[Update: I found the time to add a few links to the post below, which I had previously omitted for lack of time (hey I'm on vacation!), and I also updated it to add some commentary of Sabine Hossenfelder's latest post on "the end of particle physics".]

In this age of short-term reward strategies (in politics, in society, and in individual behaviour) planning huge endeavours 20 years ahead is harder than it used to be. In the late eighties, when the Large Hadron Collider (LHC) was conceived and argued to be doable by a few visionaries, it immediately looked like a great idea to all. 

The only other "high-energy" particle physics project on the board, the Superconducting Super Collider (SSC), promised to deliver everything a physicist could dream of: an assured discovery of the Higgs boson, plus a thorough investigation of new physics across the board and up to effective invariant mass of new resonances in the tens of TeV range. 

(Above: map of the SSC footprint in Texas, and the underground cavity excavated near Waxahachie -image taken from this blog post).

However, the SSC was positioned even farther away in the future, and due to its large cost was going to have to face political hurdles before it could be put together. We know how that story ended: in September 1993 a US Congress vote cut its funding, downgrading the SSC overnight from largest-ever human endeavour to mushroom cultivation site.

Apart from the obvious advantage of having already a tunnel ready to host the accelerator (the 27 km long LEP ring at CERN),  what made the LHC a winning project is the fact that physicists in the past century still reasoned in terms of an open competition between US and European leadership in high-energy physics. While most of the big discoveries in the sixties and seventies happened in the US, despite CERN's excellent experiments (and at least in one occasion due to the foul play of some renowned influencer), the eighties saw the revenge of Europe, with the hugely important discovery of the W and Z bosons. 

The present

Fast forward to the present now. There are apparently (but see below the note on HE-LHC) no huge tunnels ready to host the next super-duper collider; the competition between US and Europe has vanished due to the loss of momentum of US funding of high-energy physics, and the migration and contribution of US scientists to CERN experiments; and there are no obvious targets with which to convince the funding agencies. What should experimental particle physicists do in this situation, holding a hand of lame cards that do not fit together well?

At a cursory look, anybody who plays poker would argue that in this situation there are two options: pass, or go all in; and that the former strategy would seem to be the wiser one. But this is a rather superficial way of looking at the problem. Indeed, if we look at the bright side of things, a quite different picture emerges.

1) China is a new player in the game of big machines, and it has shown to be ready to take the lead in planning a new electron-positron collider in a very long tunnel, which can in due time be converted into a proton-proton collider working at a center-of-mass energy offering a big enough jump in explorable space to grant a significant hope of getting lucky and finally finding physics beyond the standard model;

2) We have found a new particle, the Higgs boson, and we are going to study it in detail with the next 15 years of LHC operation. This is an already funded project - the so-called "HL-LHC", for "high luminosity", meaning large amounts of data will be produced. Yet hadron colliders are not ideal for precision physics: the HL-LHC will do a lot, but the kind of precision we really want to reach in the determination of the strength of the coupling of the Higgs particle to all known fermions and bosons (1% or lower) is not at reach of that project. What to do? 

The answer, to any reasonable physicist, is simple: you discover particles in hadron collisions, where production rates are high; but then you study them with high precision in electron-positron collisions, where clean measurements can be performed. We did this with the SppS-LEP tandem in the eighties: after discovering the Z boson at the SppS, a proton-antiproton collider, the measurement of its properties (crucial for stringent tests of electroweak theory) was performed at LEP, an electron-positron machine. 

So the plan is quite straightforward: build a new electron-positron machine in a large tunnel, study the Higgs in detail, and in the meantime perfect the technology of high-strength magnets such that you will be able to bend very energetic beams of protons in the same tunnel, ten years down the line. The simplicity of this plan (let us call it "FCC", for "future circular collider" in the following, a name chosen by the CERN-based project, although with that name I am not choosing a geographical location for its construction) coupled with the scientific imperative of studying the Higgs boson now that we finally got our hands on it, makes it very strong and hard to argue against.

3) Particle theory is in a crisis. As my friend and colleague Gian Francesco Giudice likes to point out, crises are typically a productive moment. Since supersymmetry cannot be found by experiments, and the breathing space of its most natural instantiations is shrinking by the day, many theorists have turned to more complex ideas or to "effective theories" that describe new phenomena in a way that fits well with the measurements that experiments can produce. The point here is that at this juncture we cannot rely on theory to indicate the way. Should we then sit and wait for a new Weinberg to come along? It makes no sense.

For just think at the past 150 years of scientific advances. How many of those star discoveries (X rays, the electron, the neutron, the muon, the pion, the neutrino, 100's of new hadron resonances, CP violation, the J/Psi particle; not to mention the big bang and a host of other groundbreaking discoveries, if we are allowed to extend the search to other fields) were preannounced by theoretical studies? How many times theorists told us where to look? It did happen with the Higgs, with the W and Z, and with many beautiful discoveries; but we should not get in that spoiled attitude, as theorists are human beings, and they might be unable to conceive the unconceivable. But the unconceivable might exist! That is why technology-driven experimentation lives by its own rationale and logic.

Concerning Sabine's post

Sabine Hossenfelder, the star blogger and author of a bestselling book on the matter ("Lost in Math", money very well spent if you ask me!), argues at her Backreaction site that the advocates of the FCC plan are overhyping the potential of their plan as well as the chances that it finds new physics. In a way, what she says is correct: the indicia that new physics be just around the corner are not strong at all. 

In fact, if you know me well enough, you would be quick to guess that I would readily offer to repeat the $1000 bet I put forth in 2006 (and later won in 2013 against Gordon Watts and Jacques Distler) on the absence of signals of new physics at arm's reach. The old bet mentioned LHC energies and 10 inverse femtobarns per experiment as the threshold at which an evaluation of the catch by ATLAS and CMS would be made; in a new bet, one could stipulate that the decision on who wins is whether anything new is found at or below subprocess energies of say 10, 20, 50 TeV. (at e.g. offered payoffs respectively of 1:1, 1:2, and 1:3). [Note: "subprocess energies" means the actual combined energy of the pointlike pair that produces the hard interaction; this, in a hadron collider of 100 TeV, is effectively reduced by a factor of 6 or so, although the matter fully depends on how many collisions one can collect.] But personal beliefs are not science - in fact, we don't use Bayesian statistics in our business. 

Where I think Sabine is misguided (as has been pointed out by many commenters in her blog and in her Facebook thread) is, in my opinion too, that the absence of theoretical indications should never become a show-stopper to the investigation of Nature. To me, the fact that we can produce 40 TeV resonances if there exist any, is by itself a sufficient motivation to go out and try to do precisely that. Are there not enough anomalies in present-day data to indicate what we should look for in detail? Too bad, let us look for anything we can find, as Katie McAlpine explained well in her LHC rap.

I should add here that in the above mentioned threads I have been tagged by Sabine as a stakeholder in the FCC, or in general in experimental HEP, and that therefore my opinion is biased. That is a ridiculous statement which betrays a dangerous mindset. Of course my opinion is biased - it is biased by decades of study of particle physics and the resulting acquired knowledge! Or should we run a poll on Facebook to decide whether to fund the FCC or rather construct a ladder to the moon? Probably it would be democratic, but it would also be foolish.

The point is that my salary won't change if European funding agencies decide to leave it to China to build the next big machine; furthermore I rather fancy the idea of regaining Senator status with Lufthansa, something I lost when I stopped working for a Fermilab experiment. That is how far my personal gains go in the matter, really. So I claim I can sit here and say that the FCC is a very good idea; that it is fully scientifically motivated; that it costs less than the money the US spends for a few weeks of operation in the middle East; that those moneys could not be spent in a better way to investigate fundamental physics (no, I do not support giving them to string theorists again).

They say that a late reaction must be weaker than a prompt one, to avoid triggering an escalation (think at the start of World War I for a good example). This post is quite late as a criticism of Sabine's rant against the FCC video, so I'll try to keep it soft: I think that article was only making a point against the scientific value of the claim of a demonstrative video, and as such it is probably correct and certainly irrelevant. For we well know that to speak to the public (be it interested laypersons or congressmen with a pen and a check ready to be signed) we have to trivialize things a bit. Let us just say that the trivialization level of the FCC video was not to Sabine's liking, and move on. Unless, of course, we want to put more logs to the flame of the debate and make Sabine's book an all-time bestseller, much to my red-hot envy!

Note that in a more recent post Sabine explains why she does think that a new high-energy collider is not sufficiently motivated (while in the comments to the previous post she was more cautious and said she was only arguing that the FCC video was overhyping the chances of finding new physics). The argument she brings in now is that there is a long history of past claims (mostly by theorists) that there should be new physics at the TeV scale, based on the naturalness argument alone. So, she says, "particle physicists are nervous", as that argument cannot be made any longer. But that argument, I claim, is unnecessary (and in fact, it was not the reason for building the LHC in the first place, as the LHC was primarily built with the goal of finding the Higgs, like it or not). 

Sorry, but despite the many quotes in her post it's not like everything rotates around the topic of naturalness. There are other things to be interested about - neutrinos, for instance: what the hell is up with their masses and mixings? One could similarly find hundreds of pre-2010 claims of uncautious theorists who said the LHC should find new physics in the form of a 100 GeV-ish dark matter particle based on the "cosmic coincidence" alone. I see no mention of this very important argument in her post (and it looks strange, given that it can easily be spun the same way).

[The "cosmic coincidence" I am hinting at is the notion that if we try to explain dark matter (DM) by hypothesizing the existence of a as-of-yet undiscovered weakly-interacting neutral particle (it could be a supersymmetric particle called the neutralino, e.g.) then the cross section of its production, if it has a mass of a few 100s GeV, comes out to be exactly the one required to create, during the first instants of the Big Bang, enough of it to explain the current amount of DM in the universe. So if you imagine that there's a neutralino, this automatically explains the composition of the universe if you give it a mass at the scale of electroweak symmetry breaking.]

It is a bit sad to read between the lines that, despite all her attempts at saying she is not saying a FCC-like machine should not be built, Sabine deep inside appears to hope (at least to me) it will not be built: why, otherwise, should she title her post that "the LHC may spell the end of particle physics", or write (twice) in a half-mocking way that "particle physicists are nervous", or conclude triumphantly (sorry, that's again only how it sounds to me) that a FCC "will be a tough sell for a machine that comes at $10 billion and up"? 

Also, she is misrepresenting things in her latest post, as she says that "pretty much everyone agreed that the LHC should see new physics besides the Higgs", by having quoted mostly many distinguished theorists. Who cares about the theorists? I know Sabine draws attention to the theoretical debate, which ultimately boils down to why everybody should read her book. But Sabine, there are hundreds of experimentalists (and also a few theorists) around who did not believe that, and I gave an example of one of them above, since I myself put my money where my mouth was, 12 years ago.

But should we build a new thing? And which one?

Now let me go back to the main theme of this post: why we need a new collider, and what that could be. For we have not discussed several alternative options to the FCC plan (which is how I call a large new electron-positron machine followed 10 years later by a proton-proton collider in the 100-TeV ballpark, to be sure, and to which I do not attach a geographical location - if it is China all the better, physics won't care).

One option not completely ruled out, but which I sense is losing strength as a main player, is the one of building a very long linear collider. I will not discuss here the options and schemes; the main ones are called CLIC and ILC, and you can look them up if you wish. The point of strength of these machines, which collide intense beams of electrons and positrons at energies appropriate for the study of the Higgs boson and the top quark, and then up to a few TeV, is that they do precision physics. Their point of weakness is that they do not promise to widen the search for new physics any further than the LHC or the HL-LHC does. In addition, running at few TeV of energy in the center-of-mass means turning off the light and air conditioning of a big city to get enough electrical power. I would be happy if such a machine were built, but I do not see as this can be all we do in the next 20-30 years.

A less ambitious plan than that of the FCC is to increase the LHC beam energy by installing new magnets capable of doubling their bending power. This project (called "HE-LHC", where the E stands for Energy) would lead to getting proton-proton collisions at energies of 25-30 TeV, without having to dig a single extra ounce of earth. It is an interesting plan to keep as a backup if we get SSC-ed again, but I think we can and should aim higher, as the technology for learning more about our world is there and it would be a shame not to do all we can, as I already remarked.

The muon collider 

Finally, there is another exotic idea on the table, and one I personally like a lot: building a muon collider. Muons are the heavier brothers of electrons. They have a mass 200 times larger, which guarantees that no energy is squandered in synchrotron radiation as these particles are bent in a circular collider (as the energy radiated by a charged particle decreases with the fourth power of its mass, other things being equal). You get the point: a muon collider can be made more compact and energetic at the same time. But wait: muons are unstable! They decay in 2 millionths of a second, on average. How can we produce them, accelerate them, and produce collisions? 

Einstein comes to the rescue. Relativity explains that the wristwatch of a muon speeding around, say, at an energy equal to ten thousand times its rest mass runs slower by the same amount. For us, that muon lives 0.02 seconds, which becomes a quite manageable time interval, allowing our technology to do the trick.

But why muons?  For one thing, the muons couple to the Higgs boson also proportionally to the square of their mass, like electrons - so the chance that a muon-muon collision gives a Higgs boson is 40000 times higher than for an electron-positron collision. But there's more: there are several theoretical prejudices that point to the idea that if there is new physics to be found, that will also couple more readily to matter from the second and third generation (muons and tauons, if we speak of leptons). 

So, building a muon collider would be quite scientifically motivated; it would also keep us busy for a long while, though, because the technology to do it is not completely straightforward to assemble, let's say. But if you ask me, I would both fund a FCC plan AND a muon collider, knowing that the engine keys of the latter would probably be handled to our grandchildren.

Why I could be wrong

Above, I have mentioned that I am ready to gamble on the absence of new physics down to energies of 40 TeV or so. Why that number? And why am I so pessimistic? Well, I am pessimistic because when I bet I like to do it in a way that I always win. If we were to find new physics I would be so happy that the prospect of losing $1000 and having to ridicule myself publically would seem a very, very small price to pay!

In reality, the standard model IS indeed only an effective theory, which is bound to break at some point. And as much as people argue that naturalness (the unnaturally small mass of the Higgs boson, that forces the theory to make acrobatic jumps to level down large contributions to that physical quantity) is a false problem for the standard model, I do think it shows we have not finished our job in understanding how things really work. Furthermore, we do know that neutrinos have mass, and very soon we will start measuring them. But that's an enigma wrapped in a mystery! 

See, these are just two things (I could write five or six more, but really now let me enjoy the party for new year's eve!) that any scientist should take as a proof that we have a long way ahead to understand the world. Why should we stop now? The LHC was extremely successful: it gave us what we built it for (the Higgs), and also gave us an enormous wealth of new understanding. Ruling out theories that are falsifiable (and thus good science) IS a very healthy way to proceed in our weeding out of false explanations of Nature. The LHC did that, and I cannot see how building a bigger LHC, while at the same time finishing our business with the understanding of the Higgs particle, could be anything but sound.

There - I think I have given you some ideas of why, in my opinion, we should aim for preparing to build a new machine now, and what that thing should be. Now shoot me, I don't care - I am spending the last day of 2018 chilling by a pool in a tiny Indonesian island, and can't be reached by email. Happy new year to all !


Tommaso Dorigo is an experimental particle physicist who works for the INFN at the University of Padova, and collaborates with the CMS experiment at the CERN LHC. He coordinates the European network AMVA4NewPhysics as well as research in accelerator-based physics for INFN-Padova, and is an editor of the journal Reviews in Physics. In 2016 Dorigo published the book “Anomaly! Collider physics and the quest for new phenomena at Fermilab”. You can get a copy of the book on Amazon.