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.
re what Harlow says about quantum gravity being the ideal situation for theorists, here are Susskind’s latest thoughts on some similar issues, talking about the “barrier” reached in both particle physics and cosmology, and why quantum gravity is probably the stuff to focus on right now.
He mentions Maldacena’s latest ideas as being the new biggest excitement, though I have no clue what they might be.
Aforementioned info is between 15:50 and 19:20.
PS: I also interpret that he says that string theory models are inconsistent… Hmmmmm, I thought he was a string theorist himself. Has he flipped?
What Harlow says I think is conventional wisdom in much of the “string theory” community (which these days mostly is not doing string theory anymore…), so it’s not surprising you’re hearing a variant of it from Susskind. The idea, as Harlow explains, is that the only fundamental problem left that isn’t hopeless without new data is quantum gravity, and any approach to quantum gravity should start with holography and AdS/CFT.
I don’t want to start a discussion here of the latest things Susskind and others are doing along these lines. I’ll just note that while Harlow makes it sound like this is new, this is pretty much the ideology the string theory community has been following for the past twenty years, and it seems to me that it has led them nowhere. The inspirational version you hear of this (it made an appearance in the “Chasing Einstein” film) is that the decks have been cleared and theorists are now confronting the most fundamental issues, space-time is doomed to be replaced by something new and exciting, inspired by AdS/CFT. The only problem is that this is not new, it’s older than my students here at Columbia, and nothing promising has been found to replace the doomed space and time.
At least it looks like they they are trying to think about how to not waste further time. I guess that counts as progress. If all goes well, then in 20 years they will understand what I wrote in my book.
For the record, I have a differentiated view on what problems are are actual problems in the foundation of physics and which are merely aesthetic misgivings. It’s not like I am saying they are all just aesthetic. I have eg been very clear in pointing out that dark matter and quantum gravity are “good problems”. I have a list here, in case you don’t like to waste your time…
LHC has been mostly completed, its theoretical consequences have been mostly discussed, if nothing new happens the field will decline in the next few years. What next? Two long-term possibilities that seem not totally hopeless are:
1) explore string vacua with supersymmetry broken at the string scale.
2) make AI really I. Many deep results in physics have been achieved by a few smartest physicists, and there are reasons to think that A-IQ should be scalable.
Indeed, Alessandro’s second point makes a lot of sense. There is almost certainly unexplored potential in the already existing literature where no one has made a connection that’s hiding in plain sight. I recently wrote about an example from a different field. Readers of this blog might also enjoy looking at one of the early examples of this kind of analysis that happens to be the first string revolution.
Am I missing something or is the claim that “we do not even have one self-consistent theory [of gravity] that fits the data we already have” really as outrageous as I perceive it to be?
So neutrino masses tell us there is physics beyond standard model. Why aren’t more people working on connecting this to BSM physics theories at LHC?
He’s referring to quantum gravity and the claim is not at all outrageous. As far as string theory goes, you don’t have an understood, self-consistent version that gives four flat space-time dimensions and a small CC (the “landscape” vacua are controversial for good reason). For other approaches to quantum gravity (eg. LQG) I don’t want to get into the often religious war of claims and counterclaims, but the argument that none of them have yet given a fully consistent model compatible with the real world is a defensible one.
Plenty of people have been doing this, for decades. I think Harlow’s claim (which I generally agree with) is just that all such BSM modeling has led to no compelling model, just a large collection of possible models, with no way of choosing between them unless we get some more relevant data. So, his argument is that best to stop working on this until and unless you get more data.
Seiberg says this is unhelpful to HEP, but also factually untrue: “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?”
And the exchanges illicit nervous laughter from the crowd.
The problem for HEP is that it is *not* untrue and that the public is getting wise and hence that laughter *should* be nervous. Even better if it were not laughter and the people in that room took the issue seriously rather than making comments about trying to hide the situation from The New York Times and worrying that the talk is recorded.
It is factually true that what the people in that room *do* is write papers. And that no one has been producing anything that really makes substantial progress on these problems for quite a long time. What *is* happening (and which is an unmitigated good thing) is that the problems themselves are starting to be classified and people are *starting* to think clearly about what problems are deserving of attention.
Of the two directions that Harlow mentioned I don’t think a lot of progress can be seen. The public is getting wise to this. We’re not all stupid.
Alessandro’s 1th option (SUSY’s broken at Plankian scales) would be the final give up in falsifiability, so not interesting at short/long-term. As the 2nd option (using AI), I bet you cannot fed an AI with the spectroscopic data accumulated in the XIX century and get “full” QM as an output (uncertainty relations, Dirac’s transformation theory etc.).
thanks for the second update.
Nima Arkani-Hamed: “Reconfirming the Standard Model would just crank up the screws that are put on our theoretical imaginations even more”.
Correct Nima… correct.
And it will probably put the final nail in the coffin to stuff like Susy.
Finally, no, we don’t need to through out “as many billions as it takes” to reach those conclusions. That final comment is absolutely ridiculous, especially coming from someone who is a top theoretical physicist.
But I guess that the wheel has to keep on turning…
Jackiw, I assumed that nothing new gets discovered. If we already collected all particles accessible to realistic experiments, and we already have their low-energy theory, writing wrong models and falsifying them would be a politically-correct way of making no progress. The only hope would be matching what we know about the low energy theory (about 75 digits measured so far) with a high energy theory. Unnaturalness of the weak scale and of the vacuum energy points to a landscape of >10^150 possible vacua, so the situation might be hopeless. Maybe not. So far this failed, but attempts focused on N=1 SUSY at low energy.
Most discussions about the LHC null results make it sound like experiments go out and look for new physics with no biases or input from the zeitgeist. This is not so, CMS and ATLAS were designed to look for new physics in signature spaces theorists were excited about. That’s why they are breathtakingly good at missing momentum and electromagnetic energy resolution. Of course there is a tradeoff, they aren’t as good at some others such as long lived particles or multiple low momenta particle signatures (compressed spectra). Yes, a large swath of BSM parameter space has been searched, but there are huge and important bits we are not sensitive to. Not yet.
I read your blog often. I have not commented before but I have a, possibly interesting, historical perspective on the topics in this post: quantum gravity, lack of experiments, and switching fields from physics to machine learning.
I did a PhD on quantum gravity in the late 1970’s (supervised by Stephen Hawking) and started a postdoc in the US, but soon left physics for artificial intelligence (the term “machine learning” didn’t exist at that time). I left physics because of several concerns. One was that quantizing gravity seemed very hard and all of the existing approaches had many problems. A second was the lack of experiments to guide and test theories (which was historically almost unprecedented). A third was that the research was becoming increasingly mathematical and I wondered whether it should be left to real mathematicians like Atiyah and Singer who had stronger mathematical tools. These concerns weren’t unique to me, but other people didn’t seem to find them so worrying. At that time, quantum gravity was fairly new (apart from a few pioneers like Bryce De Witt and John Wheeler) so most of my friends thought there could be breakthroughs soon.
But it seems that all these concerns remain valid almost forty years later. It is interesting that some leading physicists don’t seem to realize how old they are. And that AI/ML is a very old escape route (though AI was done at only a few universities at the time).
I followed physics at a distance and was surprised at the growing amount of physics stories about conjectures (e.g., about extra space-time dimensions) which had no experimental support (but which non-physicists friends of mine believed because they’d read them in books or news articles) . I found your blog and Lee Smolin’s book to be helpful reality checks and insightful about the sociology of physicists.
AI has been good to me (and I’m sure I was no loss to physics). AI also suffers from excessive hype these days, but the majority of AI researchers are fairly realistic about distinguishing between what AI can do now and what it has the potential of doing in the future (provided some very difficult problems are solved). Tough peer review, including the need to benchmark performance, keeps us fairly level headed. The hype is more from some start-up companies (financially motivated?), non-AI experts who have recently jumped on the AI bandwagon, and from reporters who realize that only the most exciting stories get on the front page.