Quanta magazine has a new article about physicists “attacking” the Riemann Hypothesis, based on the publication in PRL of this paper. The only comment from a mathematician evaluating relevance of this to a proof of the Riemann Hypothesis basically says that he hasn’t had time to look into the question.

The paper is one of various attempts to address the Riemann Hypothesis by looking at properties of a Hamiltonian quantizing the classical Hamiltonian xp. To me, the obvious problem with an attempt like this is that I don’t see any use of deep ideas about either number theory or physics. The set-up involves no number theory, and a simple but non-physical Hamiltonian, with no use of significant input from physics. Without going into the details of the paper, it appears that essentially a claim is being made that the solution to the Riemann Hypothesis involves no deep ideas, just some basic facts about the analysis of some simple differential operators. Given the history of this problem, this seems like an extraordinary claim, backed by no extraordinary evidence.

I suspect that the author of the Quanta article found no experts in mathematics willing to comment publicly on this, because none found it worth the time to look carefully at the article, since it showed no engagement with the relevant mathematical issues. A huge amount of effort in mathematics over the years has gone into the study of the sort of problems that arise if you try and do the kind of thing the authors of this article want to do. Why are they not talking to experts, formulating their work in terms of well-defined mathematics of a proven sort, and referencing known results?

Maybe I’m being overly harsh here, this is not my field of expertise. Comments from experts on this definitely welcome (and those from non-experts strongly discouraged).

While these claims about the Riemann Hypothesis at Quanta look like a bad example of a math-physics interaction, a few days ago the magazine published something much more sensible, a piece by IAS director Robbert Dijkgraaf entitled Quantum Questions Inspire New Math. Dijkgraaf emphasizes the role ideas coming out of string theory and quantum field theory have had in mathematics, with two high points mirror symmetry and Seiberg-Witten duality. His choice of mirror symmetry undoubtedly has to do with the year-long program about this being held by the mathematicians at the IAS. He characterizes this subject as follows:

It is comforting to see how mathematics has been able to absorb so much of the intuitive, often imprecise reasoning of quantum physics and string theory, and to transform many of these ideas into rigorous statements and proofs. Mathematicians are close to applying this exactitude to homological mirror symmetry, a program that vastly extends string theory’s original idea of mirror symmetry. In a sense, they’re writing a full dictionary of the objects that appear in the two separate mathematical worlds, including all the relations they satisfy. Remarkably, these proofs often do not follow the path that physical arguments had suggested. It is apparently not the role of mathematicians to clean up after physicists! On the contrary, in many cases completely new lines of thought had to be developed in order to find the proofs. This is further evidence of the deep and as yet undiscovered logic that underlies quantum theory and, ultimately, reality.

I very much agree with him that there’s an underlying logic and mathematics of quantum theory which we have not fully understood (my book is one take on what we do understand). I hope many physicists will take the search for new discoveries along these lines to heart, with progress perhaps flowing from mathematics to physics, which could sorely use some new ideas about unification.

**Update**: Some comments sent to me from a mathematician that I think give a good idea of what this looks like to experts in number theory:

The “boundary condition” is imposing an identification with zeta zeros by fiat, so the linkage of any of this to RH is basically circular. The paper at best just redefines the problem, without providing any genuine new insight. More specifically, as the experience of more than 100 years has shown, there are a zillion ways to recast RH without providing any real progress; this is yet another (if it makes any rigorous sense, which it does not yet do, yet the absence of rigor is not the reason for skepticism about the value of this paper, whatever the pedigree of the authors may be).

One has to find a way of encoding the zeta function that is not tautological (unlike the case here), and that is where deep input from number theory would have to come in. This is really the essential point that all papers of this sort fail to recognize.

Real insight into the structures surrounding RH have arisen over the past decades, such as the work of Grothendieck and Deligne in the function field analogue that provided a spectral interpretation through the development of striking new tools inspired by novel insights of Weil. In particular, the appearance of the appropriate zeta functions in such settings is not imposed by fiat, but is the outcome of a massive amount of highly non-trivial constructions and arguments. In another direction, compelling evidence and insight has come from the “random matrix theory” of the past couple of decades (work of Katz-Sarnak et al.) was inspired by observations originating with Dyson merged with work of the number theorist Montgomery.

Number theorists making a major advance on the puzzles of quantum gravity without providing an identifiable new physical insight is about as likely as physicists making a real advance towards RH without providing an identifiable new number-theoretic insight. There is no doubt that physical insights have led to important progress in mathematics. But there is nothing in this paper to suggest it is doing anything more than providing (at best) yet another ultimately tautological reformulation by means of which no progress or insight should be expected.

**Update**: Another way to state the problem with this kind of approach to the RH is that without number theoretic input, it is likely to give a much too strong result (proving analogs of the RH for functions that don’t satisfy the RH). For example, see the comment here (I don’t know if this correct, but it explains the potential problem).

**Update**: Nature Physics highlights the Bender et al. paper with “Carl Bender and colleagues have paved the way to a possible solution [*of the RH*] by exploiting a connection with physics. Some wag there has categorized this work as work with subject term “interstellar medium”.

**Update**: There’s an article about the Bender et al. paper here, with extensive commentary from one of the authors, Dorje Brody, who addresses some of the questions raised here (for example, why PRL if it’s not a physics topic?).

**Update**: Belissard has put up a short paper on the arXiv explaining the idea of the Bender et al. paper, as well as the analytical problems one runs into if one tries to get a proof of the RH in this way.

**Update**: One of the authors has posted on the arXiv a note with more precise details of the construction of a version of the operator discussed in the PRL paper.

The authors of this paper are humbly sharing some thoughts they have had that are relevant to the Riemann hypothesis. They are not claiming to have made profound progress. We can ignore their work if we like, there is no need to attack them. Carl Bender is awesome.

“Why are they not formulating their with in terms of well defined mathematics of a proven sort?” I assume they are simply explaining their ideas as clearly as they can.

Anonymous,

Publishing in PRL (and a claim to have a worthwhile new idea about the Riemann Hypothesis) is not really an act of humility, but a claim to have something significant that people should pay attention to. I’m paying attention, and commenting on what this looks like from the point of view of the math community. It’s a serious question and I think one I’m posing much more politely than most mathematicians would do privately: if they think they might have some progress towards proving the Riemann hypothesis, using tools that are not particular to physicists, but which mathematicians are experts on, why is there no engagement with mathematicians and their expertise?

I’m not at all an expert, but it seems strange to me that PRL would publish a paper on such a topic. It doesn’t exactly seem to be within their scope.

While I feel the piece in Quanta is hyping things a bit too much, I think you’re being a bit harsh in criticizing this paper’s appearance in PRL. They appear to be making progress on a research question that has interested a number of physicists for a number of years. For example, see the 2011 review article Physics and the Riemann Hypothesis (https://arxiv.org/pdf/1101.3116.pdf). One quote from this review article which stands out to me is the following:

“The advantage of this approach would be that the huge number of ζ(s) zeros are known and quick numerical algorithms have also been developed to find further zeros, thus solving the Schrodinger equation for large energies would be unnecessary. The Riemann zeta function could play the same role in the examination of chaotic quantum systems as the harmonic oscillator does for integrable quantum systems.”

That’s still a bit of hyperbole, but it illustrates why someone who studies chaotic quantum systems would be interested in the article you mention. It would get them closer to a computationally-practical toy model for understanding chaotic quantum systems.

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“and a simple but non-physical Hamiltonian”

There are physical systems described by PT-symmetric Hamiltonian. They describe non-isolated systems interacting with their environments, and have been studied in the laboratory, see e.g. https://journals.aps.org/prl/abstract/10.1103/PhysRevLett.103.093902.

Anon,

The Hamiltonian I’m referring to is the one discussed in the paper, their equation 1, which doesn’t appear in the paper you link to (or, as far as I can tell, in any other discussion of a physical system).

The story seems strongly reminiscent of one told by Paul Garrett in his notes on cuspforms (section 0.3 at http://www-users.math.umn.edu/~garrett/m/v/pseudo-cuspforms.pdf). In both cases, the zeta zeros arise as eigenvalues of some spectral problem which, alas, is not self-adjoint and therefore can’t imply RH. Additionally, the problem raised by both Garrett and the linked answer at MathStackExchange is the existence of certain Dirichlet L-series which are known to not have Euler products.

Much of my research (I’m now happily retired and doing genetic genealogy) centered on quantum chaotic behavior of vibrations of molecules in size from acetaldehyde to cyclohexylaniline.

The statement quoted “The advantage of this approach would be that the huge number of ζ(s) zeros are known and quick numerical algorithms have also been developed to find further zeros, thus solving the Schrodinger equation for large energies would be unnecessary. The Riemann zeta function could play the same role in the examination of chaotic quantum systems as the harmonic oscillator does for integrable quantum systems.” is interesting. However, we eventually found that no “toy” or “effective” theory ever agreed with experiment. Only very large (for their day) direct diagonalizations of the Schrodinger equation using very high order fits of potential surfaces to quantum electronic calculations did. The exact nature of the potential energy surface really mattered.

I would be astounded if this were not still true today.

The problem with this post is that it’s not clear whether it’s criticizing the media coverage of this paper (and of course we all agree on this), the paper itself, or the fact that it is published in PRL. After reading the post I went to the paper assuming to find the usual crazy bullshit that is usually criticized here, and instead I found a very decent paper, with a proper title, no malicious claims in the abstract, very well written and direct, and it connects to a previous line of research on the topic. So the question boils down to “is it worth PRL?”, and frankly there is so much crap in PRL in recent times, this paper does not really stand out as inappropriate (and then the problem would be PRL’s policies, and the good ol’ times, not this paper).

Also, from the comment of your anonymous colleague mathematician I was expecting a very bizarre and ad hoc boundary condition on the eigenfunctions that would involve the zeta function itself. It turns out, instead, that the shape of the operator, the boundary condition, and the condition that the operator has to satisfy in order for the RH to hold are extremely simple. I don’t think this contribution is more “circular” than are the other zillion ways to reframe the problem you mentioned, including those of the superstars in the field, one of which might eventually turn out to be the best at attacking a proof, and you never know which one it is until you got it. And after all, given your favourite set of axioms, in this sense all of mathematics is “circular”.

Jean Bellissard has weighed in on the Math Stackexchange you linked. The conclusion is devastating:

“In conclusion, the sloppyness of the definitions used but the authors leads to a complete mess. Nothing is correct in this paper.”

tomate:

The presence of any quantity of crap in any particular venue is NOT an argument for the addition of more.

tomate,

The intent of the post was to supplement what was in the Quanta article with my take on what this looks like from the point of view of the mathematics community, something which was lacking in the article, and in all coverage of this I’d seen elsewhere. I’m not one for insisting on rigid distinctions between what is math and what is physics, but this is a case where the general motivating problem is purely mathematical, the specific questions being pursued are mathematical, and the techniques being used are mathematical (rather than physical). Why don’t the authors engage significantly with the mathematics community and its expertise on these questions and techniques? I haven’t seen anyone address this, and I suspect that many physicists don’t understand the question, because they don’t understand what mathematicians do.

The Belissard comment on math stackexchange

http://math.stackexchange.com/questions/2211278/riemann-hypothesis-is-bender-brody-m%c3%bcller-hamiltonian-a-new-line-of-attack/2222146#2222146

I think shows well what kinds of concerns this work raises with experts, why don’t the authors engage with them?

Peter and Frank,

if I understand well the Belissard argument only came up yesterday, so we cannot charge the authors of not responding to this yet. If they do it seriously, it might take several months. If a lot of such arguments show up, and a discussion starts, then the paper has served its purpose. That real knowledge does not proceed through peer-reviewed journals is a matter of fact.

Let me point out that I do not personally care at all about this paper, I have no expertise on either the RH or on advanced techniques in QM, though I am a fond amateur on both. But I like new ideas wherever they show up and I find it fascinating that often physics becomes the language by which certain branches of mathematics are inspected in a more speculative and fuzzy way, at times when so much mathematics is just a tedious and fancy-less job about defining things properly and extending by an epsilon the validity of older theorems (not everybody out there is a Connes or a Grothendieck, you know…). Despite Belissard’s argument, which is quite technical, I am quite convinced that there might be a way a more creative mathematician might make sense of these arguments.

The problem with PRL, and with publishing in general, is certainly not that these journals publish too many ideas that are out of their scope, but rather that they publish too much “socially acceptable” stuff that is well within the mainstream, maybe a tiny bit more clever than others, and that can gather a lot of consensus just because they are supported by well-established and extremely closed communities. When this happens, you see popping up a lot of very dishonest titles and abstracts, supported by unclear arguments. And this is the same in physics and in math (and I do read a lot of math papers, though in other areas).

To me, this is not the case with this paper, which I find quite honest in its assumptions and scope. I don’t like Peter’s argument that the authors did not interface with the proper community because it sounds like the rooking of a community that does not want to have too much interference with its own business. In this respect, I would propose an “evolutionary” argument: If so much great math has failed on the RH, then probably time is ripe to NOT get too much intertwined with all the mental process that got that math stuck.

tomate,

I don’t think it’s a good way to do science to publish a paper in a high profile journal, and only then have experts in the subject point out well-known, serious and basic problems with what the authors are doing. Among other things, note that Belissard’s comments are probably not going to be seen by readers of the PRL paper or the arXiv preprint (as for my commentary and links, the arXiv bans trackbacks to this blog because I long ago offended certain powerful people in the physics community).

Sorry, but the attitude that you’re going to not bother to learn standard facts and acquire expertise about the topic you are doing research on, but dismiss it as “just a tedious and fancy-less job about defining things properly and extending by an epsilon” of no comparison to the power of your untutored physical intuition, is an attitude that, when there is physics involved, isn’t likely to help you get anywhere, and when there is no physics involved (as here), it’s sure not to.

Phys.org has also “covered” this today here: https://phys.org/news/2017-04-insight-math-million-dollar-problem-riemann.html with all the same problems Dr. Woit covered in the above-captioned post.

“I don’t think it’s a good way to do science to publish a paper in a high profile journal, and only then have experts in the subject point out well-known, serious and basic problems with what the authors are doing.”

This. I wish more academics would heed these wise words because virtually every academic field suffers from this problem. It’s beginning to impeach the credibility of academia which is the last thing this country needs right now.

As somebody who works on the zeta function for a living (and of course other closely related objects), I could see right away that this article is not bringing anything to the table… (Un?)fortunately mathematicians do not get to make a splash by putting forward sloppy, repetitive, not well researched approaches. I think that the authors of this paper will now be able to put in their grants that their work was advertised in Quanta, Nature, etc. and is therefore important. This incentivizes such behaviour, which is dangerous for the future of science, as it turns the objective from advancing research to making a splash with controversial (but ultimately vapid) claims.

P.S: on the analytic side, there are no new ideas in their paper, the formal inversion of the differencing operator was already known to Euler, this is how he derived the Euler Maclaurin formula, from which one can also obtain the analytic continuation of zeta. This obviously involves Bernoulli numbers and their generating function, around which, coincidentally the authors argument revolves.

Articles in Quanta Magazine are usually quite good, but they do seem to be very fond of stories where some outsider(s) solve problems that have stumped specialists.

I basically agree with the points Peter is making. But I don’t fault the authors. This kind of paper is essentially impossible to publish in a pure math journal. And for a problem of this magnitude, collaboration with mathematicians is difficult because they tend to be dismissive, often for good reason. The issue of rigor is important, but only a part of the problem. I think they would pay attention to a truly novel idea. Publishing in PRL for this kind of problem almost ensures that mathematicians will not pay much attention to it, which may be justified; I prefer not to weigh in on that.

Having worked on this problem over several years, I remain skeptical about the whole Hilbert-Polya idea. It’s been a bit of a pipe dream, although not ruled out. It is well-known that the statistics of the zeros is conjectured to be described by random matrix theory (Montgomery). This motivated Berry-Keating in their interesting work, which did not conclusively resolve the problem. My own point of view is that the connection with random matrix theory would seem to cast doubts on Hilbert-Polya rather than support it. It would seem unlikely that a simple, non-random hamiltonian would capture the exact zeros, but that is not a rigorous counter-argument. Success would be analogous to being given an infinite list of essentially random eigenvalues and trying to reconstruct the operator that led to them. Heuristically speaking, the “randomness” of the zeros is related to the pseudo-randomness of the primes themselves. I agree with previous remarks that the fact that no deep aspects of number theory enter into their approach makes one wonder. As Peter’s math colleague wrote, it appears that the construction of the model brings in too much information about the zeta function itself, via the boundary condition, so that perhaps the RH is built into the model from the beginning.

Peter,

It might be useful putting another update to your post since one of the authors of the PRL posted a reply on arXiv https://arxiv.org/abs/1704.04705

Malek

Abdelmalek Abdesselam,

Thanks, I will add that. Glad to see this sort of thing, with precise statements so that one can see what exactly is going on.