I have the impression that recent advances in the deployment of AI for the purpose of mathematical research have made many people uncomfortable. I want to present my personal view on these matters, which is more optimistic.
Let me get the following assumption out of the way:
(A1) In the near future, AI results are generally always verified by trustworthy interactive theorem provers.
We assume this because it is plausible, and we do not want to discuss the problem of verifying the correctness of a potential flood of AI mathematics.
Here are further concepts which may be heavily impacted by AI, but which we do not discuss here:
- Mathematical Education
- Bachelor’s and Master’s theses
- The PhD as a research training program
- Attribution and bibliography in mathematics
The reason is that these problems are not as important or as difficult as the fundamental questions on the relevance of humans in a time of AI mathematics. I think that if we have an appropriate framework for how we think about research mathematics, then we can also figure out how to treat the above concepts. They have undergone great transformations before. We therefore focus on the perspective of the research mathematician.
Let us broadly split the possible AI futures into two scenarios:
(S1) Human-in-the-loop mathematics: AI mathematics can combine existing tools to prove theorems which are well within reach, and it can carry out further development of theories and tools in obvious directions. However, humans are needed to point the AI to problems of interest in applications and oversee the whole process, evaluating its findings and deriving value from them. Humans are needed to drive fields in new original directions and come up with genuine innovations and novel approaches.
(S2) Fully superhuman AI mathematics: There is in general no benefit to having humans around when real mathematics is done, except for educational or philosophical interest.
We are currently in a kind of (S1) situation. We should not assume that (S2) is impossible in the near future.
Let us first focus on (S2). How afraid should we be of this scenario? I don’t know, but I think: no more than anyone else. I would like to argue for the following thesis:
(T1) Humans will be useful in mathematics as long as humans are useful in any intellectual profession at all.
That is, mathematicians should not worry about being replaced at a fundamental level any more than humans in general should worry about the impact of AI on all human intellectual activity. Maybe that’s not very calming, but we also shouldn’t try to have the complete answer to a question all of humanity may be facing soon.
This question is related to the general phenomenon of the spikiness of AI capabilities, meaning that it is already superhuman in some areas, but still lacks something needed to replace human intellectual labor on a massive scale. I have the impression that the most significant thing which is missing is a sort of ability to exercise judgements. To be a successful lawyer, investor, doctor, or scientist, you need to make judgements about scenarios that involve long timescales and large quantities of people, money, components, or projects. The same is true for lower-paid professions. It seems like even frontier models, which are clearly highly intelligent in some ways, are not very good at this yet. This is why you cannot currently send out agents on the internet with the task of making money and expect them to succeed. I think this kind of ability to make judgements, and similar capabilities like intuition, vision, or vibe, are strictly necessary to go from (S1) to (S2), i.e. to completely take the humans out of the loop. This is why I claim (T1). As such, mathematicians should not worry about (S2) any more than the rest of humanity.
If this was not too convincing, I would like to say in general that I think it does not make too much sense to worry about very remote scenarios. Even though (S2) may not be so remote in time, it is certainly in economic-conceptual space. Therefore, we should not expect to be able to plan for it very well. We will just have to see what comes.
Let us now focus on what it means to be a mathematician in a (S1) world.
I think for some people (S1) is already unacceptable because they view mathematics as an activity that is fundamentally about human understanding: an art, a scholarly activity, a social status game, a great puzzle, maybe even a sort of religion. For these people, I would like to argue for the following:
(T2) Mathematics derives value at its core from being an applied science, as opposed to from human intellectual achievements.
This is similar to saying that all mathematics is applied mathematics. The philosophy is simply to consider in an inductive manner any mathematical theory or tool as applied, when it has implications or relevance for a theory or tool which is applied. In addition, theories or tools which are used in science, engineering, and other applications, are applied. Then we obtain some sort of graph, perhaps directed, where applications in physics, chemistry, engineering, biology, AI, etc., are the leaves.
Let us draw a more geometric picture. Consider the space of mathematical problems as a high-dimensional ball without origin. On its surface lie the mathematical problems which are quite literally fully applied. It is not necessary to approximate the falling cow by a falling sphere. Mathematics is perfectly capable of modelling the falling cow in arbitrary detail, including even the movement of its fur and the sloshing in its gut. Near the boundary lies what we consider applied mathematics. As you move from the boundary closer to the origin, the mathematics become more abstract, conceptual, and “higher”. In this region you would like to see surprising connections between fields and vast generalizations of concepts, which is why I like to think of it as a ball, so that higher abstraction moves concepts closer together. The origin, however, is missing, so that direction is not bounded.
Mathematical tools and theories are diffuse blobs in this ball that represent understanding of the corresponding family of mathematical problems. Between tools you have arrows that represent application of a tool in order to develop or understand another tool. The purpose of what we consider maximally pure mathematics is to eventually be used to develop tools that yield tools that yield tools that eventually reach the fully applied boundary. In practice, this almost never happens, because the space is so large and mathematicians are few. So instead we reduce a family of applied problems to a toy problem and build tools to tackle that toy problem. The study of these tools throws up new questions and problems, from which we pick again a toy problem. Then we build a more abstract tool to gain understanding of that more abstract toy problem. And so on.
The fact that our theories and tools rarely reach down to the level of applications may just be a limitation of the availability of mathematical labor. I think if (S1) comes to be, we need to become more ambitious. We either need to look towards the boundary of applications, or the center of high abstraction. Maybe let us leave the center for the top guys, and instead focus on looking towards applications.
We need to think about how we can leverage the additional labor provided by AI, and which problems our field never even considered because nobody would have the time to deal with all the difficulties. For example, in the field of PDEs, it may mean we should aim for the case of manifolds, with boundaries, and non-constant coefficients, and time-dependent forcing, and so on. We should also think about how the mathematics we do originally became of interest, and who the less-applied mathematicians or fully-applied scientists or engineers who hope to gain understanding from our field are. This shows the path to the level of applications. Ideally, we should talk to these people too. In the long run, I hope this allows us to develop a kind of integrated science, where formally verified mathematical theory, scientific modelling, statistical analysis, empirical observations, numerical simulation, and even more powerful computational perspectives, are all combined.
To say it simply, I believe there is a great demand for mathematical labor that was previously unrealistic to ever fulfill, and hence not visible. Human mathematicians may become a small part of all this mathematical labor without shrinking in absolute numbers.
I do not believe that OpenAI or Anthropic will simply fully conquer this domain, given (S1). Consider, for example, the Erdős problems, of which there are ~1200. Roughly ~450 have been solved by humans, and since the end of 2025 roughly ~100 of them have been solved heavily or fully by AI. Perhaps it is reasonable to expect that these problems would be broadly distributed along difficulty, and also that every new frontier model since already many months ago is immediately tested on all of them. That means the low-hanging fruits get picked. Note that OpenAI’s new internal “Astra” model solved “only” 3 of these problems. If we assume that every year 2 new versions are released which have steady exponential growth in capability, but also that the Erdős problems have a wide normally distributed -log(difficulty), it may be the case that only ~10 new Erdős problems get solved every year, as opposed to an ever increasing number. And the Erdős problems are just a tiny corner of mathematics. There is time and space for mathematicians to work in.
I think the real value will be generated by the people who their fields, and what kinds of problems there are, and that pick the problems: carefully, with intention, and a strategy to develop the field in a direction of interest, perhaps in applications. And just to reiterate, I believe that if AI is better at this than humans, then we are in (S2). In that case, I am happy to say that I do not know the answer, but I also do not feel a particular duty, as a mathematician, to have an answer.
Received 19 August 2026.
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