An Anthropic employee recently produced a proof of the Riemann hypothesis . He found it working with Claude, which had access to a massive amount of compute. The proof is a 17-million-line Lean library, and a day later the Lean and Mathlib communities certified it as correct.
This is a great achievement, well beyond what I expected LLM systems could do. It should now be clear to everyone that LLM-based agentic systems can turn compute into mathematics. By constantly proposing new ideas and quickly testing them, they can resolve even the hardest conjectures.
Their current problem-solving approach is probably not optimal, and it only works when a proposed answer can be evaluated quickly. Still, I suspect it is already enough to resolve more than 99.99% of the mathematical statements that arise in applied science. In a sense, it amounts to a brute-force search, guided by the structure of human language that the base model has learned.
Personally, I expected math to be harder. I assumed it would take a much better base-model to prove something like the Riemann hypothesis in a reasonable amount of time. I was wrong: today’s base models are already enough.
To me, this observation matters even more than the Riemann hypothesis itself. We should accept the new reality:
agentic systems are enough to prove or disprove essentially any well-defined mathematical statement.
There is a lot to say about the future role of pure mathematicians, and I strongly believe they still have a huge role to play. What they do is clearly different from what LLM-based agents do today. But I will set that aside and focus on applied research.
What this means for applied research
Here is the lesson for us applied researchers. Once we properly turn a research question into a mathematical statement, LLM systems can eventually prove or disprove it. After that, it is just a matter of more agentic exploration.
This changes the landscape of applied mathematical research significantly. But two things remain hard.
The first is evaluation. Not all applied research can be turned into a clean mathematical statement; often we need to run experiments that are costly and time-consuming. Math is unusual in that evaluating an idea is easy (thanks to Lean and friends), while in most applied fields it is actually very hard. LLMs can brute-force their way through many ideas to find the right one, but in reality this is often infeasible. We have limited time and resources and can run only a few experiments, so we have to make sure they are the most promising ones. I still don’t think LLM systems are good at this.
The second, and maybe the more important, is problem definition. Defining a problem well is not an easy job!
Structured fields
Think about theoretical computer science. For nearly a century, much of the field’s work has been to pose hard problems and, while leaving them open, discover how they connect. This has been anything but trivial, and the result is a remarkably complete universe of important problems.
CS theorists know how these problems are related, and they have classified them by hardness. They often know exactly what would happen to every other problem if one open problem were resolved.
Take the Exponential Time Hypothesis, which Anthropic and OpenAI each disproved in October. It was a precisely defined conjecture, and because its connections to other problems were already mapped out, its disproof had many immediate consequences. Proposing this problem was not trivial. It was based on many many prior work in the area.
Decades of human research built this network of problems into a beautiful architecture with only a few pieces missing. I expect that, very soon, LLMs will finish it by resolving the remaining open problems, with enormous implications. That would be a great success for the entire research program of theoretical computer science.
This is what a mature field of applied mathematics looks like, or should look like: well structured, with known important problems and well-studied connections between them. A field has to be this well developed before it can pose open problems this important. These are the fields that stand to benefit most from modern LLM systems.
Unstructured fields
Very few areas of applied mathematics have reached this level of maturity. Information theory is one of them. My own field, deep learning theory, sits at the other end of the spectrum.
It has no framework, and the connections between its problems are unclear. Of course, good research is being done, but it is ad hoc: there is no foundation to guide how problems are defined.
Suppose for a second that we had a machine that could reliably prove or disprove any statement we gave it (we almost do). I am not certain it would meaningfully speed up discovery in deep learning theory, because I don’t think there are any good questions to ask it.
Believe me, I have tried, and tried hard. I could not find a single worthy open problem, even though very little is known about deep learning theory.
The bottleneck has shifted from answering questions to asking them. Mature fields like theoretical CS are about to cash in on decades of careful question-building. Fields like mine still have to work out what to ask.
What comes next
So far, I have seen no progress by LLMs in unstructured fields like deep learning theory, where there are no clear open problems. Nor have I seen any indication that LLMs are good at proposing interesting theorems (and by interesting, I mean interesting to humans!).
So what should we do? I see two options:
- Work hard to structure every field so that it can leverage modern LLMs.
- Work hard to make LLMs capable of structuring unstructured scientific fields.
Either way, someone or something still has to work out what to ask.

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