Post by @tao@mathstodon.xyz

2026-09-08 20:32 UTC

Working out whether a question is actually worth highlighting is a lengthy, deliberate, and subjective process, often informed by historical experience on what good mathematics was generated (or not generated) while working on earlier problems of this type. In particular, being aware of the "difficulty landscape" in a field - what questions are very easy to answer with known methods, which ones can be solved but only with some effort, and which ones are impossible - is of crucial importance in making such determinations. And some problems only become interesting after an external connection is made. For instance, there could hypothetically be an unexpected connection between the Riemann zeta function and the 10^10^nth digits of pi for various n... at which point the previous question of determining the 10^10^10th digit suddenly becomes relevant again. (I should emphasize though that this specific scenario is incredibly unlikely to actually be the case; I use it only as a hypothetical iilustration.) Every new advance in mathematics, whether it comes from technique, technology, or infrastructure (such as access to libraries of past literature) reduces the difficulty of solving problems. This is generally a good thing; but it comes at the cost of flattening out the difficulty landscape of a field, to the point where one can no longer discern its geometry to the extent that promising questions can be extracted within the range of applicability of the tool. Often this effect is counteracted by the ability of such a tool to enlarge the radius of the sphere of results one can plausibly reach, creating new boundaries to fruitfully explore. (2/4)

Replies (4)

@tao@mathstodon.xyz 2026-09-08 20:32

However, one notable feature of the current AI era is the absence of any definitive such boundaries. While AI tools have flattened the difficulty landscape now in many areas of the subject, thus destroying the ability to locate promising new problems in that area, there are no clear frontiers that are separating the "AI-feasible" problems from the "AI-hard" problems (which certainly still exist, given that the difficulty level of problems are unbounded, and can even be undecidable). This is in part due to the rapidly changing nature of the technology, but also compounded by the refusal of AI companies to disclose their negative results, or reveal the process towards obtaining their solutions. In fact, it is now the identification of a promising problem which is the scarce and precious resource. We have now seen that even the rumor of someone working on a problem can trigger a massive amount of AI-powered effort to flatten it before the original research project has time to reach its full potential. The incentives may now be pointing in the direction of no longer sharing any promising research directions with the broader community, which would reverse centuries of traditions of open science and do serious long-term damage to the future of the field. (3/4)

Open ##5167448
@arsonatdennys@kolektiva.social 2026-09-08 22:42

@tao@mathstodon.xyz would deeply appreciate a bit of elaboration on “to the point where one can no longer discern its geometry to the extent that promising questions can be extracted within the range of applicability of the tool. Often this is counteracted by the ability of such a tool to enlarge the radius …” The metaphor is of concentric circles where the interior of inner circle’s geometry has been flattened by this new tool but area b/w the outer circle and inner circle still has sufficient ‘curvature’ to identify promising questions? and here, is promising in more than (just) understanding the difficulty boundaries of the tool? E.g. difficulty topography is a compass to other qualities of interest.

Open ##5167504
@DarkMidoriya49@mathstodon.xyz 2026-09-10 06:04

@tao@mathstodon.xyz It feels like a distinction between NP hard and NP complete problems. The best way to work in the AI is to map a problem that cannot be done by the current level of Ai and breaking it down and to make a simialrity basis to problems that are already being solved. Directly tackling the hard problems will very much affect the current small labs very much. So for small labs it is best to use the current compute available for decomposed tasks that will combine itself into helping solve the large problems. But they have to also make sure the problem they are addressing can have the expected usage, and will be worth addressing,

Open ##5167505
@uniwuni@deadinsi.de 2026-09-09 06:58

@jmma1980@mastodon.social @srinivas @tao that is quite literally the opposite of what is happening. we get proofs but no intuition

Open ##5167507