Here’s a tip. If you read an argument either for or against a successor to the Large Hadron Collider (LHC) in which the words “string theory” or “string theorists” form a central part of the argument, then you can conclude that the author (a) doesn’t understand the science of particle physics, and (b) has an absurd caricature in mind concerning the community of high energy physicists. String theory and string theorists have nothing to do with whether such a collider should or should not be built.
Such an article has appeared on Big Think. It’s written by a certain Thomas Hartsfield. My impression, from his writing and from what I can find online, is that most of what he knows about particle physics comes from reading people like Ethan Siegel and Sabine Hossenfelder. I think Dr. Hartsfield would have done better to leave the argument to them.
An Army Made of Straw
Dr. Hartsfield’s article sets up one straw person after another.
- The “100 billion” cost is just the first. (No one is going to propose, much less build, a machine that costs 100 billion in today’s dollars.)
- It refers to “string theorists” as though they form the core of high-energy theoretical physics; you’d think that everyone who does theoretical particle physics is a slavish, mindless believer in the string theory god and its demigod assistant, supersymmetry. (Many theoretical particle physicists don’t work on either one, and very few ever do string theory. Among those who do some supersymmetry research, it’s often just one in a wide variety of topics that they study. Supersymmetry zealots do exist, but they aren’t as central to the field as some would like you to believe.)
- It makes loud but tired claims, such as “A giant particle collider cannot truly test supersymmetry, which can evolve to fit nearly anything.” (Is this supposed to be shocking? It’s obvious to any expert. The same is true of dark matter, the origin of neutrino masses, and a whole host of other topics. Its not unusual for an idea to come with a parameter which can be made extremely small. Such an idea can be discovered, or made obsolete by other discoveries, but excluding it may take centuries. In fact this is pretty typical; so deal with it!)
- “$100 billion could fund (quite literally) 100,000 smaller physics experiments.” (Aside from the fact that this plays sleight-of-hand, mixing future dollars with present dollars, the argument is crude. When the Superconducting Supercollider was cancelled, did the money that was saved flow into thousands of physics experiments, or other scientific experiments? No. Congress sent it all over the place.)
- And then it concludes with my favorite, a true laugher: “The only good argument for the [machine] might be employment for smart people. And for string theorists.” (Honestly, employment for string theorists!?! What bu… rubbish. It might have been a good idea to do some research into how funding actually works in the field, before saying something so patently silly.)
Meanwhile, the article never once mentions the particle physics experimentalists and accelerator physicists. Remember them? The ones who actually build and run these machines, and actually discover things? The ones without whom the whole enterprise is all just math?
Although they mostly don’t appear in the article, there are strong arguments both for and against building such a machine; see below. Keep in mind, though, that any decision is still years off, and we may have quite a different perspective by the time we get to that point, depending on whether discoveries are made at the LHC or at other experimental facilities. No one actually needs to be making this decision at the moment, so I’m not sure why Dr. Hartsfield feels it’s so crucial to take an indefensible position now.
Good Arguments in Favor
But if you had to make the decision today, the best arguments for such a machine are that
- the naturalness puzzle of the Standard Model remains unresolved,
- the structure and details of the Standard Model are completely mysterious,
- searching at higher energy continues a path of exploration that has been scientifically fruitful in the past.
The first two arguments are very strong; the third has weaknesses, see below. Naturalness, which would imply that the Higgs boson should be accompanied by other types of particles or forces, is a principle that perhaps does not apply to the weak nuclear force; but it’s hardly a dumb idea, considering that it works perfectly for the strong nuclear force, and in other areas of physics. Meanwhile there’s hardly any understanding of the Standard Model’s structure — its array of forces and their strengths, and its array of particles and their masses, among other things. There’s clearly a lot more to be learned, and a versatile higher-energy collider is arguably the most likely place to go learn some of it.
Please note that these arguments in favor of this big future collider have nothing to do with either string theory or supersymmetry.
Good Arguments Against
What are the best arguments against building such a machine? (Most do not appear in Hartsfield’s article.)
- The solutions to the problems of the Standard Model, and to the naturalness puzzle, might not all lie at higher energy; perhaps some of the solutions are to be found elsewhere,
- even if the solutions lie at higher energy, there is no guarantee currently that they lie within a factor of ten of the LHC’s energy,
- the power consumption of such a machine would be high,
- its potential cost is high, even in future dollars.
I consider these very serious arguments. The last two arguments involve technological problems. If we will only be able to use today’s technology in this future machine, then yes, these are going to be serious obstacles. I can’t predict whether that situation will improve or not. Sometimes technological breakthroughs occur, and costs drop.
The first arguments, meanwhile, have been central in my thinking, and that of others, for decades. Even 25 years ago, I would have told you that if the LHC were to find only a Higgs boson and nothing else, then the argument for a future high-energy machine would become suspect. Naturalness argues that we ought to find something beyond the Standard Model at the LHC; if that argument is partially or completely evaded in nature, and the Standard Model survives all LHC tests, then it forces us to question whether the solution to the naturalness puzzle and/or other mysteries of the Standard Model all lie at higher energy. Maybe the key questions can only be addressed by a change in paradigm, and might require a completely different experimental approach. It’s not obvious, without an additional LHC discovery, that a higher-energy machine would bring new insights. And without clear, indisputable evidence in current experiments that the Standard Model is breaking down in some way, there is no way to infer the amount of energy that a new machine would actually need in order to address these questions.
These concerns have intensified as the LHC continues to confirm the Standard Model’s predictions at current collision energies. If particle physicists want to push hard for an expensive, higher-energy version of the LHC, they do need to find more evidence that this is really the best direction. All the more reason to squeeze every ounce of information out of the experiments that we currently have.
Why This is All Premature
But in many ways, this whole discussion is getting ahead of itself. First, the LHC era is not over; far from it. It mystifies me how many people assume that because the LHC’s data hasn’t yet contradicted the Standard Model, there’s clearly nothing for the LHC to find. In fact, there are still many search techniques which have not even been tried, much less optimized. [Witness the long-lived particle workshop held last week, among others that focus on strategies for seeking possible dark matter particles and their friends. And that’s far from the whole story.]
Second, the collider Hartsfield is referring to is not the next machine. It’s the machine-after-next. And the next machine is one for which the arguments are clear, strong, and have nothing to do either with supersymmetry or string theory — nor are the costs anywhere near 100 billion. This would be an electron-positron collider that produces lots of Higgs bosons and lots of top quarks, in an environment that makes them easier to study. We’re not talking about pipe dreams of string theorists or supersymmetry; these two types of particles are known to exist. But they are still imperfectly understood, and could hide important secrets. Indeed, if the naturalness puzzle does have a solution, or at least is a path to new knowledge, these are the two types of particles that are by far the mostly likely to reveal it.
So let’s focus on the actual path ahead. The collider that Hartsfield refers to is two steps away, not one. Scientific and technological developments in the next decade or so may change the arguments for and against it, and sway the decision as to whether to build it or not. Science is about facing reality, and there’s no place for bogus arguments based on fantasies, such as those where the price tag’s 100 billion (do I hear 150? 200?), experimental and accelerator physicists don’t even warrant a mention, and the words “string theorist”, “supersymmetry devotee” and “theoretical particle physicist” are imagined to be synonymous.