Sabine Hossenfelder on Physics, Reality, and Lost in Math
What this covers
Sabine Hossenfelder and Russ Roberts discuss the stagnation of modern physics and its parallels to the methodology crises in economics and social science. Hossenfelder argues that foundational physics has ground to a halt not because we have reached the limits of human knowledge, but because physicists have become entranced with mathematical beauty and elegance—supersymmetry, string theory, and the multiverse—despite decades of failed predictions and zero empirical support. The conversation explores how evolutionary biases and cultural aesthetic preferences have no reason to track the laws of nature, and how the structure of academic incentives traps researchers in unproductive fields by rewarding publication volume over promising directions.
The speakers examine specific failures: predicted particles that never materialized in colliders since the 1980s, the diphoton anomaly of 2015–16 that sparked hundreds of hastily published papers before vanishing as statistical noise, and the contrast between the Higgs boson (a necessary prediction to avoid mathematical nonsense) and grand unification theories (entirely optional elaborations that work fine without their predicted particles). Hossenfelder distinguishes between legitimate uses of aesthetic judgment within an established framework and the misapplication of past ideals of beauty to develop radically new theories—a mistake that mirrors the broader failure of peer review to catch methodological flaws. Roberts draws parallels to the streetlight effect in economics, where researchers study what data exist rather than what matters, and both speakers note that perverse incentives in research operate across disciplines through groupthink, citation cascades, and the difficulty of abandoning work once tenure and professional identity are invested in it.
Hossenfelder argues that modern foundational physics has stagnated because physicists use subjective aesthetic criteria (beauty, elegance, symmetry) to develop theories like supersymmetry, string theory, and the multiverse that have no empirical confirmation, and that this failure is a systemic problem in how science is organized that parallels the replication and methodology crises in economics and social science.
- Predicted particles from supersymmetry and grand unification have failed to appear in collider experiments since the 1980s, yet physicists keep using the same theory-development methods
- Beauty and symmetry are culturally biased, evolved human intuitions that have no reason to track the fundamental laws of nature
- The incentive structure of academic publishing rewards producing many papers on easy, popular topics, trapping scientists in unpromising research fields
Supersymmetry, string theory, and unification became untestable after failing because physicists kept complicating them rather than abandoning them.
- Supersymmetry, string theory, and grand unification were good ideas worth trying in the 1970s-80s, but when they didn't work physicists did not stop pursuing them; instead they made the theories more complicated and arcane until they became entirely untestable, with the multiverse being a further step that was untestable from the start.
“they didn't just stop pursuing this line of research, but instead they made these theories even more complicated and arcane, until basically they became entirely untestable”
- There is nothing wrong with finding beauty in theories that describe nature, but the problem begins when scientists use specific notions of beauty to develop new theories and then are unwilling to give up those ideals of beauty when the theories do not work.
“The problem begins if scientists use specific notions of beauty to develop new theories and then they are unwilling to give up these ideals of beauty if the theories do not work.”
- Using ideals of beauty and elegance derived from past theories as guides to develop an entirely new type of theory may get you nowhere; experience-based aesthetic judgment works while you stay within the same type of theory, but applying it to genuinely novel theory development is putting the cart before the horse.
“if you are using your ideals of beauty or elegance that you have derived from the past theories and try to use them as guides to new theories, you may not get anywhere”
- The Higgs boson was a necessary prediction because the standard model without it produces probabilities greater than 1 at LHC energies, which is mathematical nonsense, so something had to exist there; by contrast, predictions of supersymmetric particles or grand unification are an entirely different kind of prediction because those particles are unnecessary and the theories work fine without them, so there is no comparable reason to expect them in the real world.
“If you have the standard model of particle physics without the Higgs boson, this theory just does not work at LHC energies. You cannot make predictions with it. You get probabilities that are larger than 1; so this is obviously mathematical nonsense.”
- A larger collider would teach us something about the structure of the proton and is not entirely useless, but building it to test supersymmetry or unification is not promising because there is no reason to think those phenomena occur in the real world; meanwhile genuinely serious problems in the foundations of physics are neglected because they are hard, so people prefer to work on something simple.
“if you want to know something about the unification of the forces or about supersymmetry, then I would just say, 'Well, that's not a promising thing to do, because we have no reason to think that these things actually happen in the real world.'”
- Historically physics ran a cycle in which new insights about nature enabled new technologies, which enabled new insights, but that cycle is now broken—not on the data-collection side, since we have a lot of data, but on the theory-development side, where we are missing the explanations for the data we already have; the increasing difficulty of collecting new data does not explain why physics is stuck.
“that cycle seems to be broken. And it's broken not on the data collection side because we have a lot of data. It's broken on the theory-development side, where we are just missing explanations for that data.”
- The additional particles predicted by supersymmetry have no practical applications and likely won't for a thousand or two thousand years, so there is nothing one would actually do with them except write down their properties; although string theory may have separate applications in condensed matter physics, that is unrelated to its role in the foundations of physics.
“the brief answer is, no, they don't have practical applications”
Scientific institutions systematically incentivize papers over progress, trapping researchers in unpromising fields they cannot leave.
- The reproducibility crisis in psychology and sociology and the crisis in foundational physics share a root cause: known methodological flaws like p-value hacking and post-hoc selection were no secret, but fields did not fix them because doing so would make it much harder to produce papers; likewise physicists love supersymmetry models because they are easy to calculate and publish, which keeps the wheels turning and lets the unpromising work proliferate.
“people in the field could very well have improved their methodology decades ago, but they didn't do it. Why? Because it would have been inconvenient. It would have made it much harder to produce papers.”
- Horgan's End of Science thesis—that stagnation reflects a fundamental limit to knowledge or human cognition—is very implausible because the stagnation appears across many disciplines simultaneously (foundational physics, complexity research, some sectors of technology such as quantum technologies), which points instead to a systemic problem in how scientific research is organized that traps scientists in non-promising fields they cannot leave because they must keep producing papers.
“I find this very, very implausible, because we're seeing the stagnation all over the place. It's not just the foundations of physics, but it's other disciplines”
- Senior physicists who control funding largely don't care about Hossenfelder's critique, but younger researchers do respond—as shown by emails and conference reactions—because they don't want to waste their careers working on unpromising research, making them the book's main intended audience.
“the senior people in the field... basically don't care what I'm saying. But the younger people do... they don't want to work on something that is unpromising and waste the time of their life.”
- Groupthink, politely called 'social reinforcement,' is a problem in scientific communities, and the easiest way to detect it is that members of the community deny that such a thing could possibly affect them; it is mostly scientists themselves who hold an idealized picture of scientists as purely rational truth-seekers immune to ego, tenure, and peer pressure.
“the easiest way to find out that social reinforcement is a problem in a community is that people in the community deny that something like this can possibly affect them”
- The diphoton anomaly of late 2015/early 2016—an excess of decays into two photons—led many physicists to write heavily cited papers (some cited 500-600 times in months) before it turned out to be a statistical fluctuation; this 'ambulance chasing' is a systemic problem in how the field organizes citations that could be fixed but isn't.
“There were people who wrote papers that were cited 500, 600 times in a matter of months. So, that's pretty ridiculous... it's called ambulance chasing.”
Ideals of beauty and elegance derived from past theories are poor guides for developing genuinely new theories and have no justified connection to nature.
- Drawing on McAllister's Beauty and Revolution in Science, what Kuhn called scientific revolutions actually involved the conceptions of beauty changing—from a mechanistic world of gears and bolts to fields and particles, from classical to quantum mechanics, from circular geocentric orbits to elliptical heliocentric ones—so holding on to past ideals of beauty during a needed revolution is exactly the wrong thing to do.
“in each of these cases, the conceptions of beauty have really shifted. And, I think that that's what we need now. So, if you are holding on to these ideals of beauty from the past, you are doing exactly the wrong thing.”
- Our sense of beauty has a cultural bias and changes over time, which already shows it is a poor guide for developing new theories; some ingredients like the preference for symmetry may be hard-wired, possibly because healthy organisms tend to have more symmetry, but there is no reason that an evolved or cultural aesthetic would reveal anything about the fundamental laws of nature or the properties of elementary particles.
“it may be that we find symmetry beautiful because healthy organisms tend to have more symmetry. So that makes sense from an evolutionary perspective. But also, in that case, there is no reason to think that this would tell us something about the fundamental laws of nature”
The multiverse and simulation hypothesis are untestable ideas best framed as fiction, not science, when claimed as literal reality.
- From an instrumentalist standpoint, a theory is something used to describe nature and it explains when it is more useful than just collecting data; the idea that reality is math is not useful, and much of the math in theories like the multiverse is superfluous to describing anything observed, so although the math can be written down there is no reason to consider it real.
“For me, theory is something that you use to describe nature. And, it explains something if it is more useful than just collecting the data.”
- The multiverse is a thought-stimulating idea that makes for great science fiction or fantasy, and the claim that we live in a computer simulation is basically a form of the multiverse; the problem arises only when people insist these ideas are science, and assigning a probability like a 50% chance to the simulation hypothesis is unscientific.
“My problems begin if people start to insist that it is science. So, yeah, this idea of living within a computer simulation--that's basically a form of the multiverse.”
- What we know about the fundamental laws of nature implies that information cannot get lost—black holes are the only known thing that could really destroy information, and assuming that black-hole information paradox is resolved so they can't, then the information about everything that makes you who you are must persist forever, just possibly in a form no longer recognizable as you.
“it basically means that the information about everything that makes you you cannot get lost. It has to persist forever. Just quite possibly in a form that is no longer recognizable as you.”
Cognitive and cultural biases shape which research scientists find interesting and fund without correlating with actual promise.
- Having many more physicists tends to fractionalize the community into over-specialized niches, which is unhelpful for solving complicated problems that require connecting very different regions; the current organization of research favors people who specialize and leaves too little room for people who try to make connections across fields.
“it tends to lead to fractionalization of the communities. They tend to fall apart into over-specialized, niches. And that's not helpful to, you know, try to solve complicated problems that usually require that you connect very different regions.”
- Our brains developed to serve us during evolution, not to serve science, and what served us well evolutionarily does not always serve us well in science, so cultural, social, and cognitive biases shape what research we find interesting, work on, and fund without that having a good correlation with which research is actually promising for correctly describing nature.
“Our brains didn't develop to serve science; they developed to serve us. And what served us well during evolution does not always serve us well in science.”
- Many physicists implicitly assume that because they can write down mathematics for something it has to be true and that the math is real, but they have never examined what allows them to say something exists or what an explanation even is, so these are unexamined beliefs rather than justified scientific positions.
“this is why my book is called Lost in Math, because they believe that just because they can write down some mathematics for it, it has to be true”
Science offers transcendent meaning and spiritual value alongside explanation, though scientists often dismiss discussing this dimension.
- Lightman's book is best read not as a contrast between materialism and science but as an attempt to understand the extent to which even science is based on belief, a framing Hossenfelder thinks he handled well.
“It was more, you know, trying to understand to what extent even science is based on belief. Which I think he did very well.”
- There are things that science simply cannot tell us anything about, such as the ultimate meaning or point of life.
“I just think that there are things that science cannot tell us anything about.”
- Beyond explaining observed phenomena, science can give people a transcendent experience and a connection to deeper meaning, which is important for understanding what science offers society; yet scientists dislike discussing this spiritual side and will roll their eyes and walk away the moment 'spirituality' is mentioned.
“what it can give to people, besides just being an explanation for certain observed phenomena by delivering this, you know, transcendent experience, or connection to a deeper meaning. Which is something that I think scientists don't really like to talk about”