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 HE188.8.131.52/16-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.
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.