There’s a debate raging right now in particle physics, about whether and how to build the next big collider. CERN’s Future Circular Collider group has been studying different options, some more expensive and some less (Peter Woit has a nice summary of these here). This year, the European particle physics community will debate these proposals, deciding whether to include them in an updated European Strategy for Particle Physics. After that, it will be up to the various countries that are members of CERN to decide whether to fund the proposal. With the costs of the more expensive options hovering around $20 billion, this has led to substantial controversy.
I’m not going to offer an opinion here one way or another. Weighing this kind of thing requires knowing the alternatives: what else the European particle physics community might lobby for in the next few years, and once they decide, what other budget priorities each individual country has. I know almost nothing about either.
Instead of an opinion, I have an observation:
Imagine that primatologists had proposed a $20 billion primate center, able to observe gorillas in greater detail than ever before. The proposal might be criticized in any number of ways: there could be much cheaper ways to accomplish the same thing, the project might fail, it might be that we simply don’t care enough about primate behavior to spend $20 billion on it.
What you wouldn’t expect is the claim that a $20 billion primate center would teach us nothing new.
It probably wouldn’t teach us “$20 billion worth of science”, whatever that means. But a center like that would be guaranteed to discover something. That’s because we don’t expect primatologists’ theories to be exact. Even if gorillas behaved roughly as primatologists expected, the center would still see new behaviors, just as a consequence of looking at a new level of detail.
To pick a physics example, consider the gravitational wave telescope LIGO. Before their 2016 observation of two black holes merging, LIGO faced substantial criticism. After their initial experiments didn’t detect anything, many physicists thought that the project was doomed to fail: that it would never be sensitive enough to detect the faint signals of gravitational waves past the messy vibrations of everyday life on Earth.
When it finally worked, though, LIGO did teach us something new. Not the existence of gravitational waves, we already knew about them. Rather, LIGO taught us new things about the kinds of black holes that exist. LIGO observed much bigger black holes than astronomers expected, a surprise big enough that it left some people skeptical. Even if it hadn’t, though, we still would almost certainly observe something new: there’s no reason to expect astronomers to perfectly predict the size of the universe’s black holes.
Particle physics is different.
I don’t want to dismiss the work that goes in to collider physics (far too many people have dismissed it recently). Much, perhaps most, of the work on the LHC is dedicated not to detecting new particles, but to confirming and measuring the Standard Model. A new collider would bring heroic scientific effort. We’d learn revolutionary new things about how to build colliders, how to analyze data from colliders, and how to use the Standard Model to make predictions for colliders.
In the end, though, we expect those predictions to work. And not just to work reasonably well, but to work perfectly. While we might see something beyond the Standard Model, the default expectation is that we won’t, that after doing the experiments and analyzing the data and comparing to predictions we’ll get results that are statistically indistinguishable from an equation we can fit on a T-shirt. We’ll fix the constants on that T-shirt to an unprecedented level of precision, yes, but the form of the equation may well stay completely the same.
I don’t think there’s another field where that’s even an option. Nowhere else in all of science could we observe the world in unprecedented detail, capturing phenomena that had never been seen before…and end up perfectly matching our existing theory. There’s no other science where anyone would even expect that to happen.
That makes the argument here different from any argument we’ve faced before. It forces people to consider their deep priorities, to think not just about the best way to carry out this test or that but about what science is supposed to be for. I don’t think there are any easy answers. We’re in what may well be a genuinely new situation, and we have to figure out how to navigate it together.
Postscript: I still don’t want to give an opinion, but given that I didn’t have room for this above let me give a fragment of an opinion: Higgs triple couplings!!!
” While we might see something beyond the Standard Model, the default expectation is that we won’t …”
That’s a bit of hubris.
Pretty much every accelerator we have ever built has discovered something new. And sometimes what they discovered (e.g. the 3rd generation by SPEAR, LBL and Fermilab) was completely unanticipated.
Granted, the stakes have risen considerably from the days when Burton Richter could build SPEAR in the parking lot, out of the SLAC operating budget. But I think it’s not unreasonable to bet $20b that Mother Nature has not yet revealed all of her secrets.
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I don’t think an argument along the lines you’re giving can justify a higher that 95% chance that new accelerator will discover new physics. I don’t want to do the research for this comment, but I think at least one particle accelerator in the past did not discover new physics. A 95% percent chance is still much lower than the chances for the author’s example of a $20 billion primate center, and this big distinction is what the author was trying to point out.
“Pretty much every accelerator we have ever built has discovered something new. And sometimes what they discovered (e.g. the 3rd generation by SPEAR, LBL and Fermilab) was completely unanticipated.”
A lot of what has been discovered was anticipated. As soon as the first third generation fermion was observed, we knew we’d observe the other three. The Higgs was anticipated. The neutrino was anticipated well before it was observed. Almost every new hadron observed since the late 1980s or so has been predicted although the guesses as to their masses has been a big vague.
The other issue is that we know to a greater degree than we probably ever did in the past, about indirect measurements of phenomena at higher energies than we can measure directly. Lots of SM processes that would include loops with BSM higher mass particles if the existed up to a certain threshold. Some of these indirect measures point towards a lack of BSM physics up to particles on the order of 10 TeV, about ten times what we can see directly at the LHC and a bit higher up in energy scale than we are likely to see at a next collider. You can’t have a lot of BSM physics “just around the corner” without it having multiple impacts in the same direction in lots of different processes that you can see.
So, the odds of BSM physics at a next generation collider are not terribly promising.
But, we do have a close analog to the Gorilla observatory. The money that it would cost to build a next generation collider (or even a decent fraction of it) could build various kinds of astronomy equipment with existing technologies that could leave our current astronomy research in the dust.
Astronomy research is attractive because we have about as close to a guarantee as you can get that astronomy research has seen positive evidence of BSM/BeyondGR physics as you can get in the form of dark matter phenomena (and to a lesser extent dark energy phenomena). And, we are not only almost certain that there is new physics out there to be discovered, we also can point to many dozens of specific kinds of observations that we can make with this new equipment that will tighten the parameter space of possible sources of the New Physics.
Similarly, while not quite as glamorous, we can also pretty much guarantee that if we spend a billion or two dollars on increased computational resources for QCD researchers that we can translate very precise physical measurements of the properties of hadrons that have already been made into significantly more precise determinations of the values of SM physical constants such as the quark masses and the strong force coupling constant, which are among the least precise physical constants in the SM known today. The more loops to which we can do QCD calculations, the more precisely we can back the values of the fundamental constants out of existing experimental observations.
Effort devoted to both astronomy research and QCD calculations for another decade or so is likely to make efforts at building a future collider at that point more worthwhile. On the astronomy side, we will develop a much better target to design our colliders and the data filters in them to be looking for. On the QCD side, having a set of physical constants to work with that are an order of magnitude or two more precise (which we can do with existing data without smashing another atom every again if we want to), we can significantly reduce the amount of uncertainty in the SM null hypothesis against which new experimental results will be compared, which means that the collider will have more hypothesis testing power because we will be able to reduce the background noise, making it easier to discern even subtle signals in the newly collected data.
Neutrino physics research also has more problems that are definitely unsolved and can be resolved in straight forward ways with only slightly better than existing technology experiments for less pricey budgets. And, this could, like the astronomy research, sharpen our focus regarding what we should be looking for at our next generation collider.
In my view, these considerations justify pushing the pause button big budget even higher energy colliders for a decade or so. I’m not suggesting that we end collider physics entirely for a decade. But, if your only realistic expectation is to make progress on greater precision in measuring SM constants and not much else anyway, you can do a lot of that that with a baby collider much smaller than the LHC. You don’t need a bigger than LHC super high energy machine to do that. You only need a super high energy collider to see new physics that only manifest at higher energies.
As I mention in my post, this all has to come down to tradeoffs. The relevant question isn’t “is astro more productive than collider research”, it isn’t even “would astro benefit more from $20 billion”, it’s “would astro benefit more from being the focus of the European Strategy for Particle Physics”. The astro proposals I’ve heard about either are well on their way, or have been delayed for technical reasons. I don’t know which proposals would benefit specifically from more lobbying, I strongly suspect you don’t either, but that, and that alone, is the question at issue right now: where should the European physics community focus their fundraising efforts for the next few years? Is there something the community could lobby for that is higher priority than Higgs triple-couplings? I genuinely don’t know. But I’m kind of tired of other people who also don’t know arguing about it.
I certainly look at it from a bigger perspective than the European Strategy for Particle Physics. I’m not looking at what they should lobby for, but whether the people they are lobbying too should give them billions of dollars at this point at all given relative return to investment from other kinds of spending of the same dollars. And, the debate is bigger than Europe. China, for example, is also considering a collider. All of the proposals call for a more powerful machine to explore higher energies. But, really, the little nuances of which way that gets done aren’t very important.
The Higgs triple coupling would be great to observe in a world where HEP is free. But, is that possibility (nay, that near certainty) worth many billions of dollars? It is very hard to say yes, when there are other opportunities that provide greater likely reward for that money. Europe and China should probably put HEP in low gear for a while.
Nice bit of goalpost-shifting.
There has never ever been an accelerator proposed which had a “95% chance” of discovering new physics*. If that were the criterion, no particle accelerator would ever have been built.
The closest we have ever come to that is the LHC which was almost certain to discover the mechanism of electroweak symmetry breaking (whatever it turned out to be). But even there, “95%” would have been a overestimate. And, despite having achieved what it was designed to do, the LHC is the “failure” trotted out as the justification for not building the next accelerator.