Why Mathematicians May Stop Working on Hard Problems

Artificial intelligence may discourage mathematicians from working on difficult problems even while making mathematical research more productive. The mechanism is straightforward. If AI makes it possible to obtain interesting theorems quickly, while academic careers continue to depend on publishing interesting theorems, researchers will have a strong incentive to pursue work that AI can complete. Problems requiring months or years of uncertain investigation will become less attractive.

This problem is independent of OpenAI’s release of hundreds of claimed solutions to open problems. Even if OpenAI had not released a single solution, the incentive problem discussed here would be unchanged. It arises from researchers’ access to powerful tools and the way academic institutions reward their work. No public collection of AI-generated solutions is needed to set it in motion.

In my opinion, this could be a much larger negative effect of AI on mathematics than the release itself. The proportion of mathematicians who devote substantial time to major, widely recognized open problems is small, at least in some and perhaps many fields. But every mathematician faces decisions about which questions deserve attention, how long to persist with an unsuccessful approach, and what constitutes a sensible investment of research time. The change discussed here reaches every single mathematician, although its professional consequences will differ with career stage and institutional circumstances.

The difficult problems at risk need not be famous conjectures. They include understanding a particular stochastic model, finding the right assumptions for a theorem, explaining an unexpected phenomenon, or developing a method where existing techniques fail. Such projects may be important without appearing on any list of celebrated open questions.

Consider two research projects. In the first, a mathematician uses AI to explore a family of questions. The system produces several plausible theorems, some of which survive careful scrutiny. Preparing one of these results for publication requires a nontrivial investment: checking the argument, correcting the statement, improving the exposition, and placing the result in the literature. Nevertheless, the entire project takes weeks rather than years.

In the second project, the mathematician studies a difficult model whose behavior is poorly understood. Existing methods are inadequate. After a year, the researcher has developed a new technique and established a partial result, but the main question remains open. The proof is long and technical, and its eventual significance is uncertain.

Both projects may be worthwhile. But they offer very different prospects to someone approaching a hiring decision, a tenure review, or the end of a grant.

The first project offers a relatively predictable publication. The second offers a substantial chance of having little to show within the relevant evaluation period. If researchers can repeat the first kind of project several times while a colleague struggles with the second, the difference in their publication records may become considerable.

The pressure will be especially strong if journals continue to emphasize the interest of the final theorem. An editor comparing submissions may reasonably prefer a striking, complete result with a short proof to a modest partial result requiring forty pages of technical argument. The latter paper may introduce a promising method, but evaluating its promise requires expertise, time, and a willingness to make an uncertain judgment.

No hostility toward difficult research is necessary. Editors face limited space and limited referee resources. Referees can assess a finished theorem more confidently than the future usefulness of an unfamiliar technique. Readers also have limited attention. Each participant can make a defensible decision while collectively producing a system that discourages sustained investigation.

AI would intensify this imbalance by increasing the supply of attractive, completed results. A technical partial result would compete with a growing stream of theorems that are easier to state, easier to appreciate, and more immediately satisfying. Its author might have worked much harder, but effort alone has never been a sufficient reason for publication.

The resulting incentive could be severe. A mathematician might reasonably conclude that spending two years developing a difficult argument is professionally irresponsible when the same period could produce several substantial papers through AI-assisted exploration. The hard project would have to offer an unusually large expected reward to justify its risk.

This creates a potentially self-reinforcing process. Researchers who concentrate on rapidly publishable results may accumulate the credentials needed to obtain jobs, grants, students, and influence. Their publication records become reference points for evaluating others. A rate of production initially made possible by AI may gradually become an ordinary expectation. Researchers who continue to pursue slow projects then appear unproductive against the new standard.

Advice to “work on important problems” offers little protection if hiring and promotion decisions reward a different strategy. Junior mathematicians cannot be expected to absorb unlimited professional risk for the long-term benefit of the discipline.

There is an important distinction between a problem that is hard for humans and one that remains hard with the best available AI. Automating the former can be an enormous benefit. A researcher may use the time saved to investigate questions that were previously inaccessible.

The concern is what happens to the latter category. As AI solves more problems, the remaining ones may demand longer investigations, unfamiliar ideas, or substantial work before any publishable statement becomes available. The opportunity cost of pursuing them will have increased precisely because producing other mathematics has become easier.

Nor can we assume that the supply of AI-generated results will be mathematically uninteresting. That would make the problem simpler: journals could reject routine output and continue rewarding deeper work. The more serious possibility is that AI produces results that are genuinely interesting and deserve publication. Researchers would then be choosing between two legitimate forms of mathematical activity, one of which offers much better career prospects.

The loss would be difficult to measure. We would see the published theorems. We would not see the models that nobody investigated, the approaches abandoned before they matured, or the techniques that might have emerged from several unsuccessful years. Publication statistics could suggest a flourishing discipline while concealing a contraction in the kinds of intellectual risk its members can afford.

This outcome is not inevitable. Some mathematicians will continue difficult investigations out of conviction, and some institutions will support them. AI may itself make prolonged exploration more effective. But these possibilities do not remove the incentive problem. If academic evaluation remains closely tied to the production of completed results, exhortations to patience and originality will have limited force.

Preserving difficult research would require institutions to accept its actual consequences: uneven publication records, long periods without a definitive theorem, and partial results whose value may become clear only later. Such judgments are difficult and can be mistaken. There is no simple metric that will reliably identify a promising unfinished research program.

The controversy over a large release of solutions concerns, among other things, the disruption of existing projects. The problem described here concerns the projects mathematicians will choose to begin—and those they will never begin. It can operate continuously, throughout the profession, without any dramatic announcement.

Mathematicians may therefore stop working on hard problems for an uncomfortable reason: they will have found a dependable way to produce good mathematics without taking comparable risks. AI could make the profession more successful at generating publishable results while making a prolonged encounter with genuine uncertainty harder to sustain as a career.

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