About a month ago, there was a lot of noise, discussion and controversy concerning CERN‘s proposal to build a giant new tunnel and put powerful new particle accelerators in it. This proposal is collectively called the Future Circular Collider (“FCC”). (The BBC reported on it here.)
Some scientists made arguments that FCC is a great idea, based on reasoning that I somewhat disagree with. Others said it would be a waste of money, based on reasoning that I again disagree with. But any decision on whether to actually fund the building of the FCC’s tunnel is still some years off, so I was reluctant to get involved in the debate, especially since my nuanced opinion seemed likely to be drowned out amid the polemics.
But I did eventually write something in response to a reporter’s questions, and looking back on it, I think it may be of interest to some readers. So here it is.
My Opinions on the FCC
My starting point is the timeline for the machine. Quoting from the FCC website, we are looking at “start of construction after the middle 2030s, with the first step of an electron-positron collider (FCC-ee) beginning operations around 2045. A second machine, colliding protons (FCC-hh) in the same tunnel, would extend the research programme from the 2070s to the end of the century.”
Now, although they use the same tunnel, these are two utterly different colliders, with complementary goals. It’s extremely useful to compare these plans with the journey of CERN from 1985 to 2035, which the FCC is designed to repeat.
The Previous Five Decades: One Tunnel, Two Machines
In the latter 1980s, a 27 km (17 mile) near-circular tunnel was built under the French and Swiss countryside around CERN. Over the decades, two entirely different machines were built in that tunnel:
- LEP, an electron-positron collider, which itself had two stages:
- LEP-1, which created electron-positron collisions with energy-per-collision just below 100 GeV. A high-precision, targeted machine, it was intended to study the Z boson in great detail, and allow searches for possible rare phenomena involving particles of lower mass.
- LEP-2, an upgrade to LEP-1, gradually pushed the collision energy up to 209 GeV. Somewhere between targeted and exploratory, it was used to study the W boson in detail, and to search for the particle known as the “Higgs boson” to the extent that it could.
- LHC, a proton-proton machine with a collision energy of 7000 – 14000 GeV, had a largely different goal. A fully exploratory machine, it was aimed mainly at unknown particles. In particular, it was intended to search for the Higgs boson (or whatever might have taken its place in nature), as well as for other particles that might be loosely associated with the Higgs boson. And it could search for many other types of particles too; hence the long lists of published experimental searches (such as this one).
Again, although LEP and LHC occupied the same tunnel and were operated by many of the same people, they were completely different machines that shared little else.
The Next Five Decades: One Tunnel, Two Machines
In largely the same way, the proposal is for the FCC tunnel to be used for two completely different machines analogous to LEP and LHC.
- Phase 1) FCC-ee, a more powerful version of LEP, comes first and is a targeted machine at relatively low energy (electron-positron collisions at 100-365 GeV, depending on the target, but with a very high collision rate — up to a hundred thousand times more than LEP-1.) Its most important target is the Higgs boson, but it also would carry out detailed studies of the Z boson, W boson, and the top quark.
- Phase 2) After FCC-ee has operated for a long time and collected lots of data, the current plan is that it would be dismantled, and the FCC-hh would be built inside the same tunnel. This machine would be a proton-proton collider like the LHC, only much more powerful, with up to 7 times the energy-per-collision. Like the LHC, it would be an exploratory machine: a general-purpose device that can search for a great variety of unknown particles and phenomena.
To Focus on Phase 2 is Premature
Let’s work backwards from Phase 2. What are the goals for the FCC-hh?
Asking physicists of today to state a precise goal for such a distant future is somewhat like asking Oppenheimer, all the way back in the 1950s, to predict the main aims of the LHC! It’s too early to expect a reliable answer. I suspect that current speculation about what the main motivation for FCC-hh will actually be, four or five decades from now, is likely to be wrong. (That said, there are some specific questions about the Higgs boson and Higgs field that only FCC-hh can address — most notably, how the Higgs field interacts with itself.)
Of course, I do understand why people are talking about FCC-hh right now. If CERN is going to build such a large tunnel, they ought to have some sensible ideas as to how it could be used not only soon but well into the distant future.
But nevertheless, a final decision on FCC-hh — whether and when to build it, and what its goals should be — lies decades away. It’s Phase 1 that really matters now. And Phase 1 has a clear purpose and a clear motivation.
Only Phase 1 (FCC-ee) Matters Right Now
What good is FCC-ee? You might well wonder! Since LHC has already run proton-proton collisions at 14000 GeV, making it capable of creating certain types of particles whose masses are several times larger than the Higgs boson or top quark, what hope do we have that FCC-ee, at a much, much lower collision energy, could make any new discoveries?
The answers are analogous to the ones that were appropriate for LEP-1, whose collision energies were already below those of the Tevatron, a predecessor to the LHC.
- First, FCC-ee can make precision studies of large numbers of Higgs bosons (and enormous numbers of Z bosons). These studies might uncover small cracks in the Standard Model — small deviations from its predictions — giving a first clue that new phenomena are present that are either (a) at higher energy than LHC can reach or (b) too rare and/or obscure for LHC to discover. FCC-ee might not reveal any details of these novel phenomena, but it would teach us that something new was within reach. In this case, the FCC-hh would be the ideal exploratory machine to follow FCC-ee. That’s because, compared to LHC, it can both reach higher in energy and produce lower-energy processes at a higher rate, giving it many avenues in which to search for the causes of the above-mentioned cracks.
- Second, FCC-ee can search for new particles of lower mass than the Higgs boson. Such particles could have been missed by LEP and the LHC if they are produced too rarely, or if they are somehow obscured in the busy environment of the LHC’s proton-proton collisions. Collisions in an electron-positron machine are much more pristine, and more easily reveal odd or rare phenomena. For instance, both the Z boson and Higgs boson might potentially decay to what are known as “dark” or “hidden” particles, which can be very difficult for the LHC experiments to observe. If such particles were discovered in Phase 1, then, depending on those particles’ details, one might well modify the plans for Phase 2. (For instance, certain types of dark/hidden particles would be difficult for FCC-hh to study, and might motivate a different Phase 2.)
The rationale for building FCC-ee is very clear: to take full advantage of what the Higgs boson and its field can teach us. Only recently discovered, the Higgs boson is unique among the known elementary particles as the only particle that has no “spin” — no intrinsic angular momentum — and as the particle whose interactions with other particles are most diverse in strength. The corresponding Higgs field, which gives electrons their mass and makes atoms possible, is even more important: it’s crucial for planets and for life.
Our knowledge of this field and its particle will still be very limited even when the LHC shuts down for good around 2035. Few of the LHC’s measurements of the Higgs boson’s properties will be precise, and some properties simply will not be measurable. For all we will know in 2035, it could still be the case that one in every twenty Higgs bosons decays to particles that are currently unknown; the LHC experiments will be unable to rule out this possibility. The FCC-ee will change this, making far more measurements, bringing much higher precision to many of them, and allowing searches for decays to particles that LHC has no hope of observing.
Thus FCC-ee will give us a better handle on the properties of the Higgs boson and Higgs field than the LHC can achieve, and allow us access to rare and/or obscure phenomena that LHC experiments cannot discover. The potential significance of these scientific advances should not be underestimated.
The FCC-hh of Phase 2 is for the distant future. It will depend crucially on whether Phase 1 finds something, and on what it finds. It also depends on the results of many other smaller-scale experiments which will be running over the next 35 years. Any particle physics discovery before 2060 will influence the way we think about the goals of FCC-hh, and so I view it as far too early to wax poetic about what Phase 2 could do, or to criticize it as a waste of money. We can have that debate over the next generation.
By contrast, the goals of FCC-ee are clear, and the cost and benefits easier to identify. That’s why, in my opinion, Phase 1 is the only topic worthy of serious discussion and debate right now.
25 Responses
As far as I can see, there could be constraints on extracting knowledge from the raw data such colliders produce. As a data scientist and AI software developer I routinely work with tens of terabytes datasets, which is currently the limit for one-machine processing. Meanwhile LHC has already produced staggering 1000 petabytes and will do ~5x more after the upgrade. Some questions:
– Will the FCC-ee collider produce more or less raw data comparing to the upgraded LHC?
– Suppose an FCC-ee detector collaboration after painstaking processing of the data found something at 5 sigma, but nobody, including them could reproduce the analysis due to budget constraints, power availability, data transfer bottlenecks, political tensions, etc. Will it count for true discovery if it’s only reproducible in theory?
“CERN’s Giant New Particle Accelerator: Is It Worth It?” no. please allocate the money to an area that would help us instead of wasting it on a hobby.
If you don’t understand something’s long-term importance or potential, it’s easy to dismiss it as a “hobby”. If you’d given me an actual argument instead than a dismissive slur, I would give you a counter-argument; but your thoughtless response deserves no counter-response.
Thanks for your breakdown of what the next collider should/could be.
I skimmed a theoretical paper on ‘Inflation’. They don’t go into such problems.
It would not be germaine to their study. But it has to be done.
This will likely come over as implied criticism, but that would in principle be good (right!?) and the first case is only an accident of history I take it.
I do consider an FCC-ee a potentially good next step, considering that LEP-1 was just below the range needed to observe the Higgs.
But as far as “cracks in the Standard Model” goes, the current constraint that goes to highest energies is the much cheaper electron sphericity experiments.* Quoting DeMille Group page: “With further improvements in sensitivity, the electron EDM may soon be discovered. This would unambiguously signal the existence of physics beyond the Standard Model, and set an upper bound on the energy scale where new particles must exist.” “Hence, ACME III will be sensitive to new particles with mass as high as 10-300 TeV, far beyond the direct range of any high-energy collider.” Of course it would not give much detail if new particles were indicated (like FCC-ee, perhaps), it would not exclude all possibilities, et cetera – and I’m sure it is considered in the accelerator decision context. The article here do not say that FCC-ee is the only experiment that would expose, or not, cracks. But perhaps it is valuable to note the competition in the context of long term public interest?
*And of course my personal interest in neutrino experiments are directly probing a known crack of neutrinos having mass. The eROSITA gamma sky survey could publish a 2ish sigma preference for normal neutrino mass ordering (electron, muon, tau neutrino in order of increasing mass) the other week! Combined with the NOvA 2ish sigma preference for the possibility of leptogenesis as behind matter/antimatter asymmetry under normal ordering, we are a decade or so away from answering (or not) that Standard Model question … (with accelerators involved as neutrino sources).
It’s not an either-or situation.
The problem with the “EDM” argument (and the quotes on the DeMille page) is that it’s both true and false. It’s true that you can use electron properties to constrain **some** types of new phenomena at 100 TeV… and that’s fantastic. But you will be completely insensitive to others. So if you discover something, that’s great: you know that there’s something new below 100 TeV. But if you don’t discover something, that does not prove there’s nothing new below 100 TeV.
[And you should be cautious reading people’s group pages. These are very public, and read by journalists, funders, potential graduate students, and so forth. They’re true, I’m sure. But fine print regarding what they can and can’t detect doesn’t usually appear there.]
An accelerator at 100 TeV (not FCC-ee, but FCC-hh) is a much more general probe of the 10 TeV energy scales that it can reach, and it would blow any indirect measurement out of the water. So we needn’t talk about that here.
For precision measurements (though not for production of rare low-energy processes), FCC-ee is conceptually comparable in some ways to EDM measurements. But the EDM is one quantity, while FCC-ee can measure many at once, so really FCC-ee is comparable to a large number of smaller-scale experiments. More importantly, though, EDM measurements and many others are not sensitive to certain types of physics that would affect the Higgs field… whereas FCC-ee could observe those. For several reasons, the Higgs field is a particularly likely place to find new phenomena, and so it would be irresponsible to drop either EDM or FCC-ee from the list of important tasks. We do need a broad program.
I wish I were more excited about the likelihood of neutrino physics having an impact on the rest of particle physics. The problem is that the neutrino mass matrix, even if fully known, will be no more useful that the quark mass matrix is today, and in fact, will be less so if the seesaw mechanism is operating, because then it is a combination of two unknown matrices — the matrix of couplings of left-handed neutrinos to right-handed neutrinos, and the matrix of masses of the right-handed neutrinos alone. I think we are in a golden age of neutrino physics right now, albeit a slow march. But once we know as much about the mass matrix as we can know, I do not foresee a bright future beyond that point. Hopefully I am wrong about that.
Matt, your criticism to reference group pages is well taken. I read the ACME work a long time ago but when I tried to find an update I stumbled on the page and it suited as science (if not peer reviewed) context.
Yes, I expect that the different experiments would reveal different “missing” physics. But if there is cost competition, a cheaper experiment could give (or take) leverage to build another. I don’t know which is more responsible to our society. The future history of the field will hopefully be guided by enlightened groups.
Thanks for your response, and especially on the neutrino physics! If it is indeed the answer to the CP problem – adding more finetuning to the enlarged Standard Model – it will remove some urgency to the particle accelerator programs. I hope too that it has a bright future, since until observations have eliminated sterile neutrinos as dark matter candidates the two unknown matrices will imply on the edge of the map: “Here be dragons!” But again, it is not an either-or.
Which Wilson coefficients in particular would this be for? I find it hard to believe that the electron EDM can uniquely probe all Wilson coefficients
A fundamental concept in economics is opportunity cost as the real cost. That is, in making a purchase, you are forgoing purchasing something or things else. Confining the purchase to be scientific, what else could be purchased in lieu of the FCC?
“Confining the purchase to be scientific, what else could be purchased in lieu of the FCC?”
It basically doesn’t work like that. Canceling or not doing a major science project (e.g., the Superconducting Super Collider) almost never produces a flood of money for other science projects.
Does it mean that you don’t want a bigger hadron machine to exist anywhere before 2074? Do you think that you differ from any of the anti-physics activists who simply want to kill particle physics?
A collider with the center-of-mass energy below 500 GeV is very likely to find nothing new. Even if it would find some deviation of a Higgs-related rate from the SM prediction, it just wouldn’t be terribly interesting and it wouldn’t teach us much beyond having some strange generic anomaly which cannot be reverse-engineered in any unique or quasi-unique way.
It is a waste of time to follow particle physics plans of someone who wants to kill particle physics in this way. There is a damn good reason to have a 100 TeV collider – this would open a substantial new territory on the log energy space where new things may happen according to highly motivated scenarios. And it should operate within 20 years.
Your claim that the justification of the 100 TeV collider depends on seeing something in the 500 GeV collider is just totally scientifically wrong. So your article is just a pseudoscientific would-be justification for killing of particle physics.
I disagree with you just as much as I disagree with Sabine Hossenfelder. Both of you think “a collider with the center-of-mass energy below 500 GeV is very likely to find nothing new.” The word “likely” is a statement of probability for which you have no evidence; it is pure theoretical bias. The idea that all interesting forms of new physics lie at higher energy, rather than at weaker coupling, is also pure theoretical bias for which you have no evidence, and with the failure of the Higgs-naturalness argument for the hierarchy, you no longer even have a good theoretical argument. You would also have told me, back in 1900, that there was no point in looking for what we now call “neutrinos.” I don’t approve of putting theoretical bias at the forefront of decision-making about experimental facilities.
You convincingly explained why we need a more powerful version of LEP.
But you haven’t explained why we need this accelerator to be the FCC-ee.
Why not the “International Linear Collider”? Why not the “Compact Linear Collider”? Why not a muon collider?
Correct, I did not… and that’s part of the debate and discussion that we should be having at this time. However, to go into that level of detail would require another post, which, at some point, I’ll probably write. But again, the decision isn’t coming tomorrow; it’s some time off.
It has been dimostratesi by rather recent theoretical findings that a linear collider would not be as good as a circular one, due to a fundamental broadening of the energy losses due to beamstrahlung which would make the determination of the “exact” collision energy impossible. That’s why circular is preferibile to linear for “precision physics”, which is what these machines are supposed to make.
A muon collider is not yet technically doable (for many reasons) while the FCC-ee doesn’t have any showstoppers, technically.
The energy step from 209 GeV (LEP-2) to 365 GeV looks underwhelming to a layman. Is it because FCC-ee is a targeted machine, and not an exploratory one? How many millions would every extra GeV cost?
First, I’m afraid you may be suffering from the same theoretical bias as Mr. Motl. If you only look at the energy shift, you are missing at least half the story. The collision rate is equally important.
The number of Z bosons produced at 100 GeV Lep-1 was about 10,000,000. The number that would be produced at FCC-ee would be well over 1,000,000,000,000. That means that processes that are one-in-a-billion would be completely missed at LEP-1 and observable in great detail at FCC-ee. The increase in the number of W bosons is almost as large.
Second, the energy shift is more significant than it looks. The dominant way to produce Higgs bosons at a collider like LEP or FCC-ee is electron + positron –> Z boson + Higgs boson. Since the Higgs boson has a mass of 125 GeV/c^2 and the Z has a mass of 91.2 GeV, you need at least 217 GeV. LEP was just a bit too low. So yes, sometimes 10 GeV is a huge difference; FCC-ee can make a million Higgs bosons, while LEP made zero.
But why do we need a million Higgs bosons, when LHC has made just as many? Becuase FCC-ee is a clean environment, and many measurements and even new-particle discoveries that are impossible at LHC will be potentially possible at FCC-ee. Example: Higgs –> two new pseudo scalar particles, each of which decay to a bottom quark and a bottom antiquark. (There are numerous models in which this occurs.) If this happens in 1 percent of Higgs decays, this is undiscoverable at LHC and easily discovered at FCC-ee.
Finally, there are important measurements in top quarks (which require going to 365 GeV) which cannot be made at LHC and obviously were impossible at LEP. I haven’t myself thought through all the possibilities.
As I emphasized, FCC-ee is a **targeted machine**, with several targets — Z, W, Higgs and top. 365 GeV and a very high collision rate allows studies of two essential particles that LEP couldn’t reach, and a much more probing study of two that it could.
Matt, thanks. I emphasized “layman” because they will provide – or won’t provide – funding for FCC. Don’t underestimate the public relations aspect.
I don’t understimate it, believe me! Indeed, the very purpose of this post is, in large part, to change the perspective of the “layman” (and of the scientist outside of particle physics.)
Thanks for reacting to a layman. It seems to me that it might be easier to sell a 418 GeV proposal (2×209) than a 365 GeV, unless there is a steep price difference. To a politician, physics be damned.
The cost differential is very, very steep. The energy bill goes up like (energy^4), roughly, for a circular electron-positron machine in a specified tunnel — and the collision rate goes down like (energy)^2. Energy is not everything; rate is just as important, and I’m prepared to sell that.
I have a question about self-interaction of the Higgs field, in form of a thought experiment. Let a universe has only one scalar quantum field, and the field’s quantum state has zero particles. Then consider the zero-point fluctuations at some point. As there’s only one quantum field, I suppose that its changes due to the fluctuations have very little effect because the field value have no external reference, and only difference in its value to neighboring points can have some effect. But, if a universe has two or more similar fields, like in the composite Higgs models, then the zero-point fluctuations should produce much more effect as the fields interact. Therefore, probing the Higgs field self-interaction can tell us whether it’s composite or not, right?
This isn’t the way it works… the zero-point fluctuations are not separable from, for example, a cosmological constant from some other source, such as gravity itself.
However, the lesson comes from the proton. We don’t talk about an elementary proton field because we don’t have to — we use quarks — but once upon a time, that wasn’t the case. How did we learn the proton wasn’t elementary? First, it has interactions with light that an elementary particle shouldn’t have (anomalous magnetic moment). Second, it scatters electromagnetically in a way that is different from an elementary particle (form factor). Third, if struck hard enough, the proton can be excited, somewhat like an excited atom, turning into a heavier version of itself (the spin-3/2 Delta particle). Fourth, if struck hard enough in an electromagnetic process, it turns into many particles (deep inelastic scattering).
For Higgs fields, it is more difficult, because we can’t scatter make a target out of short-lived Higgs bosons, and they aren’t charged under electromagnetism either. Nevertheless, composite Higgs bosons have interactions and excited states that elementary ones won’t have; and particles like the top quark, W and Z boson, which interact strongly with the Higgs field and its boson, will also have interactions and excited states that would not be present with an elementary Higgs boson. So searches for excited states of Higgs bosons, W bosons, Z bosons and top quarks, and detailed studies of their interactions, are among the various tools that can be used to search for or rule out compositeness of the Higgs field.
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