October 8, 2026 - Thoughts on Math, AI, and Future Directions
I imagine the measure of the set of people who are here and have not seen yesterday's announcment by OpenAI (https://github.com/openai/math/tree/main) is zero. To briefly summarize, approximately 700 major problems throughout mathematics have (very likely) been solved via LLM. At the start of my PhD, where I trained in von Neumann algebra theory, there were three big guiding problems in the field: the Connes embedding problem, the Connes rigidity conjecture, and the free group factor problem. The first was solved in 2020 (with some initial skepticism) by Ji, Natarajan, Vidick, Wright, and Yuen. Connes rigidity in full generality was disproved earlier this year by OpenAI (as well as by Shuoxing Zhou with AI assistance). Connes rigidity for higher-rank lattices and the free group factor problem were both resolved in OpenAI's proof dump.
It is difficult to overstate the impact these three problems have had on von Neumann algebra theory. The Connes embedding problem inspired (or ended up being closely related to) many subfields, including the model theory of operator algebras, quantum games and quantum information theory, microstates free entropy, strong convergence and stability, and sofic/hyperlinear groups. The Connes rigidity conjecture inspired a ton of work on character rigidity, W* and C*-superrigidity, and the general role of property (T) in operator algebras, including in the study of fundamental groups, outer automorphism groups, and deformation/rigidity theory. The free group factor problem itself directly inspired Voiculescu to develop free probability, and eventually led to deep results on the structure of the free group factor, including absence of Cartan subalgebras, primeness, strong solidity, infinite 1-bounded entropy, and, also using random matrix theory, the uniqueness of maximal amenable extensions of diffuse subalgebras (the Peterson-Thom conjecture or perhaps the Hayes-Bordenave-Collins theorem). Much of my own research lives in the echoes of these problems. My first paper concerns primeness of certain crossed product von Neumann algebras; primeness wouldn't have been known for any II1 factor without a pursuit of the free group factor problem. My work with Gao, Kunnawalkam Elayavalli, and Tan on sequential commutation is in part inspired by the free group factor problem and further study into free entropy. My work with Gao and Kunnawalkam Elayavalli on sofic actions is closely inspired by the Connes embedding problem.
The point I'm trying to make is that there is a part of me that is grieving the loss of these problems as guiding lights for myself and for my colleagues. It is especially tragic that, at least at first glance, the proof of the free group factor problem does not appear to contain any particularly interesting new insights. (Though the human-made proof of the Connes embedding problem also didn't exactly inspire much follow-up work from operator algebraists, except as a black box.) It has also become clear, especially after speaking with colleagues, that we are entering an era of mathematics where theorems and proofs are "cheap". It is also certainly the case that the traditional value signals for hiring and promotion are quickly becoming heavily distorted. Journals are inundated with an overwhelming number of submissions.
I see a few immediate consequences of the new research environment. First, the previous strategy of publishing many papers (often incremental) is no longer sustainable and will not continue to be as valued by the research community. Instead, researchers will have to aim for more ambitious projects, ideally developing new frameworks/perspectives/definitions, or at least aiming for more broadly-framed goals, such as "understand the subalgebras of the free group factor". We are bound to be in for a shortage of problems (especially PhD student-level problems), so the ability to find research directions will also become correspondingly more valuable. The ability to absorb and communicate mathematics will also probably grow in importance.
Mathematics will continue on as a field of study and as a profession. It's just not clear how we should change our usage of arXiv and journals. For the time being, my plan is the following. I will attempt to digest some of the new AI results, and I may post somewhere on my website my understanding of these proofs. At the same time, I will start some new ambitious research projects. My goal with writing up the AI results is to aid my own understanding and also to help communicate to other mathematicians any new ideas uncovered. My first goal with the new research projects is to obtain some results not easily obtainable by OpenAI, which I think will require some amount of mathematical vision as input on my end. My second goal is to have fun and to learn more math -- that much hasn't changed!