In which Hossenfelder worries about the state of theoretical particle physics, but also trashes Karl Popper. I try to show that Popper could help her out.
Despite its title, the book is not really about math. It is about how the lure of a natural mathematical harmony and elegance – “beauty,” for short – dominates the agenda of theoretical particle physics, and questions whether this is a good thing and what it means for the philosophy and practice of science. The discipline involved is “foundational” physics, meaning the branch of science that it deals with the very most basic constituents of the universe – the entities, forces and fields that make up everything else. The book focuses on how the conceptual ideal of beauty permeates and shapes the thinking of the theoreticians. However, this is no starry-eyed ode to the wonders of science; the attractions of beauty are not always a good thing, says the author, Sabine Hossenfelder, a theoretical physicist herself. Her book presents valuable insights into the way theoretical science works, even as she deftly assists non-physicists like me in surfing over the mind-bending concepts and incomprehensible math to get to the matters that trouble her. Finally, she convinces us that these issues influence society and science policy (If you’d like a sample, Hossenfelder had a recent Opinion piece in New York Times that outlines her views: https://www.nytimes.com/2019/01/23/opinion/particle-physics-large-hadron-collider.html.)
Hossefelder is brilliant, sardonic, clever, funny, tough-minded, and principled. She is also a disillusioned idealist who’s worked at times in the gig-economy of science: scrambling for grants and temporary positions, while often questioning her own motivations. At times her book is strangely poignant. Lost in Math is structured around a series of interviews with luminaries in her field and, while posing hard questions to her colleagues, she digresses into highly informative asides that make for an excellent, reasonably accessible summary of the big ideas in modern physics. However, if you haven’t recently read at least a pop version of the weird worlds of quantum mechanics, the General Theory of Relativity, and the Standard Model of particle physics, you might like to brush up. (Carlo Rovelli has a helpful little book, Seven Brief Lessons on Physics, that is short, only 88 pages and readable. I’ll review it elsewhere. I thank Gerard Kiernan for calling my attention to both Hossenfelder’s and Rovelli’s books.) In any case, not to worry, you don’t have to master the theories to feel Hossenfelder’s angst and understand her concerns.
Theoretical particle physics is unlike other kinds of science in both obvious and non-obvious ways. Obviously, to do it you’ve got to be facile with highly abstract math and complex concepts, and be comfortable in a competitive environment of ultra-smart physics types. Less obviously, perhaps, you’ve got to embrace the prospect of spending your life working on questions to which you will, quite probably, never know the answers (or, in fact, know whether they are “the right questions,” to borrow from Richard Feynman). Beyond the personnel and personal issues, however, theoretical physics works in ways that are opposite to those in which much of science – e.g. biology, neuroscience – works. In more familiar fields, you do experiments or make observations which you try to understand by constructing and testing hypotheses experimentally. Lots of text books tell you that that, more or less, is how science works. But that is not at all how modern theoretical particle physics works, according to Hossenfelder.
To put her discussion into a context, we need at least a crude sense of the Standard Model of particle physics (she doesn’t capitalize it but many people do) that is at the heart of theoretical physics. The Standard Model is the most precise and successful big theory of anything that has ever been created. It can account for the existence and properties of much of the matter (including, atoms, protons, neutrons, etc.) and energy that we know about (there is a lot – Dark Matter, Dark Energy – that we don’t know much about). To do this the Model incorporates 25 fundamentally irreducible “particles” and the fields (think magnetic field) that support them and their interactions. Particles are not actually tiny, tiny, tiny billiard balls, but we can think of them that way. The main particles are electrons, photons, quarks, and gluons (things that “glue” quarks together). Together this group plus the Higgs boson are building blocks of nature as we know it. The development of the Standard Model was a group effort involving many scientists that progressed through the latter part of the 20th century and was accompanied by a number of Nobel Prizes. The Standard Model has been subjected to, and passed, numerous extraordinarily stringent experimental tests, with its most famous recent triumph being the correct prediction of the Higgs boson (a boson is a kind of particle) that has gotten so much press and that was finally detected at the Large Hadron Collider (LHC) in Europe.
Pretty snazzy!, you might think. Boy, those theoretical particle physicists must be a happy group of people who are justifiably proud of their amazing achievement! Well, yes and no. Through her interviews, Hossenfelder documents a great deal of dis-satisfacton, confusion, and downright discouragement among the theoreticians about the state of their field. The Standard Model is known to be incomplete (besides Dark Matter and Energy, it also leaves out gravity) but, more importantly, almost to a person, these advanced thinkers are repelled by its “ugliness.” Being empirically accurate is not nearly enough; they want their theories to be beautiful as well. This is not whimsy, however. The desire for beauty reflects a deep philosophical and psychological longing coupled with a conviction of how nature must be organized.
Physicists find the Standard Model ugly because many of the detailed properties of nature that it predicts e.g., particle masses – do not always emerge gracefully and organically from prior laws or principles of nature. Instead, their properties are postulated in order to enable the theory to account for experimental observations. The properties are “fine-tuned,” tailored to the theory in an ad hoc, artificial way; they are not “natural” and physicists, being physicists, have even quantified what they mean by “natural”. The key point is that unhappiness with the Standard Model stems not so much from its explanatory shortcomings, but from a non-scientific intuition, or esthetic sensibility, if you like – that it evokes. (Note this is not to say that all intuition is bad; we do not understand where any ideas come from, so attributing the orgins of scientific insights to intuition is perfectly reasonable. The larger question is whether we ought to allow major scientific programs to be guided solely by it.) Most physicists are convinced that things should fit together and make sense. Sub-atomic pearticles shouldn’t have just any old massess, but ones that can be understood; you shouldn’t just have to plug in a number because it will make the equations seem more rational, and the theory shouldn’t have precise, bizarrely large or small numbers cropping up in various places. If it’s the true theory, the numbers will be small, not far from 1 and easy to account for. And because the Standard Model is not like that theoreticians think it is ugly.
In attempting to eliminate the perceived ugliness, theoreticians have proposed many beautiful, rich, mathematically-cohesive alternatives. String Theory and Supersymmetry are two of the most prominent and promising candidates for the rescue effort. They are elaborate intellectual creations that were expected to shore up the Standard Model or replace it with something better. Unfortunately, early hopes for help from these quarterst are fading, threatened by the grim reality that decades of sophisticated experiments have left String Theory and Supersymmetry without direct experimental support. The predictions that these alternative theories make, or at least circumscribe, have not panned out experimentally. For example, it had been confidently predicted – significant monetary bets made – that the unprecedented energies that the LHC used to search for the Higgs boson, would turn up evidence for Supersymmetry. Finding the Higgs boson confirmed a major prediction of the Standard Model but, because the experiments did not point the way to new physics, the Model was, if anything, further “uglified” thereby. (The absence of predicted “super-partner” particles probably explains the curious lack of excitment shown by the theoreticians in the documentary movie about the discovery of the Higgs boson, Particle Fever. As Hossenfelder explains, for them, finding the Higgs “and nothing else” was the “nightmare scenario” that many of them had feared.) Thus we have a central conundrum of modern theoretical physics: despite being wildly successful in practice, there is an urgency to improve it that is being propelled by an urge to make it more beautiful. Theorists rationalize their quest for beauty by pointing to the ground-breaking advances it has led to in the past. Hossenfelder warns that, as the ad tag-line goes, “past performance is no guarantee of future success.”
Two less-lofty problems also deserve attention: 1) theory development in physics is heavily constrained by the requirement for compatibility with existing data and well-established theory, therefore, 2) it is very expensive and difficult to test theories. Not only do tight constraints make creating consistent theories exceedingly difficult, but the minute physical dimensions of the entities they postulate mean that enormous, expensive machinery is needed to test them. The LHC, for example, is a multi-billion dollar project involving many thousands of physicists, large physical space, and resources to match. And the latest experiments imply that the LHC is not nearly powerful enough to probe the foundations of physics at the next level.
Taken together, these intellectual and practical problems lead to a view of science where journals fill with detailed theories that are unsupported by new experimental data, in sharp contrast to the case in many scientific fields, such as the life sciences, where testing hypotheses is relatively easy and cheap, and comprehensive quantitative theories so far non-existent. As you’d anticipate, the unique demands of theoretical physics leads to unique challenges.
Let’s assume that we have a group of theories that have all cleared the high intellectual bars – they can all potentially explain the existing data and are compatible with General Relativity and quantum mechanics. They differ in the assumptions and predictions that they make and therefore generally in the kinds of experiments required to test them. The question becomes how to decide which of them is(are) worth testing; the most likely to pay off with important new results? The answer in the judgment of many physicists is by now familiar: we should look for an optimal combination of “beauty,” “naturalness,” “elegance” to guide theory selection. Hossenfelder demurs: all such opinions rest on unproven assumptions, and all are shaped by the peculiarities of the human mind. We are instintively biased and it demands special effort to see things objectively. The thought that physics, the “Queen of the Sciences,” would based on psychology, not to say poetry, causes the itch that Hossenfelder scratches throughout her book.
She makes a compelling case that a troubling state of affairs exists but, maybe unsurprisingly, does not have an equally compelling alternative to offer. Nature might, she admits, be truly “ugly,” i.e., it could be a stark, unglamorous fact that, in our universe, the Standard Model parameters take on the values they do “just because,” e.g., just because if they didn’t, human beings wouldn’t be here to wonder why This is a form of “anthropic” argument that some physicists buy into (David Deutsch, for one, doesn’t buy into it; see The Beginnings of Infinity: Explanations that Transform the World,). Indeed, one of Hossenfelder’s interviewees is comfortable with the thought of theoretical ugliness, although the author herself seems unhappy with it.
Mainly, she argues that the dream of improving the Standard Model by making it more beautiful has distracted physicists from other, more worthy projects, at a cost to physics and society. She cites a few of these more pressing problems, but they are also quite deep and she really doesn’t suggest how physicists should go about solving them. She does give a couple of stunning examples of apparently wasted effort. At one point in the gargantuan mass of data collected at the LHC an unanticipated blip (the “diphoton anomaly”) cropped up. Within 8 months “more than 500 papers” had appeared in physics journals “explaining” it. The punch line here is that shortly thereafter the mysterious blip disappeared from the data, apparently a transient statistical fluke. Hossenfelder also reports that, as of 2014, there were “193 models for the early universe” (most of which, remember, will never be tested) and concludes that “this is more than enough evidence that current quality standards are no longer useful to assess our theories.” Hossenfelder let’s us draw our own conclusions about how useful this sort of science is and reflect on the prospect (succintly put by J. Silk and G. Ellis), that the lines between science, mathematics, and philosophy have become so blurred that we no longer know where we are. Indeed, we might ask, if a theory is never tested – is it still science?
In summary, Lost in Math succeeds on a number of levels – it takes us behind the scenes and the glitzy, awe-struck headlines to reveal the nitty-gritty conflicts and limitations of our most ambitious physics projects. It introduces quirky characters and complex ideas that are new and fascinating to many of us. It encourages us to think seriously about the nature of scientific facts and their implications for both social and science policy. And it accomplishes these goals and more in an engaging and engrossing way. I enjoyed reading Lost in Math and recommend it.
My one substantive complaint is that Hossenfelder’s coverage of a fundamental aspect of scientific thinking is lamentably superficial, which occasionally leaves her in an awkward and inconsistent intellectual position. I am referring to her views on “the scientific method,” which she evidently approves of but doesn’t deal with in any depth. This omission renders her account of scientific reasoning confusing at best and inconsistent at worst. Thus when, at a conference on philosophy and physics, she hears that philosophers consider Karl Popper’s championing of the principle of “falsification” of hypotheses to be “outdated,” she is “glad to hear it” because “”nobody in science could have used [it] other than as a rhetorical device.” Since most accounts of the scientific method include some version of falsification and since she’s generally in favor of the scientific method, this breezy dismissal of Popper creates a gap in her argument. She tries to compensate: scientists do not, she says, seek to “falsify” theories, but rather to “implausify” them, by which she means that (when confronted with contradictory data) a “continuously adapted theory” becomes sufficiently unlikely that “eventually practioners lose interest.” And why do they lose interest? Because the theory becomes “increasingly difficult and arcane – not to say ugly.” I think she’s being disingenuous. For one thing, a recurrent theme of the book is that some theories, e.g. Supersymmetry, have made predictions that, for decades, have failed to garner any experimental support, and it’s clear that she’s done more than “lose interest” in them.
Why not simply say that theories that make predictions that are repeatedly falsified are themselves false? This is where things become mushy: as noted earlier, a theory of, e.g., Supersymmetry may circumscribe, but not exactly specify, the precise masses of the super-partner particles that it postulates. Rather, it allows a range of values and so, when an experiment fails to detect the postulated particles, the theory can be adjusted to predict another (presently untestable) range of values and the theory thus eludes falsification. (Critics recognize this as the same strategy that Ptolemaic astronomers pursued when anomalies in planetary orbits were found: they concocted another “epicyle” to fix it.) Hence, in view of the effectively limitless imagination of theoretical physicists, one reason for avoiding the language of falsification is that previous data do not constrain the theories enough to permit a firm conclusion about it to be drawn. The fundamental weakness here is with theories that are immune to falsification, not with the concept of falsification itself. Hossenfelder seems to disagree. We’re stuck with an implausible, though not falsified theory, she says.
But that’s not exactly what her fellow physicists seem to think. Consider, for instance, the physicist, Gordon Kane, who had incorrectly predicted that evidence for Supersymmetry would show up in the initial run of LHC experiments. When Hossenfelder asks him what he’ll conclude if the evidence doesn’t appear in the second, more advanced run, he answers, “Then the model [of Supersymmetry that he’s proposed] is wrong” and we interpret “wrong” to mean “false.” And it’s not just Kane. In an Appendix, Hossenfelder herself recommends, that to help keep science honest and vital, scientists “should build a culture of criticism” where they freely and publicly criticize each others’ ideas because “Killing ideas is a necessary part of science.” But a dead idea is a false idea.
A related difficulty lies in the murkiness of the notion of a “theory.” Does it refer to one specific formulation of an idea, or a whole class of similar ideas? Is Supersymmetry a particular theory or a general concept (e.g., “each known sub-atomic particle has a super-partner with analogous properties but a very different mass”) with various possible instantiations? This is important because, if Supersymmetry is a broad general class of explanations then Hossenfelder’s “implausification” argument makes sense; you can never test and definitively falsify it. Still, why not consider a specific instance of a supersymmetric theory falsified if its predicted super-partners do not show up experimentally as predicted? In one of her recommendations, Hossenfelder reminds us that nature is the final arbiter of the rightness of theories. Why balk at saying that a theory is just wrong?
It is unfortunate that she’s relied on what philosophers say about Karl Popper’s philosophy of science, rather than studying it herself. She, quite rightly I believe, chides scientists for being blind to their own biases, but is she overlooking the likelihood that philosophers have their own axes to grind and grind them consciously and unconsciously? Would it be surprising to learn that philosophers are also motivated by a need to distinguish themselves from previous thinkers? In any event, Hossenfelder apparently agrees that, because absolute falsification is impossible, falsification is therefore a worthless principle, only used as a rhetorical device. But this conclusion is demonstrably incorrect: biologists, neuroscientists, psychologists, among others, use the falsification standard all the time. Moreover, for a full appreciation of science, it is good to contemplate the role that falsification plays in science. As Popper says, falsification can never be final, therefore our knowledge of nature – what we believe is false as well as what we believe is true – will always be uncertain on some level and to some extent. Tests that you thought were unarguably decisive might not be for all kinds of technical or other reasons: future experiments might overturn an accepted fact, an utterly unforseen discovery (Dark Matter, Dark Energy!) might suddenly appear, etc. Popper envisions science as a dynamic back-and-forth between observation and explanation; an endless process of trial and error that depends on conjecture, criticism, and empirical testing to evaluate the explanations that it creates. We reject the falsified ones, those that do not stand up to testing and, provisionally, always provisionally, accept the unfalsified ones as the best available knowledge that we have. We act on the basis of our best information. Scientists need to keep an open mind. What’s not to like?
Evidently the typical professional philosopher of science today is baffled by Popper’s reasoning on this point. To be fair, I doubt that Hossenfelder really sides with them. In fact, in a number of places, Hossenfelder’s views align pretty well with Popper’s. When she makes suggestions to help theoretical physics turn away from beauty and get back on the right track, she states that “the only way to find out which theory is correct is to check whether it describes nature.” We can infer that a theory that does not describe nature is incorrect. Thus we might understand her to say that science is a process in which we check theories empirically, shunning the incorrect ones while seeking and preferring the correct ones. Just as Karl Popper recommended.
Lost in Math: How Beauty Leads Physics Astray, by Sabine Hossenfelder (New York: Basic Books; 2018)
- Bradley Alger, March 2019