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The biggest news in particle physics is no news. In March, one of the most important conferences in the field, Rencontres de Moriond, took place. It is an annual meeting at which experimental collaborations present preliminary results. But the recent data from the Large Hadron Collider (LHC), currently the world’s largest particle collider, has not revealed anything new.
Forty years ago, particle physicists thought themselves close to a final theory for the structure of matter. At that time, they formulated the Standard Model of particle physics to describe the elementary constituents of matter and their interactions. After that, they searched for the predicted, but still missing, particles of the Standard Model. In 2012, they confirmed the last missing particle, the Higgs boson.
The Higgs boson is necessary to make sense of the rest of the Standard Model. Without it, the other particles would not have masses, and probabilities would not properly add up to one. Now, with the Higgs in the bag, the Standard Model is complete; all Pokémon caught.
The Standard Model may be physicists’ best shot at the structure of fundamental matter, but it leaves them wanting. Many particle physicists think it is simply too ugly to be nature’s last word. The 25 particles of the Standard Model can be classified by three types of symmetries that correspond to three fundamental forces: The electromagnetic force, and the strong and weak nuclear forces. Physicists, however, would rather there was only one unified force. They would also like to see an entirely new type of symmetry, the so-called “supersymmetry,” because that would be more appealing. Oh, and additional dimensions of space would be pretty. And maybe also parallel universes. Their wish list is long.
It has become common practice among particle physicists to use arguments from beauty to select the theories they deem worthy of further study. These criteria of beauty are subjective and not evidence-based, but they are widely believed to be good guides to theory development. The most often used criteria of beauty in the foundations of physics are presently simplicity and naturalness.
By “simplicity,” I don’t mean relative simplicity, the idea that the simplest theory is the best (a.k.a. “Occam’s razor”). Relying on relative simplicity is good scientific practice. The desire that a theory be simple in absolute terms, in contrast, is a criterion from beauty: There is no deep reason that the laws of nature should be simple. In the foundations of physics, this desire for absolute simplicity presently shows in physicists’ hope for unification or, if you push it one level further, in the quest for a “Theory of Everything” that would merge the three forces of the Standard Model with gravity.
As an ex-particle physicist, I understand the desire to have an encompassing theory for the structure of matter.
The other criterion of beauty, naturalness, requires that pure numbers that appear in a theory (i.e., those without units) should neither be very large nor very small; instead, these numbers should be close to one. Exactly how close these numbers should be to one is debatable, which is already an indicator of the non-scientific nature of this argument. Indeed, the inability of particle physicists to quantify just when a lack of naturalness becomes problematic highlights that the fact that an unnatural theory is utterly unproblematic. It is just not beautiful.
Anyone who has a look at the literature of the foundations of physics will see that relying on such arguments from beauty has been a major current in the field for decades. It has been propagated by big players in the field, including Steven Weinberg, Frank Wilczek, Edward Witten, Murray Gell-Mann, and Sheldon Glashow. Countless books popularized the idea that the laws of nature should be beautiful, written, among others, by Brian Greene, Dan Hooper, Gordon Kane, and Anthony Zee. Indeed, this talk about beauty has been going on for so long that at this point it seems likely most people presently in the field were attracted by it in the first place. Little surprise, then, they can’t seem to let go of it.
Trouble is, relying on beauty as a guide to new laws of nature is not working.
Since the 1980s, dozens of experiments looked for evidence of unified forces and supersymmetric particles, and other particles invented to beautify the Standard Model. Physicists have conjectured hundreds of hypothetical particles, from “gluinos” and “wimps” to “branons” and “cuscutons,” each of which they invented to remedy a perceived lack of beauty in the existing theories. These particles are supposed to aid beauty, for example, by increasing the amount of symmetries, by unifying forces, or by explaining why certain numbers are small. Unfortunately, not a single one of those particles has ever been seen. Measurements have merely confirmed the Standard Model over and over again. And a theory of everything, if it exists, is as elusive today as it was in the 1970s. The Large Hadron Collider is only the most recent in a long series of searches that failed to confirm those beauty-based predictions.
These decades of failure show that postulating new laws of nature just because they are beautiful according to human standards is not a good way to put forward scientific hypotheses. It’s not the first time this has happened. Historical precedents are not difficult to find. Relying on beauty did not work for Kepler’s Platonic solids, it did not work for Einstein’s idea of an eternally unchanging universe, and it did not work for the oh-so-pretty idea, popular at the end of the 19th century, that atoms are knots in an invisible ether. All of these theories were once considered beautiful, but are today known to be wrong. Physicists have repeatedly told me about beautiful ideas that didn’t turn out to be beautiful at all. Such hindsight is not evidence that arguments from beauty work, but rather that our perception of beauty changes over time.
Physicists must, first and foremost, learn from their failed predictions. So far, they have not.
That beauty is subjective is hardly a breakthrough insight, but physicists are slow to learn the lesson—and that has consequences. Experiments that test ill-motivated hypotheses are at high risk to only find null results; i.e., to confirm the existing theories and not see evidence of new effects. This is what has happened in the foundations of physics for 40 years now. And with the new LHC results, it happened once again.
The data analyzed so far shows no evidence for supersymmetric particles, extra dimensions, or any other physics that would not be compatible with the Standard Model. In the past two years, particle physicists were excited about an anomaly in the interaction rates of different leptons. The Standard Model predicts these rates should be identical, but the data demonstrates a slight difference. This “lepton anomaly” has persisted in the new data, but—against particle physicists’ hopes—it did not increase in significance, is hence not a sign for new particles. The LHC collaborations succeeded in measuring the violation of symmetry in the decay of composite particles called “D-mesons,” but the measured effect is, once again, consistent with the Standard Model. The data stubbornly repeat: Nothing new to see here.
Of course it’s possible there is something to find in the data yet to be analyzed. But at this point we already know that all previously made predictions for new physics were wrong, meaning that there is now no reason to expect anything new to appear.
Yes, null results—like the recent LHC measurements—are also results. They rule out some hypotheses. But null results are not very useful results if you want to develop a new theory. A null-result says: “Let’s not go this way.” A result says: “Let’s go that way.” If there are many ways to go, discarding some of them does not help much.
To find the way forward in the foundations of physics, we need results, not null-results. When testing new hypotheses takes decades of construction time and billions of dollars, we have to be careful what to invest in. Experiments have become too costly to rely on serendipitous discoveries. Beauty-based methods have historically not worked. They still don’t work. It’s time that physicists take note.
And it’s not like the lack of beauty is the only problem with the current theories in the foundations of physics. There are good reasons to think physics is not done. The Standard Model cannot be the last word, notably because it does not contain gravity and fails to account for the masses of neutrinos. It also describes neither dark matter nor dark energy, which are necessary to explain galactic structures.
So, clearly, the foundations of physics have problems that require answers. Physicists should focus on those. And we currently have no reason to think that colliding particles at the next higher energies will help solve any of the existing problems. New effects may not appear until energies are a billion times higher than what even the next larger collider could probe. To make progress, then, physicists must, first and foremost, learn from their failed predictions.
So far, they have not. In 2016, the particle physicists Howard Baer, Vernon Barger, and Jenny List wrote an essay for Scientific American arguing that we need a larger particle collider to “save physics.” The reason? A theory the authors had proposed themselves, that is natural (beautiful!) in a specific way, predicts such a larger collider should see new particles. This March, Kane, a particle physicist, used similar beauty-based arguments in an essay for Physics Today. And a recent comment in Nature Reviews Physics about a big, new particle collider planned in Japan once again drew on the same motivations from naturalness that have already not worked for the LHC. Even the particle physicists who have admitted their predictions failed do not want to give up beauty-based hypotheses. Instead, they have argued we need more experiments to test just how wrong they are.
Will this latest round of null-results finally convince particle physicists that they need new methods of theory-development? I certainly hope so.
As an ex-particle physicist myself, I understand very well the desire to have an all-encompassing theory for the structure of matter. I can also relate to the appeal of theories such a supersymmetry or string theory. And, yes, I quite like the idea that we live in one of infinitely many universes that together make up the “multiverse.” But, as the latest LHC results drive home once again, the laws of nature care heartily little about what humans find beautiful.
Sabine Hossenfelder is the author of Lost in Math: How Beauty Leads Physics Astray. She is a research fellow at the Frankfurt Institute for Advanced Studies where she works on physics beyond the Standard Model, phenomenological quantum gravity, and modifications of general relativity.
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