Last week, Shang-Hua Teng said that we are going to have a ”Big Reset” in mathematics. In theory, it should be good that mathematics is advancing so rapidly. In reality, it will harm many mathematicians. Everything we do will change over the next few years. Right now, we are living through a revolution. The purpose of this post is to discuss what we can do now to minimize the harm and misery.
What’s happening now
AI systems are now incredibly good at solving math problems. They are so good that reasonable people expect them to become better at problem solving than all human mathematicians. There is plenty of evidence that they can solve many problems that have stumped us for decades. Our understanding of what they cannot solve, or rather cannot yet solve, is not as good1.
People using AI systems are making progress on a lot of important problems. Three of the problems I thought I could contemplate over the next few years have been solved in the last two weeks. I don’t know where I’ll find the time to read the solutions to these and whatever gets solved next week. At least, in the case of these problems, people have taken the time to write careful and helpful expositions of the results2.
Some other problems have not received the same care. A lot of people who expect fame to follow the solution of open problems have been feeding every conjecture they can find into LLMs. Often they release poorly written solutions whose correctness is uncertain. Some are being very systematic about this. There are people using agents to scrape the web for conjectures, feed these conjectures into other AI agents, and dump the results.
This is likely to hurt the field. To the extent that these papers are wrong, they make it very difficult for anyone to write a paper that is correct. They might mistakenly believe that a problem has been solved. Or, even if they doubt a posted (probably not published) solution, they will feel the need to find the mistake in it before they publish their own work. And, we don’t just want solutions to problems. We want understanding. But, the perceived incentive to write a good solution goes down a lot when a poorly written one is posted. In order to do the work to write a clean exposition of a result, most people need to believe that they will get some credit for it. They need some ownership of the problem. They have that if they’ve solved it themselves, but they won’t if everyone can see the posted slop and they don’t know how many other people are working to refine it at the same time.
Sometimes it feels like people are playing the LLM lottery. Everyone can ask LLMs the same questions, but sometimes only one gets the answer. This can happen because LLMs are stochastic. Or, it can be due to some odd phrasing of the question. People who meet with success after making an unusual prompt are sometimes proclaimed geniuses of prompting. Others copy their prompting strategies in hopes of similar success. I suspect that in most cases these people merely got lucky in the LLM lottery, and have no more genius than someone who’s convinced that they’ve found the best slot machine in the casino3. When there is any benefit in some special prompt, it seems to be absorbed in the next release of any model.
Adjusting incentives
The leaders of mathematical disciplines need to adjust the incentives we provide to encourage the best behavior.
Our usual desire is to reward those who contribute the most to science.
I believe that the value of one’s contribution to mathematical fields is what you have done minus what what have happened if you hadn’t done it. That is, what did you add to the world? This unfortunately involves a counter-factual that we cannot measure. And it is probabilistic: we care about the chance it would have happened without you.
The easiest type of contribution to observe is leadership. We value people who set the agenda for their fields by convincing others to share their values of what is important to study. This is a social phenomenon, and less susceptible to hacking by AI. But, it’s not what most people do.
Most mathematical researchers solve problems. Some of these will be known problems, and some will be of their own devising. Solving known problems is the easiest path for young researchers to establish their reputations. If you solve problems that you’ve devised, then you have to convince others that both the problem and solution are of value. That’s harder to do4.
In the past, it was believed that the first person to publish a result should get credit for it. At least, we are likely to believe that person’s work was independent of anything that came later5. It created a huge desire and incentive to publish first.
We need to change that incentive.
It’s clear that results that can be obtained from one shot queries to an LLM shouldn’t confer much credit upon the one who wrote the query. We will also be suspicious of results that seem to result from short interactions with LLMs. It’s likely that many other people could have obtained the same result, and that the individual who did it first wasn’t critical.
I don’t fully understand how to operationalize this idea. We mainly learn about how someone obtained a result by reading the AI disclosure they include in their paper. But some will yield to the incentive to distort AI’s contributions. For better or worse, there are often signs that an AI did a significant amount of the work. The most prominent is poor writing in the style of an AI. While poor writing can also be the result of a rush to publish first, the amount of pressure to do so is proportional to how easily one believes others can obtain the same result6. Someone who writes a paper after just one interaction with an LLM will feel a lot more pressure than someone who found that an LLM couldn’t solve their problem without a lot of extra assistance. If someone writes a paper in an area that they don’t fully understand and never studied until the week before, we’ll doubt that their contribution was critical.
I’d like those who set the incentives, say by hiring, publishing, or awarding honors, to favor work for which we are confident the person involved was critical.
And, someone who merely pushes a button7 shouldn’t expect credit. Some people now ask an AI to solve a problem, and send the undigested response to an expert in the hope that the expert will clean it up and make them a coauthor. That’s inappropriate. The button pusher should expect an acknowledgment, but not to share credit.
AI Companies
When I first heard that an internal model at OpenAI had written solutions to many problems that no one had time to read, I thought that they should post those to a repository where everyone could read them. As you can tell, I now believe that this could do more harm than good.
A better approach would be, for the important problems, to find experts who are interested in the problems and the solutions, and to offer them the opportunity to write good solutions. Those who write the solutions will be the authors, and the companies will receive appreciative acknowledgements8. The unimportant problems won’t matter because anyone will be able to solve them when the next model is released.
What to publish
Here’s a suggestion for how to decide whether it is worthwhile to publish a paper: only do it if you would like to give many lectures on the work. If you aren’t excited about the potential of speaking about a paper, then you should focus on writing the papers that do excite you.
If everyone were to follow this rule, it would increase the average quality of published work and decrease the amount of work editorial boards have to do.
Grants
Grants are a very special sort of incentive. In the US, we give grants for work that people propose to do. These enable us to pay ourselves over the summer, to pay for graduate students and their travel to conferences, to pay publication fees, and now to pay for LLM usage. I feel that grant proposals in mathematical fields are often fictional. We say what we hope to do but do not yet know how to do. A proposal for research that is likely to succeed is almost by definition insufficiently ambitious. People who’ve done good work before are more likely to get grants because review panels believe they are likely to do so again.
It’s difficult to write a grant proposal in our new era. If you can concretely state the problems you are going to solve, a reader will wonder why an LLM hasn’t solved them already. And, if an LLM can’t solve them, they’ll wonder if you can. There has always been a risk that a reviewer of your grant proposal might steal your ideas, even if that’s highly unethical. One reason this didn’t happen often was because it was difficult. But now anyone who hears a vague description of your grant proposal might use an LLM to solve your problems. If today’s version doesn’t solve them, the next release might.
Everyone is going to have to be much more secretive about what they are planning to do. If you don’t absolutely need a grant, it might be better not to write a proposal right now.
In the long term, we are going to have to change how we award grants. We should probably give them for past success under the assumption that it will predict the future.
Advice until we reach equilibrium
Over at least the next year, a huge number of important problems will be solved. The deluge in our brains and inboxes will take a long time to absorb. Eventually we expect to reach a new equilibrium.
Until then, many of us will feel lost. We like to plan for the future by assuming it will look something like the past. That’s why people go to senior colleagues for advice. We are old and have seen a lot, so we can guess what might happen. Until now.
Here’s my best shot at advice.
Should students study math adjacent fields?
First, ask yourself if you like studying this field. Do you love it? If so, it’s probably worth studying it even if it doesn’t become your future career. Very few people who study math adjacent fields become professors or leading researchers. It used to be standard to advise students not to go to graduate school if they could do something else. We might revert to that standard.
There were two reasons we gave different advice over the last two decades. The first was that the field was expanding and there were many more jobs. The second was the belief that mathematical training is good training, and that anyone who was trained this way should be able to do plenty of useful things. I hope that is still true, but I’m not sure.
Advice for young academics
Many young researchers are in shock right now. A lot of them have planned their career around a few problems they thought the could solve, only to find them solved in the last few months by LLMs. If you believe that your contribution to the world is your ability to solve problems, then this is a difficult time.
I suggest using your abilities to solve your own problems. Think of things that would be exciting to do, and see if you can do them. Let LLMs help you.
They way you get ahead in academia is by being known for something. So, dream up an agenda of problems. Avoid competition by doing things other people aren’t think of doing. I don’t claim this will be easy for everyone (or anyone). Unfortunately, I recommend not telling too many people what you are planning to do.
Advice for everyone
Use LLMs and don’t use LLMs. I, and many people I talk with, find that when we start to rely too much on LLMs we stop being able to think as well as we used to. So, spend some time thinking without using LLMs. The block of time will depend on the person. I like to take LLM free days for certain problems. It’s how I have new ideas.
One colleague of mine suggested asking an LLM for ways to approach a problem, and then not pursuing any of those approaches.
If you hope to keep using your brain in the future, you should practice now.
And, plan for the future
Many people are writing amazing essays about what the future could and should look like. Two people who don’t blog sent me essays they shared with a few friends.
I’m joining this effort because I think it’s the best way to figure out what could happen and to try to steer the future in the best possible direction. I suggest following posts at Proofs and Prompts and Terry Tao’s Blog, What’s New.
Also, watch The Terminator and Wall-E, in that order.
Acknowledgements
I’ve discussed LLMs with many colleagues in the last few weeks. For this post, I am particularly indebted to Shang-Hua Teng, Jamie Tucker-Foltz, Roy Lederman, and Nils Rudi.
The First Proof Project is an attempt to measure the frequency of success.
I once knew a very successful trader who believed telekinesis could give him a slight advantage in roulette and craps.
There have been many results that I now love, but did not appreciate when they first appeared. I’m too embarrassed to name them.
But, many generous people have shared credit with others who later solved the same problem independently. This was especially true of work published on either side of the iron curtain that did not cross until long after publication.
although some very smart people are just bad at explaining their work.
See Henry Cohn’s essay https://terrytao.wordpress.com/2026/09/15/the-technical-debt-of-ai-generated-mathematics/
I’ll volunteer for the constant-factor approximation of sparsest cut. If that doesn’t pan out, I’d like graph isomorphism in polynomial time. Please pick me.