There was a workshop last week at the Harvard CMSA, focusing on new ideas about physics rooted in topology. Talks are available on the workshop webpage, and those interested in high energy physics might be most interested in the ones from the first session. There was an interesting introductory talk by Dan Harlow, in which he lays out his view (which I think is a very mainstream one) of the current situation of HEP theory.
He begins by noting the problem of building higher energy accelerators (claiming that the problem is that technological limits make the maximum energy of collisions go as the square root of the radius of the machine, but I think really for proton-proton machines it is linear in the radius, for electron-positron machines the fourth root of the radius). Given the lack of new data, he describes one tactic for theorists as to change fields, e.g. to machine learning or biophysics.
If one does want to persist, he argues there still is a list of things incompatible with the Standard Model (gravity, dark matter, neutrino masses, baryogenesis, inflation) and these are not just “aesthetic” problems (here he refers to misunderstandings in the “popular media”, a clear reference to Sabine Hossenfelder and her book). From there he focuses on quantum gravity, essentially arguing that the other problems can be addressed by BSM models, but none of these seem particularly nice, so without new data progress is unlikely.
He describes quantum gravity as the ideal situation for theorists, since according to him there’s no self-consistent theory that fits the data we already have (I guess he’s saying string theory models are inconsistent…). He describes current work on this as based on two main strategies, with AdS/CFT providing a link between them:
- “Study the non-realistic corners of string theory where mathematical control is possible”, i.e. pick some non-physical string theory background (e.g. AdS/CFT) where you think you can do self-consistent calculations and do those, hoping to get some more general insight.
- “Set aside gravity for the moment, and focus on understanding the mathematical properties of QFT.” He gives a few examples of general questions being studied (which unfortunately have no obvious relevance to addressing the problem of quantum gravity, or basic problems like that of non-perturbative QCD.)
In the question section, there was an exchange between Harlow and Seiberg, based on Harlow’s reference to changing fields because of no data and to something he said during the talk (at 2:06):
Harlow: So then, what are we supposed to do in the meantime, right? You know we need to keep writing papers and posting them to hep-th and so on, so what do we do?
I suspect that for some context to the following exchange, you should also look at the video of the panel discussion earlier this year at Strings 2019, where Harlow, sitting next to Seiberg says (at 6:45) “We’re having fun, isn’t that the important thing?”.
Seiberg: I’d like to make one comment.
This was a beautiful summary, spectacular, except that one thing was fundamentally wrong and certainly should not be said. It’s not that we’re doing what we’re doing because we have to fill the time (audience laughter). We’re doing what we’re doing because it’s very important (audience laughter). I don’t think about “maybe we should write some books and this and that, until we have more information” I think this is wrong and this should not be [inaudible]
Harlow: I’m doing it, right, I don’t like wasting my time, so, I think it’s worth my time. I do think it’s important. We have this list of phenomena that we can see and can’t explain.
Seiberg: Comments like these have been used against us (audience laughter), in addition to the fact that they are wrong.
Harlow: OK, yeah, yeah, I’m not talking to the New York Times, right. (audience laughter).
Dam Son?: Is it recorded?
Harlow: I don’t know actually (audience laughter), I’ve said much worse things that were recorded, so.
HEP theory is at a very difficult point in its history, and it seems that the older generation struggling with this is not particularly amused to hear what sounds like flippant takes on the problem from the younger generation.
Update: I finally got around listening to the Susskind interview mentioned in this comment. Susskind also has given up on particle physics:
I originally was officially an elementary particle physicist. Elementary particles is not going so well, there’s no new experimental input and nobody knows what to do. It’s sort of reaching a point of, should I call it diminishing returns? It could change, it could easily change. I don’t think it’s doing very well. It’s not the fault of the physicists, it’s just the fact that they’ve reached a barrier, with no possible access experimentally to things that we’re not doing very well figuring out theoretically. So that’s not doing exceptionally well. My guess is the same thing may happen to cosmology. That they will eventually run, and they’re very close to it now, running out of new data, so there may be a barrier there.
Update: This week in Chicago there’s a workshop on the CEPC (proposed large new electron-positron collider in China). The first talk Monday was from Nima Arkani-Hamed. At the end of it, the question period started, with an exchange that resonates with the Harlow-Seiberg one:
Mike Peskin: So, let me make a quick summary of this talk: “my prediction is that when we go to high precision with the Higgs we will see no deviation from the Standard Model, but that will be a good thing because theorists will be inspired to think about these fundamental questions.”
Nima Arkani-Hamed: Absolutely. I’ve said it many times. Many people don’t believe me, but I believe it 100 percent. If we see some deviation, fantastic, great, people will have a lot of fun figuring it out, if we don’t see a deviation that’s a much, much bigger gauntlet thrown down at the feet of theorists to try to figure out what is happening.
Mike Peskin: But on the other hand you’re not promising any concrete discovery, just we reconfirm the Standard Model at a much higher level of energy.
Nima Arkani-Hamed: Reconfirming the Standard Model would just crank up the screws that are put on our theoretical imaginations even more.
Mike Peskin: How many billions of dollars do you expect people to spend to reach this conclusion?
Nima Arkani-Hamed: … However many billions it takes.
At the same conference, today Matthew Reece gave a talk on The Hierarchy Problem and the Motivation for Future Colliders. He starts out with:
I’ll review some arguments that may be well-known to many of us—but which I find are not necessarily well-known to students, some of whom are being taught that there is no motivation to search for BSM physics.
and gives this I think accurate characterization of the problem:
The better way to frame the problem, and the role of fine-tuning, is that we are seeking a theory that explains the origin of the EW scale.
If, within that theory, the EW scale is extremely sensitive to input parameters, it’s not a very good explanation. The theory does not generically describe a universe like the one we live in.
If moving around in parameter space just produces modest changes in the low-energy physics, that’s a compelling theory that predicts a world like ours.
This characterization makes clear what the correct interpretation of the null LHC results should be: they provide significant evidence that the picture of a very high energy scale GUT/string theory with lots of parameters, generically producing the weak-scale physics that we see, is just wrong. There never has been any evidence for this anyway, so the failure of the hierarchy argument was to be expected. To the extent that you believe the hierarchy problem is the motivation for BSM physics, students who are being taught to give up on BSM physics by Harlow and others are not really being misled.
My own take on all of this: what Harlow and Arkani-Hamed get wrong is their claim that thinking about fundamental issues of quantum gravity is some new, exciting question that has just come up post-LHC null results. These issues have been there for decades; they were obvious at the time I was a grad student in the early eighties. The problem is what to do facing several decades of failure by theorists, and I don’t think the answer is to make outrageous claims about how wonderful the current situation is. The motivation for a new collider is the one Reece points to, ignoring the business about the hierarchy problem: we don’t understand at all the origin of the EW scale. This is the best argument for studying the scales just above it that the LHC has started to enter. If we can get some new insight into the EW scale from a detailed study of the scales just above it, that will revolutionize physics (not just be “a lot of fun”). If we can’t, we’re facing a very, very tough time, especially if we insist on pursuing fundamental theory the way it has been pursued in the past.
