I just finished Lost In Math: How Beauty Leads Physics Astray by Sabine Hossenfelder. Here’s my review.
tl;dr: If you would enjoy a readable case study of how an entire field of science can (arguably) go off the rails, this is the book for you.
Sabine Hossenfelder works in fundamental physics, currently at the Frankfurt Institute for Advanced Studies, and writes the popular physics blog Backreaction. Like her colleagues, she wants to identify the basic building blocks of the universe, and the rules they play by. Like her colleagues, she’s puzzled and intrigued by empirical phenomena we can’t explain, such as the apparent existence of dark matter and dark energy. Like her colleagues, she’s bothered by conceptual conundrums, such as the relationship between quantum mechanics and gravity. But unlike her colleagues, she thinks the entire field is trying to explain those phenomena and resolve those conundrums in the wrong way. Or, if not the wrong way, at least a way that we no longer have any good reason to think will work. If she were me, she’d have called her book Zombie Approaches To Physics: Research Strategies That Should Be Dead, But Aren’t.
As she establishes through a series of interviews with leading physicists (interspersed with her own commentary), physicists think that fundamental theory better than what we have now will be beautiful, for some very specific value of “beauty”. For instance, many physicists think the best fundamental theory will be “symmetrical”, won’t have any free parameters that need to be estimated from empirical data, and won’t contain any quantities many orders of magnitude smaller or larger than 1. Physicists think that beauty=truth for several reasons. Perhaps the most defensible is that assuming the existence of symmetries was a productive theory development strategy through much of the 20th century. It generated models that made testable predictions subsequently upheld by data. Perhaps the least defensible is the vague but widely-shared aesthetic sense that the laws of nature simply have to be beautiful, that any other possibility is just too awful to entertain. And there are others.
Sabine Hossenfelder ably demolishes every one of those reasons. In one of the best chapters, she points out that physicists and astronomers have always thought that natural laws must be beautiful–but they disagree on what “beauty” is, and over time they’ve repeatedly redefined it. And for every case in which making a “beautiful” assumption has led to progress, there’s another in which it’s retarded progress. For instance, there was a time when astronomers thought planetary orbits “had” to be circular, because God surely wouldn’t use something as ugly as an ellipse. This chapter reminded me of one of my favorite essays, John Maynard Smith’s “Too good to be true“. In another chapter, she shreds the idea that various Standard Model parameters represent “unlikely” coincidences that demand explanation. We can’t specify a probability distribution over possible universes (not even an “uninformative” one), so it simply makes no sense to characterize observed parameter values as “likely” or “unlikely”. And she documents how physicists have spent the past few decades moving the goalposts: tweaking their models so as to predict new particles and interactions that are always just out of reach of current experimental technology. Thereby motivating a need for new technology, which when produced duly rules out the hypothesized particles and interactions. Lather, rinse, repeat.
But it seems like there’s one more reason physicists refuse to give up on the idea that the fundamental theory must be beautiful: if they gave up on that idea, they’d be completely stumped. They’d have no clue how to proceed further, at least in the absence of any new empirical data that seems not to be forthcoming. As Lakatos was perhaps the first to show, scientists basically never give up on a theory or approach until a better alternative is available. Sabine Hossenfelder only raises this issue near the very end of the book, and the way she addresses it isn’t totally convincing. She argues that this refusal to give up on the search for beauty is a sign of cognitive biases, collective action problems, and bad incentives (e.g., incentives to use the same approaches as everyone else, so that you can publish papers and get grants). She has a point, but I don’t think that’s really at the root of it. It’s not just that scientists are nudged by “the system” into sticking with the same once-successful-but-now-failing research strategy. The root of it is that scientists never give up on any really important problem, and they will always prefer having some research strategy–even one that’s been failing them for decades–to having none at all. I could imagine a physicist granting every one of her criticisms and then continuing to pursue more or less the same research, because the only alternatives are to give up completely or grope around aimlessly. Indeed, that’s more or less what several of her interview subjects say. To which the obvious reply is to ask which is better: to grope around aimlessly in the dark and realize that you’re doing so, or grope around aimlessly in the dark but not realize you’re doing so because you mistakenly think you actually have a useful search strategy?
In the long run, I wonder a bit if fundamental physicists will be forced to give up on their current research strategy. I wonder if future generations of prospective graduate students, and future funding bodies, will “vote with their feet” and go into or support other fields rather than the stagnating field of fundamental physics. Especially since each new, more powerful particle collider costs many billions of dollars more than the last one. Sabine Hossenfelder doesn’t raise this possibility, but she certainly could have.
Hossenfelder’s style is well-suited to the subject. She’s a good explainer. She has a nice turn of phrase, especially when she’s puncturing some bit of lofty-sounding rhetoric. For instance, here she is on the dream of finding a single, ultimate, mathematically-inevitable law of nature:
Finally, everything would make sense: stars and planets, light and dark, life and death. We would know the reason for each and every happenstance, know that it could not have been any different, could not have been better, could not have been worse. We’d be on par with nature, able to look at the universe and say, “I understand.”
It’s the old dream of finding meaning in the seemingly meaningless. But it’s not just about making sense. Armed with this breakthrough, physicists would become the arbiters of truth…They would change the world. They would be heroes. And they’d finally be able to calculate the mass of the Higgs boson.
I love that deflationary last sentence. And here she is on the idea of an infinite multiverse:
In the multiverse of eternal inflation, with an infinite number of recurrences launched by random quantum fluctuations, anything that can happen will eventually happen. Eternal inflation therefore implies that there are universes in which the history of mankind plays out in any way that is compatible with the laws of nature. In some of them this will make sense to you.
I can’t believe what this once-venerable profession has become. Theoretical physicists used to explain what was observed. Now they try to explain why they can’t explain what was not observed. And they’re not even good at that.
And in passing asides scattered throughout the book, she’s brave and open enough to share her doubts as to whether she should even be writing it. On meeting Steven Weinberg, who asks if she’s the writer he’s supposed to meet, she writes:
Always keen on new opportunities to feel inadequate, I say yes, thinking I shouldn’t be here, I should be at my desk reading a paper, drafting a proposal, or at least writing a referee report. I shouldn’t psychoanalyze a community that neither needs nor wants therapy. And I shouldn’t pretend to be something I’m not.
I think that openness about her own self-doubt is what makes the book work. Her deflationary style would come off as arrogant from a completely self-confident author. There’s probably a lesson here for me.
The structure of the book is a bit bloggy, as befits a book by a blogger. There’s not a single linear narrative throughout the book, but there are some running themes to which Hossenfelder repeatedly returns.
As a blogger currently trying and failing to write his own book inspired by his blogging, I really admire Sabine Hossenfelder’s bravery and perseverance. Writing a book isn’t easy or risk-free. Especially when you don’t have a permanent position, and you’re basically telling all your colleagues that they’re Doing It Wrong. It’s one thing to say that on a blog, quite another to say it in a book from a major publisher.
The book is an interesting companion piece to How The Hippies Saved Physics. That book too is about contrarian physicists who thought their field had gone down the wrong path and needed deep rethinking. But Hossenfelder’s book is more convincing. How The Hippies Saved Physics is about contrarians who were frustrated that physicists weren’t working on certain problems. But their complaints didn’t cut much ice because the field was making rapid theoretical and empirical progress on other problems. Hossenfelder is writing a generation after that rapid progress stopped. The hippies didn’t save physics because at the time it didn’t need saving. Now it does (at least arguably).
I don’t know that the book has any specific lessons for ecology. Ecologists as a group tend not to care much if their models are beautiful. I mean, yes, ecological theoreticians do often value simplicity and elegance. But nobody makes a fetish of them. Nobody would insist that correct ecological theories have to be beautiful (would they?). And one of the good things about ecology being a rather ill-defined discipline with significant disagreement on seemingly-basic matters is that there’s no risk that ecologists will fall into the same trap fundamental physicists arguably have. If everybody disagrees about which research approaches are most promising, there’s no risk everybody will make the same wrong choice. But more broadly, I do think there is a lesson for ecologists (and all other scientists) here. It’s worth thinking critically about your “research strategies”–the partially-objective, partially-subjective ways in which you decide what questions to ask and how to go about answering them. Just because ecology is immune to the specific sort of crisis fundamental physics is having isn’t an argument for complacency. Because there’s more than one way for an entire scientific field to descend into crisis. Reading Lost In Math reinforced my conviction that it’s healthy mental exercise to contemplate the possibility that your entire field is f***ed and needs to go back to the drawing board. Research programs and even entire fields can indeed go off the rails, even if every individual researcher is smart and well-meaning (as physicists are). When a field goes off the rails, scientists’ usual methods for making progress break down and they need to become philosophers to find a way forward.
Every field of science needs some contrarians. Sabine Hossenfelder is an excellent one, and Lost In Math is an excellent book. I recommend it.
UPDATE: for other reviews, all of which are from actual physicists or mathematicians, and two of which are more negative than mine, see here, here, and here. Gotta say that part of the first review (which is the most negative and least substantive one) could be read as evidence for Hossenfelder’s claims…
This may be a bit tangential, but I’m curious what your thoughts are between physics and ecology in terms of progress. You suggest that (fundamental) physics has more of a streamlined nature, which plays some substantial role in its current crisis, and that ecology might evade this by being more conceptually fragmented (e.g. “ecology being a rather ill-defined discipline with significant disagreement on seemingly-basic matters”). How do we compare the two fields in terms of progress? It has always been easier for me to understand progress in pure mathematics or physics, but as I’ve moved into other areas of science, it has become more difficult to see concrete signposts of understanding we have gained. Any insights here?
I love when I can just link to an old post. It’s like having a backup slide that anticipates an audience question after a talk. 🙂
I enjoyed your review enough to order the book.
How about biodiversity as a fetish among ecologists? I just read this, “These new findings indicate that ecosystem scientists should shift away from treating biodiversity as an ASSUMED amplifier of key ecosystem services like carbon storage, and instead treat it as a subset of factors that influence such services…” (emphasis mine) from this
The idea that biodiversity must always be beneficial is popular among some in agriculture too.
I’m as guilty as the next ecologist of starting my BEF papers with a boilerplate, caveat-free paragraph saying that biodiversity is declining, and that’s bad because it’s bad for ecosystem function. You’re right that that boilerplate doesn’t really hold up if it’s taken seriously: https://dynamicecology.wordpress.com/2014/03/05/questioning-the-value-of-biodiversity/
Thanks for the links. I started following you after those were posted.
Jeremy, I haven’t read the book but I’m going to have to. But one of the bits you quoted seems to me to be the crux of where disciplines go wrong –
“Theoretical physicists used to explain what was observed.”
Every discipline will ultimately stray from a useful path if they don’t keep their eye on that ultimate criterion – that our primary job is to contribute to developing models of the world that explain the things we see. Whenever a discipline subordinates its ability to explain/predict observations to some other aim, it’s likely off the rails. Where I see ecology edging off the trail is that we ultimately don’t choose among our enormous variety of models by asking which one best explains our observations…most of then either drift into obscurity or rise to prominence for reasons I’m not sure of (although elegance and cleverness seem often to be important). We may not have deluded ourselves that that there is some more important criterion than the connection between models and observations but we do excuse ourselves when models do a bad job – the “we live in a complex world’ caveat. This may be true but it’s just another way of saying “we don’t understand the world very well”
In fairness to physicists, the problem–which is widely recognized, though Hossenfelder seems to take it more seriously than most–is lack of new data. The Large Hadron Collider hasn’t revealed any “new physics”.
Jeff, I am glad that you said this as an ecologist, because it is almost exactly what I would say as an agronomist taking a dive (admittedly, a shallow one) into ecology.
“Ecologists as a group tend not to care much if their models are beautiful. I mean, yes, ecological theoreticians do often value simplicity and elegance. But nobody makes a fetish of them.”
Isn’t our hand-wringing about whether there are “general laws” in ecology a deep desire for beauty in the form of generality / simplicity (rather than context-dependence)? And isn’t there a phylogenetic rationale for this, given the physical provenance of many theoretical ecologists?
On the admittedly-anecdotal evidence of the show of hands at Tony Ives’ MacArthur award lecture, only a minority of ecologists think ecology is about general laws: https://dynamicecology.wordpress.com/2013/08/06/esa-monday-review-tony-ives-rocks/.
And even many ecological theoreticians have the sense that “modeling” (meaning, mathematical descriptions of specific systems or cases) as opposed to “theory” (meaning, trying to derive general laws) is where the action is at these days: https://dynamicecology.wordpress.com/2014/09/22/theory-vs-models-in-ecology/
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