I approached Lost in Math with trepidation. Its subtitle, “How Beauty Leads Physics Astray,” annoyed me because, like Albert Einstein, Paul Dirac, and many others, I have always regarded elegance, simplicity, and beauty as essential criteria for physical laws. The preface begins even more disturbingly:

They were so sure, they bet billions on it. For decades physicists told us they knew where the next discoveries were waiting. They built accelerators, shot satellites into space, and planted detectors in underground mines. … But where physicists expected a breakthrough, the ground wouldn’t give. The experiments didn’t reveal anything new.

These imprudent words demand rebuttal, but they do not characterize the remainder of the book. Sabine Hossenfelder shows even less understanding of her forsaken discipline in a recent essay for The New York Times. “Is a new $10 billion particle collider worth the money?” she asks. “If particle physicists have only guesses, maybe we should wait until they have better reasons for why a larger collider might find something new.” The purpose of costly particle colliders is not just to test theorists’ sometimes idle speculations. It is to look where no one has looked before, to explore as best we can the workings of the world we are born into. CERN’s Large Hadron Collider (LHC) has done just this. It has discovered that our Standard Model correctly describes the microverse at the highest energies yet available. Our European and Chinese colleagues now recognize—as proponents of the abandoned American Superconducting Super Collider (SSC) did twenty-five years ago—that a far more powerful instrument is needed, should we choose to learn nature’s secrets.

Reading on, I often sympathized with the author’s views about the worrisome state of what she calls the foundational sciences. Too many of our colleagues, she believes, in particle physics and cosmology, find truth and beauty nearly synonymous. A beautiful theory must be true, a true theory beautiful. They attack, those colleagues, the very nature of science with claims that theories can be meaningful even if they predict nothing at all and cannot be refuted by any conceivable experiment or observation. Such theories may be assessed only by nonempirical arguments. Aesthetic principles, Hossenfelder argues, have become adjuncts to model builders, and what was once useful is now necessary. She is concerned that so many bright stars in mathematical physics are obsessed by superstrings and multiverses, things far too tiny or too huge to have observable consequences. “[T]heoretical physics,” she writes, quoting an article by George Ellis and Joe Silk published by Nature in 2014, “risks becoming a no-man’s-land between mathematics, physics and philosophy that does not truly meet the requirements of any.” There is truth in these complaints as there is in the book’s concluding words: “The next breakthrough in physics will occur in this century. It will be beautiful.”

Advances in high-energy physics and cosmology do not come cheaply. Hossenfelder deplores the billions spent on research that revealed no surprises, but neglects to mention the Laser Interferometer Gravitational-Wave Observatory (LIGO) and its dramatic discoveries. We long knew that general relativity implies the existence of waves whose direct detection require instruments with exquisite sensitivity. In its biggest gamble ever, the National Science Foundation funded LIGO in 1994. By 2015, and at a cost of over a billion dollars, the advanced LIGO observatory was deployed. On September 14, 2015, a faint burst of gravitational waves was heard from the collapse and merger of a binary system of two black holes. Additional events of this kind were heard soon afterward.

Hossenfelder may believe that LIGO just confirmed what nobody doubted. It did far more than that. The data revealed the existence of stellar black holes with surprisingly large mass and unknown origin. Such objects could comprise part or all of the dark matter of the universe. A few months later, a burst of gravitational waves was heard from the collapse of a system of two neutron stars, and was seen and studied by both optical and X-ray telescopes. The results strongly supported one of two contending theories of heavy-element creation. LIGO has initiated the exciting new science of gravitational wave astronomy.

Satellites shot into space enabled the conversion of cosmology from a merely speculative discipline to a precise quantitative science. Satellites like COBE (the Cosmic Background Explorer), Planck, and WMAP (the Wilkinson Microwave Anisotropy Probe) enabled us to learn that our universe comprises 68% dark energy, 27% dark matter, and at most 5% ordinary matter. It is nearly flat, and 13.82 billion years old. Without these satellites, how could we have discovered the tiny temperature fluctuations of the newborn universe?

Sensitive detectors deep underground helped solve the solar neutrino problem. They discovered atmospheric neutrino oscillations, revealed that neutrinos have mass, measured their properties, and observed them coming from a supernova. Many other detectors—under land, water, and ice, both planned and existing—continue to search for dark matter interactions, proton decay, lepton-number violations, and extragalactic neutrino sources. They are or will become frontline facilities for research in particle physics, astrophysics, and cosmology.

Accelerators and colliders enabled physicists to probe the inner workings of matter. Without them, there would be no triumphant Standard Model, offering a complete, consistent, and correct description of all known elementary particles. High-energy physics has been quiescent, yet far larger and more powerful colliders are planned both in China and Europe. Surprising discoveries are almost certain to follow.

Hossenfelder is an accomplished theoretical physicist whose own research focuses on quantum gravity, black holes, and large extra dimensions. Her book is an extended adjuration against the faith many physicists display in simplicity, naturalness, and elegance.

Lost in Math is the story of how aesthetic judgment drives contemporary research. It is my own story, a reflection on the use of what I have been taught. But it is also the story of many other physicists who struggle with the same tension: we believe the laws of physics are beautiful, but is not believing something a scientist must not do?

She is discomfited that little of the research she herself has done has been confirmed, but this is largely because she has chosen to work in fields whose theories do not yet yield observable consequences. As she notes, little of what anyone has done in recent decades has revealed an empirical failure of the Standard Model. Dozens of conferences, workshops, and summer schools are devoted to physics beyond the Standard Model. New physics might have emerged, but did not. Rumors of anomalies or forbidden processes were squelched. The apparent discovery of a new particle decaying into two photons caused a stir among physicists. Since 2016, theorists have written at least 240 papers about the rumored particle. “But, this could be it, I think,” Hossenfelder writes, “the first step on the way to a more fundamental law of nature.”

The anomaly was not present in the most recent data and is now regarded as a mere statistical fluke.

Despite efforts by thousands of researchers at the LHC, no solid evidence has appeared for any elaboration of the Standard Model—neither supersymmetry, technicolor, nor extra dimensions of space-time. No addition to our particle bestiary has shown up, whether superstring inspired, beautiful, or downright ugly. Not even the anticipated luminosity upgrade of the LHC will enable it to provide decisive evidence for new physics: high luminosity is no substitute for high energy. We may be unwilling, as Hossenfelder remarks, “to stay motivated through all the null results.” These failures are due less to an excessive faith in beauty and more to an excessive faith in politics.

During the early 1980s, extensive discussions among high-energy physicists identified what was needed to push beyond the Standard Model: a proton-proton collider with a forty teraelectron volt (TeV) center-of-mass energy. In 1993, with its eighty-seven–kilometer circular tunnel completed, and billions of dollars already spent, Congress aborted the SSC. Thus ended America’s half century of dominance in particle physics. CERN, the European particle physics consortium, filled the gap as best it could. Their existing twenty-seven-kilometer tunnel holding its Large Electron–Positron Collider (LEP) would be recycled to house a proton–proton collider. A third the size of the SSC, the LHC had a third of its energy. The hope that more collisions could make up for less energy was only partly fulfilled. Nonetheless, physicists at the LHC still managed to find the Higgs boson in 2012. The last missing piece had been placed in the Standard Model, but no indication of anything more has been found.

Our understanding of the microworld has advanced slowly since the golden age of the 1960s and 70s. Take 1964 as an example, the year quarks were invented, quark color introduced, and charmed quarks proposed. Several groups of theorists described the mechanism that breaks electroweak symmetry. Experimenters were not left out. The Ω– particle, whose existence and properties Murray Gell-Mann had predicted, was discovered at Brookhaven National Lab, and the entirely unexpected violation of CP symmetry was established at Princeton. The modern age of cosmology also began with the discovery of the cosmic microwave radiation. In the first nineteen years of the twenty-first century, physicists have made just two discoveries of comparable significance: the detection of the Higgs boson, and gravitational waves.

Lost in Math is a collection of interviews with theoretical physicists, a few experimenters, a philosopher, and a mathematician. It is fascinating to compare the remarks of many of my colleagues in science, but sometimes difficult to disentangle their opinions from those of the author. Hossenfelder often refers to her interlocutors by their first names: Frank for Frank Wilczek, Nima for Nima Arkani-Hamed, and Richard for Richard Dawid. This presumption does not extend to Steven Weinberg, Alain Connes, or Gerard ’t Hooft.

Beauty is a recurrent theme in Lost in Math, as it is in the history of physics. Hossenfelder quotes, among others, Hermann Weyl, Henri Poincaré, Werner Heisenberg, and Dirac as advocates of mathematical beauty as a guide to knowledge. “[W]hen we read about new theories,” ’t Hooft remarks, “and we see how beautiful and simple they are, then they have a big advantage. We believe such theories have much more chance to be successful.” Wilczek agrees: “[T]here is no more promising guide [to Nature’s workings] than beauty itself.”

Einstein, Hossenfelder recalls, thought rigidity a desirable attribute of physical laws:

Nature is constituted so that it is possible to lay down such strongly determined laws that within these laws only rationally, completely determined constants occur (not constants, therefore, that could be changed without completely destroying the theory).

Many of today’s theorists express much the same sentiment. “[T]he beauty we seek in physical theories,” Weinberg observes, “is a beauty of rigidity. We would like theories that to the greatest extent possible could not be varied without leading to impossibilities.” This is a view that Arkani-Hamed endorses: “[B]oth relativity and quantum mechanics shockingly—shockingly!—constrain what you can do. Rigidity and inevitability is by far the most important thing. You can call it whatever you want, but for me it’s a stand-in for beauty.” The Standard Model displays no such rigidity. It involves terms for about two dozen particle masses, coupling constants, and mixing parameters; these are not rationally determined, but must be experimentally evaluated. This is why the many scientists Hossenfelder quotes find the Standard Model contrived or ugly. “I yet have to find someone,” she writes, “who actually likes the standard model.” I do. I like it very much. I remember times when we knew practically nothing about elementary particles and their strong and weak forces.

Julius Wess and Bruno Zumino discovered supersymmetry in 1974. Conventional particle symmetries, like those of the tripartite group of the Standard Model, commute with the Poincaré group. They link together different particles with the same spin, such as quarks with quarks or electrons with neutrinos. Unified theories based on simple groups like SU(5) link quarks with leptons, but no conventional symmetry can interweave fermions with bosons. Supersymmetric transformations are not so constrained. These ingenious and beautiful symmetries mix together particles with different spins. In a supersymmetric theory, every observed boson has a fermionic counterpart and every observed fermion a bosonic counterpart. The photon’s superpartner is the spin-1/2 photino; the quark’s partner is a spinless squark. The symmetry requires every observed particle to have the same mass as its unobserved superpartner. No such superpartners exist in nature. Supersymmetry cannot be an exact or even an approximate symmetry of nature.

If supersymmetry is to play any role in elementary particle physics, it must be so badly broken that every superpartner is far more massive than its observed counterpart. The simplest realistic theory is the minimal supersymmetric model (MSSM). It was introduced to solve a worrisome problem. In the Standard Model, the Higgs boson’s mass experiences quadratically divergent radiative corrections, which would make it far too massive. This could be dealt with by means of arbitrary and undeniably ugly fine tuning. Supersymmetry, on the other hand, provides an almost miraculous cancellation of the radiative corrections. This serves to stabilize the Higgs mass.

And more. The least massive supersymmetric particles are stable. Their expected mass and computed cross section are just right for them to serve as the weakly interacting massive particles (WIMPs) that make up the dark matter of the universe. Supersymmetry can also remedy two failures of theories unifying the strong, weak, and electromagnetic forces: namely that the three different coupling constants do not converge at a conjectured unification scale, and the proton does not decay at its predicted rate. If the supersymmetry-breaking scale were less than 1,000 GeV, both problems could be solved. Supersymmetry could more than achieve Wilczek’s criterion for beauty: “when you introduce a concept to explain one thing and you find that it also explains something else.”

Searches for supersymmetric particles began about forty years ago and continued at ever greater energies. Hundreds of experiments have searched for supersymmetry or its effects. No trace has been found. Naturalness arguments suggest that the scale of supersymmetry breaking should be similar to the scale of electroweak symmetry breaking. But, as Hossenfelder notes, “naturalness arguments turned out to be wrong [leaving] physicists at a loss for how to proceed. Their most trusted guide appears to have failed them.” The lack of empirical support for MSSM has engendered many mutations: next-to-minimal supersymmetry, split supersymmetry, or twisted, compact, or constrained supersymmetry. All this is to no avail. Supersymmetry was intended to explain the Higgs mass, proton decay, coupling constant convergence, and dark matter. The most recent data from the LHC indicates that supersymmetric particles, if they exist, are too heavy to perform any of their assigned tasks.

Supersymmetry, if present at all, is neither unique, natural, nor effective.

Hossenfelder cannot understand why so many theoretical and experimental physicists remain so enthralled by supersymmetry. “[I]t is hard to believe,” Jeff Forshaw remarks, “that supersymmetry does not play a role somewhere in nature.” Joseph Lykken and Maria Spiropulu agree: “[m]ost of the world’s particle physicists believe that supersymmetry must be true.” Ditto Michael Peskin, Gordon Kane, and David Gross.

How can supersymmetry possibly be regarded as beautiful? If it is to describe observed particle phenomena, it is obliged to encompass the whole of the Standard Model. If the Standard Model is ugly, supersymmetry is uglier yet, because it involves twice as many particles, half of them unseen, and consequently twice as many arbitrary parameters as the Standard Model, none of them rationally determined.

String theory demands the existence of supersymmetry. Yet the absence of observable supersymmetric phenomena at accessible energies cannot be taken as evidence against it. String theory sets no particular energy scale for its breakdown. This reflects the inconvenient truth that superstring theory cannot be falsified, but must be assessed by nonempirical methods. “If we accept a new philosophy that promotes selecting theories based on something other than facts,” Hossenfelder asks, “why stop at physics?”

[W]hether string theory really is the sought-after theory of quantum gravity and a unification of the standard model interactions, we still don’t know. … String theorists’ continuous adaptations to conflicting evidence has become so entertaining that many departments of physics keep a few string theorists around because the public likes to hear about their heroic attempts to explain everything.

She thinks physicists who depend on aesthetic principles are “collectively delusional”:

The more I try to understand my colleagues’ reliance on beauty, the less sense it makes to me. Mathematical rigidity I had to discard because it rests on the selection of a priori truths… Neither could I find a mathematical basis for simplicity, naturalness, or elegance, each of which in the end brought back subjective, human values. In using these criteria, I fear, we overstep the limits of science.

Here I strongly disagree. Beginning in the 1950s, physicists sought a higher symmetry group that could bring order to the many new particles being discovered. In 1961, Gell-Mann and Yuval Ne’eman found the scheme that works. The eightfold way, as Murray playfully called it, became a very useful framework. Sidney Coleman and I saw how the theory could be expressed far more elegantly in terms of 3 × 3 matrices. Our quest for beauty led us to our very own eponymous mass formula. Four years later, James Bjorken and I had an epiphany about quarks and leptons. How beautiful it would be if there were one more flavor of quark so that nature could have two doublets of quarks just as it had two doublets of leptons.

The charmed quark was born.

A touching section of Hossenfelder’s book consists of an extended conversation with Joseph Polchinski, the daring string theorist who proposed firewalls for black holes, D-branes for superstrings, and a plenitude of forever hidden universes, each with its own set of random physical laws. Polchinski, she judges, is “one of the most intellectually honest people I know, always willing to go with an argument regardless of whether he likes where it takes him.” Although largely responsible for the anthropic interpretation of the cosmological constant, Polchinski “felt like it was taking away one of our last great clues as to the basic nature of fundamental physics, because things we had hoped to calculate now became random.” At the time of Hossenfelder’s interview, Polchinski was already suffering from the cancer which would prematurely take his life.

The sixth chapter of Lost in Math, is a record of her interview with Anton Zeilinger and deals with the foundations of quantum theory and long-distance coherence experiments. It is here that Hossenfelder expresses her discontent with the idea that “unobserved particles can be in two different states at once,” and that upon measurement, wave functions either collapse instantaneously or spin off alternative worlds. Weinberg assures her that “there is no interpretation of quantum mechanics that does not have serious flaws.” I became confused as the chapter continued with its attempt to set psi-ontic views of quantum mechanics, like Bohm’s pilot-wave theory, against psi-epistic views, like the Copenhagen interpretation or QBism (quantum Bayesianism). I could not decide into which category Hugh Everett’s many-worlds view belongs. The debate between followers of different interpretations has proceeded inconclusively since quantum mechanics was born almost a century ago. Hossenfelder barely mentions the seminal work of John Bell, one of the bright spots in a dismal discipline. I found this portion of Lost in Math to be tedious and unrewarding.

Studies of the nature of measurement in nonrelativistic quantum mechanics are unlikely to advance our understanding of particles or the cosmos. Of such endeavors, Jeremy Bernstein has written, “Ordinary quantum mechanics cannot be made compatible with relativity and attempts to do so are misguided.” Gell-Mann and James Hartle conclude a series of a dozen papers with:

[The] resolution of the problems of interpretation presented by quantum mechanics is not to be accomplished by further intense scrutiny of the subject as it applies to reproducible laboratory situations, but rather through an examination of the origin of the universe and its subsequent history.

Lost in Math contains critical discussions of many other aspects of foundational science. Hossenfelder’s discontent with supersymmetry, string theory, and the multiverse has persuaded her to entertain Xiao-Gang Wen’s finite qubit theory, Garrett Lisi’s E8 model, and Connes’s vision of spectral geometry. Physicists are not alone. Economists too, she observes, have also become lost in math. Hossenfelder’s humor, honesty, and discontent should be appreciated both by students of physics and the foundational sciences.