Theoretical Physics: Bad Science?

A few books in the last decade wonder whether some of the ideas on cutting-edge high energy physics and cosmology have gone too far. By “too far,” I mean offering hypotheses that are outside traditional scientific thinking—untestable, and potentially unverifiable in the long term.

Examples include Lee Smolin’s The Trouble with Physics, Peter Woyt’s Not Even Wrong, and my own A Tear at the Edge of Creation.

Sabine Hossenfelder

Sabine Hossenfelder is a well-known theoretical physicist and blogger interested in quantum gravity and other foundational questions. She has just published a poignant and clearly-written critique called Lost in Math: How Beauty Leads Physics Astray.

The book’s official promo says “we have not seen a major breakthrough in the foundations of physics for more than four decades. The belief in beauty has become so dogmatic that it now conflicts with scientific objectivity.” Publisher’s Weekly says Hossenfelder “argues persuasively that physics has stalled because of a focus on mathematical ‘elegance’ rather than reality.” Ars Technica predicts that Hossenfelder’s book “is going to lead to a reasonable amount of angry Internet shouting.”

I decided to avoid the shouting and ask Sabine a few questions myself—about her book, her views, and why she considers this critique important.

Marcelo Gleiser: Can you tell us a bit about your research interests?

Sabine Hossenfelder: I am broadly speaking interested in how much mathematics can tell us about the world, but my research has mostly been focused on how to experimentally test quantum gravity.

Your BackReaction blog is known for its lucid approach to cutting-edge questions in theoretical physics. Why do find it important for a theoretical physicist to write a blog?

I really just write about what I am interested in and offer people a platform to discuss. But often I end up debunking misleading headlines in large news outlets.

Hyping shallow research isn’t only bad for the public perception of my discipline, it’s bad for the discipline itself because researchers learn to cater to what attracts attention.

What, in your opinion, are the three leading problems in high-energy physics and cosmology? Do you see possible avenues toward progress for any of them?

Dark matter, quantum gravity, and the measurement problem in quantum mechanics. On each of them we are missing experimental clues. For what dark matter is concerned, I am cautiously hopeful that missions planned for the next decade or so will deliver data that brings fresh insights. In quantum gravity, we are finally moving toward experimental tests, though that will take somewhat longer to deliver. For the measurement problem, it isn’t even on the radar for experimental test. Part of the problem is that there’s little theoretical work on it, too.

Let’s talk about your new book, Lost in Math: How Beauty Leads Physics Astray. It’s ­a thoughtful critique of the current state of theoretical physics, in particular cosmology and high-energy physics. Why do you feel such a critique is important?

In the fields that I am criticizing, theoreticians waste a lot of time trying to solve problems that don’t exist. They do this because they are unhappy that the current theories are not beautiful enough to their taste.

I think this is bad scientific methodology and it has to stop. Trouble is, if we commission experiments that test for hypotheses without strong theoretical motivations, we merely get null results. Null results, of course, are also results, but they are not good guides to theory development. So because we do unpromising experiments, we get no new information, and theoreticians continue to invent pretty theories for which we find no evidence, and so on. This has been going on for decades.

I wrote my book because I think the public has been misinformed. We have seen a lot of popular science books that praise theories like supersymmetry and string theory and multiverses for their elegance and beauty. And people have been told that we can test these ideas soon, even though it’s not true, and of course experiments haven’t found anything.

So there have been scientists telling taxpayers they should invest money in, say, the next larger collider and some bigger telescope, but then the supposed evidence for supersymmetry and the multiverse never shows up. At this point I can’t even blame people for thinking theoretical physicists are full of shit.

I hope my book causes physicists in the affected fields to think hard about what has gone wrong here, both in their research and in the way they communicate their research.

There is a deep division in some of the physics community with respect to using untestable hypotheses as aiding the conceptual advances in the field. Some find them essential, and try to explain their uses, while others find them misguided, with no place in physics research. Why do you think this is happening?

If it’s not testable, it’s not science. Why do we even have to discuss this? I’m not a historian, but I don’t think it’s happened before. I mean, scientists have certainly believed in things that they didn’t know how to test at the time (say, the élan vital), but so far it’s been agreed upon that the moment you begin talking about untestable beliefs, you’re doing religion, not science.

Why do scientists do this? Because they can. Because the lower the standards for putting forward hypotheses, the easier it is to produce papers.

I don’t so much think we need to overcome this division as to make it clear where the dividing line is. I have no problem per se with people who want to spend their lives studying things you can’t measure, though personally I think it’s pretty stupid. I just don’t want them to go around and pretend it’s science.

I like to characterize the current state of affairs as “intellectual tribal warfare.” I also wrote a book about such issues, and find the very notion of beauty as a guiding principle to be quite dangerous and misleading. Can you give examples where this approach is taking us off track?

We all want to know what dark matter is, whether it’s a new particle, and if so which, or whether we need to change something about gravity. The vast majority of proposals that have been put forward for this were beautiful theories of new particles. Not one of these particles has been measured so far. Modified gravity, on the other hand, is not perceived as beautiful and has consequently received little attention.

The relevant point here is that the type of theories that physicists propose are influencing the kind of experiments they commission. That’s why we have seen decades of searches for dark matter particles that came back empty-handed. Of course this doesn’t mean the particle doesn’t exist. Maybe they’ll find it tomorrow. But even so it’s clear now that this wouldn’t be the particle they originally expected.

And this should now make you wonder, if all these expectations turned out to be wrong, why should you believe them if they now say we have a good chance to find particles in the next experiment?

So that’s one example. Another example is quantum gravity, the missing theory that explains how space and time fit together with quantum mechanics. A lot of effort has focused here on developing theories purely based on mathematical arguments. This has resulted in several approaches to the problem, but they have remained detached from experimental test. I find it simply amazing that so much effort was spent into developing theories but until a decade ago basically no one attempted to find experimental evidence for quantum gravity. This is now slowly changing, but still the vast amount of funding goes into mathematical speculation rather than investigations of experimental accessibility.

If you had it your way, how would you see the high-energy/cosmology research field advancing?

First of all, we should try to understand what went wrong. We now know that the vast majority of theory papers written in these fields in the last decades bear no relevance to the description of nature. While it is normal that most theoretical speculations turn out to be wrong, it is not normal to spend such a lot of time fleshing out details of premature ideas. To put it bluntly, we wasted a lot of time and money and, with that, probably missed more promising research avenues. These fields need better criteria for theory development, but just exactly which is something that practitioners must discuss among themselves.

Do you have hopes for a reconciliation?

I have given up hope that people in these fields will change their ways voluntarily. It will take substantial public pressure to change anything about the current trend to work on what is popular and what is productive.

Do you attribute the presumed short-sightedness from the group “lost in math” to be coming from too much technical work and not enough philosophical reflection about the context of the work? Should physicists learn philosophy?

I’d say it’s generally a lack of introspection, and this is probably to no small part caused by the pressure to produce papers. You don’t need to be a philosopher or historian to see that beauty isn’t a reliable guide to understanding natural phenomena, but you have to sit down every once in a while and ask yourself whether what you are doing is good for science, not just for your publication list.

As to whether physicists should learn philosophy, I think division of labor is awesome, and that it’s both futile and unnecessary to force physicists to learn philosophy. But physicists who work in areas bordering on philosophy should seek the occasional exchange with philosophers, be that through workshops or collaborations or maybe just by having coffee together. The question of just how should scientists proceed with theory development when there is little or no data for guidance lies at the intersection of both disciplines, but the communication between physicists and philosophers is currently not working well.

Watch the trailer for Hossenfelder’s new book:


Templeton Prize winner Marcelo Gleiser is a professor of natural philosophy, physics and astronomy at Dartmouth College.