Grant Sanderson (@3blue1brown) – AI disproved a famous math conjecture. Now what?

1h 33m 469K views 30 Jun 2026

AI is discovering new proofs. Is that AGI?

You said it'll be another benchmark, like all the others AI are passing. AI has gotten better in a general way, but there won't be some "aha" moment when this happens.

Three years ago, the spirit of your question regarding the IMO was how some solutions seem to require creativity, as designers try to create problems you can't train for easily. The dirty secret is that you really can train for a lot of them. With the AI and math project underway, it's interesting because there's a spiky frontier to AI, and math is one of those spikes. There's a fractal nature to that spikiness; when you zoom into progress within math, some things are easier than others.

In 2024, they would have gotten a gold if not for one reason: they basically cold-solved geometry. The IMO has four categories: geometry, number theory, algebra, and combinatorics. Since 2024, it solves geometry in nineteen seconds because it's a brute force solver. Combinatorics is the wild card, with more playful, puzzly-seeming problems. There are four categories and six problems, so it's a toss-up which one has two questions. Had there been more geometry questions, they would have gotten a gold, but it struggles on combinatorics. Someone trying to keep the torch of the last holdout of math for humanity might say those require more creativity.

Your question—if they're solving a Millennium Prize problem, does that also service a lot of white-collar work?—suggests that whatever the rate limiter is between where we are now and that is the same as the rate limiter for white-collar work. If we focus on the Riemann hypothesis, what would it look like to solve that? These things are extremely good at knowing specific domains of knowledge very deeply. It's bizarre to have superhuman breadth across all fields yet not find those lightning bolts that connect them, though I think we're starting to see sparks of it finding connections between the things it's an expert at. If the nature of the solution to the Riemann hypothesis was something like that, it feels distinct from what's necessary to get good at white-collar work. I don't know if you know the story of Hugh Montgomery and Freeman Dyson at the IAS.

A number theorist was trying to understand the statistical correlation between pairs of zeros of the Riemann zeta function—the Riemann hypothesis is about whether all these zeros sit on a straight line. Freeman Dyson, a physicist, recognized the expression from studying the eigenvalues for random Hermitian matrices, which relates to the energy levels of a nucleus. The idea that the statistics of these two different things were the same prompted an exploration of whether random matrix theory might be relevant to the Riemann zeta function.

Bridging two different fields like that is how you expect LLMs to be good at math; they should see that similarity without needing Montgomery and Dyson to happen to talk about it over lunch. If you have a hard time using an AI as an editor, it's not because they know everything and you just need them to find that lightning bolt.

Consider Fermat's Last Theorem: between Fermat phrasing the question about integer solutions for xⁿ + yⁿ = zⁿ when n is bigger than three and the actual solution, there is heavy machinery involving centuries of work on elliptic curves and another mountain of ideas centered around modular forms. If the solution to the Riemann hypothesis involved building a new mountain—the ability to come up with the right new ideas—that feels different from how AI is intelligent right now.

If AI is capable of building mountains and crystallizing how we should think about a subject, that level of intelligence would likely permeate the economy beyond math. Even if it couldn't do everything white-collar humans do, it would have transformative effects, unlike getting gold in the IMO. A moderately intelligent person with that much information could come up with a medical diagnosis by seeing that one drug causes migraines and another thing does something else, and realizing the same drug could cure both.

From an outsider's perspective, finding the counterexample to the unit distance problem conjecture is a prime example of two distinct abilities: coming up with interesting problems and creating new objects or conceptualizations that unify fields. Regarding the former, we have the Millennium Prize problems because mathematicians noted them. Riemann created the Riemann zeta function because he believed its zeros connected to the density of prime numbers. The next benchmark is figuring out why we think something is interesting to study, why we build a specific object, and why we seek a particular answer about it.

For those curious about the unit distance conjecture, a video by the channel Polylog highlights a quote: "good mathematicians prove theorems, great mathematicians come up with conjectures, and the greatest mathematicians come up with definitions." That is exactly my framing; we need the conjecture generator and the definition generator.

We need to be able to say, "Yes, this is done," partly for RLVR and partly to ensure we haven't moved the goalposts. OpenAI can have a headline on disproving the unit distance conjecture because it is a clear, distinct achievement, whereas a headline about GPT-5.4 coming up with a "really good" conjecture is different. I would be surprised if conjecture-generating ability ever took the form of a quantified benchmark score.

Instead, you would feel a tone shift in conversations with mathematicians about how useful the AI is. We started this over a year ago, and it is fun to see a tone shift between mid-2025 and now in 2026. Measuring this ability will be more subjective, based on mathematicians saying they are not just using it to solve problems, but that a conversation with a model was genuinely helpful as they stepped back to decide what their research field should even be.

The verification loop on conceptual breakthroughs can be a century long

The things you can't make benchmarks for are also the things you can't easily train for in the current paradigm, as there is no fundamental difference between a benchmark and a training environment. We will probably find ways to train AIs to do these things in the near term, but it would have to be different from current RLVR training.

I am curious about what drives big progress in mathematics and science: coming up with a new way to think about a problem or understand the world that unifies different fields, spawns new fields, and solves problems we weren't even trying to solve. Einstein didn't think about GR because he wanted to explain why light bends or why black holes exist. In mathematics, some ways to prove a specific problem motivate a new, immensely productive conceptualization, while others don't. I'd be curious to hear about Galois coming up with group theory—which later became relevant to cryptography and understanding symmetries in physics—and how that distinguishes his solution to the quintic from Abel's different proof a few years earlier that didn't produce group theory.

You struck a nerve; I spent a year in 2022 thinking about Galois for a project I eventually shelved. It is a perfect example because the value of his insight did not come from immediate utility. This would be really hard to do with RLVR environments, and even with human verifiers, it took a long time to recognize it as useful. Unlike Einstein and GR, where people felt it was a good theory right away, Galois theory had a hundred-year segment of an idea flowing through many people's heads before the math community agreed it was good.

We all learn about the quadratic formula in school. The Greeks could solve quadratics, but they didn't write in algebra; the Arabs wrote down that formula. There is a delightful story about dueling Italian mathematicians who secretly found a formula for the cubic, and shortly thereafter, a formula for degree-four polynomials. Since the degree-four formula is a monster, one might believe these things have exponentially increasing complexity, making the search for a degree-five formula a natural open question. Abel, a precocious young Norwegian mathematician, is usually credited as the first to prove it is simply impossible. However, the real credit goes back to Lagrange, who found the right question to ask by recognizing that solving these polynomials is closely related to understanding how certain algebraic expressions are symmetric.

If I write down a, b, c, d and permute those four variables, it doesn't change the value of the expression. Lagrange had the insight that if you find expressions with four free variables where all permutations take on three distinct values, there is an unexpected relationship with reducing degree four into degree three. He wondered if he could extend this method to find a quintic polynomial, which would require an expression with five free variables that takes on four values or fewer over all five factorial permutations.

Lagrange realized this strategy might make finding a quintic polynomial impossible. This was the first time in history people had the instinct that symmetry was the right way to study these polynomials, suggesting that rather than searching for a formula, we should ask if it is impossible.

Around fifty years later, Abel read and was influenced by Lagrange. Galois also loved Lagrange when he was falling in love with math. It is hard to imagine these two geniuses coming up with similar insights without Lagrange's influence. Abel worked on quintics but was advised to study elliptic functions, which he did before dying of tuberculosis at twenty-six.

Galois pushed both ideas toward a true understanding of abstraction. As a teenager in prison, his math papers were rejected by the academy, the verifier function of the time. He spoke of the advent of algebra itself, moving from numbers to a fluency with pure algebraic expressions. He sensed another layer of abstraction: thinking about the symmetries underlying formulas rather than the formulas themselves.

While Abel had already proved quintics are unsolvable, Galois theory lets you take a specific polynomial and determine if its roots can be written down. For x⁵ - 1, a solution is 1; for x⁵ - 2, it is the fifth root of two. The question is whether you can find a specific quintic where you prove the solution cannot be written using radicals.

There is a romantic myth that Galois wrote up all his ideas the night before a duel, but he had actually tried to get them published five times before.

He asked his brother and close friend to get his notes to Gauss and other important mathematicians because he believed there was something there. It took twenty years for Liouville to see those notes and try to understand what Galois was getting at, and another twenty years before Jordan put together a modern treatment of group theory attributed to Galois. History could have turned differently; these ideas might have emerged from other points in math, and Galois could have been forgotten if he were a less florid character.

There is a long span from Lagrange's inkling that symmetries of roots were the right path to modern group theory. You must reach the twentieth century before Gell-Mann considers how the breakdown of certain groups relates to what particles are made of, anticipating quarks based on a purely group-theoretic question.

Similarly, Fermat's Last Theorem could have an incoherent elementary proof spelled out over thousands of pages, but the cleaner view uses elliptic curves. There might be a thousand-page proof of the Riemann hypothesis that yields nothing, whereas we want succinct, compressed versions that lend themselves to human understanding. You might use Kolmogorov complexity to quantify elegance. I don't think it's easy, but it is necessary to reward the Galois-like instinct rather than just the act of solving a problem.

Even with a thousand-page proof or a grand new physical theory, the goal is understanding. If the goal is merely predictiveness, automated engineers could build rocket ships to travel between stars without us knowing how they work. Yet, you still want a concision function to distill complicated thinking into the right one, like Newton's universal law of gravitation. We should train AIs to find that compressed representation, as people worry that AIs will prove the Riemann hypothesis without improving our understanding of mathematics.

Will we understand an AI proof of the Riemann hypothesis?

Isn't the reason humans create general, natural objects and subgoals when working on a big problem simply because it's useful for complicated, important problems? Theoretically, would this be a simpler way to solve the Riemann hypothesis than just coming up with the relevant natural abstractions?

When the AI found a counterexample to the unit distance conjecture, you could read its chain of thought. While not understandable to me since I know nothing about mathematics, it seemed understandable to other mathematicians. It used known mathematical concepts and proved relationships between them in natural language, accelerating our understanding of the connection between that object and the conjecture.

I think it depends on the nature of the solution. Another big example from this year was Erdős problem 1196 regarding primitive sets, which brought in an idea from a seemingly different field. If you present the basic idea to a mathematician—asking what if we try a Markov chain process to show this thing is one from the bottom up probabilistically rather than top down, using the von Mangoldt function—you have a small idea that draws a lightning bolt between expertise in one field and another. Those are human-parsable because you only need to show the start and end points of the connections.

If the character is mountain building, you must spend more time understanding that new thread. If the progress is raw hustle—a super long chain of reasoning with no new theories—you worry about the digestion process. Or, it could be an alien kind of mountain where we must reprocess our abstractions. The closest example is the attempted solution of the abc conjecture by a reputable mathematician in Japan. It took mathematicians a long time to parse his inter-universal geometry, which felt like an alien bit of theory building rather than a long chain of reasoning.

If we end up in that situation, David Bessis wrote a great blog post called "The Fall of the Theorem Economy." He argues that while mathematics historically involves creating definitions and problems and proving theorems about them, the theorem-proving that gets all the credit is actually a parasite on the creation of definitions.

Historically, credit apportionment hasn't been a problem because if you define a concept, you're likely the one to prove the theorem. But now, if AI automates the latter part, the valuable work becomes the insight. Imagine an AI producing Abel-like direct arguments for important conjectures, leaving us with proofs we simply possess.

In recent math history, the reach has often exceeded the grasp, with things proven long before they are understood. One of my favorite openings to an expository paper is by Timothy Chow, who was trying to understand forcing—a concept related to the continuum hypothesis, which asks about the sizes of infinity for natural versus real numbers.

Incentives in mathematics and other sciences would have to shift from proving things about the world to consolidating proofs into higher-level insights. For example, special relativity, spacetime diagrams, and Minkowski spacetime illustrate why length contraction and time dilation occur.

There seems to be a strong correlation between those who produce genuinely novel insights and those who communicate them clearly. You might imagine the opposite, as university students often find that experts are not the best explainers because they are spoiled by their own expertise.

People who come up with something truly novel—like Einstein or Claude Shannon—write lucid papers. Feynman had this characteristic too; he was a very good expositor. Perhaps the same part of the brain that discovers a correct new way of thinking at a research level also has a knack for good explanation.

I used to think AIs would become automated theorem provers while the role of mathematicians shifted toward my job of explaining. Now I suspect AIs will also be quite good at distilling and explaining, probably better than most humans.

You build a man a fire, and he's warm for one night. But set a man on fire, and he's warm for the rest of his life. Part of a teacher's function is adding clarity to a curiosity, but some of it is more relational, providing motivation and curation.

I've heard an interesting take that mathematicians will become analogous to art museum curators. The AI solves the problem, so the art exists, but you still want someone to help you navigate the nearly infinite space of which ideas are worth engaging with. Even if AIs were better at that, we would prefer a human we have a relationship with because motivation is a social phenomenon. My role, and that of other mathematicians, might shift into that curation of what ideas are worth pursuing. It's the same reason human musicians will always have a role: the social function of the story behind them, even if the objective quality of an MP3 file from a model is better.

Can AI find the hidden bridges between fields?

Now that AI has crossed the benchmark of connecting existing ideas to make discoveries or prove and disprove things, we must ask what comes next. I believe there is a flourishing future of connecting. With general relativity, you are just connecting Riemannian geometry and special relativity; as AIs improve at this, many big breakthroughs may not be of a different qualitative nature.

Much of the conversation focuses on problem-solving, like ticking off Erdős problems, but a majority of mathematicians would not characterize their work as targeting the next problem to tick down. That is a research ethos, not a field of math. Fermat's Last Theorem is one inkling of this, where a connection between two seemingly disparate things led to a solution. The mathematician Langlands wrote a famous letter spelling out how likely it is that more connections like that exist. He described a large map with a valley, a mountain, and plains; many mathematicians see their work as trying to understand the threads on this map. Time and again, big problems were knocked down by finding connections, so the goal is almost preemptively finding them. Anytime you meet a mathematician, ask if their work is more akin to the Langlands program or to targeting one particular problem.

AI as a supercharged connector could be an amplifying tool in that pursuit. If an AI knocks down a problem, there is a clear way to say it succeeded, allowing an AI company to make a PR move. However, if it draws the right connection, you can write theorems around it. I guess most useful progress in the next five years will look like filling in that landscape of connections an expert in multiple fields can draw, though it will require a "human in the loop" to determine what connection we were going for.

Yet, autoregressive chain-of-thought reasoning is a weird way to produce results. Imagine being locked in a box where you only receive a slip of paper and must predict what comes next before your memory is wiped. That process of repeatedly predicting is different from how a writer composes and thinks through an essay. You become a slave to your context; answering a question about a particular field leads you to draw on that specific context. But the connections where the substance lies are, by nature, very unlikely. No matter how much RL you use, it is difficult to incentivize these unlikely connections when the vast majority of them are not the predictable next token.

Do you just need more intelligence so that, at the level of prediction, it predicts it should make that lightning bolt to another field? I think it's more productive to reason about data instead of architecture or loss function. Diffusion models produce text, and the results are not of a wholly different character. The relevant question is: what is the data on which your architecture or loss function is incentivizing you to produce?

If you look at why models are getting better at being autonomous agents, they are in an environment where autoregressively producing steps like "Let's step back and do a search over the whole codebase" or "Let's step back and assess my mistake" is what works. I assume progress in science or math happens because mathematicians specifically design frontier problems that require connecting two different fields. There are likely clever, partially synthetic ways to make harder problems require these connections—for example, by eliminating assumptions while still requiring the answer—and then the loss function doesn't really matter. It's about whether you can create an environment that incentivizes this ability. It would be surprising if there weren't more of those lightning bolts over the next three years.

In this context, the key fact is that we can parallelize and arbitrarily scale these models. Whatever capability they have is not just one idiosyncratic genius in the history of mathematics who makes a few connections and dies in a duel; it is universally applying that waterline across all accessible problems. This is among the many advantages digital minds inherently have that we don't think enough about, including the ability to merge all their knowledge together and spawn copies with identical levels of knowledge. Even if they aren't as smart as human mathematicians, AI companies are throwing billions of dollars at this for PR reasons, and quantity has a quality all its own.

Take the conversation between Montgomery and Dyson at the IAS suggesting a connection between the Riemann zeta-function zeros and random matrices; that feels like something you could automate with agents representing expertise in all those fields. People gather in the same geographic location for serendipitous conversations. Sometimes an AI fails because it gets into a bad chain of thought that is hard to exit. There are stories of people trying to prove something for a long time before asking, "What if I tried to prove that it's impossible, or prove the opposite?" You could systematize unwinding your own context and starting with a fresh mind, or have multiple agents given different pieces of context to compare and contrast.

In this AI and math series, the first episode will be about when they solved the IMO. I want to focus on one specific IMO problem that many smart students, including Terry Tao, failed on. People called it a troll problem, yet there is an almost brain-dead solution that is the best.

The relevance to the AI story is that answering that question requires a human to escape their context. A person off the street might answer it well if approached as a brain teaser. One advantage digital minds have is a more systematic approach to refreshing thinking. You can spin off two agents with deliberately different contexts—one trying to prove a statement and one trying to disprove it.

This is interesting because people worry about entropy collapse, where AIs think the same way due to similar training. However, AIs might increase entropy by systematically trying both the negation and the positive of any statement, or by giving different agents different biases. For example, the unit distance problem conjecture took so long to be disproven because people assumed it was true and mostly tried to prove it.

In human science, Einstein was motivated by the bias that things should look the same in different reference frames, as well as the bias that "God should not play dice." You can systematically survey heuristics to see which are productive, but you must ensure all your LLMs aren't Einstein, or you might halt progress on quantum mechanics. You need multiple independent research programs with their own heuristics.

If you put a clear ontology to the distinct ways of thinking you want to prompt and explore that full ontology, each individual agent can run with its task. The easy distinction is whether you are proving or disproving; the harder part is identifying all possible tactics to ensure sufficient breadth. AI in math is making faster progress than other fields, likely because the domain is so verifiable.

Why real-world tasks don’t fit into RL environments

Computers are extremely verifiable, but computer use lacks grindability. Because websites have bot detectors and parallel rollouts require tremendous compute, it's hard to run a thousand parallel rollouts of an Amazon checkout flow without being shut down by Andy Jassy. Building clones of every website is too labor-intensive and slows you down. We currently need so many parallel rollouts to learn a skill with deep learning because we haven't solved sample efficiency—sucking supervision through a straw, as Karpathy says.

With code, you can containerize a level of progress in a repository and spin out hundreds of parallel containers to implement a feature deterministically. This solves the credit assignment problem because you know the diff is what worked. If you start at different points, credit assignment becomes harder. Most real-world things are hard to containerize, but coding and math are exceptions. If you're building a business or trading markets, interacting with a changing real world means you can't keep replaying and farming the simulator. Progress in coding and math is driven not just by verifiability, but by the fact that they are grindable.

Some argue that Lean and formalization drive AI progress, but I feel Lean doesn't matter much for the current level of progress. AI disproved the conjecture about the unit distance problem without Lean in its chain of thought. Process-based supervision seems less relevant than having a grindable, verifiable outcome. Naively, you might think Lean is unique for math because it proves correctness, similar to how DeepMind initially used old-school software as a reward. Then, the next year, it was all in natural language.

There is a yet-to-be-explored benefit to formalization: currently, a human must review a counterexample to the unit distance conjecture, which bounds how endlessly explorable things are. AlphaGo and AlphaZero-style systems exist in their own universe, exploring Go with an automated verifiable reward. You never have to check in; you just pour compute into exploring the universe of Go. It remains to be seen if it will pan out, but with Lean, you could imagine an endlessly running program constantly trying to extend Mathlib.

Mathlib is a GitHub repository that aims to contain all of math written in code. You can ask if a proof is correct, though writing these proofs is labor-intensive. Imagine an AI tasked to simply extend Mathlib. You could have a fork of a pure AI Mathlib that grows an infinite tree of its own conjectures, theories, and definitions. While many might be useless, math uniquely allows you to pour compute into this for ten years and return to find something. I don't think you can do that with natural language math.

Lean is important here in two ways. Karpathy's auto research idea involved a Python file for basic LLM training where agents made modifications; if a change sped up the speed run, it stayed. Eric Jang did something similar when building a strong Go bot. This approach is good at running experiments but bad at stopping at dead ends or doing extremely parallel things, so you would likely want a supervisor model providing heuristics on utility.

Terry Tao mentioned a research project that exhaustively searches the space of possible algebras. Every now and then, a little island of a completely different axiom system appears that seems rich in the number of theorems it produces. Exploring that space to see which islands turn out to be something is the bread and butter of automated provers. Perhaps one of those islands is something you can retroactively provide motivation for to explain the structure it is getting at.

Imagine looking at the axioms for a group without knowing they concern symmetry, only to retroactively realize their relevance. You could imagine results of that flavor exploring all possible logical consequences of any kind of axiom, rather than just exploring algebra systems.

Regarding process-based supervision without Lean, DeepSeek had their DeepSeek Math model. Because you don't know if natural language proofs are correct, they use a verifier trained by a meta-verifier to ensure the verifier gives good feedback for problems in the art of problem-solving. Coding agents are also getting better at writing and refactoring clean code; I'm sure there are process-based "LLM-as-a-judge" systems providing taste on whether a function is written cleanly.

It seems more plausible to trust a verifier for math than anything else, even in natural language. If given two student essays, models could say which is more accurate and insightful, but they might fail to discriminate between an A essay and something you actually want to read—something insightful and followable on Substack. On the math front, knowing if a proof is correct lends itself to an automated verifier, even in natural language.

I still like the tree of logic from Lean because you can really go off the rails, similar to move 37 in AlphaGo. If you have pure natural language RL environments and proofs, Alex Kontorovich has noted that even if 99 out of 100 are right, it's too labor-intensive to find the errors. Every other field would kill for a green checkmark confirming a proof is correct, even if it's complicated and a pain to understand. If models can also formalize their natural language proofs, that seems huge. I also love the extension of Mathlib as a metaphor for what's going to happen to our civilization soon.

Good writing requires theory of mind that AI still lacks

For millennia, humanity has built a corpus of knowledge and understanding, and everything we have is now distilled into these models. These models are bad at judging A versus B because they get derailed by B*, a shitty essay that hits all the bells and whistles A is supposed to hit. Furthermore, writing is not modular like code and math. You can write a function or a mathematical lemma many different ways to achieve the same functional end product, but in writing, the end product is the substance itself. Each paragraph, sentence, and word matters; it cannot be slop the way code can be and still produce the desired outcome.

For much of the writing I consume, I find it better to copy-paste it into an LLM and say, "Explain this to me," as the explanation is often better than the human's original production. Even when talking to a human expert live, if they possess knowledge not encoded in the distribution, I want them to explain it to me. That explanation is distillation. If I want a book report, I might believe the LLM provides a better one.

This is where autoregression is a weird way to generate things. To be good, writing requires an element of the unpredictable—knowing exactly when to make an unpredictable move to be more insightful. A good author explores ideas and decides which aspects are interesting and how to present them in a coherent, well-motivated narrative. In that case, you would prefer reading their book over the distillation. That deliberate choice of something novel is directly contradictory to how these models typically produce text.

I think they are also bad at building good mental models of people, which is a vital skill in writing. Andy Matuschak and another collaborator did an interesting report where they tried to teach LLMs to write good spaced-repetition prompts.

I like this because even though it seems like a random skill, people talk about recursive self-improvement in a year, yet we can't get these things to write good flashcards. They tried RL on open source models, chain of thought, and big prompts sent to the best closed source model. The key constraint is that writing a good card requires projecting someone's mind three months from now. Writing is enervating because with each word, you must think: what is happening in my reader's mind right now? If I flip the phrasing so the end phrase goes to the beginning as the first image you see, maybe autoregression is bad at that. This is a diffusion-like property of considering the whole rather than going sentence by sentence, which requires mentalizing—something these models weirdly struggle at.

Consider tests for EQ where you see a facial expression and describe the emotion. There are good online tests with a face and four possible emotions; it's surprisingly hard to describe the correct emotion, but you sense there is one. People who are socially plugged in do well, while those who are more left-brain don't. I remember an experiment where people who got Botox were much worse at reading expressions in a post-test. The thought is that understanding an emotion involves mimicking it with your own face muscles at a subconscious level to realize, "Oh yeah, that's anxiety."

If models have bad theory of mind, it's not surprising. They know everything because they've read what everyone wrote, but they can't put themselves in your shoes the way my face muscles mimic yours. They don't have face muscles; their brain works differently. It's like an alien trying to empathize. How could it have theory of mind?

I did an interview with them this year, which was interesting because they usually aren't outward-facing. In the industry, they're known for a wild retention rate. One person commented that even though employees have titles like researcher, trader, or engineer, they often don't know their colleagues' actual roles because everyone does a bit of everything. Even if you're officially a trader, you're doing research; if you're a researcher, you're coding. I suspect that's part of why they have such insane retention.

Why learning will still depend on human curation

Often, just a couple of messages down, I'm trying to understand something and they're so confused themselves that they're confusing me. I know talking to the right human could clear up my confusion in three minutes. Even pre-LLM, a relevant insight in learning was recognizing who matters more than what.

My advice to any college student choosing courses: care less about your preexisting interests, because they're arbitrary right now, and care more about whether the person teaching is a good educator you resonate with. In choosing books, the author may matter more than a prior interest; if there's a book you've liked, read what else that author has written rather than another thing on that subject.

There's a difference in feel between learning from a Wikipedia page versus the Stanford Encyclopedia of Philosophy for philosophy or the Princeton Companion to Mathematics for math. In the latter, articles are deliberately written by one individual who crafts a motivation. On Wikipedia, a local minimum is reached where every sentence must be correct. In a good exposition, you care less about correctness on the way; you can deliberately craft things that are slightly wrong and correct them along the way, which gets edited out in a crowdsourced environment.

LLM explanations feel like Wikipedia: amazing, but it's often just the references at the bottom. I like to ask an LLM, "Who should I read?" I actually got gaslit by this once while learning about semiconductors. I felt it was a visual topic, but all the resources were text. I asked, "Is there a well-visualized video explaining the concepts you're getting at?" Claude said, "Yeah, here's a couple," and the top one was from 3Blue1Brown. I could guarantee there wasn't. It was an actual link, but it had misattributed someone else's video. In that sense, I'm using it like a souped-up version of Google to zero in on the right human-written resource.

The most productive learning sessions I've had are when a human-produced artifact—an article, book, or video—organizes relevant concepts in the correct way, building motivation for why the next idea is relevant to solving the next problem. Then you use LLMs to do a little pruning around the branch the book identified. I was going through Steven Strogatz's textbook, Nonlinear Dynamics and Chaos; it was like your videos in book form. I'd have his university lecture on one-third of the screen, the textbook on another third, and an LLM on the last third. He curated the right order to understand concepts and the right problems to motivate understanding, which is another thing LLMs are really bad at.

A really good human can say, "Actually, you're not thinking about this topic the correct way. The question you want to be asking, the correct way to organize these concepts, is X." An LLM can't do that; it's too placating. This is sycophantic behavior: "Oh, what an insightful question." This cuts to theory of mind, recognizing that a certain kind of question reveals the student's mental structures are not the same as the explainer's. In a middle school math classroom, if a student asks a question suggesting they're thinking about it in a different way, it's actually really hard to take that seriously in the moment and ask, "Hang on, could you get to a right answer with that?"

Instead of saying, "Let's do this," the really good teachers jujitsu the creative way a student is thinking and bring it in. There are three levels here: an LLM is at one, a good explainer is at another, but the A+ explainer jujitsus your way of thinking to show where it is useful. Perhaps in five years, LLMs will do that better.

Students say, "I'm passionate about the subject, but seeing AI's progress, I don't know if it makes sense to pursue this as a career." This is relevant to anyone in a field getting productivity gains from AI, and coding is very adjacent to this. But even pre-AI, it is important for any job—unless you are a gentleman-scientist—to understand where the money comes from, what value you are adding, and the connection between the two.

Students often ask, "Where do people get to do this?" rather than, "What value am I adding to others, and to what extent is that why a salary flows in my direction?" This differs by case. A prestigious mathematician may provide brand value to a university. In other cases, an NSF grant is given based on the public good belief around basic science, with a bureaucracy acting as a proxy for that good and a song and dance to predict your progress will be in the spirit of that funding. You provide brand value as an expert and direct value as a teacher. Regardless of whether AIs prove theorems, or whether it is 2016 or 2026, not enough students consider this. I stumbled into a career where math exploration is monetized as entertainment; I could have avoided relying on serendipity and acted more by design had I thought critically about it.

If we have almost-automated theorem proving and LLMs are good explainers, the social role mathematicians serve doesn't change much. As a public, we still value basic science and trust mathematicians to determine where their time is best spent. Prestige comes from within that community—other members saying a result is good—rather than a grant writer understanding algebraic number theory. There will be an inner culture of valuable contributions, which may shift from theorem proving toward good definition writing or a museum curator role. That community will exist as long as society values basic science, and in an AI-driven abundance world, there may be more funding in that direction.

Regarding institutional prestige, teaching is one of the most stable post-AGI jobs because it is so relational. If parents have an abundance of wealth, they will spend it on good teaching and educating. Even if LLMs are good explainers, teaching is a social, coaching, and mentor-type role, making it one of the most stable careers for the next fifty years. Since many mathematicians' roles overlap with this, prospective students could lean into it. More students should give credence to the idea of being a math educator and the value that serves the next generation.

It feels like universal advice: know where the money is coming from and where you plug into that. Imagine a world where, within five or ten years, AIs are coming up with solutions to the Millennium Prize problems and totally novel problems, mathematical fields, and objects. AI minds will have seen furthest beyond our horizons in mathematics. In that world, if there are any jobs, distilling what the AIs have learned will be one of them. People who understand it and can decide where it should point will have more economic value as curators, pointing this behemoth of new math in a useful direction. That is a much more levered move than it had been previously.

One question for AI in math is not only can it do it, but is it any good? You described how, with group theory, we try to figure out random facts about the roots of different functions, which now have practical applications across many fields. While progress in algebraic number theory feels unlikely to unlock something, I remember a mathematician doing dynamics and PDE-solving. Boeing used to make planes, test them, and then disassemble and reassemble them based on those tests. His group had insights on how to do more in simulation to avoid deconstructing and rebuilding, saving Boeing billions of dollars, so they started funding that group. That is more obviously application-adjacent because PDEs are that. Progress in that domain likely unlocks things, perhaps making engine design more fluid, finding the right wing shape instead of running complicated CFD, or speeding up CFD simulations because pure math insights make them more efficient.

It seems less likely that massive breakthroughs in math immediately turn into massive economic breakthroughs—like solving the Navier-Stokes problems to unlock an ability to simulate more things—but you will probably see meaningful leakage of pure math insights into other areas. People working in AI engineering, physical engineering, and material science would be in a good position to decide if AI math insights are relevant. It would be disappointing and surprising if there weren't economically valuable improvements over the next five years directly referable to AI progress in math. It would be disappointing if AI just took down Erdős problems without doing math that touches the physical world. As we reach the industrial part of the singularity, we will hopefully have different ideas useful in other parts of the world. Every time we wrote grant proposals saying elliptic curve progress would help cryptography, it shone a light on the fact that maybe it doesn't.

Mentioned

People

Bernhard Riemann Albert Einstein Niels Henrik Abel Joseph-Louis Lagrange Joseph Liouville Carl Friedrich Gauss Camille Jordan Murray Gell-Mann Isaac Newton David Bessis Timothy Chow Claude Shannon Freeman Dyson Hugh Montgomery Terry Tao Andy Jassy Eric Jang Alex Kontorovich Andy Matuschak Steven Strogatz Paul Erdős

Companies

Institute for Advanced Study OpenAI IAS DeepMind DeepSeek Jane Street Boeing