Tag Archives for artificial-intelligence

From Proof Scarcity to Proof Abundance

tl;dr anyone who previously used or currently uses mathematical tools to solve problems in their field (whether in sciences, pure or applied mathematics, engineering, economics, and so on) needs to pay attention to discussions around the use of AI to solve mathematically precise problems. The revolution has begun!

Here’s what I believe: once AI-assisted proofs become abundant, their scarcity value will fall and attention will shift toward the harder tasks of formulating compelling conjectures, building theories, and creating definitions that organize rapidly expanding bodies of results. The analogy is economic: just as an influx of currency can produce inflation rather than lasting wealth, an influx of proofs can reduce the value attached to any individual proof without necessarily producing a comparable increase in understanding.

Firsthand Experience

Honestly, for me, the question of how useful AI could be in solving math problems did not begin in 2026. In November of 2022, ChatGPT was released. I had just begun my postdoc. With support from the Simons Foundation, I started thinking seriously in 2022 about what mathematics (and intellectual work more broadly) might look like in a world with advanced AI. At the time, much of this remained speculative: What would happen if mathematical reasoning became inexpensive? Which parts of research would retain their value? Would the bottleneck shift from proving statements to identifying the right questions, definitions, and conceptual frameworks?

At ICM (International Congress of Mathematicians) 2026, Terence Tao gave a lecture on Mathematics in the Age of AI. I’d encourage everyone to, at least, read the slides! Tao disusses the implications of the abundance of proofs (not necessarily correct). Recent events have made this transition feel concrete rather than hypothetical. While I was watching the 2026 World Cup final, Levent Alpöge announced a counterexample (credited to the AI system Fable) to the Jacobian conjecture. More precisely, the construction disproves the conjecture in dimension three, and therefore in every dimension n\geq 3, while the two-dimensional case remains open. The counterexample has a nonzero constant Jacobian determinant but maps three distinct points to the same output, directly contradicting the conjectured invertibility.

In recent days have also tested advanced AI systems on several problems from my own active research agenda. These were not merely exercises with known answers: in multiple cases, the systems made progress that appeared genuinely novel, uncovering arguments or directions that I had not previously considered. The important question is no longer whether AI can occasionally imitate mathematical reasoning. It is now clear that AI can perform at least some research-level mathematics. The remaining questions concern the breadth and reliability of that ability, the amount of human guidance and computation it requires, and, most importantly, how the mathematical community should evaluate, explain, verify, and build upon the resulting work.

Terence Tao on Mathematics in the Age of AI

In the rest of this blog post, I will highlight a few parts of his talk which I found illuminating!

Tao identifies the central challenge posed by mathematical AI: not merely generating correct proofs, but transforming those proofs into shared human understanding. That is, the most important question is no longer whether artificial intelligence can prove difficult theorems. I believe that Tao deliberately set that question aside. Instead, he asked what may be a more consequential question:

If AI systems become capable of performing a substantial fraction of research-level mathematical work, what exactly should the mathematical community be trying to accomplish?

We all need to think of that shift (from technological capability to institutional purpose). Most discussions of AI and mathematics focus on benchmark performance: Can a model solve Olympiad problems? Can it formalize a proof in Lean? Can it make progress on an open conjecture? Tao’s lecture asks what happens after the answer to some of those questions becomes yes. Tao asks the audience to provisionally assume that reasonably capable mathematical AI is coming. He then investigates what follows for proof, exposition, reviewing, education, authorship, and the organization of mathematical knowledge.

What I appreciate from the talk is that the resulting picture is neither utopian nor apocalyptic. (Although a large fraction of folks see it as a warning.) Clearly, we are headed towards an era in which proofs are scarce to one in which proofs are abundant; our present institutions are designed almost entirely for the former world, where proofs are not abundant.

A crisis of values rather than a crisis of logic

In the late nineteenth and early twentieth centuries, mathematicians were forced to examine assumptions that had previously remained largely implicit. Russell’s paradox, the emergence of competing foundational programs, and Gödel’s incompleteness theorems created a period of uncertainty about sets, numbers, infinity, axioms, and formal proof. This led to the development of more explicit and standardized foundations that gave mathematicians a trusted environment in which to work.

Tao suggests that AI is producing a comparable period of turbulence, although the foundations now at issue are not primarily logical. They are the foundations of mathematical values and practices: what counts as progress, who deserves credit, what authors are responsible for, why proofs matter, and what the profession is ultimately trying to produce. A disruptive development can expose assumptions that were previously invisible because they rarely came into conflict. Before AI, several goals of mathematics tended to advance together. A mathematician who solved a difficult problem often developed a new technique, trained students, wrote an influential paper, helped organize a research community, and contributed to a larger theory. Because those outputs were correlated, institutions could reward one visible quantity, such as the publication of a paper with one or more important theorems, and assume that the others would follow.

AI threatens to break those correlations.

The two questions that are often confused

Tao separates the AI debate into two questions.

The first is a capability question: Will AI tools, at an acceptable cost and with some level of human supervision, be able to perform meaningful research-level mathematical tasks with a nontrivial rate of success?

Tao formulates this as a family of conjectures because almost every term requires qualification. Which tools? Which fields? What counts as research-level? How much supervision? At what cost? What success rate? What standard of correctness? What standard of exposition? A system that autonomously proves 80 percent of new theorems in algebraic geometry is very different from one that occasionally completes a technical lemma after several days of expert prompting. Both might satisfy some version of an AI capability claim. Tao also stresses that public evidence is affected by reporting bias, commercial incentives, undisclosed compute budgets, selective demonstrations, and ambiguous levels of human assistance. The truth of a capability claim must also be separated from whether that capability is desirable.

The second question is a question about goals and values: What are the mathematical community’s actual objectives, including the implicit objectives encoded in publication, hiring, funding, prizes, and professional prestige? Tao’s key methodological move is to condition on a working hypothesis: suppose that a reasonably strong version of the capability claim becomes true reasonably soon. He does not ask the audience to endorse or welcome the hypothesis. He asks what the community should do if it holds. Very reasonable! This is a useful form of reasoning under uncertainty. To continue to do mathematics, we cannot wait until every capability forecast is resolved before examining whether our institutions are robust to rapid automation. Even a moderate probability of large changes can justify preparing publishing policies, authorship standards, review infrastructure, and educational norms.

First Proof

Tao briefly points to the First Proof project as one of the better-controlled pieces of evidence about current AI capabilities. For its second batch, First Proof assembled ten unpublished research-level problems originating in the work of research mathematicians. Four systems were tested in a controlled environment. The outputs were evaluated using a double-blind journal-review model involving approximately thirty experts, with each submission examined by multiple referees. Across the four systems, seven of the ten problems received at least one solution judged essentially correct or in need of only minor revisions. One system found a novel solution to a stochastic partial differential equations problem that differed from the human proof and impressed the referees. Other problems saw little or no meaningful progress.

The results are substantial, but their limitations are equally informative. The systems often handled routine portions of an argument in meticulous detail while moving too quickly through the genuinely difficult step. Referees found unsupported appeals to supposedly standard arguments, incorrect or missing citations, unnecessary notation, and lengthy explanations of facts that an expert would normally omit. Some submissions reproduced distinctive language and notation from earlier work without appropriate attribution (i.e., behavior that would raise serious plagiarism concerns in a human submission).

The computational costs also varied dramatically. In the reported runs, per-problem costs ranged from single-digit dollar amounts to nearly one thousand dollars, depending on the system and problem. This reinforces Tao’s point that “AI solved the problem” is not a complete scientific statement without information about models, harnesses, prompts, search procedures, human intervention, tokens, time, and cost.

Most importantly, First Proof evaluated only one part of mathematical research: generating proofs of questions selected and formulated by humans. Its organizers explicitly distinguish solving questions within existing frameworks from the equally important work of asking new questions and developing the frameworks in which those questions become meaningful.

Mathematics has more than one objective

What is mathematical research for?

Tao identifies several answers:

  • solving pure and applied problems;
  • building theories and techniques;
  • understanding the natural and social world;
  • training future mathematicians (part of my job);
  • sustaining a mathematical community;
  • contributing to a shared network of knowledge;
  • creating works of enduring intellectual or aesthetic value.

Historically, progress along these dimensions was positively correlated. Solving an important problem often required theory building. Theory building produced reusable techniques. Writing and teaching those techniques helped train students and build a community. This made it tempting to treat theorem production as a proxy for mathematical progress. Tao invokes Goodhart’s law: once a proxy becomes an explicit target, optimization can destroy the relationship that made the proxy useful. AI makes this danger especially severe because it can lower the cost of producing objects that look like the outputs rewarded by current metrics.

Suppose an institution rewards:

  • the number of problems solved;
  • the number of papers published;
  • being first to announce a proof;
  • benchmark scores;
  • citation counts;
  • the number of formalized theorems.

An AI-intensive workflow may increase each of these without proportionately increasing understanding, theory, pedagogy, reliability, or long-term usefulness.

A thousand isolated proofs are not necessarily more valuable than one conceptual framework explaining why all thousand theorems are true. A technically correct argument is not necessarily a useful argument. A formally verified statement is not necessarily the statement that mathematicians intended to prove. A highly cited result is not necessarily well understood.

The deeper point is that mathematical knowledge is not a warehouse of theorem statements. It is an organized system of concepts, explanations, analogies, techniques, examples, counterexamples, and judgments about what matters.

Tao’s proposed “oral defense” standard

Tao offers a rule of thumb: a result should not be published unless its human authors can convincingly present a clear, correct, properly attributed expert-level explanation of it. The proposal addresses several problems simultaneously.

An author capable of defending the result is more likely to have:

  • checked that the theorem says what it is supposed to say;
  • located the crucial step;
  • understood the relationship to prior work;
  • detected misleading AI-generated exposition;
  • assumed meaningful responsibility for correctness.

The idea resembles a thesis defense. Producing a document is not enough; the author must demonstrate command of its content. As a literal universal publication requirement, however, the rule would need careful implementation. It is bound to be controversial: Oral presentation ability varies, and a rigid talk requirement could disadvantage researchers with disabilities, non-native speakers, or authors whose strengths lie in writing rather than performance. Large collaborations may also have genuinely distributed understanding.

The underlying principle is stronger than any particular format: publication should require evidence of human intellectual ownership and accountability. That evidence might take the form of a seminar, an annotated proof map, a technical interview, an expository companion, or an independent human audit. (I’m hoping to implement the oral defense standard within my research group.)

Selected references and further reading

Terence Tao, Mathematics in the Age of AI, ICM public-lecture slides, July 24, 2026. (Teorth)

Mohammed Abouzaid et al., First Proof: Second Batch Report, 2026. (First Proof Project)

William P. Thurston, On Proof and Progress in Mathematics, Bulletin of the American Mathematical Society, 1994. (arXiv)

Tanya Klowden and Terence Tao, Mathematical Methods and Human Thought in the Age of AI, 2026. (arXiv)

Johan Commelin, Mateja Jamnik, Rodrigo Ochigame, Lenny Taelman, and Akshay Venkatesh, Shaping the Future of Mathematics in the Age of AI, 2026. (arXiv)

Jeremy Avigad, Mathematicians in the Age of AI, 2026. (arXiv)

Leiden Declaration on Artificial Intelligence and Mathematics, June 2026. (Leiden AI & Math Declaration)

The Usefulness of “Useless” Knowledge (and Why AI Makes Flexner Even More Right)

I just finished reading The Usefulness of Useless Knowledge again, this time with the perspective of living through a period of rapid technological acceleration driven by AI. On an earlier reading, Flexner’s defense of curiosity-driven inquiry felt aspirational and almost moral in tone, a principled argument for intellectual freedom. On rereading, it feels more diagnostic. Many of the tensions he identified (i.e., between short-term utility and long-term understanding, between institutional incentives and genuine discovery) now play out daily in how we fund, evaluate, and deploy AI research. What has changed is not the structure of his argument, but its urgency: in a world increasingly optimized for immediate outputs, Flexner’s insistence that transformative advances often arise from questions with no obvious application reads less like an idealistic manifesto and more like a practical warning.

In 1939, on the eve of a world war, Abraham Flexner published a slim, stubbornly optimistic essay with a mischievous title: The Usefulness of Useless Knowledge. His claim is not that practical work is bad. It’s that the deep engine of civilization is often curiosity that doesn’t start with an application in mind, and that trying to force every idea to justify itself immediately is a reliable way to stop the next revolution before it begins.

Robbert Dijkgraaf’s companion essay (and related pieces written from his vantage point at the Institute for Advanced Study) updates Flexner’s argument for a world that is now built out of microelectronics, networks, and software; this is exactly the substrate on which modern AI sits. Reading them together today feels like watching two people describe the same phenomenon across two eras: breakthroughs are usually the delayed interest on “useless” questions.

Below is a guided tour of their core ideas, with a detour through the current AI moment, where “useless” knowledge is quietly doing most of the work.

Flexner’s central paradox: curiosity first, usefulness later

Flexner’s essay is a defense of a particular kind of intellectual freedom: the right to pursue questions without writing an ROI memo first.

Dijkgraaf highlights one of Flexner’s most quoted lines (and the one that best captures the whole stance): “Curiosity… is probably the outstanding characteristic of modern thinking… and it must be absolutely unhampered.”

That “must” is doing a lot of work. Flexner isn’t saying that applications are optional. He’s saying the route to them is often non-linear and hard to predict. He even makes the institutional point: a research institute shouldn’t justify itself by promising inventions on a timeline. Instead: “We make ourselves no promises… [but] cherish the hope that the unobstructed pursuit of useless knowledge” will matter later.

Notice the subtlety: he hopes it will matter, but he refuses to make that the official rationale. Why? Because if you only fund what looks useful today, you’ll underproduce the ideas that define tomorrow.

The “Mississippi” model of discovery (and why it matters for AI)

Flexner is unusually modern in how he describes the innovation pipeline: not as single geniuses striking gold, but as a long chain of partial insights that only later “click.”

He writes: “Almost every discovery has a long and precarious history… Science… begins in a tiny rivulet… [and] is formed from countless sources.”

This is basically an antidote to the myth that research can be managed like a factory. You can optimize a pipeline once you know what the pipeline is. But when you’re still discovering what questions are even coherent, “efficiency” often means “premature narrowing.”

AI is a perfect example of the Mississippi model. Modern machine learning is not one idea; it’s a confluence:

  • mathematical statistics + linear algebra,
  • optimization + numerical computing,
  • information theory + coding,
  • neuroscience metaphors + cognitive science,
  • hardware advances + systems engineering,
  • and now massive-scale data and infrastructure.

Much of that was, at some point, “not obviously useful” until it suddenly was.

Flexner’s warning: the real enemy is forced conformity

Flexner’s defense of “useless knowledge” is not only about technology; it’s about human freedom. He’s writing in a period where universities were being pushed into ideological service, and he argues that the gravest threat is not wrong ideas, but the attempt to prevent minds from ranging freely.

One of his sharpest lines: “The real enemy… is the man who tries to mold the human spirit so that it will not dare to spread its wings.”

If you read that in 2025, it lands uncomfortably close to modern pressures on research:

  • “Only fund what’s immediately commercial.”
  • “Only publish what’s trendy.”
  • “Only study what aligns with the current institutional incentive gradient.”
  • “Only build what can be shipped next quarter.”

And in AI specifically:

  • “Only do work that scales.”
  • “Only do benchmarks.”
  • “Only do applied product wins.”

Flexner isn’t anti-application; he’s anti-premature closure.

Dijkgraaf’s update: society runs on knowledge it can’t fully see anymore

Dijkgraaf’s companion essay takes Flexner’s stance and says, essentially: look around, Flexner won. The modern world is built out of the long tail of basic research.

He gives a crisp late-20th-century example: the World Wide Web began as a collaboration tool for particle physicists at CERN (introduced in 1989, made public in 1993). He ties that to the evolution of grid and cloud computing developed to handle scientific data, technology that now undergirds everyday internet services. Then he makes a claim that matters a lot for AI policy debates: fundamental advances are public goods (i.e., they diffuse beyond any single lab or nation).That’s an especially relevant lens for AI, where:

  • open ideas (architectures, optimization tricks, safety methods) propagate fast,
  • but compute, data, and deployment concentrate power.

If knowledge is a public good, then a society that starves basic research is quietly selling off its future, even if it still “uses” plenty of science in the present.

AI as a case study in “useful uselessness”

Here’s a helpful way to read Flexner in the age of AI:

A) “Useless” questions that became AI infrastructure

Many of the questions that shaped AI looked abstract or niche before they became inevitable:

  • How do high-dimensional models generalize?
  • When does overparameterization help rather than hurt?
  • What is the geometry of optimization landscapes?
  • How can representation learning capture structure without labels?
  • What are the limits of compression, prediction, and inference?

These don’t sound like product requirements. They sound like “useless” theory, until you realize they govern whether your model trains at all, whether it’s robust, whether it leaks private data, whether it can be aligned, and whether it fails safely.

Flexner’s point isn’t that every abstract question pays off. It’s that you can’t pre-identify the ones that will, and trying to do so narrows the search too early.

B) “Tool-making” is often the hidden payoff

Dijkgraaf emphasizes that pathbreaking research yields tools and techniques in indirect ways. (ias.edu)
AI progress has been exactly this: tool-making (optimizers, architectures, pretraining recipes, eval frameworks, interpretability methods, privacy-preserving techniques) that later becomes the platform everyone builds on.

C) The scary twist: usefulness for good and bad

Flexner also notes that discoveries can become instruments of destruction when repurposed. He uses chemical and aviation examples to make the point.

AI has the same dual-use character:

  • The same generative model family can draft medical summaries or automate phishing.
  • The same computer vision advances can improve accessibility or expand surveillance.
  • The same inference tools can find scientific patterns or extract sensitive attributes.

Flexner’s framework doesn’t solve dual-use, but it forces honesty: the ethical challenge isn’t a reason to stop curiosity; it’s a reason to pair curiosity with governance, norms, and safeguards.

A Flexnerian reading of the current AI funding wave

We’re currently living through a paradox that Flexner would recognize instantly:

  1. AI is showered with investment because it’s visibly useful now.
  2. That investment creates pressure to define “research” as whatever improves next quarter’s metrics.
  3. But the next conceptual leap in AI may come from areas that look “useless” relative to today’s dominant paradigm.

If you want better long-horizon AI outcomes (i.e., robustness, interpretability, privacy, security, alignment, and scientific discovery) Flexner would argue you need institutions that protect inquiry that isn’t instantly legible as profitable.

Or in his words, you need “spiritual and intellectual freedom.”

What to do with this (three practical takeaways)

1) Keep a portfolio: fast product work + slow foundational work

Treat research like an ecosystem. If everything must justify itself immediately, you get brittle progress. Flexner’s “no promises” stance is a feature, not a bug.

2) Reward questions, not only answers

Benchmarks matter, but they can also overfit the field’s imagination. Some of the most important AI work right now is about re-framing the question (e.g., what counts as “understanding,” what counts as “alignment,” what counts as “privacy,” what counts as “truthfulness”).

3) Build institutions that protect intellectual risk

Flexner designed the Institute for Advanced Study around the idea that scholars “accomplish most when enabled” to pursue deep work with minimal distraction.
AI needs its own versions of that: spaces where the incentive is insight, not velocity.

AI is not an argument against Flexner (it’s his exhibit A)

If you hold a smartphone, use a search engine, or interact with modern AI systems, you’re touching the compounded returns of yesterday’s “useless” knowledge.

Flexner’s defense isn’t sentimental. It’s strategic: a society that wants transformative technology must also want the conditions that produce it: freedom, patience, and room for ideas that don’t yet know what they’re for. Or, as Dijkgraaf puts it in summarizing Flexner’s view: fundamental inquiry goes to the “headwaters,” and applications follow, slowly, steadily, and often surprisingly.

Main Source: https://www.ias.edu/ideas/2017/dijkgraaf-usefulness