Statement of AI use: This letter has been written with the help of Claude. Sinisa provided the initial draft, and sharpened the argument and the citations in interaction with Claude Opus 5 High, used within Claude Projects. The entire chat is available at https://claude.ai/share/fc545e66-5222-4a82-b673-e2d8e3d7bbc4, and it’s inputs were this draft and this presentation in Croatian.
Dear young mathematician,
I want to share with you some thoughts on the future of mathematics.
I am writing because I sense that you are worried and afraid, and that you are asking what future there is for our field, and for you within it. Some of the most distinguished members of our community have given voice to exactly this mood in recent declarations and open letters.1 Their concerns are sincere, and many are real. But read together, these letters convey a sense of loss, and at times an instinct to turn the clock back. I see it differently. What we are living through is creative destruction, in which an old way of creating value is dismantled while a new one emerges.2 This is a major opportunity. Mathematicians are better positioned, and more needed, than at any point in history, I believe.
What we need to do comes down to three things. First, embrace AI, and shape its use in the interest of humanity and of the mathematical community, interests which I believe are fully aligned. Second, think bolder, asking questions that were out of reach until now and accepting what that implies. Third, put ourselves in the service of humanity, bringing our expertise in finding, describing and beautifying abstract structures to the many areas of mathematics, science, medicine and beyond where it is desperately needed.
1. Embrace AI
The order matters. First protect knowledge; then make mathematics efficient; then use AI as the foundation for effective collaboration, and with it for new models of credit, education, discovery and dissemination.
Protect knowledge. Use AI safely, as the leading enterprises already do, in controlled environments where your unpublished ideas are neither training data nor visible to others.3
Make mathematics efficient. Automate everything that can be automated. Mathematics is an extraordinarily inefficient enterprise, in how we retrieve information, do research, communicate and publish, and it has been ripe for transformation for a long time. Mathematicians spend a large share of their mental capacity on information that is now easily retrievable and on tasks that can now be automated.4 That capacity should be released and refocused on higher levels of cognition.
This will not leave mathematicians with nothing to do. AI can now settle hard, well-posed problems.5 But I agree with Peter Sarnak that AI is a long way from discovering genuinely new theories, that is, the abstractions, concepts and bodies of theorems through which we understand why things are true.6 That work needs human guidance. AI is a tool.
It follows that mathematics will have to change its system of values. Today the majority of the value we assign to a mathematical result is tied to its technical difficulty, and to that alone. This will now change. For example, if an off-the-shelf AI can prove a statement from a single prompt, that statement should perhaps be considered only a lemma. Other measures of a mathematical result’s “utility” will quickly emerge.7
Collaborate. AI makes possible effective systems of collaboration, and they are already emerging. Po-Ling Loh has proposed a publication model that rewards collective work by groups of experts rather than a race to publish.8 I would go further, towards partially closed, collaborative systems of AI-assisted research, with credit designed in from the start. Some fear this will make mathematics less open. It will not. Mathematicians have always built moats around their expertise, in how we write, in how our knowledge is organised and in our culture, and AI lowers them.9 The system of credit will have to adapt; that is a design problem, which will be solved hand in hand with the emergence of new notions of mathematical utility. The same holds for publishing, whose workflow has been outdated for decades and can now be re-engineered and prototyped quickly with the help of AI.10
2. Be bolder
We need to ask the questions we have been too scared to ask. Navier–Stokes is perhaps the best example.
On 8 September 2026, OpenAI released an AI-generated proof, formalised in Lean, that the three-dimensional Navier–Stokes equations with a smooth external force can develop a singularity in finite time: statements C and D of the Millennium Prize formulation.11 It is a remarkable achievement. But it establishes the existence of very special, isolated solutions, a set of measure zero in any reasonable sense, and tells us little about how fluids actually behave. Statements A and B, global regularity for the unforced equations, remain wide open and seem very far from solved. Because they are no longer needed to settle the prize, they are absent from the ongoing discussion of the result.
The question that truly matters, for mathematics and for the applied sciences, is a different one, namely to describe, in a suitable sense, the dynamics of the Navier–Stokes equation as a whole. I believe that understanding A and B will require exactly this. We are far from it even in two dimensions, without external force. As my friend Thierry Gallay has patiently explained to me, on the two-dimensional torus the flow relatively quickly organises itself into a finite set of Oseen vortices, and then into just two, which persist for a very long time.12 We can describe only special cases, for instance when the vortices are well separated.13 How vortices merge, and a full classification of the dynamics, are far out of reach. We lack even the language and the conjectures to formulate the question properly. In three dimensions it is almost certainly harder still.
More generally, our culture has rewarded incremental questions. Expert mathematicians have honed the crucial skill of choosing a problem that is solvable in reasonable time, yet worth pursuing for its mathematical utility. This skill now needs to be entirely reparametrised. Our goalposts must be far more ambitious, and we need to redefine what mathematical utility means.
Terence Tao has warned that AI is depleting our supply of good problems. In his view, problems are trivial to generate, but choosing those worth the effort depends on knowing a field’s difficulty landscape, and AI is flattening it.14 I disagree with the conclusion. AI will hoover up many of the problems we have been asking so far; by construction, most of them were incremental or not ambitious enough. But AI can also help us generate many, many new problems, and then, and this is the essential step, help us prioritise them by a new notion of utility, for mathematics and for humanity. The landscape is not disappearing. It is being redrawn, and it is ours to map.
3. Serve humanity
The key skill of mathematicians is more needed than ever, namely to find abstract structure in chaos, to describe it, and then to beautify it, that is, to make it sharp and precise, and therefore useful and ripe for the next level of abstraction. The complexity around us keeps growing, and so does the need.
Let me give an example. AlphaFold, for which Demis Hassabis and John Jumper shared the 2024 Nobel Prize in Chemistry, is universally presented as a triumph of AI. I read it differently, as a triumph of mathematics. Open the paper and the code and see what the algorithm is actually made of.
A protein is first encoded as tensors, namely a representation of its multiple sequence alignment, and a pairwise representation of every pair of residues. Building the alignment is a combinatorial search through genetic and structural databases for evolutionary relatives of the given sequence. The statistical signal extracted from it is coevolution, the tendency of positions that mutate together to sit close together in space.
The pair representation is then treated as a graph whose edges are updated in triangles, so that the inferred relations between residues i, j, k remain geometrically consistent, as the triangle inequality demands. Geometry enters through an orthonormal frame attached to each residue, built by Gram–Schmidt, with an attention mechanism designed to be invariant under the rigid motions of space, SE(3). The rotations of these frames are updated as quaternions.15
Probability is the language of the output. The first AlphaFold predicted, for every pair of residues, a full probability distribution over their distance (the “distogram”), turned these distributions into a potential, and found the structure by gradient descent.16 The final step of AlphaFold 2 is classical physics, namely a gradient flow minimising the energy of the Amber force field.17
The core structures rely on graph theory, differential geometry, algebra, probability, statistics and the calculus of variations. The learning machinery that fits them to roughly 100,000 experimentally determined protein structures is, in my view, the least novel ingredient of the construction. The breakthrough lay in finding, describing and beautifying the right structures. The same toolkit runs through the neighbouring work on protein design.18
Here is a challenge for you. Build an algorithm that matches AlphaFold’s accuracy using these mathematical structures together with classical, transparent statistical and optimisation tools, with no black box. I am convinced this is feasible. It may open the door to far more ambitious questions about protein interactions and reactions. It would also help explain why so many attempts to carry AlphaFold’s success over to other problems in chemistry and biology have disappointed. They copied the black box and neglected the step that mattered, namely recognising and describing the structure inherent in the problem.19
The same programme applies far more widely.
First, mathematical knowledge itself. We need better structures for it, optimised for retrieval and discovery. That is certainly not arXiv. Nor is it Lean, since the power of mathematics lies in hierarchical abstraction, not only in encoding truth. Lean is an excellent truth-checker, but nothing more.20
Furthermore, modern theoretical physics rests on mathematical foundations that are still not consistent. The infinities of quantum field theory are cancelled by renormalisation, which has never been made rigorous in the generality physics needs.21 Nathan Seiberg, one of the architects of modern quantum field theory, stressed again this spring that, despite its enormous success, the theory still lacks a satisfactory, mathematically rigorous formulation.22 Where mathematicians have found the right structures, rigour has followed, and new mathematics with it.23 I believe that resolving these inconsistencies would open doors to a better understanding of physical reality.
Consider biology, chemistry and medicine. Clinical trials still rest largely on two-sample tests whose foundations are more than a century old,24 and most clinical guidelines are decision trees three or four levels deep. Even regulators now recognise that modern statistical methods, Bayesian methods among them, must become part of how trials are designed and judged.25 And no, AI will not solve this on its own. AI-discovered molecules now pass early safety trials at high rates, but efficacy trials, which depend on understanding the biology, far less so; and the leading structure-prediction models still reproduce their training data rather than the physics.26 We hold vast amounts of data about human biology and health, but by modern standards it is of extremely low quality and poorly structured.27 Before AI can help, someone must first find, describe and beautify the structures within it. That will be a mathematician.
Your time
So, my friend, young mathematician: do not despair. Learn. Use AI. Be brave. Reach lands that none of us has yet been able to imagine.
This is your time.
Received 7 October 202628.
- The Leiden Declaration (2 June 2026), leidendeclaration.ai; “A Severe Misalignment of AI in Mathematics” (11 September 2026), a declaration whose 25 initial signatories are all Fields Medallists, see terrytao.wordpress.com/2026/09/11; the open letter of 42 mathematician Fellows of the Royal Society to the President of the Royal Society, Sir Paul Nurse (September 2026); K. Ono, address to the National Academy of Sciences (2026), as reported by P.-L. Loh (note 8), predicting that within three to five years theoretical mathematical research will shrink to a small fraction, with the remaining academics working more like humanities scholars. ↩︎
- J. A. Schumpeter, Capitalism, Socialism and Democracy (1942), ch. 7, “The Process of Creative Destruction”; C. M. Christensen, The Innovator’s Dilemma (Harvard Business School Press, 1997). Christensen’s mechanism fits mathematics closely, since incumbents fail because they keep optimising what their established audience values (for us, technical difficulty) while a new entrant redefines what is valuable. ↩︎
- Leading enterprises deploy AI in controlled environments in which prompts and data are isolated and not used to train models, for example through managed cloud services such as Amazon Bedrock. The need is not hypothetical. In September 2026 the race to the Navier–Stokes result was triggered by a rumour about unpublished work, and OpenAI subsequently published an investigation into whether user inputs could have influenced its result (note 11). Tao has warned that even the rumour of someone working on a problem can now trigger a massive AI-powered effort to “flatten” it (note 14). ↩︎
- Anyone who has spent days or weeks verifying the precise statement of a needed technical lemma, reconstructing the exact meaning of every object through several layers of hard-to-retrieve published work, knows how much of our mental load goes on retrieval and bookkeeping. This is precisely the work that can now be automated. ↩︎
- In May 2026 an OpenAI model disproved the Erdős unit-distance conjecture, a question some eighty years old; the disproof was verified by outside mathematicians including Tim Gowers (OpenAI, “Model disproves discrete geometry conjecture”, May 2026), and within the same week Anthropic’s Claude Mythos produced an independent proof (Decrypt, 9 September 2026). On 1–2 August 2026 OpenAI released results by its unreleased Astra model on ten problems open for at least a decade, including three Erdős problems, each with a Lean 4 proof and a 249-page manuscript; peer review is pending, and mathematicians have noted that some results lean heavily on earlier work. On 10 August 2026 Anthropic reported that an unreleased Claude research model raised the proven lower bound for the proportion of zeros of the Riemann zeta function on the critical line from 41.6% to 67.2%, with a Lean formalisation, examined by Brian Conrey and Dan Goldston (anthropic.com/research/riemann-zeta). On 7 September 2026 L. Alpöge and T. Buckmaster, working with Claude and other models, released a blow-up result for the forced Euler equations, and the next day OpenAI released its Navier–Stokes result (note 11). ↩︎
- P. Sarnak, “Peter Sarnak on ‘The AlphaZero Test’ for Mathematics”, Notices of the AMS 73(7) (2026), doi:10.1090/noti3373. In the test, one gives a theorem prover with no access to outside data or theory an elementary statement, such as the Ramanujan conjecture in Ramanujan’s own formulation, and asks whether it is true. Sarnak predicts failure for most theorems whose proofs rely on abstraction and on the bodies of theorems we call theories; in his view AI will do mathematics as Stockfish plays chess, not as AlphaZero does. ↩︎
- On the shift in values see H. Cohn, “The technical debt of AI-generated mathematics”, and G. Sanderson, “If math is more than proof, we need to better celebrate the rest of it”, guest posts on terrytao.wordpress.com (15 and 18 September 2026). Tao has proposed labelling certain problems “analysis-required”, so that a bare answer without illuminating reasoning counts for little (note 14). I welcome these proposals; my point is that new measures of utility should be designed deliberately, not only defensively. ↩︎
- P.-L. Loh, “AI, From Competition to Collaboration”, IMS Bulletin, 1 September 2026. Loh proposes journals that accept only papers produced jointly by a sufficient group of experts in a sub-area, lightly reviewed for significance by researchers from another area. The precedent is the Polymath project: T. Gowers and M. Nielsen, “Massively collaborative mathematics”, Nature 461, 879–881 (2009). ↩︎
- The moats are cultural. We write up novel research with a premium on elegance, which partially hides or camouflages the reasoning that led to it. Our knowledge is organised in ways that are hard to navigate (note 4). We also celebrate solitary secrecy; Andrew Wiles worked on Fermat’s Last Theorem in near-total secrecy for about seven years (S. Singh, Fermat’s Last Theorem, 1997). One can argue that AI is making mathematics more open and accessible, not less. ↩︎
- The IT systems used by most mathematics publishers are obsolete, and the workflow of submission, refereeing, revision and typesetting has barely changed in decades. New workflows and systems can be prototyped relatively quickly with the help of AI. ↩︎
- OpenAI, “On the Navier–Stokes Millennium Prize Problem”, 8 September 2026, with a paper and a Lean formalisation. OpenAI states that the result establishes statement C (and D) of the official problem description (C. Fefferman, claymath.org); it does not intend to claim the prize, and the Clay Mathematics Institute continues to list the problem as active. Statements C and D allow a smooth external force; A and B (global regularity on ℝ³ and on the torus) concern the unforced equations and remain open. See also L. Alpöge and T. Buckmaster (7 September 2026) on blow-up for the forced Euler equations, and OpenAI’s companion result on the unforced Euler equations. ↩︎
- T. Gallay, personal communication. The numerical picture goes back to W. H. Matthaeus et al., “Selective decay and coherent vortices in two-dimensional incompressible turbulence”, Phys. Rev. Lett. 66, 2731 (1991). On the Oseen vortex as the universal long-time attractor in the plane, see T. Gallay and C. E. Wayne, “Global stability of vortex solutions of the two-dimensional Navier–Stokes equation”, Comm. Math. Phys. 255, 97–129 (2005). ↩︎
- T. Gallay, “Interaction of vortices in weakly viscous planar flows”, Arch. Ration. Mech. Anal. 200, 445–490 (2011). ↩︎
- T. Tao, Mathstodon post, 8 September 2026, reported by Decrypt, 9 September 2026. Tao answers the objection that infinitely many problems exist with the analogy that a region can suffer a shortage of drinking water while surrounded by ocean. See also his curated summary of views at teorth.github.io/tao-web/ai-views.html (updated 17 September 2026). The prioritisation step I propose is aimed at exactly this point. ↩︎
- J. Jumper et al., “Highly accurate protein structure prediction with AlphaFold”, Nature 596, 583–589 (2021), and its Supplementary Information (Algorithms 21–23: rigid frames by Gram–Schmidt, invariant point attention, quaternion backbone updates); code at github.com/deepmind/alphafold. Hassabis and Jumper shared the 2024 Nobel Prize in Chemistry with David Baker. ↩︎
- A. W. Senior et al., “Improved protein structure prediction using potentials from deep learning”, Nature 577, 706–710 (2020). ↩︎
- AlphaFold repository, Amber relaxation step: energy minimisation with OpenMM. ↩︎
- J. Ingraham, V. Garg, R. Barzilay and T. Jaakkola, “Generative Models for Graph-Based Protein Design”, NeurIPS 2019. Local frames, quaternions, autoregressive probability and likelihood-based statistics all appear there. ↩︎
- A black box that reproduces its training data, without capturing the structure of the underlying problem, works where a new case resembles what it has seen and fails where it does not. The first two examples apply AlphaFold to neighbouring questions; the last two concern its extension to protein–ligand complexes.
(i) Mutations. A single amino-acid change barely alters the sequence but can unfold a protein. A model that had captured the physics of folding would register this; a model that matches sequences to known structures returns the familiar fold. The AlphaFold database itself states that AlphaFold has not been validated for predicting the effects of mutations, and for five patient variants of antithrombin with documented folding defects it returned the native structure every time (“Analysis of AlphaFold and molecular dynamics structure predictions of mutations in serpins”, PLOS ONE, 2024).
(ii) Proteins with two folds. Some proteins switch between two distinct structures. D. Chakravarty et al., “AlphaFold predictions of fold-switched conformations are driven by structure memorization”, Nat. Commun. 15, 7296 (2024), show that AlphaFold finds the second fold when it is present in its training data, not by inferring it; it recalls rather than explains.
(iii) Ligands. M. R. Masters, A. H. Mahmoud and M. A. Lill, “Investigating whether deep learning models for co-folding learn the physics of protein–ligand interactions”, Nat. Commun. 16, 8854 (2025), mutated or removed the residues that hold a ligand in place, so that physically it could no longer bind. AlphaFold 3 and similar models often still placed the ligand in its original pose, reproducing a remembered complex rather than the interaction.
(iv) Prospective drug screening. In “Large scale prospective evaluation of co-folding across 557 Mac1–ligand complexes and three virtual screens”, eLife reviewed preprint (March 2026), co-folding succeeded roughly in proportion to how similar a target was to its training structures, while classical docking, which models the physical interaction explicitly, performed surprisingly well. In every case the model is reliable only within the range of what it has already seen. ↩︎ - Tao has observed that once a well-curated database of precise problems exists, others can build on it systematically, by human and AI means alike (terrytao.wordpress.com, 22 January 2026, on the Erdős problems database), a small precedent for what better structures for mathematical knowledge could achieve. Formal verification is becoming routine; in September 2026 a formalisation of the proof of Fermat’s Last Theorem was reported (Decrypt, 9 September 2026). This is why structure and abstraction, not truth-checking, is the scarce resource. ↩︎
- “The Yang–Mills Millennium problem”, Nature Reviews Physics (January 2026), nature.com/articles/s42254-025-00909-2. On the gap between physical belief and proof, see also M. Aizenman and H. Duminil-Copin, “Marginal triviality of the scaling limits of critical 4D Ising and models”, Annals of Mathematics 194 (2021), show that the simplest interacting scalar theory in four dimensions is trivial in the continuum limit, while four-dimensional Yang–Mills theory is widely believed, but not proven, to exist and to have a mass gap. ↩︎
- N. Seiberg, “What Is Quantum Field Theory?”, lecture at the annual meeting of the Simons Collaboration on Probabilistic Paths to Quantum Field Theory, 30 April 2026. In the abstract of his lecture of the same title (Van Winter Memorial Lecture in Mathematical Physics, University of Kentucky), Seiberg states that despite enormous success we still do not have a completely satisfactory presentation of the theory, and that it is not yet mathematically rigorous. ↩︎
- A. Connes and D. Kreimer, “Renormalization in quantum field theory and the Riemann–Hilbert problem I”, Comm. Math. Phys. 210 (2000); M. Hairer, “A theory of regularity structures”, Invent. Math. 198 (2014). ↩︎
- Student, “The probable error of a mean”, Biometrika 6, 1–25 (1908); R. A. Fisher, The Design of Experiments (1935). ↩︎
- US Food and Drug Administration, draft guidance “Use of Bayesian Methodology in Clinical Trials of Drug and Biological Products” (January 2026), addressing Bayesian primary inference in pivotal trials. ↩︎
- M. K. P. Jayatunga et al., “How successful are AI-discovered drugs in clinical trials? A first analysis and emerging lessons”, Drug Discov. Today 29(6), 104009 (2024), report 80–90% success in Phase I, about 40% in Phase II, comparable to historic industry averages. An analysis presented at ASCO 2026 counted 117 AI-enabled therapeutic assets in human trials, of which only 8 had completed Phase 2. A 2026 review in Frontiers in Pharmacology (doi:10.3389/fphar.2026.1870527) concludes that AI compresses discovery timelines but that important gaps, particularly in safety prediction, remain. On structure prediction see note 19. ↩︎
- Drug Target Review, “AI in drug discovery: predictions for 2026” (April 2026), identifies data quality as the primary technical barrier. ↩︎
- The post was written on 21st September. As of 19th October, the author’s views stated in the post have not changed. ↩︎

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