The Future of Research in the Age of AI

Published on 2026/10/01.

Thanks to Francis Bach and Edwige Cyffers for careful proofreading and suggestions.

1. Context and Positioning

Artificial Intelligence has made breathtaking progress in mathematics and computer science over the past four years, driven by the rise of large language models (LLMs). ChatGPT was launched at the end of 2022 and Claude in 2023; the end of 2024 then saw the arrival of the first so-called "reasoning" models, which marked a major turning point in the scientific capabilities of these systems. Technically, these models are training through reinforcement learning, which allows them to improve with less human supervision. Progress has been swift ever since: in the course of 2025, these models went past the level of a good high school student, then past the level of the International Mathematical Olympiad, before starting to solve major research conjectures in 2026. This has led the mathematics research community to a state of crisis as it braces with the prospect of automation.

There is much discourse around those topics nowadays by many wise researchers. As such, I do not feel desire nor legitimacy in trying to convince others of the route to follow. In particular, the attitude of researchers towards LLMs will naturally depend on their field and on their personal sensibilities, since these tools touch on the deep motivations behind our work, our very raison d'être. As such, I do not claim to give advice or pass judgment. I more modestly want to share my perspective, and hopefully to convey a dose of reasonable optimism.

So where am I speaking from? I am a tenured French civil servant, currently employed by INRIA as a research scientist. I therefore enjoy the privilege of lifelong employment. The ongoing changes raise fundamental questions about how researchers work, and how they are evaluated and hired. Obviously, these questions are easier to ask when one is not personally looking for a job in the short term. I work on the theory of deep learning, which puts me in a peculiar position at the crossroads of mathematicians and of LLM people.

2. Working Hypotheses

I present here four hypotheses that structure my thoughts about LLMs, either because they seem natural in light of recent developments (Hypotheses A and D), or because they lead to the most interesting evolution of research (Hypotheses B and C). In the next sections, the point will no longer be to discuss whether these hypotheses are relevant, but to examine their consequences, assuming they all hold together. This structure has been inspired by Terence Tao's "Mathematics in the age of AI".

Hypothesis A (Problem-Solving Capabilities): publicly available LLMs already surpass, or will within a few months, the problem-solving capabilities in mathematics and computer science of the vast majority of researchers, for a small fraction of their salary (let's say, up to €200/month). The discussion on the accessibility of such subscriptions is crucial, but orthogonal to my point here. Let me stress the notion of problem solving. It is certainly an important part of research in mathematics and computer science, but only a part, which leads us to the next hypothesis.

Hypothesis B (Capabilities Beyond Problem Solving): LLM capabilities will remain below those of experienced researchers, at least in the medium term (3-5 years), on two categories of tasks:

  • The dissemination of knowledge (consolidating and spreading knowledge within a research community, teaching, training students in research, science outreach, consulting for companies and public administrations, etc.). These tasks have a collective and social nature that makes them fundamentally human.
  • Potentially even more crucially, actually doing science: choosing research directions, the "good" problems to work on, modeling problems and their interaction with the real world, and interpreting numerical experiments or theoretical results.

When it comes to doing science, LLMs currently show much weaker capabilities than in problem solving. This can be related to how they are trained: reinforcement learning lends itself well to so-called verifiable domains such as math or coding problems, but less to "softer" tasks such as assessing the relevance of a piece of research, or open-ended exploration. Nonetheless, things could change if models keep progressing very fast across the whole range of intellectual tasks. In that case, the question of the relevance of human research becomes even more pressing, as explored in other essays. Conversely, if our hypothesis holds, then it paves the way for human-machine collaboration in research.

Hypothesis C (Acceleration Without Skill Erosion): it is possible to use LLMs to accelerate one's scientific output by at least an order of magnitude in the medium term, while still cultivating one's scientific skills. This hypothesis is central to current debates about the impact of LLMs on research, and it is worth taking the time to spell it out. The first part relies on the automation of a large share of the tasks we used to perform by hand: mathematical calculations, software implementation, making figures, literature search, etc. These tasks represent a large fraction of the time we devote to research, and LLMs carry them out much faster than we can. Think of turning a week into an hour. We will discuss later how to make the most of this time saving. Clearly, using the freed-up time to scale up our professional activity proportionally would hardly make sense (what would be the point of submitting a paper every two weeks?), while being truly alienating.

The classical objection is that the intellectual process at play in research, made of fumbling and trial and error, is the very heart of our activity. It is what allows us to truly understand the substance of our problem, and thereby to develop our scientific skills and appetites: a "taste" for "good" problems, intuition, guided serendipity, the pleasure of research. These skills are absolutely central to developing fruitful (human) research areas and synthesizing a coherent body of knowledge. If one believes that using LLMs in research is incompatible with developing these skills and appetites (a view expressed by a number of mathematicians, and put clearly by Hugo Duminil-Copin on the blog Proof and Prompts), then one cannot hope for a lasting acceleration of scientific progress through collaborations between researchers and LLMs. In that case, there would be no revolution in research: LLMs could be used naively to mass-produce results that are presumably true but do not translate into knowledge that can be absorbed and built upon, while more seasoned researchers would keep pushing the frontier of science, consolidating knowledge and opening new research areas.

The hypothesis we build upon is, on the contrary, that it is possible to automate a large number of manual tasks while still cultivating one's scientific skills. It opens the door to a much deeper rethinking of the way we work, since AI-assisted progress would no longer be confined to the convex hull of existing knowledge. While the validity of this hypothesis remains to a large extent to be demonstrated, I am reasonably confident in our ability, and even more so in that of the AI natives, to find ways to use these tools wisely. Obviously, some ways of doing things are counter-productive. For example, frontier labs solving high-visibility conjectures focus the debate on "solving mathematics", preventing the scientific community from taking ownership of these tools. On a more modest scale, asking an LLM for a ready-made solution to a well-posed research problem is not always the best way to develop one's intuition. Experimenting with the concrete use of LLMs to find the right ways to use them is crucial, and the success of this experimentation is a prerequisite for the rest of my argument here. This echoes the much broader question of the impact of AI on education, from elementary school up to PhD level. It is likely that some good practices that will emerge in education can transfer to research.

Hypothesis D (Collapse of h-Index): the system of career evaluation based on publications is collapsing. Computer science conferences, and increasingly mathematics journals, are overwhelmed by a staggering number of submissions. This puts the reviewing system under immense stress, dilutes high-quality work, and lowers the value attached to a publication.

3. Two Possible Responses to LLMs

In this section, I present two attitudes that seem reasonable at first sight, but which I will argue are not desirable under Hypotheses A-D. To keep things simple, these positions are presented in a somewhat extreme form; most people defend an intermediate position. Studying them is nonetheless instructive, to clear the way for a middle ground.

Response 1: Refusing to Incorporate LLMs into One's Work

This response stems from a number of objections or concerns (ecological, economic, social, political, moral, sovereignty, privacy) regarding the use of these tools. Some of these concerns relate to Hypothesis C (which we are therefore setting aside by assumption). The remaining concerns do lead to the defensible position of simply ignoring LLMs. Nonetheless, I find it hard to knowingly set aside tools that could lead to a massive acceleration of knowledge. This is in my opinion the heart of the distinction between art and science. The raison d'être (and the reason for the salary) of a scientist is to advance knowledge (including fundamental knowledge that does not lead to direct applications), by using the tools at their disposal within the framework of scientific ethics. One could perhaps imagine part of so-called pure mathematics turning into an art, funded by patrons and freed from any efficiency requirement. This is, however, not an economically viable model beyond a tiny minority of today's scientists, nor is it the horizon for which many of us chose to go into science.

Response 2: Accelerating for the Sake of Accelerating

The spectacular recent increase in peer-reviewed submissions demonstrates that we are already well within the era of over-abundance of research discourse. Because we are incentivized to always produce more, this makes the temptation of acceleration hard to resist (some would even say impossible). There is no need to dwell on the harmful effects of such an acceleration (which predates LLMs). However, we should emphasize that the structure of incentives will need to adapt to the over-abundance of publications. This is where Hypothesis D comes in: since producing papers becomes a commodity, their value for evaluation and hiring will mechanically collapse. This shift can happen fast, since evaluation and hiring partly follow market dynamics. One can expect mechanisms that reward quality independently of quantity (for instance assessing only the three best recent works as is already done in many top institutions). While this question of incentive alignment is important, we leave more discussion on that to others, and rather focus on a more optimistic and positive view for research.

4. A Desirable Future

The goal of this section is to sketch a desirable horizon for research: using LLMs as a superpower to accelerate the progress of science.

Let us take the example of neural network theory. The promise of the field is to leverage fundamental understanding to propose practical improvements towards efficiency, privacy, etc. Despite promising theoretical progress, these concrete outcomes are still mostly out of reach. Why this mixed success? It largely comes from the sheer difficulty of the exercise: studying a tractable problem already keeps us busy full time, and publishing such work is enough to demonstrate one's value as a researcher. It takes even more talent and luck to stumble upon an analysis that paves the way for tangible progress. We have all published work that we knew realistically had very little chance of leading to any downstream impact. I argue that LLMs give us an incredible opportunity: leveraging the acceleration of research to finally deliver the advances we have promised. What once seemed an unattainable prospect is within reach if LLMs explore the space of possibilities 10x or 100x faster than we could.

The optimistic horizon is that human researchers leverage LLMs to accelerate the development of their understanding and intuition, in order to identify and solve the central problems of their field. In practice, the ridge between that bright future and enslaving ourselves to churning out pointless papers ever faster will likely be narrow. Our ability to stay on that ridge will depend on the pace of publication, on how we collectively evaluate scientific productivity, and on keeping pleasure and serendipity at the core of the scientific endeavor.

This requires rethinking the way we work, publish, evaluate and train, within the research system put in place during the second half of the 20th century. It opens up unprecedented prospects for scientific progress, to which human researchers hold the key. From this perspective, the value of a well-funded (human!) research community increases: if automation shifts the bottleneck towards judgment, taste and verification, then human researcher time actually becomes more valuable. In other words, the cheap exploration enabled by LLMs increases the marginal return of an additional researcher instead of decreasing it.

This evolution will be gradual and should come from the community. I will simply list here a few avenues that can be applied at the level of an individual, a research group, or a community:

  • Significantly slow down the pace of publication. Stop publishing work that does not have a credible chance of addressing a downstream question or of being absorbed into the body of knowledge of one's field.
  • Use LLMs not only to solve problems that are already well posed, but also to explore the tree of possible formulations, in search of problems that are both solvable and "useful" (in the sense that they lead to fundamental understanding or downstream impact, or can be integrated into the corpus of the field).
  • Experiment with ways of using LLMs that leave us in control of our scientific output and allow us to develop or maintain our skills, without seeking to maximize short-term productivity. Not becoming the reviewer of solutions written by an LLM, but building solutions together. Formulating good practices regarding the level of assistance requested from LLMs, so as to benefit from automation without eroding one's own skills.
  • Draw inspiration from other professions (commercial airline pilots, for instance) that have faced the erosion of skills caused by automation: a doctrine for choosing the level of assistance, and recurrent unassisted practice.
  • Use formal verification tools (such as Lean or Rocq) to certify the outputs of LLMs and limit the cost of verification.
  • Put training back at the heart of the PhD, instead of productivity. A PhD student might initially be less efficient than an LLM, but they need to be trained to acquire the skills to pilot this superpower. Concretely, one can imagine gradually increasing the acceptable level of automation over the course of the PhD. This assisted skill development does not remove the need to regularly maintain one's skills throughout one's career.
  • Most importantly, keep having fun!