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.