Some recent AI-produced mathematical advances and their significance
Related post: A historic day for mathematics
The last several weeks have seen a dizzying array of announcements of noteworthy (and in some cases very significant) mathematical advances discovered autonomously by AI models. Here is a timeline of the recent announcements:
July 10: Cycle double cover conjecture proved
July 19: Jacobian conjecture disproved
July 26: Improved upper bound on the length of superpermutations of orders 8-10
July 27: Crouzeix's conjecture proved
August 1: Ten advances in mathematics and theoretical computer science
August 11: Improved results on Riemann zeta zeros on the critical line
August 12: New constructions of Hadamard matrices
How significant are these results?
The results range in significance from being mildly interesting to major advances. (This is of course subjective, and opinions will vary on the significance question. I offer here my personal, necessarily biased opinions.) From my point of view, the three most significant among these results are:
Disproof of the Jacobian conjecture. This conjecture has a simple statement, sounds plausible, and interested many mathematicians, having been proposed in 1939 (and in an earlier version as far back as 1884 for the two-dimensional case, which remains open) and been the subject of an extensive literature. I have not worked on it myself, but know people who did and who regarded it as a very important open problem.
In terms of the disproof, this seems like one of those cases where a positive resolution of the conjecture would likely have been a lot more interesting than a negative resolution; indeed, the disproof was very short (and announced via a 5-line X post). So in some sense this is a disappointing outcome, and it seems possible that it will not yield any particularly important insights. The fact remains however that Claude Fable managed to discover something that had eluded mathematicians for 87 years. And because the human discoverer shared so few details (none other than the statement of the solution, as far as I'm aware), we still don't know how the AI came up with this stunningly simple counterexample. So there may be more to understand here, and I predict that research on this problem, particularly in the two-dimensional case, will continue in earnest, probably also benefiting from assistance from AI.
Riemann zeta zeros. This was a stunning advance on one of the most classical topics in mathematics: the Riemann zeta function and the location of its zeros. The advance is a numerical improvement to a well-known bound: the proportion of the zeros of Riemann zeta that are located on the critical line, which was improved from "at least 41%" (a result of Brian Conrey from 2011) to "at least 67%". The venerable history of this problem, involving famous work of Hardy, Littlewood, and Selberg, and its status as being "adjacent" to the Riemann hypothesis, undoubtedly makes this one of the most attention-grabbing AI math research breakthroughs we've seen.
Does this advance mean that we are any closer to proving the Riemann hypothesis itself? No: Anthropic say themselves they do not expect the techniques to help with RH (and neither do I). Still, the result is clearly very impressive and, as far as research mathematics advances go, "flashy".
New bounds for high dimensional sphere packing. This is a problem that relates to my work and that I am personally very fond of. The result announced by OpenAI settles one line of investigation that began in 2001 in work by Henry Cohn and Noam Elkies: the so-called Cohn-Elkies sphere packing bounds. (Shameless self-promotion: my book Topics in Complex Analysis gives a readable exposition of the Cohn-Elkies sphere packing bounds that can be useful to anyone wanting to study the OpenAI results.) The OpenAI paper discusses the question of the asymptotic power of the Cohn-Elkies bounds in very high dimensions. The main result from the opening chapter of the paper settles the question in a sharp way, and implies as a corollary that the density of sphere packing in N dimensions is bounded from above by \(2^{-\alpha N}\) where \(\alpha = \frac12 \log_2(2\pi/e) \approx 0.6044\). This is a small improvement over a classical bound from 1978 of \(2^{-\beta N}\) for \(\beta \approx 0.599\). A tiny improvement numerically (of around 0.4% in the multiplicative exponent), but one that, in the hyper-competitive area of research on famous mathematical open problems, is nonetheless seen as quite significant. And for a good reason, I think: the issue is that, whenever mathematicians find themselves unable to improve a bound for almost fifty years, that is seen as evidence that they are completely stuck on the problem and are in need of a new idea. At that point, any improvement, even a tiny one, to the bound, is hailed as a major achievement because it necessarily required a genuinely new idea to make.
How significant is the fact that these results were proved by AI models?
As with the case of the unit distance problem breakthrough from back in May, while these results give ample reason for excitement just for the mere fact of their being discovered, the fact that this was done as autonomous AI mathematics research gives perhaps even greater cause for excitement: it means that AI is increasingly establishing itself as a force to be reckoned with in its ability to come up with impressive research advances, with little or no human steering, on a regular basis. This is something that a lot more people are paying attention to (like the 39 million people who viewed Levent Alpöge's X post about his disproof of the Jacobian conjecture).
What can we learn from these discoveries about the emerging capabilities of AI models?
I observed in my earlier post that the mathematical breakthroughs AI models are coming up with seem to be focused around the discovery of counterexamples or so-called "rare" objects, and usually involve proofs that are very ingenious but are relatively short.
The current slate of discoveries partially confirms this pattern: as the Jacobian conjecture counterexample and the Hadamard matrix and superpermutation constructions show, frontier AI models once again seem exceptionally strong in their power to detect hidden structure in complicated mathematical landscapes and exploit that in the service of discovering rare objects that mathematicians have been searching for for many years, sometimes decades.
In terms of the length of the proofs however, I would say that the proofs we are seeing AI coming up with are starting to seem quite long and technically involved. The proofs still don't match the complexity of some notoriously complicated human-generated mathematics (say, Hales' proof of Kepler's conjecture, the Fermat-Wiles theorem, the classification of finite simple groups, and so on); but they seem comparable in length and complexity to the sorts of papers many professional mathematicians write when presenting top-level research discoveries.
One can try to further analyze what are the particular strengths of AI models and the way they will change how progress in research mathematics is going to be made from now on. I will offer a simplistic model (related to my observation above about the improvement to the sphere packing bounds from OpenAI's recent result requiring a new idea): it seems to me that progress in mathematics can be classified as coming roughly in two forms, consisting of "genuinely new", creative ideas on the one hand, and of "optimization on old ideas" on the other. The genuinely new ideas are the sort of dramatic breakthroughs that we hear about only every so often, being the product of some brilliant mind coming up with an unbelievably clever insight or idea. These ideas are used to produce fundamental new results improving on what is known up to that point in some significant way: an example would be Yitang Zhang's breakthrough on the twin prime conjecture in 2013. The "optimization" phase is a long and arduous process in which mathematicians work very hard to mine the earlier discovered new ideas and "squeeze the juice" out of them, pushing them to the absolute limit of what they can do. (In the case of the twin prime conjecture, the optimization was carried out in a Polymath project following Zhang's discovery.) After this long phase, the community gets stuck and runs out of steam, until some time afterwards a new creative person proposes another "genuinely new idea", and the cycle repeats itself.
My impression is that the main contributions AI has made to research so far are of the "optimization" type: AI these days has a fantastic ability to take known techniques and apply and combine them in clever ways to obtain improvements to state-of-the-art results. On the other hand, we have not seen so many examples of AI producing a "genuinely new idea". The OpenAI breakthrough result on the unit distance problem is perhaps the only example I can think of that was of this type, and that is perhaps one reason why that breakthrough was hailed as so significant. Indeed, this discovery was so unusual that it led to speculation that perhaps the idea the AI came up with wasn't actually as "creative" as it seemed, and might have been simply the result of the AI's incredible breadth of knowledge about many areas of mathematics rather than of true "creative genius" (whatever that is).
If my analysis is correct about AI being strong at optimization and less strong at new ideas, what this could mean for mathematics research going forward is that the optimization phase of research is now going to be dramatically shortened: whenever the next genuinely new idea comes along in some research area, we will see people managing to use AI to squeeze all the juice out of the new idea in a much shorter amount of time than they used to do before: a process that previously unfolded over, say, twenty years, is now going to unfold over a few years or even months. The corollary is that mathematicians will have to prove their continued worth to the research enterprise by working harder to come up with the sorts of new ideas AI still cannot come up with on its own.
It will be interesting to see if the dynamic will play out in this way and how it will affect the culture (and employment status) of mathematicians. Of course, it's quite possible that I'm completely wrong and by this time next year AI will get as good as humans at coming up with new creative ideas as well. We shall see... 🤷♀️