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Has Physics Gone Astray?

Sabine Hossenfelder interviewed by Tam Hunt.

First-time author Sabine Hossenfelder, has produced a highly readable and entertaining book about the problems with physics today: Lost in Math: How Beauty Leads Physics Astray. This is an increasingly crowded field, since there are apparently a great many problems with modern physics.

The subtitle of her book summarizes her main point succinctly: modern physicists have let subjective feelings about mathematical beauty become too large an influence in determining what theories are considered promising or valid.

Hossenfelder is a long-time blogger and practicing Ph.D physicist, living and working in Germany at the Frankfurt Institute for Advanced Studies. She focuses on quantum gravity and the foundations of physics, and has published widely in her field.

Her well-known Backreaction blog is a watering hole of sorts for both professional physicists and laypeople interested in physics. Topics range widely but the quality is always high and discussion often heated. Sabine is unusual in that she not only blogs regularly, she also responds to most questions or comments on her blogs – often in her trademark direct manner that comes across as highly intelligent, incisive and a bit grumpy.

Her book’s key point – that subjective feelings about beauty have led physics astray – is well-supported with interviews, examples, and personal observations and ruminations.

Beauty is a tricky concept. It’s been the subject of philosophical speculation for millennia. Plato placed it in his trio of most important values alongside truth and goodness. I’ve speculated about “a science of beauty” a little here, taking a “process philosophy” approach to beauty in which all aspects of nature are attracted toward beauty, in a generalized manner, and repelled by its opposite.

But should beauty have a place in theory selection? Hossenfelder suggests that it should not and, at its root, she’s arguing that modern physics has become uncomfortably anti-empirical because of two things: 1) decades-long timeframes and a ton of funding required to test many new theories (particularly in particle physics); 2) a taste for mathematical beauty rising up to fill the gap left by actual data for testing new theories.

Her book focuses mainly on problems but also a little on solutions. The book is as much, perhaps more, a work of philosophy rather than physics per se because it’s all about scientific method, theory creation, and evaluation, rather than being focused on specific theories.

I’m not a physicist so I can’t tell, of course, how impactful her admonitions will be for her colleagues – after all, she includes a subtitle to one chapter in the uncorrected proof called “why no one gives a fuck about what I think.”

But I can state my fervent hope that her colleagues, and other observers of physics like myself, pay heed to her warnings. Physics has indeed become dangerously anti-empirical, with well-established physicists actually arguing that we need to move away from falsification as the gold standard of good physics.

I interviewed Sabine via email during late 2017 and early 2018.

3:AM: Your book is full of excellent one-liners. A couple examples: “Beauty is a treacherous guide, and it has led physicists astray many times before”; “It smells like science; by which I mean coffee.” How did you, a German-speaking physicist, become so good at writing witty English? 

SH: I spent six years in North America — three in the U.S. and three in Canada — and if nothing else I suppose it at least helped my English.

3:AM: What about physics really excites you? What made you go into physics as a career?

SH: I originally studied mathematics. I went into physics because I was amazed by the link between math and reality. That’s still what excites me about physics: it tells you something about the structure of reality.

3:AM: What is “quantum gravity” and why is this your primary focus in your research? 

SH: Because “structure of reality” isn’t a research field and quantum gravity was the closest I could find. I also work on quantum foundations and modifications of general relativity; to me it all belongs together.

3:AM: Why do we need a theory of quantum gravity? What real world impacts might it have? 

SH: Quantum gravity is necessary to remove contradictions between general relativity and quantum theory. This is to my knowledge the only presently existing mathematical inconsistency in our theories of nature, and hence a very strong indicator that the theories we have are incomplete.

Saying that we ‘need’ quantum gravity is saying too much. It’s not that we need quantum gravity like, say, clean water or sustainable agriculture. But it is, in my opinion, one of the presently most promising avenues for progress in the foundations of physics.

 Real world impacts are hard to predict and often amount to little more than science fiction. To find a theory for quantum gravity, we will have to better understand quantum theory itself. Quantum theory is the theory underlying literally all modern electronics, and it’s also the basis of the next generation of electronics that might rely on quantum computing or more generally quantum information. Any fundamentally new knowledge in this area could have a large impact on our future. That’s as much as I can say about potential impacts.

3:AM: You write in your book about beauty leading physics astray, particularly in particle physics, because it costs so much and can take decades to test new theories. But this isn’t necessarily true in other areas of physics, like cosmology or quantum foundations, is it? And if so, why would ideas about mathematical beauty have become so prevalent in those other fields too? 

SH: In cosmology, and astrophysics too, experiments are costly and take decades to plan and execute. The field of quantum foundations is somewhat different, as I also explain in the book, in that people there are really debating interpretations rather than looking for a more fundamental theory to begin with.

The problem is similar in all fields in that fruitless arguments have become accepted modes of procedure. These methods persist not because they are useful to make scientific progress, but because they are useful for publishing papers and getting jobs.

3:AM: Your comments and criticisms of physics in your book remind me of Lee Smolin’s similar cri de coeur, the 2006 book The Trouble With Physics. He assailed groupthink and the lack of testability of string theory. You assail a focus on aesthetic beauty in mathematics and theory-making, and the lack of testability in many theories today, particularly supersymmetry. You also are surprisingly critical of the achievements in physics by your generation of physicists, describing them as “the unsuccessful generation” and: “Maybe I’m just here to find an excuse for leaving academia because I’m disillusioned, unable to stay motivated through all the null results. And what an amazing excuse I have come up with — blaming a scientific community for misusing the scientific method.” So here’s my question: how many of your colleagues quietly share your and Smolin’s concerns about modern physics?

SH: I don’t know. How should I know?

3:AM: I’m not asking for a quantification or survey, but, rather, how many physicists that you talk to or have talked to personally have conveyed similar feelings to you over the years? None? A few? Many? Most?

SH: All string theorists I know who have read Lee Smolin’s book disagree with him. I’d be surprised if that surprised you.

 Having said that, pretty much everyone I have spoken to agrees that in the foundations of physics (especially cosmology and high energy particle physics) we have an overproduction of useless models, and fruitless methods persist simply because they’ve become accepted procedure. But, as I mention in my book, the “false consensus effect” probably leads me to overestimate how many people agree with me. And that’s leaving aside the fact that I have no reason to think the people I speak to are a representative sample of the community.

 Even among the people I have discussions with, not everyone agrees that we should worry about the current situation or that we should do something about it. The longer someone has worked in the field and the better their funding, it seems, the more likely they are to think nothing is wrong (Google “survivor bias”). And even if they agree something is wrong, they have faith that science is self-correcting and nothing must be done (“status quo bias”). And in any case, they think it’s not their role to do anything about it. And also see Douglas Adams’s perceptive exposition of the powerful force fields emanating from “Somebody Else’s Problem.”

3:AM: If it goes beyond a small minority, why aren’t things changing? 

SH: Provided the premise of your “if” is fulfilled (which, as I said, I don’t know), it’s a classic example of a collective action problem. Every researcher individually would put themselves at a disadvantage by not working on what’s popular, hence nobody makes a change, even though collectively we’d benefit.

3:AM: In reading your book, the phrase “follow the money” came to mind a few times even though you don’t use that phrase yourself. You talk about the competition for funding research, the competition for tenured jobs, the competition for reputable publications, so how much of the problems you allude to in physics more broadly can we blame on how physics research and jobs are funded? 

SH: It’s not the funding bodies which are to blame. No one who hands out money has any interest in wasting it on fruitless research. But almost all funding bodies rely on peer review, which is done by people who judge others by how popular the topics they work on are, which more often than not means whether they work on something similar to the reviewer, and so on. In the end, no one wants to be responsible for anything, and everyone blames others.

Having said that, there are some changes funding agencies can make, which I also list in the book, that would help alleviate the problem. One is, for example, to financially support researchers who want to change fields of declining promise.

If funders do not support those who want to change fields, they essentially force researchers to continue doing the same thing while telling them and everyone else that it’s a good thing to do. In other words, if you don’t offer researchers a way out you are likely to pour money into bubbles.

 There are other, rather obvious, changes we can make, such as we shouldn’t base decisions on whether to hire or fund someone based on whether they have previously received grants or awards. That’s just exporting responsibility to others, and leads to a rich-get-richer, poor-get-poorer dynamics, which amplifies initial fluctuations.

 The biggest obstacle to any of this happening is that researchers do not want to even consider that the current system negatively affects their ability to make objective judgments.

3:AM: Due to funding constraints, which are endemic in physics and most sciences, you’ve tried creative solutions like your “ask a physicist” service for amateurs to get serious feedback on their ideas and research. How is this going for you so far?

SH: I didn’t set this up for amateur researchers to debug their ideas. I set this up to give everyone a chance to shoot their questions about the foundations of physics at researchers like myself who actually work on this stuff. The target group includes, but is not restricted to, amateur physicists.

I never planned to make a living from this, my research area doesn’t attract enough interest for that. Since I have experience with science communication, I thought it would be a way to make some money on the side, and that’s what I did. But there are only so many people who want to roast a physicist about what’s up with black holes or dark matter. I am now working with a handful of other people. We’re getting a steady stream of clients, many of them return, but we’re talking of a couple every month. So I’d say it’s going nicely, but it’s definitely not a solution to alleviate funding pressure on researchers.

3:AM: You discuss the “sunk cost fallacy,” which occurs when so much money and effort has gone into a particular research area that people generally assume it just has to bear fruit at some point. You mention only supersymmetry as an example, but would you agree that another good candidate is the search for dark matter?

SH: Yes.

3:AM: You mention elsewhere in your book that none of the various candidates for dark matter have shown up yet, after thirty years of looking. At what point would a more ideal physics community abandon the search for dark matter and look elsewhere? 

SH: I don’t know. The point I’m making in my book is that we should remove the existing incentives for scientists to stick with large, popular research programs and see what happens then.

3:AM: Can you venture an opinion? This is a significant theme of your book so clearly you’ve thought about it.

SH: I cannot tell you how long we should look for evidence in support of a theory before abandoning the approach — where would I get such a number from? I can merely tell you that the present organization of academia encourages researchers to continue with already existing programs — even if those programs seem increasingly less promising — and discourages them from working on unpopular alternatives.

3:AM: You discuss the search for dark matter and dark energy, as well as evidence for the various inflation theories, all of which are needed for our observations of normal matter to match the predictions of general relativity. You’ve argued elsewhere that we might need a theory of modified gravity rather than these seemingly epicyclic features of the concordance model of cosmology. Beyond the usual publishing of papers and attending conferences, how can physics move into new paradigms that might require sacrificing a sacred cow or two? 

SH: As I explain in my book, there are steps we can take as a community and steps that funding agencies can take to prevent researchers from repeating the same things that haven’t worked for decades. Funding agencies should, for example, offer support to people who want to leave fields of declining promise. Decisions to hire or fund should not be based on whether a researcher works on what is popular or has previously gotten a grant because this just exports responsibility to others. As a community, we should make sure that researchers identify both advantages and shortcomings in papers and lectures. (You can find a list in Appendix C of my book.)

3:AM: Your career focus has been on theory development related to fundamental physics. You write in your book that this craft is not taught: “The invention of new natural laws — theory development — is not taught in classes and not explained in textbooks… Handed from one generation to the next, much of it is experience, a hard-earned intuition for what works.” You also describe the idea of “rigidity” with respect to new theories, how these new proposed theories must agree with well-confirmed old theories to within measurement precision, as a first test of the new theory. This idea of rigidity reminds me of how many large software packages today are built on older packages, simply because it’s too difficult to start from scratch. So any hidden flaws in the old software are simply transferred over to the new package. Is this a big risk in allowing rigidity to guide new physics theories, in that old assumptions and ways of doing things, which may in some cases simply be wrong or outdated, are carried over into the new theories, perpetuating the same old problems? 

SH: Yes, it’s the same problem. It’s a local optimum but if you want to reach a global optimum, you first have to tear something down and build it up again.

3:AM: It seems to me — and I’m sure you’ll tell me if I’m incorrect — that finding a satisfactory theory of quantum gravity (perhaps the holy grail of modern physics) will require that parts of both quantum theory and general relativity will have to “give.” My money is on general relativity needing to give a bit more, but we’ll also need a more sensible interpretation of the screwy mathematics of quantum theory. Which of these two pillars of modern physics will need to be modified more, in your view, to achieve a theory of quantum gravity? 

SH: I don’t know, but I’m guessing the culprit is the quantization procedure itself.

3:AM: Turning to the philosophy of science, you state in your book your view that modern standards of mathematical beauty seem to have been carried over directly from an overtly religious way of thinking. Newton and many other early modern scientists were believers and felt that their work examined the work of God and glorified God through such examinations. This trend has diminished sharply in the last couple of centuries, as modern science has become increasingly associated with atheism or at least agnosticism. However, there is a common thread through much popular and biographical writing in physics that references God, perhaps as metaphor only, or mystical and spiritual feelings more generally. Do you think there is a place for mystical or spiritual feeling in physics or science more generally, or is the key point of your book that we need to abandon this apparently deeply-ingrained sentiment and “stick to the facts and only the facts”?

SH: Scientists should stick to the facts and not let their beliefs affect their research. But religion and spirituality are of course strong personal motivators, and nothing is wrong with that. They also serve to integrate science into culture, and that is very valuable. Indeed, I think the religious and spiritual implications of our research deserve a larger role in science communication.

3:AM: Your book brings up an interesting point about Kuhn’s notions of paradigm change in science, and McAllister’s modified notion of paradigm change: “He is proposing an updated version of the Kuhnian idea that science proceeds through revolutions. According to McAllister, scientists don’t throw out everything during a revolution; they only throw out their conception of beauty. So whenever there is a revolution in science, they have come up with a new idea of beauty.” You don’t come down in favor or against this notion in your book. Do you agree with McAllister? And if so, it would suggest that a way out of the current dead ends of physics would be to come up with a new and more appealing notion of beauty. Do you know of any candidates for such a notion? Or should we simply dispense with the notion of beauty in physics?

SH: As I say in the book, I think beauty is something that we find in nature, not something that we can demand of nature. Thus, we should not “come up with a new notion of beauty” but be open-minded and see where evidence leads us. Chances are we’ll come to find beautiful whatever nature has in stock for us. 

As for McAllister, frankly I find the attempt to explain the dynamics of scientific communities by way of philosophy silly. Scientists by and large don’t care much about the philosophy of science. Thus, if you want to understand how knowledge discovery works, you should look at sociology, not philosophy. The idea that you can derive a rule for paradigm change sounds pretty idiotic to me. 

Having said that, you can of course look at the history of science and ask what changed in the community at this or that particular instance. And on that account I think McAllister is making a good point. Indeed many paradigm changes in physics were accompanied by shifting ideals of beauty. Bear in mind that a correlation is not a causation.

Tam Hunt is a writer and lawyer based in Hawaii.

First published in 3:AM Magazine: Saturday, August 4th, 2018.