The Multiworse Is Coming

You haven’t seen headlines recently about the Large Hadron Collider, have you? That’s because even the most skilled science writers can’t find much to write about.

There are loads of data for sure, and nuclear physicists are giddy with joy because the LHC has delivered a wealth of new information about the structure of protons and heavy ions. But the good old proton has never been the media’s darling. And the fancy new things that many particle physicists expected – the supersymmetric particles, dark matter, extra dimensions, black holes, and so on – have shunned CERN.

It’s a PR disaster that particle physics won’t be able to shake off easily. Before the LHC’s launch in 2008, many theorists expressed themselves confident the collider would produce new particles besides the Higgs boson. That hasn’t happened. And the public isn’t remotely as dumb as many academics wish. They’ll remember next time we come ask for money.

The big proclamations came almost exclusively from theoretical physicists; CERN didn’t promise anything they didn’t deliver. That is an important distinction, but I am afraid in the public perception the subtler differences won’t matter. It’s “physicists said.” And what physicists said was wrong. Like hair, trust is hard to split. And like hair, trust is easier to lose than to grow.

What the particle physicists got wrong was an argument based on a mathematical criterion called “naturalness”. If the laws of nature were “natural” according to this definition, then the LHC should have seen something besides the Higgs. The data analysis isn’t yet completed, but at this point it seems unlikely something more than statistical anomalies will show up.

I must have sat through hundreds of seminars in which naturalness arguments were repeated. Let me just flash you a representative slide from a 2007 talk by Michelangelo L. Mangano (full pdf here), so you get the idea. The punchline is at the very top: “new particles must appear” in an energy range of about a TeV (ie accessible at the LHC) “to avoid finetuning.”

I don’t mean to pick on Mangano in particular; his slides are just the first example that Google brought up. This was the argument why the LHC should see something new: To avoid finetuning and to preserve naturalness.

I explained many times previously why the conclusions based on naturalness were not predictions, but merely pleas for the laws of nature to be pretty. Luckily I no longer have to repeat these warnings, because the data agree that naturalness isn’t a good argument.

The LHC hasn’t seen anything new besides the Higgs. This means the laws of nature aren’t “natural” in the way that particle physicists would have wanted them to be. The consequence is not only that there are no new particles at the LHC. The consequence is also that we have no reason to think there will be new particles at the next higher energies – not until you go up a full 15 orders of magnitude, far beyond what even futuristic technologies may reach.

So what now? What if there are no more new particles? What if we’ve caught them all and that’s it, game over? What will happen to particle physics or, more to the point, to particle physicists?

In an essay some months ago, Adam Falkowski expressed it this way:

“[P]article physics is currently experiencing the most serious crisis in its storied history. The feeling in the field is at best one of confusion and at worst depression”

At present, the best reason to build another particle collider, one with energies above the LHC’s, is to measure the properties of the Higgs-boson, specifically its self-interaction. But it’s difficult to spin a sexy story around such a technical detail. My guess is that particle physicists will try to make it sound important by arguing the measurement would probe whether our vacuum is stable. Because, depending on the exact value of a constant, the vacuum may or may not eventually decay in a catastrophic event that rips apart everything in the universe.*

Such a vacuum decay, however, wouldn’t take place until long after all stars have burned out and the universe has become inhospitable to life anyway. And seeing that most people don’t care what might happen to our planet in a hundred years, they probably won’t care much what might happen to our universe in 10¹⁰⁰ billion years.

Personally I don’t think we need a specific reason to build a larger particle collider. A particle collider is essentially a large microscope. It doesn’t use light, it uses fast particles, and it doesn’t probe a target plate, it probes other particles, but the idea is the same: It lets us look at matter very closely. A larger collider would let us look closer than we have so far, and that’s the most obvious way to learn more about the structure of matter.

Compared to astrophysical processes which might reach similar energies, particle colliders have the advantage that they operate in a reasonably clean and well-controlled environment. Not to mention nearby, as opposed to some billion light-years away.

That we have no particular reason to expect the next larger collider will produce so-far unknown particles is in my opinion entirely tangential. If we stop here, the history of particle physics will be that of a protagonist who left town and, after the last street sign, sat down and died, the end. Some protagonist.

But I have been told by several people who speak to politicians more frequently than I that the “just do it” argument doesn’t fly. To justify substantial investments, I am told, an experiment needs a clear goal and at least a promise of breakthrough discoveries.

Knowing this, it’s not hard to extrapolate what particle physicists will do next. We merely have to look at what they’ve done in the past.

The first step is to backpedal from their earlier claims. This has already happened. Originally we were told that if supersymmetric particles are there, we would see them right away.

“Discovering gluinos and squarks in the expected mass range […] seems straightforward, since the rates are large and the signals are easy to separate from Standard Model backgrounds.” Frank Paige (1998).

“The Large Hadron Collider will either make a spectacular discovery or rule out supersymmetry entirely.” Michael Dine (2007)

Now they claim no one ever said it would be easy. By 2012, it was “Natural SUSY is difficult to see at LHC” and “"Natural supersymmetry" may be hard to find.” 

Step two is arguing that the presently largest collider will just barely fail to see the new particles but that the next larger collider will be up to the task.

One of the presently most popular proposals for the next collider is the International Linear Collider (ILC), which would be a lepton collider. Lepton colliders have the benefit of doing away with structure functions and fragmentation functions that you need when you collide composite particles like the proton.

In a 2016 essay for Scientific American Howard Baer, Vernon D. Barger, and Jenny List kicked off the lobbying campaign:

“Recent theoretical research suggests that Higgsinos might actually be showing up at the LHC—scientists just cannot find them in the mess of particles generated by the LHC's proton-antiproton collisions […] Theory predicts that the ILC should create abundant Higgsinos, sleptons (partners of leptons) and other superpartners. If it does, the ILC would confirm supersymmetry.”

The “recent theoretical research” they are referring to happens to be that of the authors themselves, vividly demonstrating that the quality standard of this field is currently so miserable that particle physicists can come up with predictions for anything they want. The phrase “theory predicts” has become entirely meaningless.

The website of the ILC itself is also charming. There we can read:

“A linear collider would be best suited for producing the lighter superpartners… Designed with great accuracy and precision, the ILC becomes the perfect machine to conduct the search for dark matter particles with unprecedented precision; we have good reasons to anticipate other exciting discoveries along the way.”

They don’t tell you what those “good reasons” are because there are none. At least not so far. This brings us to step three.

Step three is the fabrication of reasons why the next larger collider should see something. The leading proposal is presently that of Michael Douglas, who is advocating a different version of naturalness, that is naturalness in theory space. And the theory space he is referring to is, drums please, the string theory landscape.

Naturalness, of course, has always been a criterion in theory-space, which is exactly why I keep saying it’s nonsense: You need a probability distribution to define it and since we only ever observe one point in this theory space, we have no way to ever get empirical evidence about this distribution. So far, however, the theory space was that of quantum field theory.

When it comes to the landscape at least the problem of finding a probability distribution is known (called “the measure problem”), but it’s still unsolvable because we never observe laws of nature other than our own. “Solving” the problem comes down to guessing a probability distribution and then drowning your guess in lots of math. Let us see what predictions Douglas arrives at:

Slide from Michael Douglas. PDF here. Emphasis mine.

Supersymmetry might be just barely out of reach of the LHC, but a somewhat larger collider would find it. Who’d have thought.

You see what is happening here. Conjecturing a multiverse of any type (string landscape or eternal inflation or what have you) is useless. It doesn’t explain anything and you can’t calculate anything with it. But once you add a probability distribution on that multiverse, you can make calculations. Those calculations are math you can publish. And those publications you can later refer to in proposals read by people who can’t decipher the math. Mission accomplished.

The reason this cycle of empty predictions continues is that everyone involved only stands to benefit. From the particle physicists who write the papers to those who review the papers to those who cite the papers, everyone wants more funding for particle physics, so everyone plays along.

I too would like to see a next larger particle collider, but not if it takes lies to trick taxpayers into giving us money. More is at stake here than the employment of some thousand particle physicists. If we tolerate fabricated arguments in the scientific literature just because the conclusions suit us, we demonstrate how easy it is for scientists to cheat.

Fact is, we presently have no evidence –  neither experimental nor theoretical evidence –  that a next larger collider would find new particles. The absolutely last thing particle physicists need right now is to weaken their standards even more and appeal to multiversal math magic that can explain everything and anything. But that seems to be exactly where we are headed.

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* I know that’s not correct. I merely said that’s likely how the story will be spun.

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