Sabine Hossenfelder’s new book Lost in Math should be starting to appear in bookstores around now. It’s very good and you should get a copy. I hope that the book will receive a lot of attention, but suspect that much of this will focus on an oversimplified version of the book’s argument, ignoring some of the more interesting material that she has put together.
Hossenfelder’s main concern is the difficult current state of theoretical fundamental physics, sometimes referred to as a “crisis” or “nightmare scenario”. She is writing at what is likely to be a decisive moment for the subject: the negative LHC results for popular speculative models are now in. What effect will these have on those who have devoted decades to studying such models?
Back in 2006 Lee Smolin and I published books concerned about where fundamental physics was heading, and five years ago Jim Baggott’s Farewell to Reality appeared with another take on these issues. Hossenfelder’s is the first book on this topic to appear since the LHC results showing a vanilla Standard Model Higgs and no evidence of supersymmetry or other speculative BSM physics. The remarkable thing she has done is to address this in a characteristically direct manner: go talk to those responsible and ask them what they have to say for themselves.
Four of the people that Hossenfelder interviews would be on any short list of the most influential figures in theoretical particle physics, both responsible for where we are now by their past actions, and looked to by others for a vision of where the field is going next. They are Nima Arkani-Hamed, Steven Weinberg, Frank Wilczek, and Joe Polchinski.
Arkani-Hamed is introduced with:
He’s won loads of awards, including the inaugural 2012 Breakthrough Prize for “original approaches to outstanding problems in particle physics.” The problems are still outstanding. So is Nima.
and here’s an extract from the interview
“Has the LHC changed your perspective on naturalness?” I ask.
“It’s interesting–there is this popular narrative now that theorists before the LHC were totally sure that susy will show up, but now there’s a big blow. I think that the people who are professional model builders, the people I consider to be the best people in the field, they were worried already after LEP… The good people, they were not at all sure susy would show up at the LHC. And nothing has changed qualitatively since 2000. Some loopholes have been closed, but nothing has changed qualitatively…”
As with many of the interviews, Hossenfelder intersperses her own internal response to what she’s hearing:
But not one of those “best people” spoke up and called bullshit on the widely circulated story that the LHC had a good chance of seeing supersymmetry or dark matter particles.
She doesn’t mention, but surely is aware, that many prominent theorists pre-LHC had made public bets that the LHC would find SUSY, and that those wagering this way included Arkani-Hamed himself. For accounts of the 2016 Copenhagen event where the bet was paid off, see here and here. You can read there what Arkani-Hamed had to say then about losing the bet, and the quote:
“I think Winston Churchill said that in victory you should be magnanimous,” Damgaard said after Arkani-Hamed’s talk. “I know also he said that in defeat you should be defiant. And that’s certainly Nima.”
In the interview with Hossenfelder, Arkani-Hamed goes on to say:
The people who were sure it would be there are now positive it’s not there. There are people now who speak out about being depressed or worried or scared. It drives me nuts. It’s ludicrously narcissistic. Who the fuck cares about you and your little life?
There’s a lot more in the interview and you should get the book and read the whole thing. Hossenfelder does a wonderful job of portraying both Arkani-Hamed’s serious arguments and his aggressive “Damn the torpedoes” self-confident attitude. This is not someone who is going to admit that, whatever bet he lost, some failure has occurred that indicates this is a time for reflection on mistakes made and reevaluation of the path forward.
Hossenfelder travels to Austin, Texas to talk to Steven Weinberg, who it appears may not realize she is a physicist, just has been told he is supposed to talk to a “writer”. She notes that:
Weinberg doesn’t talk with you, they told me, he talks at you. Now I know what they mean. And let me tell you, he talks like a book, almost print-ready.
I won’t try and reproduce much of her conversation with Weinberg, the multiverse is a main topic (she thinks it’s an empty idea, Weinberg is willing to go along with it). About where particle theory is headed, Weinberg says:
I don’t know how much elementary particle physics can improve over what we have now. I just don’t know. I think it’s important to try and continue to do experiments, to continue to build large facilities… But where it will end up I don’t know. I hope it doesn’t just stop where it is now. Because I don’t find this entirely satisfying…
I don’t take seriously any negative conclusion that the fact that the LHC hasn’t seen anything beyond the standard model shows that there isn’t anything that will solve the naturalness problem… Supersymmetry hasn’t been ruled out because it’s too vague about what it predicts.
Her next interviewee is Frank Wilczek, who she finds in Tempe, Arizona. His take on string theory unification is rather negative:
… it’s not clear what the theory is. It’s kind of miasma of ideas that hasn’t yet taken shape, and it’s too early to say whether it’s simple or not–or even if it’s right or not. Right now it definitely doesn’t appear simple.
Asked about the argument that string theory could reproduce gravity, Wilczek responds:
If your standards are low enough, yes. But I don’t think we should compromise on this idea of post-empirical physics. I think that’s appalling, really appalling… If there was any bit of experimental evidence that was decisive and in favor of the theory, you wouldn’t be hearing these arguments. You wouldn’t. Nobody would care. It’s just a fallback. It’s giving up and declaring victory. I don’t like that at all.
Wilczek is still unwilling to give up on SUSY and the idea of a SUSY GUT, with his main argument the coupling constant unification calculation he did with Dimopoulos and Raby back in 1981:
“They haven’t found susy partners, though,” I say. “Is this something that worries you?”
“I am starting to get worried, yes. I never thought it would be easy. There have been bounds from [the LEP experiments] and proton decay for a long time, and this indicated that a lot of the superpartners have to be heavy. But we have another good shot with the [LHC] energy upgrade. Hope springs eternal… I would definitely not believe in supersymmetry if it wasn’t for the unification of gauge couplings, which I find very impressive. I can’t believe that’s a coincidence.”
It’s not mentioned in this book [actually, she does mention this], but Wilczek has already paid off one bet about SUSY (with Garrett Lisi) and likely will have to pay off another next year. I don’t know if by “energy upgrade” he’s thinking of the HE-LHC, or the 100 km much bigger proposed ring, but in any case those won’t happen before at least 2040. No matter what happens, I don’t think Wilczek will ever change his mind about the SUSY-GUT paradigm he has found attractive since the 1980s.
In January 2016 Hossenfelder traveled to Santa Barbara to talk to Joe Polchinski, who was already sick with the brain cancer that ultimately would take his life two years later. Unlike Wilczek, Polchinski was a fan of string theory and of evaluating it by “post-empirical” criteria. He at one point published a “Bayesian” calculation arguing that string theory is correct with probability “over 3 sigma” (i.e. over 99.7%). Asked about prospects for a unified theory, Polchinski says:
I think string theory is incomplete. It needs new ideas… But string theory has been so successful that the people who are going to make progress are the people who will be building on this idea.
Arkani-Hamed, Weinberg, Wilczek and Polchinski reflect a range of points of view about the current situation and what it means. Unfortunately it seems to me that they share an unwillingness to face up to failure, and this doesn’t bode well for the future of particle theory, with “more of the same” the agenda that is being set.
Besides these four interviews, the book also contains accounts of meeting and discussions with quite a few other physicists, all well worth reading, and often written with a sly humor. The description of visiting Garrett Lisi on Maui is not to be missed, and he has a lot of sensible things to say (“For a surf bum, he’s surprisingly intellectual” the author writes). He tells the story of how Jacques Distler and others threatened (unsuccessfully) to organize a boycott of Scientific American if it published an article by him. In addition to the interviews there’s a great deal of valuable discussion of the problems with the way research is organized and the reward structures scientists operate under (for instance, publicly admitting failure is definitely on the “not encouraged” list).
So far I’ve ignored the main framing device that Hossenfelder uses throughout the book, that of her questioning the idea of “beauty” as a motivation for evaluating ideas about physics. This is not because I disagree all that much with what she writes, but instead that I fear a complex set of issues is likely to get over-simplified, and this over-simplified version of the book’s argument is all that much of the public is ever going to hear about it. Hossenfelder explains that the concept of “beauty” she is challenging is a specific set of ideas about “symmetry, unification and naturalness” that she sees as dominating physics research. I agree that there’s a problem with this specific set of ideas and how they have been used, but I’d keep them separate and don’t see putting them together as “beauty” to be helpful. At various points she makes it clear that her worry is that we are getting stuck due to outdated notions of “beauty”, while still believing that successful new ideas will come with a new form of “beauty”.
The book ends with
We know that the laws of nature we presently have are incomplete. To complete them, we have to understand the quantum behavior of space and time, overhauling either gravity or quantum physics, or maybe both. An the answer to this will without doubt raise new questions…
…There’s much work to do. The next breakthrough in physics will occur in this century.
It will be beautiful.
Update: Science magazine has a review. For some reason they seem to have decided it was a good idea to have the book reviewed by a postdoc doing exactly the sort of work the book is most critical of. The review starts off by quoting nasty anonymous criticism of Hossenfelder from someone the reviewer knows on Facebook. Ugh.
Update: I’ve written a similar but somewhat different version of this review for MAA Reviews, one aimed more at mathematicians.
Update: More reviews here and here, as well as a posting from Hossenfelder where she explains her current professional situation in the context of deciding to write the book.
Update: I’m glad to see that Science has edited the review there to remove the use of an unattributed quote.
Garrett brings up the bet with Frank Wilczek and I mention this bet and the other susy bet in the last section (to say who won and who lost). Thanks for the review! Best,
Raising these issues 20 years ago was useful and needed courage. Now it’s useless
@AS: Raising these issues 20 years ago was useful and needed courage. Point is, nothing changed: so, may be, it’s not completely useless to continue raising these issues.
Yes, I did notice while reading the book that you had mentioned the bet with Garrett, but had forgotten that when I wrote the review, just edited to fix it.
The “demand for alternatives” style of riposte comes up so frequently I think it deserves its own blog. Not so much a refutation of the “only game in town” assertion, which is really a separate issue. I’m thinking more of this highly prevalent notion that, assuming there really is only one game in town, one is therefore compelled to play it or shut up. In fact, the original joke is only funny because the players know the game is rigged. It doesn’t seem to occur to them to just stop playing and find some other way to occupy their time. A rather sad explanation might be that they’re compulsive gamblers, and simply can’t help themselves.
Why doesn’t it occur to people that it’s quite enough to point out the game is rigged? Why is it incumbent on him or her doing this service to also have another game at the ready, or refrain from comment? Of course it would be preferable if an alternative could be proffered immediately, but that’s not the point. It’s the responsibility of the player of the rigged game to act on that knowledge rationally, i.e. stop being cheated, maybe take a break and at least think about your next occupation if you’ve got nothing better to do. Why is it someone else’s job to figure all that out for you? Apparently many folks feel that it very much is the critic’s job, which is truly strange.
Oh come on! LHC has not found evidence of new physics *in the easy to look for signatures*: lepton or jet resonances, large missing momenta, multiple leptons, etc.
There are so many ways we could be missing the new physics signals. It could be decaying to many jets (the multi-jet background is millibarns, and we don’t understand jet production even to leading order, so it is tough picking out a new physics signal at femptobarn production cross section). It could be long lived. It could be very low mass (LHC detectors can be blind for low mass signal, but we are figuring out clever new techniques). It could be a high mass thing decaying via lots of intermediate states, shooting off very soft pions at each step. There are so many hard to find places that new physics could be hiding, and we have just started. LHC data taking started less than a decade ago.
(of course, when I say “easy to look for” I mean doable, but with LOTS of hard work)
A multiverse believer probably should not think that our universe has beautiful laws, simply because universes with ugly laws obviously outnumber universes with simple, beautiful laws.
Once I met Sabine Hossenfelder at a conference in Warsaw. I was standing in front of the conference schedule, and she dropped by and pointed out to me her own talk in the schedule, and said that that was the talk I absolutely have to go see. I thought it was pretty strange and narcissistic. I didn’t go to listen to her talk. Nor will I go read this book.
I think the reference to negative LHC results “for popular speculative models” is pretty accurate, specifically I had in mind technicolor, SUSY, extra dimension models. In, for example, minimal SUSY with 100+ extra parameters, it’s not completely clear what “generic” means but the possibilities you list seem to me to correspond to arguably “non-generic” cases. The full parameter space will never get covered and minimal SUSY will never get completely ruled out, but it becomes less and less plausible that the superpartners are hiding in exactly the regions hard to access experimentally.
To be clear, while it’s accurate to say that the LHC has so far seen no non-SM physics, that certainly doesn’t mean it’s not going to, there’s a very long ways to go and many places to look. To the extent early searches have been focused on looking for specific signatures of implausible SUSY and extra-dimensional models, as those searches get done and people move on to look for other things, arguably the chance of success will go up…
I met Sabine in person for the first time a few months ago, and she did not strike me as unusually narcissistic, but did strike me as unusually direct. At your conference in Warsaw likely all the other speakers standing around also thought that you should be going to their talk, but unlike her they didn’t directly tell you this.
I’m curious to see what the reaction to her book will be, as compared to what happened back in 2006 with my book and Lee Smolin’s. Smolin and I certainly both thought our ideas were important and people should pay attention to them, but I think we both lack Sabine’s directness, which may be useful to her in getting attention for her ideas.
Michael Harris’ “Mathematics Without Apologies” made the point that mathematicians and physicists are some of the last people to still use beauty as a criterion for their efforts, artists having long ago abandoned that standard. I recall being quite struck by that.
” The review starts off by quoting nasty anonymous criticism of Hossenfelder from someone the reviewer knows on Facebook. Ugh.”
I’m starting to get the impression that Science mag is losing respectability a bit.
“Raising these issues 20 years ago was useful and needed courage. Now it’s useless.”
Not at all; as Peter points out, this book comes out post-LHC results. Sounds interesting and I’m hoping to get it. Thanks for the review.
Peter, first please call me Amit.
Basically any beyond-SM stuff that shows up (at LHC or in some underground tank ) has a mass scale, some effective coupling to the SM, and possibly quantum numbers like charge, flavor, color, lepton number. A complete top-down model like SUSY is one way to generate these but frankly simple ad-hoc models that map out the space of possible new physics signatures are more helpful right now.
So even if the parameter space for (some minimal version of) SUSY is more or less covered, that hardly means that the parameter space for all possible new physics signatures allowed by field theory is eliminated.
I can’t recall neither you nor the conference, but clearly we don’t share the same sense of humor.
20 years ago many influential theorists did not want to see what was going to happen, so it was useful and “dangerous” to point out the problem. It was as useful as alerting about a possible subprime mortgage bubble. After that both bubbles bursted, it’s now useless to write a book about “idiots who lost their house”. What was overpriced is now underpriced: there are potentially interesting ideas which are not being explored because they belong to fields that presently have an excessively bad reputation among young theorists.
“For some reason they seem to have decided it was a good idea to have the book reviewed by a postdoc doing exactly the sort of work the book is most critical of. ”
Why do you need to specify she is a postdoc ? How is this relevant ? Why not say “a researcher” ?
Dear @Luca, what AS was saying (most probably) that, raising these issues 20 yeas back would have been fruitful and would have directed the physics to the meaningful trajectory but now it has gone to irreversible and unfortunate distance…. so that it is now useless even to talk about it. But, it is never too late…. for a good thing or correction.
^^^ After the bubbles burst, it is worth understanding what happened to keep it from recurring.
Peter, you said:
>as those searches get done and people move on to look for other things, arguably the chance of success will go up…
Both ATLAS and CMS already have large groups looking at non-SUSY signatures for new physics.
Both experiments have set up multiple physics groups that concentrate on a specific type of signature and build up analysis expertise. Both have an “Exotics” group that is separate from the SUSY group, and searches for things like microscopic black holes, long-lived signatures, quark substructure, multi-jet resonances, particles with both lepton and baryon number, 4th generation particles, Majorana neutrinos…
If you are under the impression that somehow experimental physics is in the thrall of SUSY and only when it is completely wiped out (ha!) will our imaginations be freed, you are mistaken.
PS: If you have any clever ideas for possible beyond-SM stuff that you feel is being ignored (SUSY or not), feel free to share. Of course your ATLAS colleagues at Columbia might like to get a first crack at it 🙂
We begin to see more and more questions paraphrasing “has physics gone off the rails?” In other words, has the *science* gone off the rails? But this is backwards.
Dr. Hossenfelder’s book shows that the political environment of the field has gone *completely* off the rails, as shown by the fact that people who have real ability and real accomplishments are quoted spouting utter, patent nonsense.
When this happens, to any field, the substantive efforts must follow the politics off the rails. (If this is not obvious, I do *not* refer to the internal party politics of any nation or even to the corresponding meta-politics; I refer to the ideological premises that constrain the public discourse within a field of inquiry.)
I was just trying to come up with some reason for optimism… Was not trying to imply that the LHC experiments are currently overly devoted to looking for SUSY. Actually, over the past year or so I’ve been struck by how little activity there is on that front (i.e. few new SUSY limits based on 2017 data).
The problem of who to share my promising new idea about an LHC testable improvement of the Standard Model with has not yet come up…
The level of experience in the field of the reviewer is relevant. I still think it is an odd decision of Science to commission of a review of a book like this from someone only one year past their Ph.D. (and, as far as I can tell, no experience writing book reviews).
Enjoyed your informative review of Sabine’s book. Gave me a sense of the book. It’s unfortunate that the review published in Science was more focused on snark than being informative.
Allow me some replies to three comments:
@Thomas, in addition, a postdoc is not tenured yet so highly dependent on their seniors’ views of them.
@Amitabh, the point is that all predicted (either minimal or reasonable) parameter space by the theories criticized here has been excluded. This is very different context than the general searches at LHC experiments. Also, during the first years of LHC running, the physics groups had to make very real-world decisions on which analyses get priority (in computing and human time).
@AS, right now we are in the middle of the “bubble bursting” but it shows no sign of slowing down. For instance, multiverse has started taking over public science writing during the last year.
There are disciplinary issues here as well. Biologists quickly learn that “brilliance” alone is not sufficient to understand the complexity of (history-dependent) biological systems.
Physicists, particularly of the theoretical-type, appear to believe that everything can be deduced from first principles or hypothetic, unobservable constructs – that brilliance is everything (together, perhaps, with an excessive self-confidence even in the face of serious miscalculation).
see Bernstein, R. (2015). “Belief that some fields require ‘brilliance’ may keep women out.” Science. http://www.sciencemag.org/news/2015/01/belief-some-fields-require-brilliance-may-keep-women-out
I’ve heard Wilczek stress the coupling constant unification/SUSY calculation several times. As a rank outsider, I’ve always been impressed with this, but then you read that maybe it’s not so special after all. I have no way of evaluating this. On the one hand, Wilczek is obviously in the first rank, and you can’t ignore his opinions. On the other hand, the coupling constant unification is his baby, and maybe he seriously overstates its importance. Wish I knew.
Dempsey : from Bee, 2007
Read the comments too.
Dempsey, you may want to have a look at what Wilczek wrote in his Future Summary from 2001:
“5.5. Produce the New Particles!
Of course, the ultimate test for low-energy supersymmetry will be to produce some of the predicted new R-odd particles. Even in the focus point scenario, there must be several accessible to the LHC.”
Now that the results from the LHC are in, it is clear that at least low-energy SUSY is plain wrong.
The idea that “science is being led astray by aesthetics” (as I put it) was the thesis of my 2012 book Truth or Beauty: Science and the Quest for Order (Yale UP). Glad to see that some physicists are coming round to the same idea!
I looked into this when writing “Not Even Wrong” and wrote about it there. At the time, one recent source was this
“The supersymmetric gauge coupling unification misses by about 10%. More precisely, the experimental value of the strong coupling is about 10-15% lower than the value computed by running down theoretically from the point were the SU(2) and U(1) couplings meet.”
I haven’t looked for more recent versions of this calculation. From what I remember, one part of the story is that the two-loop calculations make agreement worse, people often refer to the better agreement at one-loop. Also, how you numerically categorize the accuracy of this calculation depends on how you formulate things (I think it looks better if you fix observed couplings and compare extrapolated couplings at the GUT scale).
There are also two generic problems with this kind of calculation, indicating one shouldn’t take any particular numbers too seriously:
1. The result depends on what you choose as your scale of SUSY breaking, as well as other details of the many coupling in the SUSY model.
2. These calculations inherently assume a “desert”, that there is no physics affecting the coupling constant running, in between the TeV scale and the GUT scale. I think most theorists have always felt this is an implausible assumption.
All in all, this has always struck me as a rather weak argument, and I suspect Wilczek’s fondness for it has something to do with his involvement at its birth.
A more recent SUSY unification++ calculation: nothing much changes, I think. https://softsusy.hepforge.org/doc/threeLoop.pdf
I’m a professional comedy writer, and an avid reader of Sabine’s writings (e.g., her blog, her comments to others’ blogs). I can’t wait to read her book.
She’s absolutely hilarious, and when I read your comment about what she said, I laughed out loud (for the most recent time) at her wit, self-awareness, irony.
Perhaps there’s a language barrier, perhaps you are humorless (or “differently humored”). Dunno.
I don’t know why everyone is so concerned what the Very Intelligent People are thinking about the multiverse or the landscape or whatever. I’m not up on my history of science but wasn’t a similar group declaring physics over with in the late 19th century? This is what happens when theory runs ahead of experiment.
We need the 21st century versions of the Michelson–Morley and Rutherford results. And I am hopeful on that front. I can only speak to my small corner but the work going on in detector design, data analysis, triggers, etc is stunning. Truly bleeding edge. There are techniques being developed for microsecond trigger decisions that rival full offline analyses from a couple of decades ago. If it’s there we’ll find it. It won’t be “here’s SUSY” or “here’s the techni-pions” or whatever. It will start out as an excess that won’t go away, and build. Theorists (the good ones anyway) will jump on it and all this metaphysical talk will be forgotten like that 19th century end-of-physics talk.
I wish people would stop using “physicists” or “theoretical physicists” to mean “high-energy particle physics theorists” when issuing condemnations such as Mike Klymkowsky’s above:
or more importantly because it’s being read by more non-experts, Dan Falk’s article about Sabine’s book:
There’s a lot of top-notch theoretical physics going on today in many fields – condensed matter physics, fluid dynamics, biophysics, astrophysics, etc. Experts will realize that the above complaints are really complaints about one specific branch of theoretical physics. But ordinary people may not realize this. They may actually believe it when people say theoretical physics is going down the tubes! I think anyone who really cares about physics should avoid spreading this wrong impression.
Well, I said “high-energy particle physics theorists”… but maybe what people are really complaining about is “theoretical physicists seeking new fundamental laws”, or something like that. I just want people to be specific about their complaints, not to tar lots of innocent victims with the same brush.
Thank you, John. Bear in mind that often it’s not just journalists, but the high energy theorists themselves who use all of “physics” as shorthand for their piece of it. It would be great to break them of that habit.
Finally someone pointed to this issue here. Many times physicists (high energy theoretical physicists, more especifically) use the term theoretical physics as synonyms for high energy theoretical
physics, and this is a huge mistake. For exemple, in my research area (condensed matter physics)
We living a great moment, hot topics , for example, topological phases of matter, exotic excitations, high temperature superconductors, transport in
mesoscopic systems (non-equilibrium dynamics), open systems, low-dimension physics and the Fermi liquid breakdown, strongly correlated electrons, etc. All topics above using complex theoretical techniques and bring up important new results in theoretical and mathematical physics every day (and more important,
for us physicists, with experimental results). Then, I believe that high energy physcists must be more carefull with the term “theoretical physics” .
Yes, Douglas, it’s the physicists themselves who should take the lead, by explaining that there’s a lot more to theoretical physics than the quest for a “theory of everything”… and the rest of physics is doing just fine. Theorists focused on this quest may not want to admit this, but in the long it’s in their own best interest.
Nature Magazine also has a review out.
I rather like Siegel’s unequivocal focus in his review, a point he’s made again and again: beauty may or may not be a reliable guide, but it must be acknowledged that the beautiful ideas in question have simply failed. No mealy-mouthed excuses about the unexcluded regions of whatever parameter space, or undue acknowledgement of those counter-arguments. They have already proven to be wanting. When evidence falsifies, it’s false. When evidence is unobtainable, it’s folly. Period. Evidence is the only truly reliable guide, period. Seek it elsewhere, and only where there’s some hope in finding it. It’s worth shouting from the rooftops. Cognitive biases and fashion and sociology are all worth mention, but should be painfully obvious culprits in human affairs. How anyone could claim to be free of them is hard to fathom. That they do is still unsurprising. Trust empirical evidence, reproduced, and nothing else. I believe that is not only the key to the survival of all science, but of our species as well.
My problem with this is that I don’t think it’s so simple, in particular I don’t think it’s a simple failure of “beauty”. For instance, in the case of SUSY, there’s a good argument that the super-extension of the Poincare group is a “beautiful” idea, but this idea immediately runs into the problem that you need to break the symmetry (explicitly or spontaneously) and what you get is very unbeautiful (eg. over 100 extra parameters to describe the possibilities). So, to me, what the LHC was testing (SUSY extension of the SM, softly broken at the TeV scale) was not a beautiful idea but an ugly one. A believer in beauty to my mind would have said that SUSY was already disqualified at the beginning, once one realized it had to be badly broken, and there was no beautiful way to do that. I think what Hossenfelder is pointing to as flawed is not actually arguments from “beauty”, but arguments that start with a symmetry principle which has to be badly broken to agree with reality.
As for the “just trust experiment” idea, the problem we have is often a lack of any relevant experiments. That some small part of the theory community has gone off into ridiculous claims about “post-empirical” theory is a bit of a red herring. Few theorists really take that bizarre move seriously. The “post-empiricists” are doing great damage to the public perception of the subject, but the more significant issue is the large number of theorists working on the same failed ideas, hoping they can somehow extract something empirically testable out of these ideas. We’ve seen over the years that all you get by pushing “empirically testable” is moving people in the direction of studying ugly complex models that somehow might be testable, even though they are highly implausible and explain nothing. We might actually be better off with people giving up for now on testability and trying to find a new beautiful idea (i.e. new forms of symmetry). I think Hossenfelder in the end agrees that a successful new breakthrough will produce a new form of “beauty”. To me it’s thus not unreasonable to try and find that, independent of experiment if you have to. But you have to be really honest with yourself about when ideas don’t work and are unbeautiful, and the sociological reasons why people can’t or won’t do that are a big problem (one that Hossenfelder has written a lot about).
hi peter — just got hold of the book and began reading it. the beginning was interesting and then after that it is quite confusing. Have to read it more carefully. The interviews with scientists are interesting.
I dont really get what the issue with beauty is, that Sabine is trying to convey. If some beauty driven theories are falsified that is part of the scientific process — to come up with falsifiable theories. Is it the time we are taking to abandon them? Whats happening currently is not very beautiful — to try and come up with theories that may have consequences for LHC even if they have problematic things like very small couplings for parameters you’d think are order 1 on grounds of beauty. The other thing that is currently being done that is not beautiful is to try and save theories like SUSY — which solved the hierarchy problem and could be falsified from that point of view. Like Nima wanting a 100 TeV collider to make sure that the hierarchy problem is not resolved even at that scale (or if it is then to discover the new particles/physics) — that collider would probe theories not as beautiful as the solutions LHC probed.
Anyway I think the biggest miss in the book is the neutrino masses and mixings which is the new thing that has happened experimentally — neutrino physics was anticipated considering symmetries such as B-L and parity.
Have had the book only for an hour or so. Will read more.
I truly hope you are right, Peter, and I would be extremely happy to be wrong. My admittedly rank-amateur outlook is one of pessimism without some breakthrough experimental guidance. I’m not all that convinced people should keep hammering away at the current data set while the elders hope that some day a young genius theorist, free of the shackles of these failed ideas, will save HEP theory from itself and bring enlightenment. I’d put the odds on that as roughly equal to the odds that SUSY will be confirmed by the 100 km collider. I.e., while it could happen, I see zero reason to expect it.
The problem is that if you insist people wait for experimental guidance to try and make progress, you’re basically arguing that theorists should abandon research on these questions. There is some sign that’s already happening, as HEP theorists give up and try to rebrand themselves as condensed matter or quantum information theorists. Unfortunately their “giving up” often is taking the form of “we have discovered that the multiverse did it, so these questions are hopeless”, discouraging anyone else from working on the questions that they failed at.
Personally it seems to me that there are huge unexplored areas at the intersection of QFT and mathematics. Some HEP theorists have moved from failed ideas to trying to work on fundamentals of QFT (without experimental guidance) and that’s great. My one problem with Hossenfelder’s book is that I fear her argument will be read as discouraging this, that it’s “searching for beauty”, so hopeless, whereas her real argument is with a narrow failed set of ideas, not “beauty” in general.
Nor maths, for that matter. Rules-of-thumb, such as “naturalness”, witness a dearth of rigorous arguments, not an abundance.
“The alternative to naturalness, often neglected as an alternative, is having a theory.” (Kane 17, p. 33, p. 57)
I find the fight over the “demarcation problem” to be tedious and don’t have much of an opinion myself, but could the situation for theorists interested in exploring the intersection of maths and subjects like QFT be improved simply by moving to a different department? It might be pure semantics, but if one chooses to call it a form of “applied mathematics” one can avoid a certain amount of philosophical angst, I suppose. It might also be a healthy development for HEP theory, if people in that bucket are perceived as going too far off the reservation (as opposed to just refusing to give up on failed predictions as such practice is more conventionally understood).
This truly is more of a question than a proposal, as I’m not really qualified to have an opinion.
I agree that the problem is caused by people who don’t have a theory, but Kane has no credibility since he is a perfect example of what you don’t want. Yes, he has a theory, lots of theories, one for every possible experimental result…
I don’t think the “demarcation problem” has to do with the boundary between mathematics and physics, it’s about the boundary between testable and untestable statements about the physical world, which is something different.
The problem here is people refusing to give up failed ideas, and thus flirting with non-science, not that they have moved into mathematics. While many physicists would love to get rid of this problem by dumping it on a math department, the math departments are not going to go along with this. There is a very healthy overlap between math and physics, but it’s something very different.
The broad properties of the G2-MSSM which G. Kane is highlighting, such as the crucial “slightly split” susy, are not controversial (there was also some informed discussion of this on your blog a while back here). Kane et al. discuss the latest exclusion of parameter ranges in arXiv:1803.04394, this is not anything goes.
But even if the G2-MSSM is experimentally excluded tomorrow, a good point remains: This is a top-down model embedded in a coherent ambient theory, and with properties argued from by systematic analysis of the theory instead of by rules-of-thumb, avoiding the folklore fallacies that are being criticized here.
Of course the precise numbers extracted depend on assumptions, or else we are living in a Douglas Adams novel. It’s easy to make fun of this from the sidelines, but it remains a truism that the job of model builders is to tune the assumptions admitted by their models to fit the data.
Kane’s book is really good, sober and to the point. He has a great quote in there along the lines of better risking to make a fool of oneself than not trying the worthwhile. That’s the attitude that the community could use more of.
Your love for SUSY hype is getting off-topic, I’ll just point out that “really good, sober and to the point” is an extremely inaccurate description of Kane’s books about SUSY, for reasons that are laid out here:
To bring the discussion back to the topic of the book, Kane does appear in it. Hossenfelder describes the scene at the 2015 Munich conference, where Gross and other string theorists interrupted Kane’s talk, making it clear they did not think his “predictions” followed from string theory, but thought that he was using “additional hand-selected assumptions in order to reproduce what we already know about the standard model”. When she asked Kane about what he would do if his prediction of a run 2 gluino didn’t work out, he said that he would “wonder what one could change in the model”, gave no indication he would under any circumstances give up on string theory. This (and the book edits I documented) are not the way science is supposed to work.
In the Arkani-Hamed interview, he makes very clear that Kane does not count as what he considers one of the “good people” in the subject.