Blogging has been light here, since little worthy of note in math/physics has been happening, and I’ve been busy with teaching, freaking out about the election, and trying to better understand Euclidean spinors. I’ll write soon about the Euclidean spinors, but couldn’t resist today making some comments about two things I’ve seen this week.
Sabine Hossenfelder yesterday had a blog entry/Youtube video entitled Particle Physicists Continue to Make Empty Promises, which properly takes exception to this quote:
A good example of a guaranteed result is dark matter. A proton collider operating at energies around 100 TeV will conclusively probe the existence of weakly interacting dark-matter particles of thermal origin. This will lead either to a sensational discovery or to an experimental exclusion that will profoundly influence both particle physics and astrophysics.
from a recent article by Fabiola Gianotti and Gian Francesco Giudice in Nature Physics. She correctly notes that
They guarantee to rule out some very specific hypotheses for dark matter that we have no reason to think are correct in the first place.
A 100 TeV collider can rule out certain kinds of higher-mass WIMPs, but it’s simply untrue that such an exclusion will “profoundly influence both particle physics and astrophysics.” Very few people think such a thing is likely since there’s no evidence for it and no well-motivated theory that predicts it.
Where I part company with Hossenfelder though is that I don’t see much wrong with the rest of the Gianotti/Giudice piece and don’t agree with her point of view that the big problem here is empty promises like this and plans for a new collider. Twenty years ago when I began writing Not Even Wrong, I started out by writing a chapter about the inherent physical limits that colliders were starting to hit, and the significance of this for the field. It was already clear that getting to higher proton energies than the LHC, or higher lepton energies than LEP was going to be very difficult and expensive. HEP experimentalists are now facing painful and hard choices about the future, which I wrote about in detail here under the title Should the Europeans Give Up?. The worldwide experimental HEP community is addressing the problem in a serious way, with the European Strategy Update one aspect, and the US now engaged in a similar Snowmass 2021 effort.
Many find it tempting to believe that the answer is simple: just redirect funds from collider physics to non-collider experiments. The problem is that there’s little evidence of promising but unfunded ideas for non-collider experiments. For the last decade there has been no new construction of high energy colliders, with as much money as ever available worldwide for HEP experiments. This should have been a golden age for those with non-collider ideas to propose. This continues to be the case: if you look at the European Strategy Update and Snowmass 2021 efforts, they have seriously focused on finding non-collider ideas to pursue. This should continue to be true, since I see no evidence anyone is going to decide to go ahead with a next generation collider and start spending money building it during the next few years. The bottom line result from the European process was not a decision to build a new collider, but a decision to keep studying the problem, then evaluate what to do in 2026. For the ongoing American process, as far as I know a new US collider is not even a possibility being discussed.
While HEP experiment is facing difficult times because of fundamental physical, engineering and economic limits, the problems of HEP theory are mostly self-inflicted. The decision nearly 40 years ago by a large fraction of the field to orient their research programs around bad ideas that don’t work (SUSY extensions of the Standard Model and string theory unification), then spend decades refusing to acknowledge failure is at the core of the sad state of the subject these days.
About the canniest and most influential HEP theorist around is Nima Arkani-Hamed, and a few days ago I watched an interview of him by Janna Levin. On the question of the justification for a new collider, he’s careful to state that the justification is mainly the study of the Higgs. He’s well aware that the failure of the “naturalness” arguments for weak-scale SUSY needs to be acknowledged and does so. He also is well aware that any attempt to argue this failure away by saying “we just need a higher energy collider” won’t pass the laugh test (and would bring Hossenfelder and others down on him like a ton of bricks…).
The most disturbing aspect of the interview is that Levin devotes a lot of time (and computer graphics) to getting Arkani-Hamed to explain his 1998 ideas about “large extra dimensions”, repeatedly telling the audience that he has been given a \$3 million prize for them. This paper has by now been cited over 6300 times, and the multi-million dollar business is correct, with the prize citation explaining:
Nima Arkani-Hamed has proposed a number of possible approaches to this [hierarchy problem] paradox, from the theory of large extra dimensions, where the strength of gravity is diluted by leaking into higher dimensions, to “split supersymmetry,” motivated by the possibility of an enormous diversity of long-distance solutions to string theory.
At the time it was pretty strange that a \$3 million dollar prize was being given for ideas that weren’t working out. It’s truly bizarre though that Levin would now want to make such failed ideas the centerpiece of a presentation to the public, misleading people about their status. The website for the interview also promotes Arkani-Hamed purely in terms of his failures, presented as successes:
Nima Arkani-Hamed is one of the leading particle physics phenomenologists of the generation. He is concerned with the relation between theory and experiment. His research has shown how the extreme weakness of gravity, relative to other forces of nature, might be explained by the existence of extra dimensions of space, and how the structure of comparatively low-energy physics is constrained within the context of string theory. He has taken a lead in proposing new physical theories that can be tested at the Large Hadron Collider at CERN in Switzerland,
This is part of the overall weird situation of the failed ideas (SUSY/strings) of 40 years ago: they still live on in a dominant position when the subject is presented to the public.
At the same time, the topics Arkani-Hamed is working on now are ones I think are more promising than most of the rest of what is going on in HEP theory. The interview began with a discussion of Penrose’s recent Nobel Prize, with Arkani-Hamed explaining Penrose’s fantastic insights about twistor geometry and noting that his own current work involves a fundamental role for twistor space (personally I see some other promising directions for using twistor geometry, more to come about this here in the future).
In contrast to Hossenfelder, what I’m seeing these days in HEP physics is not a lot of empty promises (which were a dominant aspect of HEP theory for several decades). Instead, on the experimental side, there’s an honest struggle with implacable difficulties. On the theory side increasingly people have just given up, deciding that it’s better to let the subject die chained to a host of \$3 million prizes for dead ideas than to honestly face up to what has happened.
Update:
In case anyone needs any reminder of how bad the propaganda problem is:
https://kids.kiddle.co/String_theory
It appears this kind of thing is driven by a propaganda problem on Wikipedia.
Hi Peter,
Thanks for the reasoned response.
A few remarks. Firstly, the rest of the Giudice & Gianotti piece repeats unconvincing arguments I have debunked many times before, see eg here for a summary. Take eg the “spin offs” and “other benefits” claim. True. But the same can be said about any similarly large investment into science funding. Doesn’t have to be a collider. So then we should put the money in a science experiment that also makes scientific sense.
Second, and more importantly, you state “This should have been a golden age for those with non-collider ideas to propose.” Excuse me for being frank, but have you ever even considered to write a proposal for a large scale experiment? Probably not. Because if you had you would realize that you need funding to even put together a proposal. You need people. You need expertise. But all the people and the expertise are in particle physics. And of course particle physicists propose more particle physics experiments.
This whole process is so obviously incestual; it is beyond me why it’s still allowed to happen. It’s a chicken and egg problem: people go where money goes and money goes where people go. To make matters worse, then there are outside people, like you, who don’t understand how it works and say “But look, this is where money and people go, so this must be where we should put in more money and people.” *facepalm*
Third, I don’t want to start this all over again because I have literally written a whole book about it, but I think we need to make more efforts to evaluate the promise of investing huge amounts of money based on looking at what strategies worked in the past. As I have explained, theory-based breakthroughs have only been successful when they were studying inconsistencies. There isn’t any such inconsistency in the range in the new 100 TeV collider.
Fourth, that the last decade should have made it easy to get funding for other things is just wrong, look eg at the funding troubles of the SKA. The SKA was a good idea, once, but after it was slimmed down it failed making much sense which led more nations to pull out. We are talking here about a billion that was missing, not 20 billions. And you know what they’re building next to Frankfurt what’s been eating up 2 billions? A particle collider. Srsly. Not a 100 TeV machine, but a particle collider. And as you have probably heard RHIC is getting an upgrade that will eat up a few billions too. So please stop claiming there ain’t no money going into this field, it’s just wrong.
As to Arkani-Hamed. Fun fact. I was recently interviewed by someone who writes for a little known German science magazine (I believe it’s a German version of the MIT Tech review). He told me he previously spoke with Nima. And you know what Nima told him? The good old finetuning story with the balanced pen and all that. (It’s in print now, so not like I’m spilling secrets.)
It’s really hard for particle physicists to give up their numerological arguments (naturalness, WIMP miracle, etc) because those are the only arguments they have. If they’d stick with the truth, nobody would give them funding, and they know this. That’s why they continue to make false claims about dark matter and dark energy and new particles and fuzzy things about the baryon asymmetry, all of which fall apart to dust if you look a little closer.
Peter and Sabine,
now I am an old theoretical physicist, reading your blogs since almost from when they started, but I still do not understand both of you. Allow me to explain the reason.
It is indeed correct that both theoretical particle physics and quantum gravity have not come up with the correct approach to go forward. And this is so since decades. You both have shown this in great detail, and for this you indeed deserve much praise. You both stress the importance of experiment, the fallacies of wrong arguments, the traps of untestable premises, etc.
After so many years, it is obvious that in the vast field of possible approaches, the correct one is like a tiny plant still waiting to be discovered among the large number of wrong ones. What today’s theoretical physics needs, is a guidance from older experts to younger ones on where to go on searching.
We have a crisis in theoretical physics, not a crisis in experimental physics. But both of you also explicitly state “don’t send me your TOEs”. And you also act consequently. Indeed, there are so many bad ideas around. But it implies that you do not give *any* approach a chance. Not even the correct one. Ok, I can understand this attitude as well – time is valuable.
But if we cannot give answers to younger people, we should at least give them questions. However, you both have become so negative that it is not even allowed to write questions in your blogs. You do not believe it? Let me add some questions to this comment. It will lead to rejection.
(1) To Peter and Sabine: It is clear since decades that gravitation is of thermodynamic origin and that black holes have microscopic degrees of freedom. One goal of quantum gravity is to discover these microscopic degrees of freedom: What are they? How do they make up black holes and space?
(2) To Peter: How are these microscopic degrees related to twistors?
(3) To Sabine: A correct approach to particle physics must explain the fine structure constant or the mass of the electron. Yes, strings failed, and so did loop quantum gravity. Can other microscopic degrees of freedom achieve this?
We need to pass on questions such as these to younger people. We need to distinguish carefully between telling people not to take a wrong path and telling people not to take any path. As long not even asking questions is possible, we stifle progress.
Fact check: “a proton collider operating at energies around 100 TeV will conclusively probe the existence of weakly interacting dark-matter particles of thermal origin” is not true. Not even close. CERN is struggling for its survival, and it’s not struggling in the best way.
The good way should have been: recognise that LHC will be scientifically over soon and that it’s time to either invent how to build a smarter muon collider in the LHC tunnel, or to return the place to cows.
The bad way is: keep LHC running until its generation retires (current funds: ≈1 billion/year) and try exaggerations and public relations to get ≈30 billions for a bigger collider.
Hi again,
It occurred to me I should add something for context, which many of us “out here” tend to forget. I suspect the vast majority of particle physicists have no idea what we are even talking about. They live in a bubble in which there’s only particle physicists. They haven’t heard that naturalness arguments and the WIMP miracle died 5 years ago — and that’s in the optimistic case that they know how much they relied on these arguments to begin with.
The reason I suspect this is that each time I am asked to “debate” a particle physicist they tell me 30 years old stories. They say that dark matter should be made of WIMPs and that there is supposedly something special about the TeV scale, and when I tell them the predictions made with these arguments have been falsified they are just stunned. It’s like the past 5 years didn’t happen.
(A small fraction of them will then argue one can’t falsify numerological arguments, but, well, either way — falsified or unfalsifiable — it’s arguments on the basis of which you should not invest tens of billions of dollars.)
Alessandro (above), btw, is the rare exception of a particle physicist who understands the situation (if you look at his publications, probably understood this long before I did).
Its a long shot, but I consider the most likely “effort” to succeed in getting theoreticians “on track” to success is “An experimental effort in astronomical observations measuring cosmological parameters with emphasis on no systematic errors” aka “pushing the cosmological constant to the other sign” plus “which side is wrong on Hubble?”.
Perhaps accurate full 4 pi measurement of the cosmic microwave background at numerous widely spaced different wavelengths, or even at continuous wavelengths, not just spot ones. That would spend a bundle. It would also pay for developing better continuously powered helium refrigerators for space use.
Doug McDonald,
What I’m discussing here is the situation with high energy particle (HEP) physics. Cosmology and astrophysics are a completely different story. Trying to do better CMB measurements is a very active and well-funded subject. I see zero reason to believe that any CMB measurement will ever tell us anything about the questions a next generation collider would be designed to address: the details of the behavior of the Higgs and whether the SM continues to work perfectly at scales of 1-10 TeV.
Johannes,
What I’m discussing is HEP physics, not quantum gravity, especially the increasingly common attitude that HEP physics is dead, with quantum gravity the only thing worth thinking about. The problems of quantum gravity are a completely different story.
It’s currently very much not true that I give no alternative approach a chance, since I now see a relatively clear path towards progress along the lines of the ideas about twistor geometry I’ve advertised.
Alessandro,
Yes, part of the story is that CERN’s future is at stake, and those with jobs there have a vested interest in large projects that would keep it in business. This is worth keeping in mind when evaluating people’s arguments.
A muon collider in the LHC tunnel would be an ideal project in terms of keeping CERN going. I don’t see any reason to believe that the reason for not pushing that instead of the 100 TeV idea isn’t simply lack of feasibility (among other problems, such a thing might produce unhealthy levels of neutrino radiation over a large chunk of France and Switzerland).
I wouldn’t be at all surprised though if in 2026 CERN gives up on the 100 TeV pp idea as unfundably expensive and instead turns to the muon or some other lepton collider idea.
Sabine,
If you listen to Arkani-Hamed, he is acknowledging that the “new weak scale physics will restore naturalness” argument has been pretty much discomfirmed by the LHC. Unfortunately I think what’s going on is that he hasn’t abandoned the naturalness argument, he’s just drawn a conclusion from it that he doesn’t want to talk about.
For many years he would give talks about how the LHC would lead to one of two possible outcomes: new physics restoring naturalness, or the anthropic multiverse. I suspect what’s going on with him and many others is that they still believe these are the two possibilities, have drawn the conclusion that the LHC has vindicated the anthropic multiverse, and as a result have given up on HEP physics. They’ve seen the reaction of their colleagues and the public to the campaign for anthropic multiverse pseudo-science, so they’re not repeating this publicly. You see this fairly clearly in some of Witten’s statements of the order of “I don’t like the multiverse but I now don’t have an argument against it”.
About the funding issues, I have no idea whether giving up on HEP physics will free up money for other currently under-funded fields which I know little about. My point was just about HEP experiments. The argument for an energy frontier collider is that it’s the only way to get better information about details of Higgs and 1-10 TeV scale physics. If anyone had a better, cheaper way to do this, it would get a lot of interest. The US already a long time ago did what the Europeans are faced with doing (giving up on energy frontier machines), and the experience here provides a pretty clear idea of what will happen if the Europeans do the same (very good for neutrino physics…).
Any obstructions to people with good but much cheaper proposals getting funded are worth addressing, I just don’t believe the main problem is collider spending crowding everything else out.
Contra Sabine’s claim that particle experimentalists only do more particle experiments, and speaking as an old timer who got his (theory) degree back in the ‘80s, I know 3 HE experimentalists from that era, two now quite senior. All three have since switched to other experimental areas, one working on the LSST and now on ground based CMB, another one now doing CMB stuff, and the third doing stuff with liquid xenon, first to look for neutrinoless double beta decay, now to look for other interesting things with the “backgrounds” from that setup. Oh, and a fourth friend – an ex-phenomenologist – now works on improving the cosmological constant measurement with large-scale galaxy surveys.
Physicists can change their spots. Not everyone gets permanently attached to unproductive lines of work.
Personally, I still think the ideas that have come out of string theory – particularly gauge/gravity duality and the related and more recent “it from qbit” ideas – are tremendously interesting, even if connecting them to the standard model looks very far off. That our society allocates a small fraction of the cost of one more pointless jet fighter to giving a few talented people the resources to pursue those ideas seems to me a good measure of our merit as a civilization, and it’s a shame that the meagerness of that commitment pits people who should be allies against each other.
The muon-g2 experiment at Fermilab, would that be considered HEP? It seems to be poking at a possible discrepancy of the standard model.
As for the 100 TeV collider in Switzerland, I just don’t see that happening. Building a 150 km tunnel would be ridiculously expensive, and its not like there is a new Higgs boson to look for.
Anders,
The muon g-2 experiment is a good example of the sort of the thing US HEP is doing in the absence of an energy frontier collider. Unfortunately, the only information such low energy experiments can give you about what is happening at higher energy scales is quite indirect and just one number. If the g-2 result comes out in conflict with the Standard Model, that will be interesting evidence that there’s something beyond the SM, while at the same time telling you almost nothing about what it is.
Please! Enough with this big physics vs. little physics death matches. Govt. money simply does not work that way. Case in point, the US govt. sent me (a tenured professor!) over $3k a few months ago just for…well I don’t know what for. Money rules are not the same when you own the printing press for dollars.
The only valid reason for NOT continuing down our path towards short distance physics would be if someone could guarantee there is NO new physics at these higher energies (or energies that would be reached by the next next collider). If you could prove there was no new physics until the Plank scale then fine, colliders are pointless.
If I was a 2nd year Ph.D student having taken particle physics courses and maybe attended a few colloquia/seminars etc, my first reaction would have been after reading that article is
“Wait a minute. We already know from neutrino experiments that there is evidence for Physics beyond standard model. So why are Giudice/Gianotti talking as if there is no evidence. what have we learned about TeV scale physics from 20+ years of neutrino mass results.? Else if neutrino experiments can tell us nothing about BSM of particle physics, besides measurements of delta m^2, sin^2 theta and delta CP, then why waste money on neutrino experiments? Conversely why aren’t top theorists (like Nima) working on these issues?”
Also I don’t see reporters asking this question to HEP theorists or Sabine/Peter stressing these points.
Peter, Amitabh,
searching for new physics is the wrong path. We have new physics in front of us since 100 years! Here it is: What is the origin of the coupling constants? And what is the origin of the particle masses?
The trouble is that 99% of the proposed answers are by crackpots. But the truth it that this is the problem to solve. Do we need colliders to solve it? Maybe. Maybe not. But who is working on this problem? Nobody. That is the real scandal of (theoretical) particle physics.
The problem is clear, and everybody is avoiding working on the solution. Avoiding to work on a solution has indeed allowed many people to get a lot of money from funding agencies. Avoiding to work on a solution has also created a wide spectrum of fantasy theories.
Physicists and the funding agencies have a century old problem, but the search and use money in all sorts of directions – except in the correct one. Look at Snowmass 21. Look at what their theory frontier group does on this issue: NOTHING. Look at what CERN does in this direction: NOTHING. Look at what the rest of the world does: NOTHING.
String theorists gave up. Loop quantum gravity gave up. I know too little about twistors, but chances seem slim that they will solve the problem.
Fact is, asking for calculations of the parameters of the standard model is the best way to discard wrong theories.
The real scandal of particle physics is (1) that nobody is looking at understanding the parameters of the standard model. (2) That nobody encourages such research. (3) That nobody funds such research. And (4) that nobody even mentions that this is the real issue.
And to be a little direct: point (4) is true for most of the people who comment on this blog as well. As long as we keep sweeping the problem under the carpet, nothing will happen. Point (4) is the silent agreement of all particle physicists. As long as it holds, there will be no progress. As long as this silent agreement is kept, particle physics will not prosper.
We should tell young people that this is what we need to find out.
Peter,
thank you for posting my comments. One more remark in the same direction. Some months ago, a blogger whom usually I admire a lot wrote that any TOE is tested by looking for deviations from the standard model. Even though many have agreed, many will agree or tend to agree, this is wrong. And it is misleading.
A TOE is first of all tested by checking its calculation of the coupling constants and the particle masses. (We do not know whether deviations from the standard model exist.)
This anecdote shows how deeply we all – the whole HEP community – have buried the goal to understand the parameters of the standard model below other, much less important activities and aims. Without noticing, we are misleading young people. (And I include myself here.)
We must tell the younger people what the goal is: understanding masses and couplings. The goal is NOT understanding supersymmetry, nor strings, nor loops, nor quantum gravity, nor the amplituhedron. The goal is NOT understanding baryon-antibaryon asymmetry, nor dark matter, nor dark energy. And: The goal is NOT finding deviations from the standard model.
The real goal we have before us, since over 100 years, is to understand the ratio 511 keV/Planck mass for the electron, the corresponding ratios for the other particles, the number 137.036, and the other two coupling constants, and a few more parameters (and, of course, the running with four-momentum of all of them).
Why are CERN, NSF, research agencies, sponsors, and research ministers not taking up this goal? It is the biggest problem in physics. It is orders of magnitude bigger than Fermat’s last theorem. There are of course many obvious reasons (money does not help solving it in an obvious manner, accelerators probably will not help solving it, it is hard to plan, we have no clue yet how to get to a solution).
But let me be a bit provoking: If you, Peter, or I, or any of several dozen of other people had a billion dollars every year to spend on this goal, then you, or I, or any of this dozen of other people would be able to organize a world-wide project that would achieve that goal. And probably they would need less that a billion dollars a year.
In this sense – but only in this one – I agree and understand Sabine’s point. And working towards this real goal would not be an empty promise. It would be a worthwhile effort.
@Amitabh Lath:
Do you really believe this? Suppose you knew that the probability of discovering a new particle at the next-stage collider was one in fifty million (the chance of winning the lottery). Would it be worth it? Do you buy lottery tickets?
Assuming that the cost of the next machine is $20 billion, your expected value is positive at this probability if you put the benefit of a new particle at one quadrillion dollars. But surely, nobody would think of claiming that it would be worth it to pay a quadrillion dollars to discover a new particle. That’s the GNP of the U.S. over 50 years.
So now that we’ve established that it’s just a matter of probabilities, at what probability of seeing something would it be worth building the next collider?
Clearly, we should wait until the LHC run is finished and see whether there’s any hint of new physics. But if the LHC doesn’t give any hint of new physics, do you really think the probability of seeing something with the next-generation collider would be more than 10%?
Johannes,
The problem is that no one has a good idea about this, and a billion dollars is not likely to change that. This is actually one of the strongest arguments for a new collider: the source of the mass problem is the Higgs sector, so the highest priority should go to a machine able to study the Higgs, and this has to be done at the energy frontier. Yes, it’s possible that all an experiment will see are the SM-predicted numbers, but this is not guaranteed (and the Amit/Peter Shor comments show that this is the crux of the funding question).
The situation is somewhat analogous to that of the Riemann hypothesis. All indications are that we’re missing some basic idea there, that the problem is not going to be solved by more strenuous efforts to apply ideas we already know about. A billion dollars in grant money handed out to people engaged in such strenuous efforts likely would change nothing.
A big difference of the Riemann hypothesis case is that RH hasn’t been the victim of a campaign to claim that the best research has proved that it is inherently insoluble. This is what has happened to HEP physics: there has been a huge and all too successful “we couldn’t solve it, so no one can” campaign to convince people that string theory research has shown that the problem of particle masses is inherently insoluble, that these numbers are just random environmentally determined artifacts of some very complicated and unknowable physics going on at the Planck scale.
One aspect of the particle mass problem is that there are obvious more basic questions we have no good ideas about, in particular that of why there are three generations. Before we can explain an entry in a matrix, likely we first need to explain the dimension of the matrix.
If you look at how the great unsolved problems of mathematics get solved, it’s often not by a large well-funded group effort. The solutions of the Poincare and Fermat problems by Perelman and Wiles are instructive examples. In neither case would money have helped, probably quite the opposite, since accepting money would have likely required producing reports about their progress, something neither of them thought was a good idea. The way such problems get solved in when the best people in the field think hard about them, engage in research programs designed to turn up new fundamental ideas, and don’t get convinced the problem is insoluble and stop thinking about it.
Peter,
to avoid excessive neutrino radiation (while keeping desired luminosity) one needs to make narrower muon beams. Achieving this seemed impossible, but now there are ideas, see e.g. https://arxiv.org/abs/1509.04454.
45 years ago Rubbia and Van den Meer could persuade the field to pursue a risky new idea. 20 years ago I saw the resistance to the LEP to LHC transition: a new collider meant a change of generation. This is not happening now that the field is dominated by mega-collaborations.
OC: “more recent “it from qbit” ideas” certainly did not come from string theory. They came from John Wheeler long before string theory was fashionable.
Peter Shor: Yes it is worth it to me because the Standard Model pisses me off. It’s hodgepodge and annoyingly half-baked.
I am not going to play the “how much money is too much money” game because as we have discussed before, money spent on big science is research and infrastructure spending, it pays for itself many times over.
Peter: since I come from a region very close to CERN, your argument about unsafe neutrino radiation makes me worry. Is this a joke ? Or do we have any knowledge about how bad can heavy neutrino radiation be ?
@George Ellis: (*the* George Ellis?!?) I’m well aware of the history of “it from bit”. I saw JW present the idea in person, with his self-gazing, eyeball-bearing U at the Einstein Centennial celebration at the IAS in 1979. But JW’s ideas were pretty inchoate, or at least I didn’t understand them (not surprising – I was an undergrad at the time). I don’t think anyone else understood them as a real direction for research then either, though in hindsight perhaps they’re related to the then-new Bekenstein-Hawking ideas about black holes and entropy, though I’m pretty sure Wheeler was concerned more with issues related to the measurement problem.
Anyway, the string theory connection, as best I understand it, is the effort to translate gauge/gravity duality into ideas about how entangled quantum bits give rise to geometry. The detailed formulations of these ideas that have come out in the last decade were – at best – very implicit in JW’s slogan.
martibal,
Not a joke, but I wouldn’t worry right now.
The main reason a muon collider is difficult is that muons have a lifetime of only two microseconds. So, very hard to store and collide. Everything in the beam is decaying quickly, with decay products including two high energy neutrinos, which you can’t shield. Normally one thinks of neutrinos as famously harmless: huge numbers come from the sun, and then go through the earth without interacting (mean free path a light-year of lead). But the cross-section goes up with energy and is much higher for TeV scale neutrinos. Also, you need a lot of muons in the beam. So, the neutrino radiation problem is real for a muon collider. Alessandro may be right that there are ideas for keeping this to a low enough level.
In any case, if you’re worried you should figure out the coordinates of the circle where the plane of the LHC tunnel intersects the surface of the earth, and just make sure not to live there.
Damned ! I made (rightly) fun of people fearing black hole production at LHC, but I’ll have to be more careful about neutrinos then ! I had in mind the usual story you recalled (“lots of neutrino from the Sun pass across the Earth all the time etc). The surface of the Earth is far from flat around Ginevra, that may not be so easy to figure out the intersection of the circle with the surface.
Private joke for the italian readers: let’s ask Gelmini, she is an expert in neutrino 🙂
Dear Martibal, don’t worry about neutrinos. Neutrinos emitted by pp colliders are a problem only for Dark Matter searches. Neutrinos are one reason why a 100 TeV pp collider cannot “conclusively probe the existence of weakly interacting dark-matter particles of thermal origin”. If you want to worry about something, I would suggest perfluorocarbons
The FCC statement from the Nature article is in contradiction with the FCC CDR.
> No experiment, at colliders or otherwise, can probe the full range of dark matter (DM) masses allowed by astrophysical observation.
https://link.springer.com/article/10.1140/epjc/s10052-019-6904-3#Sec8
Both authors are on both publications.
+1 for muon collider
It would be something new.
When you look for something completely new, you’d rather use something completely new. HE-LHC can serve the current generation, with the new generation doing something new.
While no one will put huge money to the same (just bigger, but still the same) collider, muons can be sold as a new way that nobody has ever walked. And if it will provide a lot of neutrinos, you can make it a double experiment.
The procrustean effect… Hossenfelder kinda believes theoretical displeasure with the WIMP miracle, but also lambasts other theoretical claims that she thinks provided a false basis for other experiments.
As a matter of fact I have written a lot of proposals and have organized big teams of researchers. Hossenfelder reminds me of Pickering and “Fabricating Quarks”.
Look, `twas ever thus. Experiment goes kinda where it can go, we only have tools to illuminate under certain lampposts. Often we’ve found incredible surprises… Harry Lipkin used to be eloquent about that…. the poor record of theory in guiding discovery in particle physics in the 20th century. But nonetheless, surprises were many.
Seems like Peter Woit, you get it. The experimental community is earnestly struggling. Doesn’t seem like Hossenfelder gets it at all, and the hardbitten hardcore gnomes who roll around in the radioactive dust pulling cables and stuff don’t yet listen much to her. But she could still be right, whatever it is she is saying. That is the shocking nature of all profound discovery… it could appear from anywhere.
Martin S.
The problem with the HE-LHC idea is that the needed magnets are very expensive (3 billion) and only give a factor of two in energy above the LHC. The current plan for the next few years emphasizes working on the magnet technology, maybe that will help the situation.
Yes, a muon storage ring would make a great neutrino factory. It is definitely a project for a new generation, only question is whether it’s a generation that has yet been born…
@Johannes,
I don’t think the problem is so much that the old guard is not giving open questions to the younger generation, but rather they are also providing the supposed answers. For any number of open questions in high energy physics, the answer is given to be “string theory”. So the young people are primed to accept that the answers must have a given form, the form of string theory.
Dear Peter,
thank you for trying to balance out. What I really like about your blog, is that you do not have an obvious agenda (as Hossenfelder has, or Smolin had in his book that was published parallel to yours).
Building accelerators is much less empty than a TOE or QG. It should not be underestimated that CERN is a peaceful facility that has quite an outreach+attraction to and on young people. This spin-off is worth a lot and will not be acquired by proposing to focus on quantum foundations or inconsistencies.
I happened to be in Geneva last year as they opened up CERN for the general public. It was a completly fee-free event. There would be much to tell about seeing the detectors, the special facilities (like the Anti Matter Factory) and much more, but the most important thing I really liked about it was the positive message this community conveyed.
They might oversell a lot of things (but so do all us if we want the money, Hossenfelder not excluded!), but they at least provide also a vision that science is something worth doing, that there are things beyond your imagination and everyone can be part of it. A positve perspective.
All the best