to have improved the upper bound from exponential in to exponential in for any .
2. I asked it to write that in preprint form too, which took it a further 47 minutes and 39 seconds.
3. That preprint would have been hard for me to read, as that would have meant carefully reading Rajagopal’s paper first, but I sent it to Nathanson, who forwarded it to Rajagopal, who said he thought it looked correct.
4. Both ChatGPT and Rajagopal speculated a little on what might need to be done to push things further and get a polynomial bound, so I got greedy and asked ChatGPT to give that a go.
5. After 13 minutes and 33 seconds it told me it felt optimistic about the existence of such an argument but there were a couple of technical statements that needed checking.
6. I asked it to check them.
7. After 9 minutes and 12 seconds it got back to me with the check having been done, so I asked for this too to be written in preprint form.
8. After 31 minutes and 40 seconds the “preprint” was ready. Here it is.
9. Isaac Rajagopal looked at it and declared it to be almost certainly correct. It was clear that he meant this not just at a line-by-line level but at the level of ideas.

Isaac made some very interesting remarks about the nature of what the additional ideas were that ChatGPT contributed. Since, as I have already said, my mathematical input was zero, I invited him to write a guest section to this post. Just before we get to that, I want to raise a question (that will undoubtedly have been raised by others as well), which is simple: what should we do with this kind of content? Had the result been produced by a human mathematician, it would definitely have been publishable, so I think it would be wrong to describe it as AI slop. On the other hand, it seems pointless even to think about putting it in a journal, since it can be made freely available, and nobody needs “credit” for it (except that Isaac deserves plenty of credit for creating the framework on which ChatGPT could build). I understand that arXiv has a policy against accepting AI-written content, which makes good sense to me. So maybe there should be a different repository where AI-produced results can live. But various decisions would need to be made about how it was organized. I myself think that one would probably want to have some kind of moderation process, so that results would be included only if a human mathematician was prepared to certify that they were correct — or, better still, that they had been formalized by a proof assistant — and perhaps also that they answered a question that had been asked in a human-written paper. On the other hand, I wouldn’t want a moderation process that created vast amounts of work (unless the work was itself done by AI, but there are obvious dangers in going down that route). Anyway, until these questions are answered, this result is available from the link above, and perhaps, now that LLMs are so good at literature search, that will be enough to make it findable by anyone who wants to know whether Nathanson’s problem has been solved.

Isaac’s evaluation of what ChatGPT achieved

With just a few prompts, ChatGPT was able to improve the upper bound on (which I will define very soon) from exponential in to polynomial in . While its first improvement of the bound, from exponential in to exponential in , was a routine modification of my work, the improvement to polynomial in is quite impressive. To do this, ChatGPT came up with an idea which is original and clever. It is the sort of idea I would be very proud to come up with after a week or two of pondering, and it took ChatGPT less than an hour to find and prove, using similar methods to those in my own proof. My goal is to explain that idea, in a manner that will be digestible to my friends who are computer science majors as well as my math major friends.

The problem of bounding is closely related to a problem I worked on at the Duluth REU (Research Experience for Undergrads) program, of determining . In particular, is the set of possible -fold sumset sizes , where can be chosen to be any set of integers. is the minimal such that we can achieve all of the values of using -element sets . I spent last summer explicitly characterizing the set for large , by constructing sets such that achieves all sizes which I could not rule out as impossible. So, can be upper-bounded by optimizing my constructions.

I constructed these sets by combining smaller component sets which are simpler to analyze. Some of these components are the geometric series

for various values of and . Unfortunately, the elements of and are exponentially large in terms of . So, I asked ChatGPT (through Tim) whether there exist sets of elements which have similar sumset sizes to these geometric series, but contain only numbers of polynomial size in : I had no idea if this was possible, or how to begin constructing such sets. ChatGPT came back with an answer, constructing sets and which behave like “half a geometric series squeezed into a polynomial interval,” which is counterintuitive. Before I discuss the construction of and , I will explain the important properties of the sumset sizes of and which they recreate.

For , a set is called a set if the only solutions to

with in are the “trivial” solutions, by which I mean that one side of the equation is a reordering of the other side. If is a set of size , then elements of correspond exactly to choices of elements of , with repetition allowed. Using “stars and bars,” one can see that and this is the maximum possible value of among sets of size . So, another definition is that is a set if . Sidon sets, which Tim discussed, are exactly sets.

To make things more concrete, let us assume that in (1). Then, is a set, but it is not a set because of the relations

for any choice of in . In particular, , as these relations are the only ones preventing from being a set. lacks the relations in (2) because is not in . So, is a set, but it is not a set because of the relations

for any choices of in . This gives relations, and one can check that . To summarize, we have seen that

(a) is a set.

(b) is a linear function of .

(c) is a set.

(d) is a quadratic function of .

ChatGPT was able to find sets and of elements which satisfy (a)-(d), but whose elements all have polynomial size in . The construction of and uses -dissociated sets, which are sets where the only solutions to

with and in are the “trivial” solutions, i.e. and one side of the equation is a reordering of the other side. For , it is possible to construct an -dissociated set , where is approximately , and in particular polynomial in . Constructions of such a using finite fields date back to Singer (1938) and Bose–Chowla (1963) and are described in Appendix 1. Define

and

In hindsight, I have good intuition for the construction of and . All of the relations in (2) and (3) are formed by combining one or two relations of the form . There are approximately relations of the form in and , and approximately such relations in and . There are few other low-order relations in and , and similarly in and because is -dissociated. So, and manage to contain half as many -relations as their geometric series counterparts, while also containing few low-order relations.

We now see why (a)-(d) hold with and replaced by and , respectively. For concreteness, we assume that and , so contains no nontrivial relations as in (4) with . Then, is a set, but it is not a set because of the relations

for any choice of in . If we let , we can check that is linear in . In particular, (a) and (b) hold with replaced by , and the linear function replaced by . We can also see that is a set, but it is not a set because of the relations

for any in . If we let , we can check that is quadratic in . In a similar manner, (c) and (d) hold with replaced by , and the quadratic function replaced by .

Even though I can motivate it in retrospect, ChatGPT’s idea to use -dissociated sets to control relations of order at most feels quite ingenious. As far as I can tell, this idea is completely original.

ChatGPT’s proof that its construction produces the desired values of is very similar to my proof that the sets which I construct achieve all possible values of , after replacing and by and , respectively. Properties (a)-(d) capture many of the important properties of and (or and ) which are used in this proof. The final constructions involve combining the sets and (or and in my paper) for each value of between and with another set which is the union of an arithmetic progression and a point. Intuitively, and (or and ) have large sumsets, while arithmetic progressions have small sumsets, so it is plausible that one could get sets which achieve all the medium-sized sumsets by combining them. However, the proof of this is quite involved, and it occupies Section 4 of my paper and the entirety of the ChatGPT preprint. In Appendix 2, I work out the details of the ChatGPT construction to show that for sufficiently large,

For comparison, it is easy to see that is at least on the order of , and it is unknown what the real value is. In Appendix 3, I give details of the correspondence between my paper and the ChatGPT preprint, which will be helpful for those who want to read either.

Finally, I want to express my deep gratitude to Tim for allowing me to contribute to this blog. I am still stunned by the coincidence that the problem he chose to put into ChatGPT 5.5 Pro led him to my paper on the arXiv.

Tim on what this means for mathematical research

I would judge the level of the result that ChatGPT found in under two hours to be that of a perfectly reasonable chapter in a combinatorics PhD. It wouldn’t be considered an amazing result, since it leant very heavily on Isaac’s ideas, but it was definitely a non-trivial extension of those ideas, and for a PhD student to find that extension it would be necessary to invest quite a bit of time digesting Isaac’s paper, looking for places where it might not be optimal, familiarizing oneself with various algebraic techniques that he used, and so on.

It seems to me that training beginning PhD students to do research, which has always been hard (unless one is lucky enough, as I have often been, to have a student who just seems to get it and therefore doesn’t need in any sense to be trained), has just got harder, since one obvious way to help somebody get started is to give them a problem that looks as though it might be a relatively gentle one. If LLMs are at the point where they can solve “gentle problems”, then that is no longer an option. The lower bound for contributing to mathematics will now be to prove something that LLMs can’t prove, rather than simply to prove something that nobody has proved up to now and that at least somebody finds interesting.

I would qualify that statement in two ways though. First, there is the obvious point that a beginning PhD student has the option of using LLMs. So the task is potentially easier than proving something that LLMs can’t prove: it is proving something in collaboration with LLMs that LLMs cannot manage on their own. I have done quite a lot of such collaboration recently and found that LLMs have made useful contributions without (yet) having game-changing ideas.

A second point is that I don’t know how much of what I have said generalizes to other areas of mathematics. Combinatorics tends to be quite focused on problems: you start with a question and you reason back from the question or if you reason forwards you do so very much with the question in mind. In other areas there can be much more of an emphasis on forwards reasoning: you start with a circle of ideas and see where it leads. To do it successfully, you need to have some way of discriminating between interesting observations and uninteresting ones, and it isn’t obvious to me what LLMs would be like at that.

Of course, everything I am saying concerns LLMs as they are right now. But they are developing so fast that it seems almost certain that my comments will go out of date in a matter of months. It is also almost certain that these developments will have a profoundly disruptive effect on how we go about mathematical research, and especially on how we introduce newcomers to it. Somebody starting a PhD next academic year will be finishing it in 2029 at the earliest, and my guess is that by then what it means to undertake research in mathematics will have changed out of all recognition.

I sometimes get emails from people who are interested in doing mathematical research but are not sure whether that makes sense any more as an aspiration. I have a view on that question, but it may very well change in response to further developments. That view is that there is still a great deal of value in struggling with a mathematics problem, but that the era where you could enjoy the thrill of having your name forever associated with a particular theorem or definition may well be close to its end. So if your aim in doing mathematics is to achieve some kind of immortality, so to speak, then you should understand that that won’t necessarily be possible for much longer — not just for you, but for anybody. Here’s a thought experiment: suppose that a mathematician solved a major problem by having a long exchange with an LLM in which the mathematician played a useful guiding role but the LLM did all the technical work and had the main ideas. Would we regard that as a major achievement of the mathematician? I don’t think we would.

So what is the point of struggling with a difficult mathematics problem? One answer is that it can be very satisfying to solve a problem even if the answer is already known, but I don’t think that is a sufficient reason to spend several years of your life on this peculiar activity. A better answer is that by solving hard problems you get an insight into the problem-solving process itself, at least in your area of expertise, in a way that you simply don’t if all you do is read other people’s solutions. One consequence of this is that people who have themselves solved difficult problems are likely to be significantly better at using solving problems with the help of AI, just as very good coders are better at vibe coding than not such good coders, or people who have a solid grasp of how to do basic arithmetic are likely to be more skilled at using calculators (and especially at noticing when an answer feels off). Mathematics is a highly transferable skill, and that applies to research-level mathematics as well. By doing research in mathematics, you may not get the same rewards as your equivalents a generation ago, but there is a good chance that you will be equipping yourself very well for the world we are about to experience.

Appendix 1 (Isaac)

We will construct an -dissociated set , where is approximately . This construction is a very minor modification of Bose–Chowla (1963)’s construction of a set, which I learned about from this paper. For whatever reason, the GPT preprint (Lemma 3.1) uses a different, less efficient construction using moment curves.

Let be a prime, let , let be the finite field with elements and fix a generator of , so that is equal to . Define a set of elements

Then, each element corresponds to a unique value of , by taking . Now an additive relation of the form in (4) with can be reframed by taking powers of as

As is a degree- extension of and is a generator of as an -extension, this means that does not satisfy any nonzero polynomials in of degree . So, both sides of (6) are identical as polynomials in and thus the additive relation in (4) is trivial. So, is -dissociated, and of course one can prune a few elements to reduce to size .

Appendix 2 (Isaac)

Fix constants such that (in my paper I arbitrarily chose ). Let the two sets in (5) be called and . Let denote the set of integers satisfying . Similarly to my paper, the constructions of such that achieves the desired sizes will combine sets of the following four types:

• with choices of and .
• for each value of , with choices of .
• for each value of , with choices of .
• A set of the correct size so that .

One reason that this construction needs to be complicated is that we need to create at least many sets. To do this, we vary parameters and in the domain and parameters and in the domain . We can choose to be slightly bigger than , and then the above construction gives us different sets where can be made arbitrarily small. So, if we were to remove any of the above parameters from the construction, and not change the others, this construction would no longer create many sets. In comparison, Nathanson’s construction when only needs to create sets. He does this by combining a Sidon set, an arithmetic progression, and one extra value, and varying the size of the arithmetic progression and the extra value in ranges of size .

We want to combine sets , which are given by , for the values of , for the values of , and a set. By Appendix 1, for all , there exists a -dissociated set of diameter . By the constructions of and , we can take each , where . Let have basis vectors . To combine , we can define as

Similarly to my Lemma 4.9, this construction ensures that the generating function product holds, which is the identity that both my paper and the GPT preprint use (see either paper for a definition of these generating functions). By (the standard) Lemma 2.3 of the GPT preprint, is Freiman-isomorphic of order to a subset of . Therefore, for sufficiently large (the whole construction relies on this for the same reasons as in my paper),

Appendix 3 (Isaac)

In Section 4.2 of my paper, I use a different, simpler construction to construct sets achieving the values in which have , for some small . These sets are subsets of , meaning that all elements have polynomial size in . This is observed in Section 5 of the GPT preprint.

Section 4.3 of my paper carries out the construction which combines many components including and . This corresponds to Sections 2, 3, 4, and 6 of the GPT preprint. This section has a lot of moving parts; I give an outline in Section 4.3.1.

In Section 4.3.2, I describe how the different components will be combined, using a construction which I call the disjoint union, and introduce generating functions as a bookkeeping tool to keep track of the sumset sizes of a set . This corresponds to Section 2 and Section 4 of the GPT preprint.

In Section 4.3.3, I compute the generating function of each of the component sets, including (Lemma 4.15) and (Lemma 4.17). This corresponds to Section 3 and Section 6.1 of the GPT preprint. In particular, is computed in Lemma 3.3 and is computed in Lemma 3.4. Once these generating functions have been computed, the remainder of the proof is almost identical in my paper and in the GPT preprint.

In Section 4.3.4, I put all the pieces together to show that as we range over the sets which I have constructed, the values of will assume all of the elements of . The key idea is to show that the set of all values of forms an interval, and contains numbers both smaller than and equal to .