Natalie Wolchover at Quanta has an article about a campaign by string theorists to argue that we have to accept string theory as our theory of fundamental physics even though there is no evidence for it because it is “unique”, the only possible theory. This is obviously utter nonsense. I’m headed out on a three-week trip tonight, with no time to write about this, but I will include much of two emails I wrote to Wolchover when she asked me about the papers she’s discussing.
Hi Natalie,
I have to admit that I have a really strong negative reaction to this sort of thing. A lot of people spent decades leading the field far down a blind alley. Now that it’s increasing clear to everyone that’s where they are, instead of admitting failure and hiking back to start over again, they’re working on sophistry to explain why the blind alley is the only possibility.
I haven’t looked at the two papers you mention carefully, but from a quick look:
1. Cheung et al. say they “argue for the uniqueness of string
theory from the fewest assumptions possible.” The sophistry is that by “fewest assumptions possible” they mean not “fewest assumptions possible grounded in what we know about nature”, but “fewest assumptions possible that lead to string theory”. Why make two assumptions (ultrasoftness and minimal zeros) about amplitudes that don’t correspond to anything about observed amplitudes or amplitudes in successful theories (i.e. QCD at short distances)? Of course, because those are characteristics of string theory amplitudes, and your agenda is to convince people to stay in the blind alley.2. Elvang et al. involves technicalities I know little about. But it seems to explicitly not be about quantum gravity, but about (SUSY) gauge theory in the planar limit. They’re finding the Veneziano amplitude there, but this is not really surprising. That the right way to understand a strongly coupled Yang-Mills theory like QCD is to look at the large N limit (planar is a version of this) and try and understand it in terms of open strings is a very old idea with a lot of evidence for it. That you need N=4 SUSY to make this work is certainly plausible.
It’s really wrong here to say that this “arrives at string theory as the unique UV completion.” Gauge theories, SUSY or not, are UV complete and have no short distance problem (they are asymptotically free, or for N=4 scale invariant). The short distance problem is for gravitational theories. Gauge theories instead have an IR problem (what are the strongly coupled at long distance states?) and this is what string theory is supposed to be good for in gauge theory.
By bringing the swampland and gravitational theories into it at the beginning and at the end of the paper, when their result is about something very different (the story of strings and gauge theory), it seems to me that the authors are all too willing to sign on to the “the blind alley is the only way!” campaign, encouraging a misreading of what they have done.
About SUSY, I just had an interesting experience today. Joanne Hewett was giving a colloquium talk about what you can learn about the Higgs at colliders. At the end, someone asked about SUSY: since it didn’t appear at its “natural” scale at the LHC, was there any reason for it to appear at new proposed colliders. Joanne admitted that she had believed the “naturalness” argument and expected SUSY at the LHC. She said that now she still “believes in SUSY” but acknowledges there’s no reason it should show up at the next energy scale.
She seemed to realize that a scientist saying they “believed” in something, even though it hadn’t shown up where expected and now they had no argument for where to look for it is kind of odd. So she explained that her argument was that SUSY is the only extension of Poincare symmetry (with certain properties), so she “believed” it had to be there.
I think where she and many people go wrong with this is not with the “SUSY is too beautiful a structure extending spacetime symmetry to not exist” argument. I’m somewhat sympathetic to that. The problem is that by “SUSY”, Joanne means a very specific way of implementing this structure as an N=1 SUSY extension of the Standard Model. For a very long time I’ve thought that specific proposal is ugly, and introduces vast numbers of unseen degrees of freedom and unknown parameters, instead of telling us anything about the ones we know about.
The N=4 SUSY gauge theory story is very different: this gives you a whole new sort of highly constraining symmetry (conformal symmetry). It tells you a huge amount about an otherwise completely mysterious subject (strongly coupled theories). The problem is this is not directly relevant to the real world theory. But it’s the kind of thing that tells you you’re on the right track. So, I’m happy to “believe” there is something about the real world captured by some version of SUSY, but if so it will have something to do with the N=4 SUSY gauge theory story, nothing to do with the supposed N=1 extensions of the SM that people have been unsuccessfully looking for.
……
(a later email)What I was referring to was first of all some well-known things about N=4 SYM that make it special (zero beta function, so conformal symmetry of classical theory is a symmetry of the quantum theory, also integrability in planar limit, the dualities you mention). These indicate there is something very interesting about this very special example of a SUSY theory.
But then you get the usual problem: the mathematically beautiful aspects don’t match the real world. So, you introduce mathematically ugly and very non-unique structures to break the symmetries and try and match the real world (with N=1 SUSY).
But the other thing I was referring to is that there are things going on in N=4 SUSY that I don’t think are well understood. You see this in the fact that many of the interesting applications of N=4 SUSY use “twisting”, with many different ways of doing this. This “twisting” mixes spacetime rotations and internal SU(4) (from N=4) symmetries. At the same time there’s a really confusing situation with the relation between the Euclidean and Minkowski version of the theory. When I asked one expert on how they were handling this in the work on lattice versions, he said “we do it in Euclidean signature, then just hope for the best if one tries to Wick rotate”
These problems are treated as technicalities, my guess is they’re not properly understood, so maybe there’s a different way of understanding things in which you end up with something like N=4 SYM that does have an interesting connection to the standard model and the real world. There are serious reasons for believing this, since in the work I’ve been doing, you get unexpected mixing between spacetime and internal symmetries when you understand how spinors behave when going from Minkowski to Euclidean. I certainly don’t though have a specific proposal about how to make this work for N=4 SYM, if I did I’d have written that up. But such speculation is one motivation for the things I’m doing now trying to sort issues like this out in simpler contexts.
As I test case, I wonder if the Cheung et al. style arguments can start with an effective field theory of pions (a sigma model) and show that from some general properties of the amplitudes of the effective field theory you are forced to arrive at QCD amplitudes. This seems like an analogue of the quantum gravity problem, in which GR is the the EFT but we do not know the UV completion.
Bob,
Cheung et al seem to me to be assuming string-type high energy behavior, so they will always get strings, can’t get anything like short distance QCD.
Bootstrapping pions suggests string-like amplitudes with a variety of Regge trajectories. It misses QCD. So maybe something similar happens with quantum gravity: the bootstrap might miss some theory where space-time emerges out of some unknown (fermion-like?) dynamics, that (similarly to QCD) becomes stringy in some ideal limit.
“…Woit, when I asked for his take, called Elvang’s finding “not really surprising.” He noted that trying to understand certain limits of QFTs in terms of strings is “a very old idea with a lot of evidence for it.”
In my view, this is overly dismissive…”
Giving the above emails such short shrift kind of infuriates me. It feels like Wolchover asked for your opinion for click/rage-bait purposes. She ignores your response about Cheung, et al., then misrepresents your take on Elvang, et al. by omitting the vast majority of your response to her inquiries.
I’m just an idiot layperson but it also seems intellectually/journalistically dishonest to couch your so-called ‘dismissive’ response in terms of, “…trying to understand certain limits of QFTs in terms of strings…”, when you don’t mention QFTs more broadly in your response at all; this is particularly glaring when your previous blog post noted that “…[a] basic problem with any claim to have ‘formalized QFT’ is that we don’t actually have an accepted definition of what a QFT is…”
I suppose it just bothers me immensely that you engaged with her inquiry in good faith, gave a thoughtful response after a quick look through the papers, and she brushed all of that aside, subtly implying that you’re just some string theory curmudgeon yelling at these new, intrepid, pioneers to get off your lawn.
Ryan,
I think Wolchover is making a good faith effort at understanding what is going on, and at reporting that there is a difference of opinion.
At the same time, the problem here, as often with string theory research, is that the technical issues are very complex and impossible for journalists to understand. Journalists who talk to experts hear from some of them claims that string theory is alive, healthy and the only way to go, from others that the subject is dead, don’t know what to believe.