The European HEP community is now engaged in a “Strategy Update” process, the next step of which will be an open symposium this May in Granada. Submissions to the process were due last month, and I assume that what was received will be made publicly available at some point. This is supposed to ultimately lead to the drafting of a new European HEP strategy next January, for approval by the CERN Council in May 2020.
The context of these discussions is that European HEP is approaching a very significant crossroads, and decisions about the future will soon need to be made. The LHC will be upgraded in coming years to a higher luminosity, ultimately rebranded as the HL-LHC, to start operating in 2026. After 10-15 years of operation in this higher-luminosity mode, the LHC will reach the end of its useful life: the marginal extra data accumulated each year will stop being worth the cost of running the machine.
Planning for the LHC project began back in the 1980s, and construction was approved in 1994. The first physics run was 16 years later, in 2010. Keep in mind that the LHC project started with a tunnel and a lot of infrastructure already built, since the LEP tunnel was being reused. If CERN decides it wants to build a next generation collider, this could easily take 20 years to build, so if one wants it to be ready when the LHC shuts down, one should have started already.
Some of the strategy discussion will be about experiments that don’t require the highest possible collision energies (the “energy frontier”), for instance those that study neutrinos. Among possibilities for a new energy frontier collider, the main ones that I’m aware of are the following, together with some of their advantages and drawbacks:
- FCC-ee: This would be an electron-positron machine built in a new 100 km tunnel, operating at CM energies from 90 to 365 GeV. It would provide extremely high numbers of events when operated at the Z-peak, and could also be operated as a “Higgs factory”, providing a very large number of Higgs events to study, in a much cleaner environment than that provided by a proton-proton collider like the LHC.
In terms of drawbacks, it is estimated to cost \$10 billion or so. The CM energy is quite a bit less than that of the LHC, so it seems unlikely that there are new unknown states that it could study, since these would have been expected to show up by now at the LHC (or at LEP, which operated at 209 GeV at the end).
Another point in favor of the FCC-ee proposal is that it would allow for reuse of the tunnel (just as the LHC followed on LEP) for a very high energy proton-proton collider, called the FCC-hh, which would operate at a CM energy of 100 TeV. This would be a very expensive project, estimated to cost \$17 billion (on top of the previous \$10 billion cost of the FCC-ee).
- HE-LHC: This would essentially be a higher energy version of the LHC, in the same tunnel, built using higher field (16 T vs. 8.33 T) magnets. It would operate at a CM energy of 27 TeV. The drawbacks are that, while construction would be challenging (there are not yet appropriate 16 T magnets), only a modest (27 vs. 14 TeV) increase in CM energy would be achieved. The big advantage over the FCC-hh is cost: much of the LHC infrastructure could be reused and the machine is smaller, so the total cost estimate is about \$7 billion.
- CLIC: This would be a linear electron-positron collider with first stage of the project an 11 km-long machine that would operate at 380 GeV CM energy and cost about
\$7\$6 billion. The advantage of this machine over the circular FCC-ee is that it could ultimately be extended to a longer 50 km machine operating at 3 TeV CM energy (at a much higher cost). The disadvantage with respect to the FCC-ee is that it is not capable of operating at very high luminosity at lower energies (at the Z-peak or as a Higgs factory).
For some context for the very high construction costs of these machines, the CERN budget is currently around \$1.2 billion/year. It seems likely that member states will be willing to keep funding CERN at this level in the future, but I have no idea what prospects if any there are for significantly increased contributions to pay for a new collider. A \$10 billion FCC-ee construction cost spread out over 20 years would be \$500 million/year. Can this somehow be accommodated within CERN’s current budget profile? This seems difficult, but maybe not impossible. Where the additional \$17 billion for the FCC-hh might come from is hard to see.
If none of these three alternatives is affordable or deemed worth the cost, it looks like the only alternative for energy frontier physics is to do what the US has done: give up. The machines and their cost being considered here are similar in scale to the SSC project, which would have been a 40 TeV CM energy 87 km proton-proton collider but was cancelled in 1993. Note that the capabilities of the SSC would have been roughly comparable to the HE-LHC (it had higher energy, lower luminosity). Since it would have started physics around 2000, and an HE-LHC might be possible in 2040, one could say that the SSC cancellation set back the field at least 40 years. The worst part of the SSC cancellation was that the project was underway and there was no fallback plan. It’s hard to overemphasize how disastrous this was for US HEP physics. Whatever the Europeans do, they need to be sure that they don’t end up with this kind of failure.
Faced with a difficult choice like this, there’s a temptation to want to avoid it, to believe that surely new technology will provide some more attractive alternative. In this case though, one is running up against basic physical limits. For circular electron-positron machines, synchrotron radiation losses go as the fourth power of the energy, whereas for linear machines one has to put a lot of power in since one is accelerating then dumping the beam, not storing it. For proton-proton machines, CM energy is limited by the strength of the dipole magnets one can build at a reasonable cost and operate reliably in a challenging environment. Sure, someday we may have appropriate cheap 60T magnets and a 100 TeV pp collider could be built at reasonable cost in the LHC tunnel. We might also have plasma wakefield technology that could accelerate beams of electrons and positrons to multi-TeV energies over a reasonable distance, with a reasonable luminosity. At this point though, I’m willing to bet that in both cases we’re talking about 22nd century technology unlikely to happen to fall into the 21st century. Similar comments apply to prospects for a muon collider.
Another way to avoid the implications of this difficult choice is to convince oneself that cheaper experiments at low energy, or maybe astrophysical observations, can replace energy frontier colliders. Maybe one can get the same information about what is happening at the 1-10 TeV scale by looking at indirect effects at low energy. Unfortunately, I don’t think that’s very likely. There are things we don’t understand about particle physics that can be studied using lower energies (especially the neutrino sector) and such experiments should be pursued aggressively. It may be true that what we can learn this way can replace what we could learn with an energy-frontier collider, but that may very well just be wishful thinking.
So, what to do? Give up, or start trying to find the money for a very long-term, very challenging project, one with an uncertain outcome? Unlike the case of the LHC, we have no good theoretical reason to believe that we will discover a new piece of fundamental physics using one of these machines. You can read competing arguments from Sabine Hossenfelder (here and here) and Tommaso Dorigo (here, here and here).
Personally, I’m on the side of not giving up on energy frontier colliders at this point, but I don’t think the question is an easy one (unlike the question of building the LHC, which was an easy choice). One piece of advice though is that experience of the past few decades shows you probably shouldn’t listen to theorists. A consensus is now developing that HEP theory is in “crisis”, see for instance this recent article, where Neil Turok says “I’m busy trying to persuade my colleagues here to disregard the last 30 years. We have to retrace our steps and figure out where we went wrong.” If the Europeans do decide to build a next generation machine, selling the idea to the public is not going to be made easier by some of the nonsense from theorists used to sell the LHC. People are going to be asking “what about those black holes the LHC was supposed to produce?” and we’re going to have to tell them that that was a load of BS, but that this time we’re serious. This is not going to be easy…
Update: Some HEP experimentalists are justifiably outraged at some of the negative media stories coming out that extensively quote theorists mainly interested in quantum gravity. There are eloquent Twitter threads by James Beacham and Salvatore Rappoccio, responding to this Vox story. The Vox story quotes no experimentalists, instead quotes extensively three theorists working on quantum gravity (Jared Kaplan, Sabine Hossenfelder and Sean Carroll). Not to pick specifically on Kaplan, but he’s a good example of the point I was making above about listening to theorists. Ten years ago his work was being advertised with:
As an example question, which the LHC will almost certainly answer—we know that the sun contains roughly 10^60 atoms, and that this gigantic number is a result of the extreme weakness of gravity relative to the other forces—so why is gravity so weak?
Enthusiasm for the LHC then based on the idea that it was going to tell us about gravity was always absurd, and a corresponding lack of enthusiasm for a new collider based on negative LHC results on that front is just as absurd.
Update: Commenter abby yorker points to this new opinion piece at the New York Times, from Sabine Hossenfelder. The subtitle of the piece is “Ten years in, the Large Hadron Collider has failed to deliver the exciting discoveries that scientists promised.” This is true enough, but by not specifying the nature of the failure and which scientists were responsible, it comes off as blaming the wrong people, the experimentalists. Worse, it uses this failure to argue against further funding not of failed theory, but of successful experiment.
The LHC machine and the large-scale experiments conducted there have not in any sense been a failure, quite the opposite. The machine has worked very well, at much higher than design luminosity, close to design energy (which should be achieved after the current shutdown). The experiments have been a huge success on two fronts. In one direction, they’ve discovered the Higgs and started detailed measurements of its properties, in another they’ve done an amazing job of providing strong limits on a wide range of attempted extensions of the standard model.
These hard-won null results are not a failure of the experimental program, but a great success of it. The only failure here is that of the theorists who came up with bad theory and ran a hugely successful hype campaign for it. I don’t see how the lesson from seeing an experimental program successfully shoot down bad theory is that we should stop funding further such experiments. I also don’t see how finding out that theorists were wrong in their predictions of new phenomena at the few hundred GeV scale means that new predictions by (often the same) theorists of no new phenomena at the multiple TeV scale should be used as a reason not to fund experimentalists who want to see if this is true.
Where I think Hossenfelder is right is that too many particle physicists of all kinds went along with the hype campaign for bad theory in order to get people excited about the LHC. Going on about extra dimensions and black holes at the LHC was damaging to the understanding of what this science is really about, and completely unnecessary since there was plenty of real science to generate excitement. The discussion of post-LHC experimental projects should avoid the temptation to enter again into hype-driven nonsense. On the other hand, the discussion of what to defund because of the LHC results should stick to defunding bad theory, not the experiments that refute it.
Update: Some more commentary about this, from Chris Quigg, and the CERN Courier. In particular, the CERN Courier has this from Gerard ‘t Hooft:
Most theoreticians were hoping that the LHC might open up a new domain of our science, and this does not seem to be happening. I am just not sure whether things will be any different for a 100 km machine. It would be a shame to give up, but the question of whether spectacular new physical phenomena will be opened up and whether this outweighs the costs, I cannot answer. On the other hand, for us theoretical physicists the new machines will be important even if we can’t impress the public with their results.
and, from Joseph Incandela:
While such machines are not guaranteed to yield definitive evidence for new physics, they would nevertheless allow us to largely complete our exploration of the weak scale… This is important because it is the scale where our observable universe resides, where we live, and it should be fully charted before the energy frontier is shut down. Completing our study of the weak scale would cap a short but extraordinary 150 year-long period of profound experimental and theoretical discoveries that would stand for millennia among mankind’s greatest achievements.
Update: Also, commentary at Forbes from Chad Orzel here.
Update: I normally try and not engage with Facebook, and encourage others to follow the same policy, but there’s an extensive discussion of this topic at this public Facebook posting by Daniel Harlow.
While discussions about plasma wakefield technology are fun to be had. It’s also important to remember that particle physics colliders represent the forefront of accelerator technologies. New SRF technology and magnet development are only done at a few places in the world. These potential experiments aren’t only interesting from the point of view of fundamental physics. They represent the technological bleeding edge, and knowledge that will be lost if we as humans don’t continue to pursue it. While it can be viewed as 22nd century technology, it’s not clear that it will ever arise if it isn’t invested in. Given how prior magnet/accelerator technology has ended up so beneficial to society (the vast majority of accelerators in the world aren’t for particle physics), it’s important to think about the technological advances not just the fundamental physics. While the standard world wide web is trotted out for CERN, it’s important to remember that a lot more than the web has come from particle physics. New technology as I recall, was one of the original driving interests for the CEPC and SPPC proposals in China, not just the prestige of fundamental physics.
The only black holes that the LHC revealed were the careers of the non-hardware post-docs…
Given that the LHC has failed to find any particles other than the Higgs, and there is nothing in the Standard Model that suggests there will be anything to find within the capabilities of colliders in the forseeable future, what is the justification for another larger collider? If there were supersymmetric particles we ought to have seen some of them at the LHC.
Even if a FCC will eventually be built, will this not only shift this same discussion to 30-50 years later, when it must be decided what to do next? Built a ~100-billion-500-TeV-Collider (with appropriate e-p-mode before proton-run)?
I am all in for spending as much money for science as one can, but the sensible (a.k.a. politically managable) decision might be, to increase incrementally and choose HE-LHC and see what magnet-technology, colliding muons etc. can do for us in the future and keep a running Collider.
Hi Peter,
A great summary and thanks for the links. A note about the SSC/LHC comparison though. As I am sure you know the LHC is pushing hard on the computing frontier too. They have huge amounts of data to cope with and must do so quickly to decide what to keep and what to toss. The SSC would have reached an energy high enough to produce the Higgs but the data analysis would have been nowhere near as good as what we can do today.
I am not aware of any actual estimate for what this would have meant in terms of physics insights, but I think it’s something one should keep in mind when one compares then to now. Best,
Sabine
Peter,
Having done my thesis on the tau lepton and its neutrino (decades ago!), I’m intrigued to know more about the neutrino sector: what is the source of their mass and why is it so small but non-zero? Does anyone know if any of these proposals will give deep information about the neutrino sector, even good values for the neutrino mass matrix?
I also am tempted to think that a Higgs factory where we can measure the Higgs’ behavior to high precision could be revealing: does anyone know if there is any hope of new physics there, or is it likely that we will merely find out that, yes, the Higgs does indeed give other particles their masses?
Your closing paragraph and the comment from Turok is key: what is the selling point to sell this to responsible politicians or intelligent members of the general public?
Dave
A question no one ever seems to consider is what happens in the future if we don’t keep on building accelerators and training a generation of physicists in the use? These are complicated entities that require the input of a vast army of experts. Once these experts grow old and die, if there is no one to replace them, where will the knowledge and experience come from to build accelerators in the future?
Hi Peter,
I think you have a bit outdated cost numbers (today 1.00 USD = 1.00 CHF):
– CLIC cost: 5.9 billion USD for the 380 GeV Stage
– FCC-ee cost: 11.6 billion USD (5.4 tunnel + 5.1 injetors +1.1 RF)
Updating CLIC to 1.5 TeV would cost an additional 5.1 billion USD and after that to 3 TeV an additional 7.3 billion. So for approximately the same amount you can get 1.5 TeV CLIC or 365 GeV FCC-ee
Marco,
All the numbers I used came from the documents (Yellow Reports) issued last month. In particular, for CLIC, I used
https://arxiv.org/abs/1812.06018
which has on page 68 (for 380 GeV, in millions of dollars or swiss francs)
5890 +1470/-1270 (drive-beam based)
7290 +1800/-1540 (klystron based)
The reason for giving 7 billion as a rough number was partly that when someone gives you two numbers for the price of something, in my experience it’s always going to cost the higher number…
In any case, these are all rough numbers. The only one of them that surprised me was the HE-LHC cost estimate, which seemed much higher than I would have expected (since I would have thought you could reuse most of the LHC infrastructure, mainly needed only to pay for the new magnets).
Hi Peter,
I understand, however, the 7 billion number is not the baseline concept, but a concept that uses klystrons instead of the drive-beam. This is not a caveat to the original machine, but a completely different machine meant to show that the drive-beam acceleration is more cost effective then klystrons (page 69 in the same document). In your writing the cost difference between CLIC and FCCee is 3B instead of 6B, which I think is a huge difference.
As for the HE-LHC cost estimate, this is not an actual cost estimate, it’s more a target cost. The majority of the cost comes from the magnets. The R&D for 16T magnets is far from finished, and the industrialization of such devices has not even begun, subsequently any price tag for this kind of magnets bears very large error bars.
Scott P.,
I recommend Tommaso Dorigo’s blog posts that I linked to for his arguments about this.
The relevance here of my “don’t listen to theorists” advice is that, while it may be true that theorists have no good motivation for any new physics beyond the SM, until one gets to the Planck scale, that’s no better argument than the “naturalness” arguments made pre-LHC that said you had to see BSM physics below the TeV scale.
The difficult question here is not whether it’s worth investigating smaller distance scales despite lack of motivation from the theorists. It’s that the technology limits make the cost numbers vs. the energy reach not obviously attractive. If the HE-LHC could be done for \$ 1 billion I think the project would already be underway. If \$25 billion would buy a 1000 TeV collider, there would be a lot of enthusiasm to try and do that, no matter what theorists were saying.
In the current global economic situation, there´s a slim chance CERN member states will be able to shoulder the cost of a significantly more powerful machine.
On thing CERN has proven is that different nations can and will cooperate in the advancement of science.
Since the whole world will benefit from the data obtained from a big cruncher, it´s time for CERN to invite other European and non-European nations to invest in the next one and accept physicists and engineers in the design, operation and analysis of whatever come out of it.
The time has come for CERN, the US, Russia, Japan and maybe even China to unite.
Marco,
Thanks for the clarification, I hadn’t understood that point.
The number I used for the FCC-ee was based on the \$ 10.5 billion total construction cost estimate given in the executive summary (page xxvi) of the CDR.
Sabine Hossenfelder wrote this for the NYT:
https://www.nytimes.com/2019/01/23/opinion/particle-physics-large-hadron-collider.html
A lot of interesting points including: do we need theorists to predict discoveries and then go after them or do we take a technique that has produced many unexpected discoveries in the past and scale it up until we can’t afford it any more? I would personally vote for the latter as it seems to work. But we’re getting close to the cost limit.
We need new ideas on how to improve acceleration technology cost-effectively. Grants focused on supporting talented young people to pursue this line could help.
abby yorker,
Thanks. I’ll add something about this as an update to this posting. My initial reaction after a quick read is that the piece comes off as blaming experimentalists for the behavior of theorists.
Thank you Peter for pointing out that null results are not a failure. In fact some of the LHC searches have been breathtakingly clever and beautiful. Unfortunately articles like Sabine’s in the NYT do give the impression that it’s time to pack up our bags (and do what exactly?) even if that’s not what she meant.
The FCC and the like will be built and operated by scientists and engineers who are kids right now; undergrads, high schoolers. They are reading Sabine’s views, and I fear that they will take her glum outlook to heart.
Peter,
your “update” is really great at summarizing the core problems in this discussion. I’m pleased to see that although you are also critical against a certain way to do physics (hype, untestability, strings,..) your vision here remains very clear.
I cannot say the same for Sabine, although most of her stronger statements look milder if you read (really) carefully her replies on her blog. I think that dramatizing this discussion as she does on public media is just a harm for science (and not HEP only).
BTW, the “Europeans” expression needs an explanation (not for you Peter of course):
for me “Europeans” means CERN-based experiments but LHC is really a global effort and even so would be FCC. The same for a China-based collider. Europe by itself would not be able to put together enough money and manpower for such large endeavors.
So “should Europeans give up” should be read as “should WE..” or “should CERN…” .
USA might be over with SSC, but DUNE is still a very large scale US-based international project and their deep involvement in the LHC is beyond any doubt.
P.S. I’m not an US citizen and it is not my intention to “defend” US, CERN, the FCC project or whatsoever organization, even if I’m a particle physicist.
Nature has an editorial this week on the controversy:
https://www.nature.com/articles/d41586-019-00234-6
Dear Peter,
I am not sure it is a good idea to label falsifiable theories as “bad theories” after the experiments falsified them. For example TeV scale SUSY that solves the hierarchy problem made predictions that were sought out by LEP and LHC and has been falsified.
I would disagree with your observation that theorists “came up with bad theory.” They solved an important problem that had predictions for experiments. The null results from LHC are baffling and probably tell us something deep about nature which we are still trying to unravel. That SUSY and other TeV scale physics solutions to hierarchy problem have been falsified is important by itself.
I do agree that the hype should not have been there. I do think that going for 100 TeV collider without any real theoretical motivation for that scale is a good idea, as the only reason not to find anything is Occam’s Razor and this can also be tested in a sense.
First off: I am 100% behind the idea of my taxpayer money going to fund the FCC-ee or whatever the next generation ring winds up being. Simply because the energy frontier is there. I have no problem whatsoever with someone spending the money needed just to have a look. I can think of about 20-odd ways my country wastes more money every year in the present, and if I had my way I would happily lop those things off the budget and throw it all onto basic science. Something good always comes out of that kind of spending. It’s just very hard to predict what what it will be. I think that’s the most honest way to put forward the proposal. Unfortunately the most noble and truthful arguments for the SSC were much the same, and they failed to persuade. So my perspective is obviously one shared by a powerless minority, especially these days.
Given that, I’m puzzled by the argument that concern over a lack of theoretical guidance is overblown, and that the importance of strong odds in favor of a new fundamental discovery was never that relevant. Ideally, no, but this is the real world we’re talking about, not the ideal. These things sure seemed awfully salient when earlier projects were being debated publicly, at least in the USA. Even in Europe, can we say with confidence that if there were not a virtual guarantee that the mechanism of EWSB would be revealed by the LHC it would have been built anyway? That’s news to me, if so.
Dear Peter,
many thanks for quoting my posts on the matter. I concur with all that you wrote, especially appreciating the updates. In particular one of the things I dislike the most about Bee’s posts is exactly what you pointed out – she blames “particle physicists” as if there was one single kind of them; and she does this intentionally, because by blurring the image she is able to spin the story the way she wants. Indeed, the ones responsible for most of the hype are theorists, and they are the ones whose theories dictated our agendas.
I will give one example – we spent a lot of time and energy investigating SUSY scenarios, which is excellent science… But there is a budget of personpower that we invest in different avenues, and e.g. B physics has been seriously lagging behind (some analyses still deal with 2012 data today) because of lack of perceived interest in what is in fact a quite lively area of research, which produced lots of surprises and interesting new signals (yes, new particles!). I guess what I am saying is that the scientific output of the LHC experiments has indeed been influenced – negatively – by that hype to some degree. So experimentalists are the victims in some sense 🙂
Cheers,
T.
LDK,
Yes, ultimately whether any of these projects happens will depend on participation of other countries. In particular, the US has an HEP budget of around $1 billion/year, so some fraction of that could help make a new collider feasible. I have no idea what the Chinese situation is, whether the proposal to build something there is realistic, or whether they would help construct something located at CERN.
Also to keep in mind is this new gilded age: Jim Simons could just pay for the FCC-ee himself, likely just out of his income, not even have to touch principal (he supposedly has \$ 20 billion). Same for a bunch of others.
Anon,
You can be falsifiable and still “bad theory”. My theory that at FCC-ee luminosity, at the Z-peak you will open a portal to another universe and angels will fly out is quite testable and falsifiable. I think it would be a really bad idea though for CERN to use it to justify the cost of the FCC-ee.
For what’s “bad theory” and what isn’t, you really need to discuss specific examples. The problems with string theory, large scale extra dimensions, SUSY extensions of the SM have all been endlessly discussed on this blog and in my book, and for each one, what’s “bad” is a long story. One that shouldn’t be very controversial though is the extra dimensions: it was an extremely bad idea to try and sell the LHC based on those models. I haven’t seen anyone try that with the new proposals.
The NY-Times text is worth reading closely to see what is really going on here. Consider the alternatives that are being suggested after…
The first suggestion for these is then given as follows:
From the comment from Dec 9 here, this must be referring to the author’s proposal here to use micro-force scales as in arXiv:1602.07539 for measuring quantum corrections to the gravitational attraction of two masses.
Now the first quantum gravity correction to the Newtonian potential can and has been unambiguously computed, Donoghue 95, Section 9 (arXiv:gr-qc/9512024). Even at 1 fm distance, it is still 38 orders of magnitude smaller than the classical effect. Contrary to the claim in the NYT pieces, this is utterly out of reach.
The second suggestion then is given as follows:
So this is saying that experiments should be looking for violations of the rules of quantum physics.
These are just not a serious contributions to the debate.
LMMI,
Sure, if there is good evidence that there will be some interesting and completely new phenomenon for a new machine to study, that’s a serious point in favor of building it, and optimizing the design for that purpose. There’s also though a good case for investigating a new energy scale, even without an assurance there will be something completely new there to study. It’s a fact that the case for building any of these new machines is weaker than the case for building the LHC. But I think that’s just a reflection of the fact that the case for the LHC was unusually strong. I suspect though that without the Higgs it would have gotten built anyway. The new proposals won’t have a slam-dunk argument like the Higgs, but I think can be justified on their own merits. A big problem is the high costs: if they were an order of magnitude lower I think the decision would be easy.
What about spending the next decade or two simply improving technologies? Dyson once said that an experiment should be performed when it is affordable. Maybe we have to acknowledge the fact that we cannot run development and implementation concurrently. No big experiments -> no big expectations -> no crazy hypotheses. Maybe, by moving the starting date of a new accelerator sufficiently far in the future would motive to start seeking the truth rather than beauty.
Urs,
I suspect you’re not properly interpreting what the author has in mind in these cases, and the thing to do is go discuss it with her at her blog to clarify. I happen to disagree with her about some of these arguments, but attributing straw-man non-serious arguments to her isn’t helpful.
In the particular cases you mention, I think in the first case a more relevant counter-argument is that the gravity experiments she mentions are table-top experiments and the issue of how to pay for them is completely independent of the issue of paying for a new collider, where the cost is inherently huge. As for “quantum foundations”, as far as I can tell “quantum” is the buzzword of the day, with companies and private foundations throwing vast sums of money at anything “quantum”, and governments redirecting large parts of their research funding in this direction. So, I’m skeptical that good ideas about quantum foundations are being held up because of meager funding, something that could be fixed by using proposed HEP funding. To the extent we’re talking about theory funding in either case, it’s peanuts. irrelevant to the collider funding issue.
I think that costs are the main factor why there are people interested in this discussion. The other potential discovery machines are roughly an order of magnitude cheaper. Their potential for discovery is arguably stronger, the only weaknesses is that there is a smaller scientific community involved and (possibly related) there are fewer non-discovery related publications and citations expected. Many of these discovery machines will not be built, possibly especially if a new collider is pursued.
I would love for a new collider to be built, but not at the cost of LISA or Hyper-K (for example).
Julius,
The problem is that the limiting factor for hadron colliders is the magnet strength, and progress in recent decades towards increasing the strength of these magnets has been very slow. If you decide not to build a machine like the HE-LHC or FCC-hh because 16T magnets are not good enough (they require a 100km machine to get to 100 TeV, and cost scales with length), and wait for, say 32T magnets to bring the cost down by a factor of 2, you’re not talking about a delay of a decade or two. More likely, 50-100 years.
I think this is a really important point. If we decide we can’t afford these current proposals, we’re not talking about a temporary hiatus, we’re talking about the end of this kind of science for the rest of our lives. Maybe forever, since 50-100 years from now, we’ll perhaps all be cyborgs owned by Google, with the curiosity about how the world works subsystem no longer there.
And as for whether no experimental results to keep them honest will cause theorists to change their ways for the better, I don’t see why that should happen, the opposite seems more likely. “Post-empirical science” has not been working out well so far.
Jonathan Miller,
The problem is that there are no other discovery machines on the table that will do what these colliders will do, investigate the 1-10 TeV energy scale. Deciding to instead investigate other things because it’s cheaper is fine and that may be where we are headed. I just think people need to not fool themselves: taking such a path is giving up and putting an end to the long history of trying to understand the world at shorter and shorter distance scales. Arguably this was always going to happen sooner or later, the debate is just whether now is the time to give up due to the expense.
Peter, I want to push back a little on the idea of “time to give up due to the expense”.
Money spent on fundamental research does not simply disappear into some large extra dimension.
Look at Fermilab. In middle school (mid-70s) we had a field trip there and the area was all corn fields. Now it is a technology corridor. It has probably added multiples of what it cost to build into the local and national economy.
The FCC will throw up design, construction, and data analysis challenges that we would never encounter otherwise. Surmounting them will take thousands of the best brains from around the world and give them a training you can only get at the frontier.
Of course having said all that, some of us really just want to see some BSM signatures.
I am an outsider to this field. I have an interest in it – it has been at the leading edge of science for a long time. Thus, you can classify me as your typical tax payer who the HEP community should try to convince about the desirability of these new accelerators (it would of course be up to elected politicians, not me – but, you know what I mean.)
The truth is, such as things are right now, this would be a very difficult sale. My main issue here is Sabine Hossenfelder’s argument, to wit, we have no compelling theoretical reasons to expect that those accelerators would find any new physics. It seems to me that we are talking huge amounts of money just to see if we are lucky and something is indeed out there. At this point in time, I would vote against such projects, recommending to devote the resources to other, more promising undertakings, of which there are many, not only in physics, but particularly in biology and genetics.
Amitabh Lath,
I basically agree and don’t think the “we can’t afford this”argument makes sense. The EU yearly GDP is around \$ 20 Trillion, so devoting \$1 billion of that to building a collider is not crowding out anything else. And yes, the money is not being poured down a hole, it’s employing people and paying their salary.
The real argument is that this funding has to come from a limited stream of public (or private?) funding for activity not devoted to making a profit. Lots of people have other ideas about what non-profit making activities they’d like to pay people to do other than build a collider.
This general issue (should we spend X on HEP physics?) tends to generate endless comments about how the money would better be spent elsewhere, according to the personal preferences of the author. This gets tedious fast and is a sort of discussion that goes nowhere (please try and restrain yourselves from such comments here). The economy and governmental budgets are not about to get reorganized along lines I’d approve of, so you’re not going to hear from me an accounting of how the world should be run.
What I’d rather see discussed is the actual situation we are facing, with a realistic discussion of what the numbers look like. We are now just seeing total construction numbers, and over the next year or so those responsible for running CERN will have to see if they can somehow fit these into a plan that can plausibly be funded from available sources. I think Hossenfelder was making a mistake by starting on this campaign now. Let’s see what draft plan emerges from CERN next year, and evaluate that. It will have real budget numbers and one can have a serious discussion about the implications of the collider spending vs. other sets of choices about what to do with the same source of funds.
HGB, I have a comment on your “we are talking huge amounts of money” statement. Huge compared to what? As Peter points out, the world is fairly rich, we can afford this easily. This time around countries like China and India will contribute a larger fraction because their economies are bigger than in the 90s (they have both sent probes to the moon).
As I pointed out above, the monetary payoff will be thousands of scientists, engineers, and technicians educated to think creatively in a way that is just not possible at Google or Tesla.
Not to mention the technical breakthroughs. We don’t like to talk about these because we would prefer everyone to focus on the physics, but aside from the WWW there are klystrons and niobium-titanium superconductors and proton beam therapy and a bunch more. Currently there is work being done on machine learning and ultrafast pattern matching that will undoubtedly seep outside HEP at some point.
So in terms of money, the world economy will get back far more than it puts in.
Hi Peter — A theory based on angels wont solve the hierarchy problem. What I said was that TeV scale SUSY solved an important problem and was falsifiable. Though I did not ever believe in SUSY, I think it still is one of the most amazing solutions for the Hierarchy problem, but nature seems more ingenious.
I think on of the things that requires more grants and boost is the neutrino sector — like the neutrinoless double beta decay experiments and leptonic CP phase. These and proton decay experiments if taken to the next level of precision (improved by factors of 10 or even 100) will pbly tell us more about natures.
If there is a slim chance that an FCC will discover something, I am all in favor of building it, although I realize that I belong to the rather small fraction of the tax-payer collective that would actually care about the outcome. However, if failure to see something interesting is almost guaranteed, not so clearcut.
So I wonder how much results from precision experiments, such as the absence of EDM, are constraining possible deviations from the SM up to say 100 TeV. But then again, all such constraints are of course based on some theoretical assumptions that may be flawed.
Then I have a purely egotistical concern about the timeframe. If FCC does not start to produce results until 2050, I will probably not be around, or at least to old to appreciate them.
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Another puzzling aspect of the debate is that the flavour anomalies show every sign of being a real signal of New Physics (more). I suspect there is psychological inertia involved in not appreciating precision effects in loop contributions over the long-familiar direct detection events. But if EDM-bounds on new particle masses are anything to go by (e.g. Nature:s41586-018-0599-8), precision loop effects will only become more important in the future.
Peter,
The problem is that without the “bad theory” predictions, there are no predictions that indicate a larger collider would find anything new. “Look anyway” is all well and fine but not a convincing argument for such a big investment, especially because it’s likely to negatively affect funding of more promising avenues. Maybe the situation will change with the LHC data still to come, in which case this whole discussion will become obsolete. But if not, I don’t think a larger collider would be money well-invested.
As I lay out in my book, null-results are not particularly useful results if you want to develop a new theory. You really need evidence of new phenomena. It’s this absence of data for new phenomena that results in “bad theories” becoming grandfathered to begin with. To break this vicious cycle of “null results – bad theories – null results”, we should focus on those areas where we either already know there’s something new to find (dark matter), or where we have good theoretical motivations (quantum gravity, quantum foundations).
I don’t expect you to agree that those are the best areas to currently invest in, but at least I *have* an argument for why that’s the most promising thing to do.
(Btw, I no longer work on quantum gravity. No need to fix that statement, just for the record.)
Should add, another way to move on would of course be if particle physicists came up with actually good predictions. I do not consider this impossible, but it would require them to acknowledge that their current methods aren’t working and to come up with something better. I cannot see this happening. Sorry if that sounds cynical, but if they haven’t seen light by now I don’t think they ever will.
Urs,
By all due respect, you misunderstand the point of the experiment you are referring to. It’s not measuring qg corrections to one mass, it’s about producing a quantum superposition of masses and measuring their field. But I was not specifically referring to the Aspelmeyer group. There are various closely related ideas, see eg here https://arxiv.org/abs/1707.06050 and here https://www.nature.com/articles/549031a
Regarding your comments about quantum foundations. There are many things we simply do not understand about quantum field theories but those often receive little attention. (Think non-pert formulation, Haag’s theorem, even the IR limit isn’t as well understood as we thought only a decade ago.) As to your remark that it’s “not serious” to test quantum foundations, that’s a plainly stupid argument. I have written a whole book making my argument very clearly. I hope you’ll read it before you produce further ill-informed and easily dismissive comments.
Hi Peter,
Regarding your comments
> The number I used for the FCC-ee was based on the $ 10.5 billion total construction cost estimate given in the executive summary (page xxvi) of the CDR.
Indeed this is written in FCCee executive summary.
> The construction cost for FCC-ee amounts to 10,500 million CHF for the Z, W and H working points including all civil engineering works.
But this does not include the tt treshold at 365 GeV, for this you need to scroll to page 275 of the CDR where it is stated
> Operation of the FCC collider at the tt working point will require later installation of additional RF cavities and associated cryogenic cooling infrastructure with a corresponding total cost of 1,100 MCHF.
And this is how you come to 11.6 billion in total. This number is also in line with what the CERN DG presented at the New Year presentation (https://indico.cern.ch/event/779524/) slide 62.
Thus operating CLIC at 1.5 TeV is still cheaper then FCCee and for instance you could measure the Higgs self coupling and quartic coupling which you cannot at the FCCee, among many other things.
Dave: The short answer is no. There is no connection between theories which predict non-0 neutrino mass and those which make predictions for LHC and beyond LHC experiments. They re completely decoupled form each other. Nothing we’ll learn from neutrino experiments will tell us about collider physics or vice-versa. It disturbs me that no one else is concerned about this (esp. in the days of “grand unified theories” etc)
So many different ways of being a ‘bad theory’ – but what does it mean to be one, in the sense the phrase is being used here ?
E.g. ‘so implausible and badly motivated that it’s not worth spending even a few thousand dollars to test/disprove’ (for instance .. perpetual motion machines?)
or ‘badly motivated enough that it’s not worth employing even one person to investigate experimental consequences’ ?
or ‘bad enough that they should never appear to be one of the principal science goals of a billion-dollar experiment’ ?
Those are very different levels of badness. We know of course that LHC was planned and funded long before anyone came up with the prime examples of large extra dimensions / low-scale quantum gravity. And apparently even these were not quite bad enough to dismiss out of hand – without spending some years of PhD students’ lives on calculating experimental signatures and then setting upper limits from actual data.
Anon,
For reasons I’ve often written about here, I’m dubious that the “hierarchy problem” is a real problem. Even if you think it is, doing this (SUSY) by invoking models with 120 or more new parameters, carefully tuned to explain why no effects of the huge number of new fields introduced has ever been seen, is what I would call “bad theory”. Doing it with ill-defined extra dimensional models is “really, really, bad theory”.
Proton decay experiments are an interesting case to compare to colliders. There’s no evidence at all for GUTs, so no reason to believe they’ll see proton decay. Should one go ahead and build such experiments anyway? The answer seems to me to depend on cost + hope to learn something else (i.e., see supernova neutrinos). Should one spend \$20 billion on a huge proton decay experiment? Probably not, the money would be better spent on a less special-purpose machine, like a collider. But, at much lower cost, it’s worth doing, and one can have a sensible argument about the specific HEP experiments like a proton-decay one that could not be funded due to collider funding. My understanding is that this kind of thing is exactly what the European strategy process is about. They very well may decide a collider is just too expensive, and follow the US into restricting plans to non energy-frontier experiments.
Sabine,
I share your cynicism about the state of HEP theory. Best would be progress in theory that gave plausible ideas about how to improve upon the SM, which could guide choices about which experiments to fund, but that seems unlikely, with HEP theory split between those who have given up, and those intent on pursuing failed ideas.
But, once you give up on the theorists, if you don’t want to give up completely, your only hope is the experimentalists, and whatever they can come up with to look somewhere new. Let’s see what emerges from the strategy process. My understanding is that they’ll be doing exactly what you want, comparing expensive collider proposals with other proposals. It’s entirely possible the outcome will be a decision that the collider proposals are just too expensive for the chance they provide at something new, and Europe will head down the same road as the US HEP program.
Personally, I just haven’t seen any evidence that there are other (non-collider) equally promising and cheaper places to look that aren’t already being pursued. In particular, the search for “dark matter” has been a huge priority among theorists and experimenters for decades now, I’m dubious there are promising experimental avenues corresponding to well-motivated theory models that are not being actively and aggressively pursued.
There is good physics coming out of the LHC. Hadronic cross sections (relevant to perturbative and nonperturbative strong-interaction physics), nucleus-nucleus scattering, etc. The intersection of this with the sales pitches is the null set, but it is science that nuclear (and some particle) physicists really care about.
The LHC was sold to the public as a big-bang-higher-dimensional-supersymmetric-hierarchy-problem-string-proving gadunzel. Perhaps if press releases had given a more complete picture of the science, there wouldn’t be as much hand-wringing now.
Well, that’s just it, isn’t it.
Explaining the challenges of nonperturbative QCD to the average layperson (like me) is, well, very, very hard, much less what makes it worthwhile to study. Hopefully it’s not harder than nonperturbative QCD, though.