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How serious/promising is Connes' work on the Riemann Hypothesis?

Connes is mostly known these days for his work in non-commutative geometry, having previously earned a Fields medal* for his work on the classification of factors. He is a trusted mathematician with deep insights.

On the other hand, his essay on RH doesn't seem to identify one clear idea on how to approach the problem. At least, none that I can see.

I'm wondering if anybody looked into it. After all, he seems to have been working on RH, one way or another, for twenty years, now.

I am mostly curious, specifically, in conceptual reasons (if any) why this approach is, or may be, regarded as "not promising", or "conceptually incorrect", in contrast to the other questions already on MO, that usually inquire about what such approach may or may not be "still missing", or what it already accomplishes.

*See Araki's article for the 1983 ICM Proceedings (requires subscription; the entire proceedings are free via https://www.mathunion.org/icm/proceedings

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    $\begingroup$ Although many questions about RH tend to lead to opinion based answers, which is why some users voted to close this one, I kind of have a strong feeling, judging from the contents and writing style, that the answer this question got, is not actually opinion based, but based on expertise, and if this question shows "on hold", I also have the feeling this may get kind of weird, at some point $\endgroup$
    – user113393
    May 30, 2018 at 6:25
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    $\begingroup$ What happened to my comment, suggesting this might be a duplicate of mathoverflow.net/questions/259263/… ? $\endgroup$ May 30, 2018 at 7:08
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    $\begingroup$ I have my own opinions on the matter, but Connes himself (perhaps in preparation for the Bristol workshop next week) put a preprint on arXiv a few days ago. arxiv.org/abs/1805.10501 $\endgroup$ May 30, 2018 at 9:09
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    $\begingroup$ As a minor point, I don't think he got the Fields Medal for his work on non-commutative geometry. By 1982 he had already started with it, but his great triumphs were the classification of type III factors, and of (almost) all AFD factors; and all the work and ideas that came with them. $\endgroup$ May 30, 2018 at 21:30
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    $\begingroup$ @MartinArgerami This accords with my own understanding, based on the dates and also on Araki's article for the ICM. I've updated the main text, just because some of this NC(D)G revisionism grates slightly with me $\endgroup$
    – Yemon Choi
    Jun 3, 2018 at 13:44

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Answering to this kind of questions is not an easy task, but one can sympathize with the curiosity.

Just some personal thoughts.

To my mind, an approach to RH could be regarded as "serious" (by which I mean "with hope to at least yield interesting and genuinely new partial or related results") essentially in the sole case it also yields, as a bi-product of the methods, a "cohomological construction" of Hasse-Weil $L$-functions and zeta functions (completed with their respective archimedean local factors as predicted by Serre) for all smooth projective varieties over number fields, much as for Grothendieck's cohomological construction of $L$- and zeta functions of smooth projective varieties over finite fields using geometric $\ell$-adic cohomology.

This would be a first hint at how promising such approach can hope to be.

We currently lack insight into where such cohomological interpretation could possibly come from, and such accomplishment will probably entail the introduction of some kind of analytic geometry "over the integers", imbuing both complex, real, and $p$-adic analytic geometry, on equal or comparable footing.

The literature does contain evidence, at times even explicit and quite strikingly strong, for the existence of such cohomological interpretation to (completed) $L$- and zeta functions, or for why one should expect it.

Connes' work seems to suggest non-commutative geometry should somehow provide the (or, maybe more appropriately, "an") answer, although I honestly cannot fathom how (but, probably, that's just me). It seems to me Connes does humbly acknowledge that he doesn't either.

I'm not sure to what extent he himself puts trust into his more recent preprints on the matter ("arithmetic and scaling sites" etc. I think).

I personally do not believe for a moment, that the datum of a site (essentially a piece of algebra) and as simple minded as those put forth there, can possibly encode deep analytic information such as some arithmetic analog of Hodge-Weil positivity, to which RH should amount.

There's also, spread over some literature, a line of thought that seems to suggest that a cohomological interpretation to $L$- and/or zeta functions of smooth projective varieties over number fields could come out of a version of Topological Hochschild Homology, but this really doesn't sound promising either.

Even if this were the case, remember that even over finite fields, the crux of the matter was not, in the end, (just) coming up with a robust enough cohomological formalism able to provide spectral interpretations to zeta functions of smooth projective varieties over finite fields. Grothendieck did so, but he, remarkably enough, did not succeed in proving RH anyway.

So, betting everything (or much) on the fruitfulness of a cohomology theory in its own right, amounts to me to burying the problem under a pile of formal nonsense in the hope it solves itself on its own, without actually gaining a deeper understanding of it.

Back to Connes' work, I believe one thing he's trying to do, by keeping working on it to some extent to this day (which he can do fearlessly, since he's already had a life rather full of remarkable accomplishments) is keeping the interest and fascination into the problem "alive", the risk being, otherwise, that nobody will ever try to ever even touch it, given the mythology surrounding it.

Of course, at the end of the day, what we lack of is not a cohomology theory, technical prowess, motivation, or inspiration, but, simply, a real idea.

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    $\begingroup$ Fantastic answer! $\endgroup$
    – user92332
    May 30, 2018 at 3:48
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    $\begingroup$ Just curious: how does Christopher Deninger's approach to RH fare by your criterion? See e.g., this. $\endgroup$ May 30, 2018 at 9:41
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    $\begingroup$ @MikhailKatz To my mind, C. Deninger's intuition that some appropriate class of "foliated solenoids" equipped with compatible flows, and their "foliated de Rham-Betti cohomology", might play a key role into the picture, is suggestive and far-reaching. It may well be that, in some appropriate precise sense, this will indeed turn out to be the case. One can trace motivation in support of this, spread all over non-obviously-related areas of mathematics (complex, real, $p$-adic Hodge theories, some aspects in Riemannian geometry and ergodic theory, analytic and algebraic number theory, et al.). $\endgroup$
    – user87684
    May 30, 2018 at 20:42
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    $\begingroup$ One also appreciates the fact that Deninger humbly and carefully refrains from selling such intuitions as a "program", or anything of the sort, and it rather seems to me his work is explicitly designed and presented to only raise awareness. Still, it cannot really be "progress" insofar there's, to this day, no evident connection to global class field theory (or number theory at all). It deserves to be taken as a genuinely interesting perspective, quite opposite to invoking "characteristic one" black magic, which is usually only a synonym of "we don't really know what to do" $\endgroup$
    – user87684
    May 30, 2018 at 20:47

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