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Background: Once an analytic number theorist remarked to me that all attempts to prove the Riemann hypothesis using number theoretic methods have failed. Since then that remark stuck in my mind.

The veracity of the above alluded number theorist's opinion does not really matter for the question to make sense; I just included it for background.

Question:

What are some promising methods from outside number theory to approach Riemann hypothesis?

I know two:

  1. The geometric approach of Artin, Hasse, Weil and Deligne, the most important result being the proof of the Weil Conjectures.

  2. The Bost-Connes approach. This is outlined by Lieven Le Bruyn for instance and has a hint of thermodynamics .

I imagine that both of the above are cited by some people as the basis for the hopes that the theory of the field with one element will prove the Riemann hypothesis. Again, this question formally has no need to be connected the theory of field with one element to make sense. Other than just mentioning the above, let us not get into that aspect.

I am interested in other possible and promising methods. I am not interested in an equivalent formulation of Riemann hypothesis which is no better than the original. Both the above are very promising in terms of undiscovered things and might give a much better "big picture".

An approach I am ambivalent about, is that of Baez-Duarte. Though it does provide some evidence. I do not know whether it is any easier to prove Riemann hypothesis that way, rather than the original statement.

Please give me examples of any other methods; preferably very "promising" ones.

Edit 1: The meaning of "methods outside number theory" is the following: Nothing in the book of Ivic or Titchmarsch and Heath-Brown. More precisely, methods outside the traditional sybjects of elementary number theory and analytic number theory. I have given two examples above. One with algebraic geometry and one with thermodynamics.

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    $\begingroup$ I personally don't believe that any proposed approach to the Riemann hypothesis, including the two you listed, deserve to be called "promising". $\endgroup$
    – David Hansen
    Commented Aug 5, 2010 at 23:05
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    $\begingroup$ "All attempts to prove the Riemann hypothesis using number theoretic methods have failed". Isn't this just a special case of "all attempts to prove the Riemann hypothesis have failed"? $\endgroup$
    – Tom Smith
    Commented Aug 6, 2010 at 0:12
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    $\begingroup$ Shouldn't this be tagged "open-problem" and made CW, per FAQ? Also, in the absence of a proof, whether a method is viewed as promising or not is highly subjective. $\endgroup$
    – Victor Protsak
    Commented Aug 6, 2010 at 4:24
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    $\begingroup$ You have a very narrow view of what constitutes number theory. $\endgroup$
    – Felipe Voloch
    Commented Aug 7, 2010 at 2:47
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    $\begingroup$ Just to give one defense of Hardy (who surely regarded himself as a number theorist) against Weil's charge (not that one is needed; his legacy can speak for itself), let me remark that his proof of the existence of an infinitude of zeroes of the zeta function lying on the critical line uses the Mellin transform relationship between the zeta function and the Jacobi theta function (a relationship introduced by Riemann, by the way!), and then studies the question on the automorphic side (so to speak). I don't think that you can get into much deeper number theoretic territory than this. $\endgroup$
    – Emerton
    Commented Aug 7, 2010 at 6:23

8 Answers 8

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It's impossible to say whether an approach is promising. In my view, the most interesting approach is via constructing $\mathbb{F}_1$. The wikipedia page has links to the various attempts. One hopes that after a suitable theory is constructed, one of the proofs of the function field analogue of RH will be translatable to the number field case.

http://en.wikipedia.org/wiki/Field_with_one_element

p.s. I think this is number theory and I don't agree with your analytic number theorist.

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    $\begingroup$ I already mentioned the field with one element in thecquestion itself and it was with the hopes that the answers will not spend time on that topic. $\endgroup$
    – Anweshi
    Commented Aug 6, 2010 at 13:37
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    $\begingroup$ But if F_1 is the most interesting approach to RH currently available (as it appears to be the consensus) why not discuss it? $\endgroup$
    – Felipe Voloch
    Commented Aug 6, 2010 at 15:26
  • $\begingroup$ I wanted to know about approaches that were not already known to me. Besides some overly strict people are raising objection to the question itself as being subjective and argumentative, in the comments over there. I was in fear of the question getting closed and so steered away from anything with any hint of speculation. Note that by such fears I already CW-ed the question. $\endgroup$
    – Anweshi
    Commented Aug 6, 2010 at 16:40
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    $\begingroup$ The relevant part of $F_1$ and RH appears as: Weil's RH proof for curves over fin. fields started with $C/k$, took its product $C \times_k C$, and then examined its diagonal. If the integers were a curve over a field, the same proof would prove the RH. The integers $Z$ are 1-dim, which suggests that they may be a curve, but they are not an algebra over any field. One of the conjectured properties of $F_1$ is that $Z$ should be an $F_1$-algebra. This would make it possible to construct the product $Z \times_{F_1} Z$, and it is hoped that RH for $Z$ can be proved in the same way as RH for $C/k$ $\endgroup$
    – Junkie
    Commented Aug 7, 2010 at 5:57
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So far as I know, there is no approach to the Riemann Hypothesis which has been fleshed out far enough to get an even moderately skeptical expert to back it, with any odds whatsoever. I think this situation should be contrasted with that of Fermat's Last Theorem [FLT]: a lot of number theorists, had they known in say 1990 that Wiles was working on FLT via Taniyama-Shimura, would have found that plausible and encouraging. Wiles' work was absolutely a tour de force, but at the ground level it used preexisting tools in the number-theoretic community, tools (e.g. Mazur's theory of Galois deformations) whose power and relevance to the problems at hand were appreciated and known not to have been fully exploited. Similarly, the proof of Serre's Conjecture by Khare-Wintenberger represents some of the best number-theoretic work in the last decade, and if you were an expert in the field in 2000 (again, not me -- but I have friends), then unless you could somehow predict the powerful techniques that Mark Kisin would develop over the course of the next several years, your estimate of when Serre's Conjecture would be proven would probably be off by as much as a decade. But people knew (or felt they knew, correctly as it turns out) that it was just a matter of time.

In contrast, despite the existence of several "programmes" by leading mathematicians to prove RH, if it were actually proved in, say, 2012, there would be the mathematical equivalent of worldwide rioting. It's just not at all clear that we can get there from here: most of the work which has been done on RH in the last 150 years has led (only) to our having a suitably healthy respect for the problem and its importance in mathematics as a whole.

That said, I think that approaches to RH should not be evaluated on whether they are likely to culminate in a proof of RH -- who knows? -- but whether they are interesting and seem likely to lead to interesting mathematics along the way. A lot of people seem to like the $\mathbb{F}_1$ approach for this reason, as in Felipe's answer. (And indeed, this answer began as a comment to his.)

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    $\begingroup$ I think that the question is highly speculative, and this answer clearly enunciates many of the reasons for that. Just a tiny complement involving FLT: before Wiles's proof, approaches using the $abc$-conjecture and Bogomolov-Miyaoka-Yau inequality were viewed as "promising". However, to this day, neither of them has yielded a proof. $\endgroup$
    – Victor Protsak
    Commented Aug 6, 2010 at 4:34
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    $\begingroup$ Thanks for your comment, VP. What you describe is a little before my time, mathematically speaking -- I remember exactly where I was when Wiles first announced his proof of FLT: in high school. I certainly believe what you say. Anyway, of course the mathematical world was quite stunned when the proof of FLT had been announced, because Wiles had been playing it quite close to the vest. A big reason that he did so was a (very plausible) perception that other experts would identify his approach as promising, to the extent of dropping what they were doing and try to get to FLT first. $\endgroup$
    – Pete L. Clark
    Commented Aug 6, 2010 at 7:06
  • $\begingroup$ I concur. Miyaoka was a big deal in the mid 80s. I remember when I took a history of math course in the mid 90s, this was actually a project (in our book from a few years prior): look up refs to the recent attempt on FLT and write something about it. I think I annoyed the prof by skipping the "look up refs" part (which sort of defeated the purpose of the exercise), relying on sci.math hearsay instead I suppose, but then I kind of blew off the course anyhow. $\endgroup$
    – Junkie
    Commented Aug 6, 2010 at 9:26
  • $\begingroup$ "...was a (very plausible) perception that other experts would identify his approach as promising, to the extent of dropping what they were doing and try to get to FLT first" Indeed, at least one other expert tried a remarkably close approach: modularity of the residual representation at the prime 2 and deformation. I shall not name him because he was apparently slightly abashed by Wiles announcement, but a good acquaintance with the field and a search for a publication gap in the crucial period between the proof of epsilon by Ribet and Wiles announcement should do the trick. $\endgroup$
    – Olivier
    Commented Mar 22, 2012 at 15:32
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There is Deninger's approach in which one hopes to produce the Riemann Zeta function via the trace of an endomorphism of an infinite dimensional cohomology group, related to foliated spaces: Read his own account or this talk by Eric Leichtnam.

It is sort of what you call the geometric approach in the question, but spiced up with dynamical systems and foliations.

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    $\begingroup$ There was a buzz back in the 90s with Deninger-ology, and some even said that a proof of RH was maybe a decade away. One cynic (an algebraist) was rather negative: Just need a good cohomology theory over things that aren't finitely generated and... $\endgroup$
    – Junkie
    Commented Aug 6, 2010 at 9:37
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    $\begingroup$ This is related to F_1 also. The absolute Galois group of F_1 is the additive group of the real numbers (as suggested by class field theory) so an action of the reals (i.e. a dynamical system) replaces the action of Frobenius in the function field case. $\endgroup$
    – Felipe Voloch
    Commented Aug 6, 2010 at 15:29
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I think, tautologously, any method proving the Riemann Hypothesis (or even seriously improving our knowledge on the zeroes) becomes "number theory" immediately. That said, I know what the question means: is there a dinky way of looking at the heat equation, say, that reduces what we need to prove to some piece of mathematics that is within reach?

Well, I don't know, and it is decades since I thought about these things seriously. I once thought topological entropy was a good start (and never heard the starter's pistol for that).

The most hopeful thing I have heard about this recently has been the work of Akiyama and Tanigawa (see http://www.ams.org/journals/mcom/1999-68-227/S0025-5718-99-01051-0/) which begins the process of connecting Sato-Tate with RH. I know no details, but Sato-Tate has come within reach. http://people.math.jussieu.fr/~harris/SatoTate/notes/equidistribution.pdf knows much more about this than I do, which wouldn't be hard. Assuming Extended Sato-Tate has some sort of traction on GRH at all, this is hopeful to me not because this is going to be the answer, but it might be "within one really new idea" of the answer. GRH is to be fitted into the general automorphic representation theory as the Artin conjecture has been for many years (?!). So there may emerge a conditional proof that is only (?) dependent on some things in Lie theory fitting together combinatorially or functorially as they should (?). I.e. we prove RH for the rationals by Harish-Chandra's technique over induction over all reductive groups and the way they fit into each other (?). People can tell where this is going by now. Weil's positivity derived from the explicit formulae doesn't come softly from commutative harmonic analysis, but perhaps there is a "hidden secret" in non-commutative harmonic analysis that will do.

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    $\begingroup$ The A/T note is not that meaningful, and such was already spun about by Ogg to some extenet in the 70s. They just say that fast enough convergence to the S-T distribution means that zeros are on the half-line. The S-T theorem is saying that (in essence) that there are no zeros on the 1-line for various symmetric power L-functions -- I guess it is better to say, S-T shows that these Sym have analytic continuation. So you have the familiar critical strip chasm, with the 1-line known, and the half-line expected. A simpler version is to say that $\sum_{n < X} \mu(n)/X$ converges to 0 fast. $\endgroup$
    – Junkie
    Commented Aug 6, 2010 at 9:45
  • $\begingroup$ A similar rephrasing appears (to me at least) in some of Fesenko's ideas about RH, where he uses. One of his equivalences just says that $\sum_{n < X} \mu(n)a_n$ has some convergence with $X\rightarrow\infty$, where $a_n$ come from an elliptic curve, maybe when the summand is weighted by some polynomials in $n$. UI'm not sure this made the final version of the paper. $\endgroup$
    – Junkie
    Commented Aug 6, 2010 at 9:54
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    $\begingroup$ Hmmm, I thought the point of Deligne's Weil II was that the gap between Re s = 1 and Re s = 0.5 could be bridged by "enough" tensor products. Well, no one is going to believe such ramblings, but if nothing else, Sato-Tate shows that the "moment method" isn't pie in the sky. $\endgroup$
    – Charles Matthews
    Commented Aug 6, 2010 at 14:58
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    $\begingroup$ Dear Charles: Alas, Deligne's trick with tensor powers relies on the $L$-functions being in $q^{-s}$, hence periodic in the imaginary direction, so non-vanishing on the line ${\rm{Re}}(s) = 1$ implies same on ${\rm{Re}}(s) > 1 - \epsilon$ for some $\epsilon > 0$. That little bit of positive gain can then be amplified using tensor powers, etc. So it doesn't seem to have relevance for the number field case. Even when the "moment method" is used over number fields (such as for Sato-Tate), it never gets off the line. See page I-22 of Serre's book "Abelian $\ell$-adic representations..." $\endgroup$
    – BCnrd
    Commented Aug 6, 2010 at 16:33
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Hey,

I remember that in an interview, Selberg said that what Conne did was essentially getting a "different access" to the explicit formula, but that his proof did not yield new "hard facts" about the riemann zeta function. However take me with a grain of salt: I am not an expert in algebraic fields.

At the same time analytic methods give us information that are of a statistical nature. So for example they are quite well suited to prove that there is a positive proportion of the zeros on the half-line (40%, which is impressive enough I think). They can also show that almost all zeroes are concentrated in a box of height T and width $10^{10}/\log T$ around the line $\sigma = 1/2$. So those results are very useful in their own rights: For example they allow us to prove that the prime number theorem holds in intervals of length $x^{1/2+1/10}$ something you would expect to know only assuming the RH or a quasi-RH. In fact for many arithmetic applications the results we already know allow us (often/sometimes?) to by-pass the Riemann Hypothesis.

So I wouldn't say that all approaches failed hopelessly. We are armed to deal with the problem, and paraphrasing Montgomery: "Sometimes I have the impression that we are missing just a fundamental insight to prove RH" .

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This is well below the technical level of the replies you seek and deserve (and which others more knowledgeable will no doubt supply), but I can't resist mentioning Freeman Dyson's idea, which I encountered in his "Birds and frogs" article in the Notices of the American Mathematical Society [56 (2): 212–223, 2009]. Here it is from a Wikipedia entry:

"The Riemann hypothesis implies that the zeros of the zeta function form a quasicrystal, meaning a distribution with discrete support whose Fourier transform also has discrete support. Dyson suggested trying to prove the Riemann hypothesis by classifying, or at least studying, 1-dimensional quasicrystals."

Update (9Nov12). See Nick S's recent comments.

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    $\begingroup$ When I met Dyson in 1998 or so, addressing a bunch of number theory grad students, he said the same: "Solve RH by classifying quasicrystals", though I can't say it has more value than as a catchphrase. $\endgroup$
    – Junkie
    Commented Aug 6, 2010 at 1:59
  • $\begingroup$ In his lecture "Birds and frogs" he devoted five whole paragraphs to this approach, so I think he is quite serious. $\endgroup$
    – Junyan Xu
    Commented Oct 22, 2011 at 6:28
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    $\begingroup$ Well his definition of quasi-crystals is not the one used by the quasi-crystal community (we actually don't have a formal mathematical definition yet).... His statement about icosahedral group is false, actually most 3-dimensional models don't have any symmetry group. Same issue for the 2 dimensional quasi-crystals, most of them are not related to polygons in the plane. And now lets move to the actual important point, what he said so far is irrelevant to the RH question (but shows that he probably learned about them from a non-expert).... So 1-dim quasi-crystals.... $\endgroup$
    – Nick S
    Commented Nov 9, 2012 at 22:54
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    $\begingroup$ ... cont. I really ahve no idea what he mean by "it is well known that "a unique quasi-crystal exists corresponding to every P- V number". The existence is true, the uniqueness is far for true... Unless I make a terrible mistakes, there are constructions which produce pure point diffractive sets from PV numbers, and they produce uncountably many... In many situations, but not always, one can probably get that most of them are "eqiuavalent" in some sense, but not all of them... And the big issue is that any equivalence in this sense, unless one adds very strong extra conditions, allows for $\endgroup$
    – Nick S
    Commented Nov 9, 2012 at 23:02
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    $\begingroup$ ... small translations of the points... And there are of course uncountably many models which are not associated to PV numbers....... Another issue is that the zeroes of the RZF are not a Delone set, so anything done so far by the quasi-crystal community is not relevant to the problem... And last, I really don't see how one can go around the following issue: Let $\Lambda$ be the set of zeroes. Let $\Lambda'$ be the set obtained by moving all the zeroes, such that the $n$'th zero is moved by at most $\frac{1}{n}$. Then diffraction cannot differentiate between $\Lambda$ and $\Lambda'$. $\endgroup$
    – Nick S
    Commented Nov 9, 2012 at 23:07
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I have no idea to what extent the idea of Saharon Shelah, about which I read in David Ruelle's popular account the mathematician's brain that uses mathematical logic to prove the RH is promising, but certainly it is different. For as far as I can understand (from Ruelle), it basically comes down to proving that RH is undecidable in Peano arithmetic, in which case the consistency of Peano arithmetic would imply its truth (also in ZFC).

EDIT: Here is the quote from Shelah's paper:

2.3 Dream: Prove that the Riemann Hypothesis is unprovable in PA, but is provable in some higher theory.

What basis does my hope for this dream have? First, the solution of Hilbert’s 10th problem tells us that each problem of the form “is the theory ZFC +φ consistent” can be translated to a (specific) Diophantine equation being unsolvable in the integers, moreover the translation is uniform (this works for any reasonable (defined) theory, where consistent means that no contradiction can be proved from it). Second, we may look at parallel development “higher up”; as the world is quite ordered and reasonable.

Note that there is a significant difference between $\Pi_2$ sentences (which say, e.g., for a given polynomial $f$, the sentence $\varphi_f$ saying that for all natural numbers $x_0 , \ldots , x_{n−1}$ there are natural numbers $y_0 , \ldots , y_m$ such that $f (x_0 , \ldots , y_0 , \ldots ) = 0$) and $\Pi_1$ sentences saying just that, e.g., a certain Diophantine equation is unsolvable. The first ones can be proved not to follow from PA by restricting ourselves to a proper initial “segment” of a nonstandard model of PA. For $\Pi_1$ sentences, in some sense proving their consistency show they are true (as otherwise PA is inconsistent). Naturally, concerning statements in set theory, models of ZFC are more malleable, as the method of forcing shows.

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    $\begingroup$ I would be grateful for any (one-two sentence) summary of Shelah's idea, which is not easy (for me) to extract from his Logical Dreams. $\endgroup$
    – Joseph O'Rourke
    Commented Aug 6, 2010 at 22:17
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    $\begingroup$ Is there actually an idea here, or just a dream? $\endgroup$
    – BCnrd
    Commented Aug 7, 2010 at 0:11
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    $\begingroup$ Has anything remotely like RH (on locations of zeros of a non-artificial function) been shown to be unprovable in PA? This dream sounds to me like the old canard that when you have a hammer everything looks like a nail. $\endgroup$
    – KConrad
    Commented Aug 7, 2010 at 5:39
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    $\begingroup$ OK, now that the except from Shelah's writing is given, I see there's no underlying idea at all; it is a speculative dream, so to speak of it being "promising" to yield insight on RH is putting the cart before the horse. In view of the fact that people have proved RH-type results in other settings (via the hard and brilliant work of Grothendieck, Artin, Deligne, etc.), I see no reason to take this dream seriously. It reminds me of the speculations "maybe FLT is unprovable?" before 1993, which were all forgotten after Wiles contributed real ideas to solve the problem. $\endgroup$
    – BCnrd
    Commented Aug 7, 2010 at 5:45
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    $\begingroup$ That survey has no statements I would consider number-theoretically interesting. The section on pp. 7--8 has some statements about the zeta-function, but none are naturally interesting on their own. The reference to Schinzel's Hypothesis H possibly being unprovable in PA also strikes me as completely speculative (along the lines of "we can't prove it, so maybe it's unprovable", with no more substantive rationale). I know Friedman has been trying for many years to find naturally interesting statements in number theory that are of broad interest and indep. of PA. AFAIK, the search continues. $\endgroup$
    – KConrad
    Commented Aug 7, 2010 at 8:37
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I heard it said by a number of mathematicians that the thing that sets the Riemann Hypothesis apart from (almost all) other famous unsolved problems is that no one has ever suggested a reasonable first step toward a proof.

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    $\begingroup$ I think twin primes is essentially the same. There's a lot of flotsam around both of them (like partial results with sieves, or density estimates on zeros), but none of it reaches the core of what is really going on for a proof of the desired result. $\endgroup$
    – Junkie
    Commented Aug 6, 2010 at 1:53
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    $\begingroup$ For the most part I agree with you, but I think the progress made toward twin primes is much more significant. $\endgroup$
    – Micah Milinovich
    Commented Aug 6, 2010 at 3:20
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    $\begingroup$ I can't name one progress toward twin primes, that has a chance of working to prove it. I was excited about Friedlander/Iwaniec and $X^2+Y^4$ for awhile, as it critically broke the parity problem, but it can't handle sparse enough sequences. Upper bounds are similar to density estimates on zeros -- simply what the technology can currently spit out. Chen's theorem is another mild chip, maybe somewhat like a zero-free region. None are close to twin primes. I might even argue the other way around, that the minimal progress toward RH is more significant, particularly the function field analogue. $\endgroup$
    – Junkie
    Commented Aug 6, 2010 at 9:34
  • $\begingroup$ @Junkie: One potential yardstick for progress towards twin primes might be any progress towards the Elliott-Halberstam conjecture, of which there has been very little indeed. $\endgroup$
    – David Hansen
    Commented Aug 6, 2010 at 23:24
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    $\begingroup$ Yes, I thought of E/H last night. Goldston/Yildirim again "comes close" to twin primes (or at least bounded gaps) in some metrical sense, but the sqrt bound on moduli is a huge barrier for Bombieri-Vinogradov (it can be crossed in very stringent circumstances, but these are not easy to enhance), so again I'm not sure it is real progress as I would like it. I could think to rephrase this: many ideas of attacking twin primes have yielded some partial results, but turn out to fall short in the end, and in some cases have exemplified what the deeper matter is (parity problem, sqrt bound). $\endgroup$
    – Junkie
    Commented Aug 7, 2010 at 2:45

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