I am not a blogger, and I’m not on Twitter or other social media, so I’m not used to this. But I think it is very important that we, as more senior mathematicians, offer a vision for the future of our field. I owe my career to an environment that gave young researchers room to grow, and I feel a responsibility to pay it forward to those now facing an uncertain future. I don’t really think of myself as that senior or influential, but I’m putting something out here in the hope that others will follow. I will happily link to their thoughts here, including those I disagree with. They do not have to be well organized or well articulated (mine certainly aren’t; and yes I used AI to edit this text). I hope this can help get a more nuanced discussion going. I will add to these thoughts as I have time.

Being of two minds

I think it is important to recognize that it is OK to be of two minds about AI. AI is definitely useful for many things, and it has helped me and others tremendously. It has improved my workflow and removed barriers in my own creative process. One of my goals as a researcher is to advance knowledge, so I also welcome the contributions AI has made toward answering central questions in our field. At the same time, I regret some of its effects, particularly on the mathematical community and on the goal of actually understanding the material. (There are also environmental concerns, risks to the labor market, and much else that I won’t get into here.) So it is OK to be both excited and regretful.

My thoughts on Navier–Stokes and OpenAI’s conduct

For several years, AI companies have told us that they want to support research, and mathematical research in particular, by providing us with powerful tools. This sounded like a commendable offer—I doubt that anyone is opposed to having more tools. In fact, Buckmaster and Alpöge recently used Codex and Claude, together with substantial human input, to advance a research program on singularity formation in fluid equations. As Buckmaster explains in his statement, the basic ideas behind this program came from Córdoba and Martínez-Zoroa. My understanding—apologies, this is not exactly my domain—is that these ideas carried substantial theoretical weight, while extending them towards the resolution of the Navier-Stokes problem required a great deal of difficult technical work. So this second step seems like an ideal application and testing ground for AI tools.

However, the promise of providing tools to aid research stands in stark contrast to OpenAI’s conduct after hearing rumors of progress on the Millennium Problems. According to its own announcement, OpenAI began its effort after hearing these rumors and eventually concentrated its resources on Navier–Stokes, with a group of roughly 10,000 agents working on the problem. To me, this looks like using an extraordinary advantage in resources to put themselves at the front of the line.

How does racing to get ahead of fellow researchers square with the promise of providing us with tools to do our research? It is hard to believe that helping us was what this was about. AI or not, I find this behavior unacceptable. If a colleague of mine got wind of a paper that I was about to finish up and decided to work day and night to scoop me, I would find that completely unethical. It would also make me more secretive about my work or force me to cut corners in the final (and important!) writing and presentation step. Often, it is not the solution itself that is the important advance, but the recognition that a problem is solvable.

This goes far beyond mathematics. We are continually being told that AI will give us tools to tackle the problems of the twenty-first century, increase productivity, and “supercharge” the economy. These are great goals. But how can we trust that these are your goals when your response to hearing about someone’s progress is to race ahead of them? Is your goal to give us tools to do our work better, or are you planning to use your unlimited (and borrowed!) resources to compete against us?

What I would like to see from AI companies

I think AI companies that want to participate in mathematical research share our responsibility to think about how young mathematicians can grow in this new environment. There is an unspoken expectation in mathematics—unfortunately, not always met—that a major breakthrough should come with some discussion of what comes next. Papers that settle important conjectures should point to the further questions and discuss research directions that their results open up.

For example, after my colleagues Marques and Neves proved the famous Willmore conjecture, their techniques and their leadership helped generate a great deal of activity in min-max theory. This gave young mathematicians opportunities to grow and establish themselves. I would like to see this kind of discussion accompany OpenAI’s recent publication. You are announcing a solution to an important question that has driven mathematical activity and innovation. I think this comes with a responsibility to explain how your work can create opportunities for further research and for the people doing it.

We also need a clearer picture of what to expect from AI. If you really want to help our field, here is my suggestion: be more open with us about what your models can do and where you believe their limitations lie. Can you find useful ways to measure things like endurance, creativity, and the ability to develop a novel idea? We need to know so that we can plan for the future. Again, this goes far beyond math: how should an ordinary white-collar worker plan for the future? Which skills should they acquire? Which will best complement AI?

If you truly believe that every part of mathematical work can be replaced by AI, then let us know. But in that case, I do not see how we are supposed to sustain a good mathematical ecosystem. I suspect we will still need mathematicians in the future, if only to help us understand and deal with the problems AI itself might create. Otherwise, who will be left to battle the pink robots?

What is math about?

All of this raises a question that I think we will have to discuss more openly: what is math about? I have two closely related answers.

One is that math is about understanding things and developing new intuitions. We want to know why something is true, how it fits with other things we know, and how to think about it without having to repeat a hundred pages of arguments in our heads. A surprising amount of mathematics is driven by human laziness, in this rather productive sense. We get tired of cumbersome calculations and look for a definition or a point of view that makes them easier to think about. What feels simple, natural, or beautiful is partly a matter of human perception. In this sense, math is a bit like art: it can express how we see the world, guide our perception, or play with our intuitions.

Take complex numbers, for example. We could insist on treating them as pairs of real numbers and write out every operation in terms of those pairs. But it is tiring to keep doing that, and treating them as actual numbers simplifies our calculations. It also challenges our intuition in a curious way, at least when we first encounter them as students. Once we have accepted this slightly weird concept, it gives rise to beautiful subjects such as complex analysis and complex geometry. An AI does not have this kind of human laziness (though, admittedly, I can’t say this with certainty). So it might be perfectly happy carrying around pairs of numbers and enormous expressions, with much less reason to seek a change of viewpoint. In the process, it could miss a lot of beautiful theory. The ideas that help a system produce answers need not be the same as the ideas that help us understand them.

My second answer is that math is also about keeping ideas alive and allowing them to trickle through to places where they can be useful.

So far, we have not really needed to think about these things very much, because they more or less worked out on their own. For centuries, mathematicians have been driven by the desire to prove conjectures. In the process, they have thought about the broader subject and come up with new techniques, simplifications, intuitions, or questions for others to work on. There was a natural pace to this process, and problems were abundant and diverse. Young researchers could try their luck on easier problems to hone their skills and prove their value on the job market. Senior mathematicians were generally expected, or encouraged, to focus on harder and possibly riskier questions. All of this generated engagement with the subject at many levels: from questions that gave us a reason to organize conferences to those that could be used at REUs to train the next generation. Knowledge cannot simply be left in books and libraries. If people stop using it and engaging with it, it gets forgotten.

With AI changing this pace, we can no longer simply assume that all of this will keep working on its own. We have to ask more explicitly what we value about mathematical activity and how to keep it going.

Often the value of mathematical activity can also be quite indirect. Suppose I teach a class about some advanced topic X. Along the way, I might explain or use a less advanced topic Y. The fact that Y is needed to get to X may underscore its general importance. Some students might come away with a better understanding of Y and go on to do something actually useful with it. They may never use X themselves, but teaching X gave me a reason to explain Y and show why it matters.

So most of our research results are not important by themselves. We can still be proud of our results and feel that we are doing important work. In fact, we are: our work keeps the academic flywheel turning. For example, no single result of mine is important on its own. But I hope that my work has at least inspired some students, or helped pass on ideas that were eventually used to do something that is actually important. And if that is not the case, I hope my results have at least generated questions that helped train students, who became mathematicians and trained other students who went on to do important work. Here’s to hoping…

No, math is not a sport

I take offense at the suggestion that math is like chess and that, if AI gets better at it, we can simply keep doing it for fun. Of course I enjoy mathematics, and many of us are competitive by nature. We might get a rush from solving a problem that others cannot. But what gives this competition its meaning is the larger goal of advancing the subject. We are trying to understand something and contribute to a body of knowledge that other people can use. We choose our questions, invent concepts, and change the way a subject is understood. The competition is part of this activity. It is not the reason for doing it.

When a problem has been solved, that changes what there is to contribute and may change which questions we choose to work on. This matters to someone who wants to help develop the subject. It also matters to the students we train, the research programs we build, and the people who may eventually use the ideas. Telling us (and especially younger researchers who aspire to make a difference) that we can carry on as a hobby does not answer the question of how this work, and the community that sustains it, should develop.

Math as a microcosm

I also think mathematics is an exemplary part of human culture, because we see so many fundamental questions in a particularly pure form: What is the value of human intellectual effort? What do we mean when we call someone a “genius,” and does this notion make sense at all? How do we credit an idea, and how do we distinguish the person who saw the right question from the person who completed the argument? Our answers shape how we recognize talent, train students, and decide whose work deserves attention. Of course, we sometimes get really worked up about this sort of stuff. But in the end, it’s a fascinating discussion, and mathematics is a relatively small world in which these questions can be explored and discussed openly.

There may be a rather strange and unexpected value that we bring to society here. Our interactions create stories that can be told: very personal stories about ambition, pride, generosity, loyalty, and the desire for recognition. These are concerns that everyone can understand, even if the mathematics itself is inaccessible, and they sometimes appear in rather extreme forms. There is almost something of Greek drama about it. Through particular people and their work, we can discuss what it means to devote a life to an idea, to be recognized for it, or to see someone else arrive first. In that sense, the stories of how we do mathematics can contribute to culture alongside the mathematics itself.

This relatively small world may also make us guinea pigs. That may not sound very comforting, but I think we should be open to experimentation—with new AI workflows, ideas about achievement and credit, hiring practices, and ways of working together. I would much rather see us try these things out in mathematics than in medicine. When trying a new research workflow, for example, we can choose projects where we have room to try an approach, inspect the result, and start again if it fails. We should do this openly and with care for the people involved, especially younger researchers.

Again, this goes well beyond math: AI is making some of our assumptions about human achievement unusually visible. We are one of the first groups affected by these changes. How we respond to this will be a model for other disciplines to follow. So we should really get this right.

It was never about the theorems

Luckily, I suppose, my field does not have that many high-stakes problems that may attract the attention of OpenAI or Anthropic. Well, Perelman already settled our Millennium Problem. Take that, AI! So far, I have mainly noticed the effects of AI through a few counterexamples to conjectures I was keeping an eye on, and an uptick in arXiv papers solving minor open problems. Some seem to come from students prompting public AI tools with a bunch of well-known open problems and publishing the ones they can solve, though I recognize that there is skill in using these tools well.

To be honest: I do not care very much about these problems themselves. I cared a little more a few years ago because their solutions helped me keep track of promising students and postdocs. What interested me was what solving these problems told me about the people behind the solutions. I also used to invite students and postdocs who solved these kinds of problems to our seminar. I did so because I expected that someone who had spent enough time with a problem to solve it would also have other interesting thoughts about our field. I can no longer make that inference from the solution alone. I may still scan some of these solutions for new ideas, but I don’t really have the time to do this systematically.

In fact, many of the younger colleagues I hold in the highest regard have never solved an advertised open problem. Instead, they have come up with their own questions and produced beautiful answers, often through a series of theorems that shed light on those questions. They have shown an ability to combine taste, technical skill, and a stubborn vision. You know a good researcher when you meet one. I will have to find other ways to assess junior researchers’ qualities, perhaps through more personal interaction, instead of counting the conjectures they have solved. I believe this is possible, and I am actually a little relieved. I’d much rather talk to colleagues about the big picture and find common ground in our intuition and vision.

Fewer papers, please!

This also makes me wonder whether we could put less pressure on people to publish. There was a time when students were not expected to publish papers before applying to graduate school. They were expected to spend time studying: reading textbooks, taking classes, going to seminars, and perhaps attending a local conference. At the end of their studies, they would write a thesis that brought together what they had learned. These theses sometimes offered a clearer, more coherent account of the material. They were a useful way of digesting research.

Unfortunately, this tradition has been pushed aside. Students are racing to publish as many papers as possible in the hope of getting into a good graduate program. These papers often need to be refereed, which creates a lot of further work. There are just too many papers. AI may change some of these incentives. A paper written by an applicant to graduate school will tell us less about the applicant if it could easily have been written by AI. The same may be true of papers by graduate students and more senior researchers. We may end up with fewer papers that we regard as substantial evidence of their authors’ abilities. In itself, I do not think this is a bad thing.

One serious paper per graduate student, and perhaps one paper every two or three years for a senior researcher, might be good enough. The rest could be “AI noise”: reproducing, generalizing, optimizing, or formalizing known techniques in slightly different settings. As long as we know what we are looking at and assign value accordingly, this might actually help us cut through the noise.

What should we value?

As I mentioned before, finding solutions to open problems has never been the real point of mathematics. But those problems gave us an incentive to engage with our field and come up with great new theories, techniques, definitions, concepts, and intuitions. Most importantly, solutions to open problems helped us gauge which of these ideas were powerful or meaningful. For example, in my own research, we have come to see Ricci flow as a powerful technique because of its role in proving the Poincaré conjecture (and various other conjectures). So we think of Ricci flow, in some way, as the right choice and attach some intrinsic value to it. We could come up with and study other geometric flows—some of my colleagues have, and it is a worthwhile endeavor—but as long as these flows don’t help resolve a well-known problem, they will never rise to the same level in our minds. By the way, none of this would change if AI came up with some sort of alternative proof of the Poincaré conjecture tomorrow (unless it was very simple). In our minds, there is a certain philosophical proximity between Ricci flow and 3D topology.

With AI in the mix, potentially finding solutions by brute force, this important gauge may become less reliable. So we have to look for alternative ways of judging whether our theories are meaningful. For example, we may have to do a better job of discussing alternative proofs. If a student comes up with new techniques that can be used to reprove a result previously shown by AI, then in many cases we should value this work and give it almost as much credit as if it had produced the first proof. I say “in many cases” because this may require a closer look at the arguments and perhaps a slightly more philosophical discussion of which approach is more meaningful. We have been doing this already to some extent, but I think we have to become better at it, more precise in our judgments, and more explicit in expressing these philosophical points of view. It will be less binary, with less emphasis on “approach X was used to solve Conjecture Y.”

We should also be more welcoming toward other forms of mathematical expression and other ways of recognizing value. Perhaps we could pay more attention to theories that have an impact on physics or computer science (and ask our colleagues in those fields for their opinions), or encourage students to produce software packages, formalizations, or other mathematical products—and value them similarly to proofs of conjectures. Many of these things are already done in some subfields, but not as much in others. Or perhaps we could run a competition for the best explanation of an AI-generated proof. These suggestions don’t ultimately have to become the norm, but I think there is value in trying them out and seeing what sticks.

Looking for breadth

One direction I would like to explore is a division of tasks in which a human supplies the ideas and the bigger picture, while AI helps with the long combinatorial arguments or iterations of tedious estimates. Perhaps there is value in deliberately seeking out problems that lend themselves to this kind of work. The human contribution would be to identify a promising problem, put it into a form where the remaining argument is feasible but tedious, and guide an AI through it. In this picture, AI supplies the breadth, while the human supplies the depth and identifies where that breadth would be useful. Part of the work might be learning to express a mathematical strategy clearly and economically enough for an AI to carry it through without losing the thread, especially as we move to more complicated problems.

Take, for example, a question I have always wondered about: is there a non-round Einstein metric on $S^4$? My understanding is that the question remains open even with $T^2$-symmetry, without further curvature assumptions. Under that symmetry assumption, the case of nonnegative sectional curvature is settled by Tianyue Liu’s work. Now fix a normalization, say $\operatorname{Ric}(g)=3g$, and suppose that $\lvert K\rvert<100$. Could one study the Einstein equation through a triangulation of the two-dimensional orbit space, with rigorous estimates that rule out incompatible combinations of geometric behavior on the triangles? In spirit, this might resemble a finite element computation, with the estimates and exclusions checked formally, perhaps in Lean. Maybe an extremely tedious combinatorial argument could narrow down the possible geometries, or even show that the round metric is unique within this class.

I have not worked out whether this particular approach is feasible. Finding estimates that make the computation rigorous, handling the boundary of the orbit space, and ensuring that the argument covers all possibilities could themselves require substantial new ideas. But that is part of what makes the question interesting to me: can we use our understanding of a problem to put it into a form where AI could help carry out an argument that would otherwise be impractical?

Even if the particular problem is not especially important, I think there could be a good reason to work through the whole process: identify a question, develop a strategy, guide the AI through the technical work, and understand and check the result. I would expect some version of this workflow to be useful in many disciplines. This is close to the original promise of “AI as a tool”: a researcher’s creativity and judgment give direction to work that AI helps carry out. The broader impact—in the ordinary sense of the phrase, not the NSF sense—could lie in learning how to make this process work well enough that others can use it for questions that matter to them.

Trying out crazy things

I think AI may give us a chance to try things that I would previously have waved off as unfeasible or “crazy.” For example, take a 100-page paper developing a theory for an equation X. Work through it carefully and identify the main mechanisms. Then try, with AI’s help, to generalize those techniques to a much more difficult equation Y. Much of the value in such a project would lie in understanding the original theory well enough to identify promising choices of Y. The final product might be a formalized proof. If the main techniques are already well explained in the paper about X, there may be less value in working through every technical detail of their application to Y. Perhaps the adjustments to Y could still be summarized in a companion paper.

I can imagine tremendous value in using AI to push a theory over a technical “hump.” I have often wondered about such possibilities, only to dismiss them because I could not see a feasible way forward. Now there may be a chance to give them a try. These projects might be particularly well suited to students. Students sometimes have new ideas that we as professors do not take seriously enough because we cannot imagine how to get through all the steps. AI may give them a chance to find out whether those ideas can work.

Set yourself a goal

My personal recommendation to students and young researchers is to try to find a long-term goal or dream: something you would really like to understand, beyond the next paper or the next application. It does not need to be a specific conjecture (it is probably better if it isn’t). It could be a class of objects or techniques you want to understand, an intuition you want to make more concrete, or a connection between two seemingly distant ideas. Of course, finding such a goal is not easy, but it is OK if it starts out vague or evolves as you learn more.

Having such a goal can give your research a direction. Partial results become parts of a larger story. When you present your work, for example in a job talk, you can tell a story that connects your results and conveys your motivation. It then matters less whether AI helped you obtain some of them, because you are following a path and using the tools available to you. And if AI helps you reach your goal sooner, then even better. Presumably, you chose it because you cared about the question. You will still want to understand every step along the way and explain the results as clearly as possible.

The future

I want to end with the advice I often give young people. If I could send a note to my younger self, it would say: worry less about the future, enjoy the present, and spend more time on the things you really care about. I realize that this is convenient advice to give from a tenured position, especially since my research is probably less affected by AI than that of many of my colleagues.

Still, I think there is usually more opportunity in the future than we can see from the present. I am trying to be optimistic: I think mathematics as a profession will survive, and that in 5-10 years we will have a much clearer picture of what our work will be about. Getting there may be painful. There will be contentious discussions, and math might look quite different by the end. For now, we are going through a period of uncertainty, and we cannot really predict what is waiting on the other side. We may have to plan for the next 1-2 years, rather than the next 1-2 decades.

In such times, I don’t see much point in choosing a field or a set of skills mainly because we think it will put us in the best position ten years from now. My advice is to follow your own interests, goals, and visions. Be a bit stubborn about them and listen less to other people’s advice—nobody really knows what is coming. Following your interests gives you a reason to work hard, acquire skills, and perhaps leave a legacy. I am optimistic that such efforts will find recognition. And with a little flexibility, you may be surprised by the opportunities that open up.