# Reaping without sowing > Source: > Published: 2026-08-02 13:07:15+00:00 If you are at all connected with academic circles it would have been hard to miss the announcement: OpenAI has just published [Ten advances in mathematics](https://openai.com/index/ten-advances-in-mathematics/), ten results in mathematics and theoretical computer science, author listed simply as “OpenAI”, accompanied by [Lean certificates on GitHub](https://github.com/openai/ten-proofs), and, per Noam Brown, a token bill of under $2K for the lot (pretty cheap huh?). Sphere packing, non-sofic groups, a counterexample to Connes’ rigidity conjecture, parallel repetition for entangled games, and three Erdős problems. Forgive the indulgence, but I called it: [Back at the start of summer](https://www.linkedin.com/posts/tobias-osborne-601830a5_tobias-osborne-large-language-models-a-share-7467875590973382656-9qXC/) I warned that “you are probably going to have your LLM ‘oh f*** moment’ this summer”, and I called the mechanics in [Proof inflation](https://tjoresearchnotes.wordpress.com/2026/07/28/proof-inflation/) and [Conjecture sniping](https://tjoresearchnotes.wordpress.com/2026/07/20/conjecture-sniping/). Well, here we are. It is August, and the moment has arrived horribly on cue. Let me say the important thing first, before receding into the criticism class: I *do not* want to diminish this. My first impression is that these results *are* legitimately impressive. I have flirted with two of these problems myself, and they are properly challenging. This is not conjecture sniping, and nobody stumbles onto a non-sofic group by prompting harder. Something real happened here. Now let’s begin. I essentially want to make an observation, and then follow it to one rather uncomfortable conclusion. ## Twenty pages of tex Look at the shape of the artifacts. The manuscript is 249 pages, but that is ten separate results somewhat hastily and lovelessly stapled together: the individual chapters run from seven pages (the Ramsey bound) to fifty (the coding bounds), with most sitting in the ten-to-thirty band. Every single one of these proofs fits, with room to spare, inside a single context window. Twentyish pages of tex is comfortably under 100K tokens. That leaves a nice 900K for in-context learning. This is telling, and it is suggestive (to me) of how these results may have been found. Here is the thought experiment. If you gave me an infinite-token glitch, an OpenAI flamethrower with which to light tokens indiscriminately on fire, I might have attempted the following to get similar outcomes: 0. Use fast mode. If I can access inference on Cerebras-class hardware, I am definitely using it. 1. Swarm the entire mathematical literature with thousands of agents to build a database of high-value conjectures. Do sentiment analysis with hindcasting to validate the community importance of each one. Aim: at least 10000 conjectures. 2. Presort the conjectures by perceived difficulty. There is no point attempting Riemann. The goal is a good set of conjectures which might be provable in less than, say, twenty tex pages. 2′. Crucially: you do *not* want to build a mountain of theory to prove a conjecture (see below). Way too risky. Go for the ones which will fall within ten to twenty pages using tools already in the literature. 3. Spawn several orchestrator agents in parallel per conjecture, each overseeing, say, 64 subagents whose sole job is generating candidate proofs. Increase the temperature a bit on the provers to widen the output distribution. 4. Run an adversarial loop on every candidate. This is the “proof sampler” stage: we are hunting for approaches at the edge of the distribution. One might imagine 99% of all conjecture-approach pairs die here. Now we have, say, 100 warm conjectures. 5. Take the warmest 100 and iterate a proposer-critic loop on each until termination. This kills *at least* half of what remains. Call it 50. 6. We want to be hella cool, so we don’t stop there: farm the survivors out to subagents to build Lean 4 proofs. Here we encounter the uneven surface area of mathlib, so we audition the remaining conjectures for viability against it. (Note that the Lean certificates for the ten advances live in a separate repo. Catalogue keepers have already had to invent a new status for this genre of result: apparently “open (Lean)”, means formally certified but humanly undigested.) (7) Reach out to our math besties and ask what they think of the remaining proofs. Maybe ten respond 😉 (The acknowledgments sections suggest OpenAI did exactly this. Popa, Houdayer, Charles, and others are thanked as readers.) (8) The rest is easy: get agents to write the papers, and it is time to announce. The point is that all of this is *embarrassingly parallel*. If the probability of success on any one conjecture is 0.1%, you may well end up with ten good candidates. Want more? Deploy more compute. The advertised $2K is the price of the *winning* tokens, not the harvest. As several people immediately asked: how many conjectures went into the hopper to get ten out? Nobody outside the lab knows, and that undisclosed denominator is precisely where the recipe above hides. ## Not entirely vibes I would love to tell you the numbers above are pure vibes. They are not, well not quite. In a weird moment of synchronicity the night before the announcement, I ran, as a joke, a small version of exactly this recipe on my own field. I [published the entire run](https://github.com/tobiasosborne/QIP-submission), warts and all: every prompt, every subagent transcript, every dead end. The setup: one human-written prompt, three brief steering messages, and then hands off. Overnight, in 14 hours of wall-clock time, an orchestrator ran roughly 85 subagents in coordinated fleets (scrapers, miners, verifiers, attackers, and referees), burning about 17 million output tokens, or somewhere in the range of $700 to $900 at list prices. (I did not pay that amount though! I have a subscription, it cost me about 10% of my weekly quota. Call it 5 euros.) What came out the other end: a statistical profile of 783 accepted QIP talks from 2021 to 2026, a hindcast validation showing that 40% of SciRate’s top-25 papers became QIP talks (four times the base rate, so community attention is measurable, and therefore targetable), 62 explicitly stated open problems mined from around 100 papers of TeX source, and eight attacker agents assigned to the eight most promising problems. The kill list then did its work: five problems were eliminated (one had been answered 25 lines below where it was posed, and one attacker constructed a rigorous counterexample to its own hypothesis). Three candidates survived. The winner emerged with a claimed proof of a conjecture from the recent literature, half a million adversarial numerical instances with zero violations, sign-off from two independent hostile referees, two rounds of simulated programme-committee review, and a compile-clean 20-page paper. One candidate “advance”, one night, well under a thousand dollars. Now multiply by a collosal VC backed war chest. The mandatory disclaimers: 1. The result is not very good, 2. No human has checked the mathematics in my experiment. 3. The result is unverified and very possibly wrong, and 3. I consider the workflow to be extremely poor scientific behaviour, verging on unethical. That was the point. The experiment demonstrates what a cynical actor with little to zero domain knowledge can achieve in an evening. Two findings deserve pulling out. First, over half the budget went on agents whose only job was destroying other agents’ work; generation is cheaper than verification, and slop is a choice that costs a few hundred dollars less. Second, the hindcast that validated my topic selection is exactly the mechanism that makes community hype an attack surface. ## Why you cannot factory-farm long proofs So if short proofs can be harvested at industrial scale, why not long ones? Why not Riemann? This is, I think, the genuinely interesting question, and my answer is *not* the comforting platitude that LLMs “lack taste” or “aren’t truly creative”. Start with what LLMs are demonstrably good at. They will happily give you broad proof strategies, provided the ideas and methods already exist in the literature. They are great at task decomposition. And they are *amazing* at adversarial verification and validation, which is, I would argue, the single most underrated capability in the current stack. It all starts to break down when you need to build *new theory*: new definitions, new conjectures, and new language. An important proof often requires you to build a mountain of seemingly irrelevant results in order to *express* the final argument concisely. The image to hold in mind is Grothendieck’s rising sea: you do not crack the nut, you submerge it until the shell dissolves. You may need hundreds of pages of new definitions and lemmas before the “twenty-page proof” even becomes writable. Here we hit the exploration-exploitation dilemma *hard*, and LLMs have a failure mode that thwarts the standard RL playbook for it. Left to explore definition-space, they reward hack, *happily* and *all too readily*, by generating endless nightmarish streams of similarish definitions and conjectures. They engage in progress theatre, minting grandly named “new” conjectures which are simply reformulations of each other. The catalogue of definitions and open conjectures grows like a tidal wave, a kind of eutrophication of the mathematical ecosystem. And once the pond is choked, the reward signal falls below the noise floor lost forever in a sea of sludge. Anyone who has left an agent swarm running overnight on an open-ended research goal knows exactly the smell. This is why I do not believe, for example, that an LLM trained on pre-Grothendieck algebraic geometry would invent schemes. Yeah nah. ## The counterfactual test Demis Hassabis has proposed the thought experiment: could an LLM trained on a pre-1905 corpus have invented general relativity? Let me pose a few more, closer to home: - Could an LLM trained on a 2003 corpus have proved the entropy area law for 1D quantum systems? It took Matt Hastings years to build the theoretical infrastructure for that result. - Could the same 2003-corpus model invent 2D tensor networks, before Cirac, Vidal, and Verstraete, to numerically study two-dimensional many-body systems? - Would a 1996-corpus LLM discover AdS/CFT? - Would that same model invent Kitaev’s toric code? - Would a pre-1992 LLM invent quantum computation as we know it, replete with Shor’s algorithm and quantum error correction? I bet you can come up with dozens more from your own field. The pattern in every case: the breakthrough was not a clever derivation within the existing language, it was a *new language* in which the derivation became short. These are not idle counterfactuals. A frontier lab could, in principle, actually run this test: train a model using cutting-edge architectures, I don’t care, on a *corpus* truncated at 1992, or 1996, or 2003, and see what it can rediscover. I would regard this as one of the more scientifically valuable experiments any lab could perform. I personally highly doubt if any of them would pass it, for the reasons above. But! I have been wrong a *lot* recently. ## The harvest is on None of this dims my conviction that we have entered a golden age for science: we have genuinely reached the point where scaling compute yields substantial new results, and that is a wonderful, vertiginous thing. But be clear-eyed about what this first crop is. The ten advances are the *harvestable* results: the conjectures that fall within a context window, provable in the language mathematics already has. You can bet multiple actors are busy proof harvesting right now, this weekend, on exactly the recipe above. I know, because even I accidentally beat one of them to the punch by a day, at a five-orders-of-magnitude discount on the compute. There is one genuinely hopeful note buried in my little experiment. The same pipeline, pointed at verification instead of production, becomes the strongest reviewing tool anyone has ever had: hostile referee fleets, quote-provenance audits, and openness sweeps, all for a few hundred dollars a night. We are going to need it. I rather expect we will see a lot more twenty-page papers in the very near future. This is, however, reaping without sowing. Eventually the field will become infertile. The hundred-page ones, the ones that need key new definitions before they need a proof, those are still ours. For now. 😉