Transcript: Sabine Hossenfelder on the Crisis in Particle Physics and Against the Next Big Collider – Episode #8

Steve: All right, three, two, one. Our guest today is Sabine Hossenfelder. She is a theoretical physicist, a longtime friend of mine. She is currently at the Frankfurt Institute for Advanced Study, and she has a new book out which we’ll discuss. She also has written recently an editorial that appeared in The New York Times and actually ruffled the feathers of a lot of high-energy physicists. We’ll get into that as well. I want to say at the outset that I anticipate angry reactions from one individual and one group of people from having you on our show. The first, the individual, as you know, is Luboš Motl, who will probably send me an angry email asking me why I had you on my show, and then the high-energy physics ATLAS group at Michigan State will be angry because they didn’t like your New York Times editorial. So having said all that, let’s start by talking a little bit about your biography. I like to introduce our guests a little bit by having them tell me just a little bit about their life story. One of the interesting things that you said in your book was that you got into physics because you felt you could not understand people, and maybe you can just explain when you realized that and, you know, if that was when you were a child, how your childhood might have been different from other people’s.

Corey: And hopefully what you meant by not understanding people.

Sabine: Yes, that’s right. So I wrote in my book I went into physics because I don’t understand people. I’ve always felt that really, the natural sciences and physics in particular are the easiest part to understand about the world. When it comes to human beings, you know, things get complicated very, very quickly. I have a lot of difficulties understanding why people do what they do. I thought that going into physics was kind of the safe thing to do, you know: I would be sitting there with my equations and try to understand how the universe works, and I wouldn’t have to bother all that much thinking about all this human baggage. But it didn’t quite work out that well. It turns out that there’s a lot of sociology in science, somewhat more than I anticipated. Yeah, people sometimes ask me how I got into talking so much about sociology. It’s not that hard to understand. So I originally studied mathematics, and I had a boyfriend who also studied mathematics but he also studied sociology, so naturally I developed an interest in sociology, especially for what the mathematical modeling is concerned. And that was at the time in the mid ’90s when Stuart Kauffman’s book At Home in the Universe came out, and I got very interested in this idea of agent-based modeling and complexity systems and self-optimization and all that kind of stuff. And so it was kind of obvious to try to apply the system’s thinking to science and the people in the system themselves — and once you have the system thinking in your head, it’s really hard to get rid of.

Steve: I think you and I had a lot of discussions just after the financial crisis about agent-based modeling of economies and things like this. But specifically to physics, I think I am very sympathetic to your views on this: that the type of person who goes into physics at the beginning is a very rational person, or thinks of himself or herself as very rational, [laughs] and kind of looks forward to the physics world as being kind of like the Vulcan Science Academy, where everyone is completely logical and rational; and then when you actually get into it it’s just another branch of academia, where there’s tons of sociology, it’s maybe less meritocratic than you had hoped, and there are battling cliques trying to advance their own interests and own theories. Maybe you can comment on your sort of realization that this was the case.

Sabine: Well, I guess it took me some while to figure out. I really only noticed this when I started getting into the community of particle physicists. So originally I come from a completely different community, which is heavy ion physics, because that’s what people did at the institute where I made my PhD. But I never myself really worked on heavy ion physics, so I was kind of shielded from this whole community thing because it didn’t really concern me, like I just did my thing, and we had a group that was like five people and that was pretty much the contact that I had. And I didn’t want to stay in Frankfort. I moved to the United States after I made my PhD — I was in Tucson and then in California — so I started going to those particle physics meetings. I also mentioned this briefly in the book. There’s first and foremost the SUSY conference about something like supersymmetry and the fundamental interactions or something — so it has this complicated name that I keep forgetting, but everyone calls it the SUSY conference — that used to be a really huge conference. It since shrunk down a little bit, but it used to be like 800 people, so one of the really large events in the field. I found it really creepy that when you were listening to people, they were all literally saying the same thing. You would be listening to the plenary talks and to the talks in the parallel sessions, and they all had the exact same motivations for why supersymmetry is the right thing to do. They were never talking about any shortcomings of their models. I’d ask them a question like about naturalness or something like that, and they would all give the same answers. It just freaked me out, you know, I thought that’s not really how it’s supposed to be, there’s something strange going on here. You know, I looked into this issue with naturalness (and I go on about this in the book) and that was really kind of the deal-breaker, why I didn’t want to have actually to do with it anymore. And so I decided to get out of this community, and then I started working on the phenomenology of quantum gravity, where basically there’s no community [laughs] — maybe there’s a little community now, but it’s like maybe a hundred people or something, so not in the order of thousands.

Corey: Can you tell us what’s meant by naturalness in the theoretical physics community? — because it’s a big part of your book.

Sabine: Yes, so naturalness is one of the criteria for theory development that has become very influential — in particular in high-energy particle physics, but also in cosmology to some extent — and it’s a criterion that you expect a good theory to fulfill, that basically says that the parameters in that theory — so that’s the numbers without units — they should be of order 1, so they should not be really large, they should not be really small. And so that’s the general notion of naturalness. And then in high-energy particle physics they say actually a more relaxed version of naturalness that says well, sometimes very small or large parameters can be okay if there is reason for that, you know, if you have an explanation — symmetry, for example, can be an explanation for that. That’s this idea of naturalness. And I call it an argument from beauty, because I think that’s where historically it comes from; but some philosophers have told me I should just call it a metaphysical argument, or maybe just a philosophical argument, or maybe it’s just a belief. So I don’t really care what it’s called. The point is that it’s an additional assumption that you impose on your model.

Steve: Maybe to elaborate a little bit more on that, I think it’s fair to say that it’s not a completely well-defined notion of what naturalness is. It was a — I don’t know about the current situation, but certainly when I was a student and early in my research career and well into my research career — it was a dominant notion that if you noticed some aspect of a model of fundamental physics where there were some strange coincidences — so, for example, some number had to be extremely large or extremely small to fit the data — and I’m talking about a dimensionless number, so not something measured in units, because obviously big or small depends on what units are used to measure it in —  but in some models, many models there are dimensionless numbers sort of given by God, if you like, and why should this number have to be 10 to the minus fifteen [10-15] in order to fit the data? The most well-known case is, the mass of the Higgs boson is much lighter than if you just sort of randomly put down numbers of order 1 into your model you would get a much heavier Higgs boson, and so it was considered a huge mystery why the Higgs boson would be so light or its mass would be so small. Now, as Sabine points out, it’s fundamentally a kind of aesthetic question. So you can write down a mathematical model that fits all the data, and then the question is, are you happy with the model, or do you find that because it has some “unnatural” aspects that you suspect there’s actually a more fundamental theory underlying it that you have yet to discover, which would explain that unnaturalness.

Corey: So this seems to be an added constraint that’s a part of physics that I’m honestly not sure if it’s part of other fields. I think almost everyone’s familiar with Ockham’s razor and the idea that the theory should be simple; and my question to you is, do you see this as simply an extension of Ockham’s razor, or an added limitation that physicists are placing on their theories, that be natural in addition to being simple?

Sabine: So it’s definitely not Ockham’s razor because, loosely speaking, if you think of a theory in physics as some collection of mathematical axioms together with some identification of those mathematical things with observables, then Ockham’s razor is basically a statement about the number of assumptions, so it tells you that if there’s anything superfluous, get rid of it. So that’s basically Ockham’s razor. Naturalness instead is an assumption about the type of axioms that you use. One of the axioms that you will use, for example, for the Standard Model might be something like the mass of the Higgs boson is so and so, and then you can ask well, is there a better explanation? And so the issue with naturalness is now that people claim that for certain numbers you need to have an additional explanation. Let me maybe phrase this differently, because sometimes people claim that I’m saying we should not look for deeper explanations, which is nonsense, of course. So generally you would always want to have a better explanation, say, for the values of the masses in the Standard Model. But the use of this criteria from naturalness is that scientists say there are certain numbers in those theories that particularly require our attention and require an explanation — and the mass of the Higgs boson is an example for that, so it’s supposed to guide your attention basically. What happens is that people focus on solving this particular problem to develop new models, and what I’m saying is basically, well, you know, the mass of the Higgs boson is not in anymore need of an explanation than all the other masses in the Standard Model — they’re just parameters, they may just be whatever they are and that’s the end of the story. So it’s not a good problem to work on. So that does not mean that it wouldn’t be nice to have an explanation for that — it certainly would be — I just think that it’s not a promising route to make progress.

Steve: I think the sort of weak use of naturalness, that I think maybe very few people would doubt is reasonable, is just to say that, if you see some aspect of your model that looks “unnatural,” perhaps there is an underlying something that you’ve yet to discover which explains that unnaturalness. But it doesn’t have to be the case. We don’t know whether that is going to be the case in the ultimate theory of everything.

Corey: In your book I really liked your example from the Copernican theory and trying to explain while the heliocentric model wasn’t accepted. And you had an example of naturalness from, you know, effectively five centuries ago that I think for laypeople might allow them to get a grasp of the idea, whereas most people aren’t gonna get Higgs boson. Could you explain how you thought that the naturalness argument played a role in people trying to reject the Copernican theory?

Sabine: Yeah, so this was the first historical example that I could find, and it went roughly speaking like this: so if you have a system where the earth is in the center and the planets and also the sun go around the earth, then it’s natural to expect that the stars do not move, because by assumption, kind of, the earth is in the center and so why would they move? Now if you have a system where the sun is in the center and the earth goes around the sun, then you would expect the relative positions of the stars to each other to change over the course of the year, and this is called the parallax. At the time astronomers could not see it, so what they concluded from this is that either this parallax is very small, which would have meant that the stars had to be very far away, or we sit in the center of the solar system. For some while at least, they thought that this was a good argument for the earth being in the center of the universe, and it was based on this argument that there should not be this large gap in the scales between the distance between the known celestial objects, with the planets at the time and the stars. So now, of course, today we know that the stars are actually much further away than the planets in our solar system, and that there’s nothing unnatural about it because that comes into being by a rather complicated process where galaxies form and the solar system forms, and so on and so forth. Implicitly what went wrong there is that the astronomers at the time assumed a certain distribution of the objects that they thought was natural. Well, it did not work out. So that’s, I think, one of the first arguments from naturalness, and to a certain extent the arguments that are being used today are still kind of similar, the idea that you don’t want this mismatch in the proportions. It’s just that they have become much more abstract, and especially when it comes to the mass of the Higgs boson, we’re not actually talking anymore about quantities that are indeed observable. You were speaking about a random distribution of the parameters, from which you may conclude that the mass of the Higgs boson is kind of unlikely. The thing is that you never actually observe those parameters, by assumption. The only thing that you eventually observe is the mass of the Higgs boson, and that’s something which you measure either which way. From what the content of this argument is concerned, it’s entirely philosophical, it has no relevance for the computation of any actual observable.

Steve: Well, I  guess the way… When I was a student and I first learned about this issue with the Higgs boson mass, I  always said to other people, you’re making a kind of a priori assumption about the measure or the distribution of parameters in the more fundamental theory, which — and we don’t know what that distribution will be — subject to your prior, maybe you strongly suspect some special conspiracies going on to keep the Higgs boson light. But it is subject to that prior. That brings me to the subject of aesthetics. So there’s a famous comment about the unreasonable effectiveness of mathematics in describing nature, and I think all scientists sort of appreciate that to some degree; but that naturally leads into what I sometimes refer to as the tyranny of aesthetics. So the notion that there will be simple mathematical models that successfully — perhaps unreasonably successfully — describes nature, naturally leads your brain to sort of want to see beautiful aesthetic models and to desire them. And so the question is, you know, have we gone too far in valuing aesthetics as a kind of principle for model selection?

Sabine: Well, the problem is not aesthetics per se, but that physicists are using very narrow conceptions of beauty, like this criterion from naturalness. You could have the attitude to say, well, if it describes nature then it’s beautiful, right? But that’s exactly not what physicists are doing. It’s that they are postulating certain kinds of symmetry that they want a more fundamental theory to fulfill — for example naturalness, but also they like to have more symmetries, and they also like it to be simple in an absolute way — so not in the sense of Ockham’s razor, that if you have several different theories you take the one that achieves the most with the least input, basically, but they want a theory that is simple, period. A good example for this is string theory. String theory is based on a very simple idea: everything’s made of strings — and then the devil’s in the details. But so I think the reason that a lot of theoretical physicists like string theory is that it has this all-encompassing, unified aspect that comes from this very simple idea, and I think that makes it appealing. And I can certainly understand that appeal. It’s just that I don’t see any good reason why, if we look deeper into the structure of matter — or if you want to include spacetime, maybe one should say, deeper into the structure of reality — why the laws necessarily must continue to get simpler. I see no particular reason for that.

Steve: Yes, I think that’s a prior, that’s a prior that we hope will be realized. Before we get into string theory, can we discuss a little bit more particle physics? Your editorial in The New York Times, could you just recapitulate in a couple of sentences what you were trying to get across in your editorial?

Sabine: Yeah, so I was trying to get across that, given the information that we currently have, building a next larger particle collider is not a good investment, if what you want is to make progress in the foundations of physics. It’s a very expensive experiment. From the experimental foundations of physics you can think of building the next larger collider, and it is, I think for what’s presently on the tables, it’s the most expensive one. But we don’t have any good predictions that there should be anything new to find. So of course you can say well, let’s just measure more precisely the properties of the particles that we already know, and that’s all well and fine. It’s just that we run the risk that we build this machine, and the only thing we get within the next 30 years is more confirmation of the Standard Model. And now we do have problems in the foundations of physics that we know require a solution — dark matter is one of them, congravity is also one of them — and so the only thing we get is further non-results. It will not help us developing this theory further. And so my argument is basically, there are better things we could be doing with the money.

Steve: Right.

Sabine: And of course, particle physicists don’t like to hear that.

Steve: So we’re talking about a sort of 50 to 100 billion dollar machine, and I would say the only likely place it could be built is in China. And even a couple years ago there were some, I guess, very optimistic people who thought the Chinese government had sort of put something into their five-year plan about possibly doing this. But just to be precise, I think your argument is that, were that money to become available, it would be, there are better uses for it within physics than to build sort of the next huge machine. Is that fair?

Sabine: Yes, given all that we currently know. You know, I always make this little asterisk and say that this is actually important information to take into account. So certainly, if — so the LHC is not done right? So they are now having their upgrade, then there will be the third round, and then there will be the upgrade to the high luminosities phase. And so if they find something new there, you know, if maybe we’re lucky and some supersymmetric particles will show up after all, we’ll totally change this argument, of course.

Steve: Yes.

Sabine: But currently it doesn’t look like there is anything new. Given all that we presently know, I think it would be better if we collected more information about aspects of our measurements where we know we have something that needs explaining. Like dark matter, for example: there’s certainly more things that we can measure that might help us try to find out what it is, which then again would help us to make better predictions for what experiment to build here on earth to maybe reproduce those things. You know, if it’s a heavy particle, then yes, building a next larger particle collider would be the thing to do. But maybe it’s not, you know, maybe it’s a really light particle, and you need a completely different type of experiment. It seems to me just smarter to first figure out in more detail what is going on, and put some more money into this. And that’s also for quantum gravity — I already mentioned this — we at least know that there has to be an explanation for this, whereas when it comes to the Standard Model, that just might be it, you know — all the way up to the Planck scale, of course, you know, but that’s like a factor of a billion or something away from what even the next larger collider can test.

Corey: We periodically read about discoveries coming out of the LHC, the Large Hadron Collider, and I think most people have seen it — at least people are informed — as an incredible success. We found the Higgs boson, it’s a very exciting discovery. But your book is painting a very different picture. You’re trying to say that in many ways it’s been a failure, we haven’t found anything, as I recall, predicted since 1973. We’ve found these things that are predicted before that, but none of the new theories, predictions have been confirmed by the LHC, and that’s, as I understand it, part of what makes you skeptical about putting more money in a larger collider. Could you maybe let me know am I right about that, or react to that?

Sabine: So I don’t think that the LHC has been a failure, and I don’t think I ever said that, I’m pretty sure, because I think it’s been a huge success, because we knew that there had to be some new physics to appear at the Large Hadron Collider — not necessarily the Higgs, but something had to appear. And that was the case, so they found the Higgs and everyone was happy, you know, the champagne bottles were opened and all that kind of stuff. What has been a failure have been the predictions for new physics beyond that, and those are predictions that physicists started making soon after the completion of the Standard Model, started with this idea that there had to be a grand unified theory that then predicted proton decay and experimentalists looked for that — maybe they’re still looking for it, but they haven’t found anything. So some of those models were ruled out, but you can always go and twist those models. And then there has been supersymmetry, of course, which was always supposed to be found on the next larger collider, basically. There are various dark matter candidates that have been looked for in dozens of experiments and not have been found. So this is why I say, you look at what the theorists have been doing: those predictions have been wrong for 40 years. The prediction of the Higgs actually predates the completion of the Standard Model in the ’70s — it was made in the 1960s — so what the LHC actually did was that it confirmed the prediction that’s even older than the Standard Model.

Corey: But you do claim that there been no new data in decades. So what do you mean by that?

Sabine: There has been a lot of new data, like the LHC collects a lot of new data every time they make collisions. It’s just that this data only confirms the theories that we already have. What we do not have is data for some new physics, some new phenomena, something that would help us develop those theories that we’re trying to get done. We have a lot of non-results from those dark matter searches, for example, you know. Every time they complete a search and find nothing, you get better constraints. It’s just that if you want to find out what the particle is, it’s not particularly useful information. What you really want is, you want to have an event where the damn thing actually interacts with your detector. And it’s the same with these searches for supersymmetry. So you can say, well yes, so we’ve run the LHC for 10 years now, and this has ruled out a lot of the parameter space of supersymmetric models. But does this actually tell us what is going on with quantum gravity or with dark matter or what have you? No, it doesn’t. So what have we learned from it?

Steve: If I could maybe clarify for our listeners, so… There were pre-existing models of fundamental physics, say the Standard Model, which predicted some particles which had not yet been directly seen or discovered, and so LHC was a huge success insofar as it discovered the Higgs boson, but that had been predicted long ago. If you look at new theories, new ideas written down by theorists in the last, say, 30 years, basically none of the new phenomena that were novel in those models that hadn’t been thought about before — say particles, superpartners, things like that — none of that has been discovered, right? I think that’s what she’s saying. Now, it is true that in the neutrino sector there is… so we didn’t know whether neutrino, something called neutrino oscillations occur, and we’ve since discovered those, and those kinds of phenomena in the neutrino sector do suggest physics beyond the Standard Model. But we haven’t directly been able to probe that physics yet. Do you agree with my summary?

Sabine: Yes, that’s correct. So the theory for the neutrino masses also goes back to the 1950s, so that’s also not a new thing. But it is correct, of course, when you say that once you know that the neutrinos have masses, you know that there has to be something more than the Standard Model. And that, I think, is a solid argument. It’s just that you don’t know where the new phenomena are supposed to appear.

Steve: Yes.

Sabine: You can only tell it’s very similar with quantum gravity. It has to be at the latest, I don’t know, two orders of magnitude below the Planck scale or something like this, so it’s ridiculously high basically. So if we build that new collider, we will not be able to scan that whole parameter space. It’s way beyond what we can possibly do.

Steve: Right. So another way of saying this is, that the things that we know are out there that we still don’t understand but we know they’re out there, it is very possible this next hundred-billion dollar collider won’t tell us very much about those mysteries that we know of already, and so, you know, want to spend the money elsewhere. But can I refine your question a little bit and ask, imagine that the 100 billion or 50 billion dollars was coming. If they didn’t build the next huge machine in China or wherever, instead of that money being freed up to do dark matter or dark energy experiments or quantum information experiments, imagine it went into building missiles. As a veteran of the efforts to save the US super collider back in the ’90s, people were very optimistic — sorry, the enemies of the super collider made arguments saying it should not be built and, of course, there are these experiments in condensed-matter physics or in biology that’ll be much better than use of the dollars than the super collider — but when the super collider was killed, the money didn’t show up in science budgets, it showed up in completely, what we would consider useless budgets. And so in that scenario, would you still favor building the next big collider?

Sabine: Yeah, so I constantly hear this argument, I call it the zero-sum argument. So that’s an argument that every particle physicist I know has offered me at some point. I think it’s a pretty stupid argument for the following reason: it does nothing to explain why the next bigger collider is a good thing to do, right? It basically says well, but if we don’t get the money you might not get it either, so shut up.

Steve: Yeah.

Sabine: And so I don’t think that’s convincing. [laughs]

Steve: The version of the argument that you just gave, I think you know, obviously I don’t support that version of it. I think the sort of realist attitude is, we have this very big consortium of particle people, and we think we can extract another 50 billion or 100 billion from mainly the Chinese government, I think, to further advance our subject. The exact gain or return on that investment is unknown at this point, and you can make arguments either way whether it’ll be good or bad, it’ll be a good ROI or not But we are set up to extract that next project, so let us do it — I think that’s sort of more their argument — and if we don’t succeed, it doesn’t mean that you’re gonna get the money.

Sabine: Yeah, so I don’t expect to get the money [laughter], trust me. So look, I think what you may be trying to say is that there are a lot of factors that will enter this decision that have very little to do with the science, you know: there’s national interest, there’s international competition, there are lots of political aspects, you know, maybe the Chinese want some shiny project and they think that building a collider is the thing to do, maybe it all depends on who knows whom in which ministry or who had a beer with whom last summer, something like that… So that’s all possible, but those are all aspects that I really can say nothing about. I can really only speak about the scientific potential, and to some extent about the technological situation. And I think if you look at this, it’s just not going to be a good investment. There are better things that you could invest in at the moment.

Steve: I think it’s back to those inexplicable humans and their weird hijinks. [laughs] Yes, a big part of it would be sort of national pride, or the Chinese wanting to be at the forefront of what at least used to be a super high-prestige area of science. I don’t know if it will be in the future. Another justification for big high-energy physics has always been that, by having very lofty goals, like discovering the fundamental laws of nature, you attract a lot of talent into the field that is idealistic and wants to work on these problems. So you kind of, it’s almost like building… you have to build a big pyramid to get a lot of people engaged in an effort. And maybe the most beneficial things that come out of it won’t be the actual — certainly not in practical terms — the particle physics knowledge, but getting these people together to solve huge compute problems, or transfer large amounts of data around, might lead to the worldwide web or some other thing which affects the rest of the world. And so that’s kind of another argument for why you might want to build this big pyramid which isn’t very practical, but the sort of side consequences of building that pyramid more than justify the cost.

Corey: That sounds like this actually will create an enormous distortion in human capital, right? You’re going to create this project that you’re not sure is gonna have any benefits, suck a lot of very talented people in this area, and perhaps even take them away from doing more productive things with their…

Steve: Right, so this is a very subtle claim. The claim is that you do something which is impractical but very beautiful, very attractive to bright young people. They devote their lives in a monastic way — the way that Sabine and I have for our early decades of our lives — and yeah, maybe the practical use of knowing about quantum gravity is going to be very limited for hundreds of years for humans. However, the fact that so many people worked so hard on this means that they solved a bunch of other technological problems along the way, and the spin-offs from those — I think you could make a pretty strong argument about this in the past, I’m not saying it will continue to be true in the future — but that the side consequences more than justify the amount of money spent.

Corey: What I’m going to say is, I think the natural critique of that is that’s similar to putting a distortion to the economic system in other areas, where you’re taking human capital that can be doing other productive things, could be creating new imaging machines to help cure cancer perhaps…

Steve: I mean, if you believe in homo rationalis and you’re an economist, you maybe don’t understand this argument. But if you realize that humans really are under the tyranny of aesthetics, okay… So if you talk to a brilliant 19 year old and you say, what do you want to do, he doesn’t say, I want to make the TeV 10% better; he says, I want to discover the secret of quantum gravity. And so you have to take that into account, an aspect of human psychology.

Corey: I think no one’s not taking that into account. But the general point is that there are opportunity costs, and that the people you’re attracting to this pursuit could be doing other highly productive things, and you may just be attracting them with this fetishization of aesthetics, when in fact they could be spending their time maybe working on other fundamental things that, had you not hung this enormous dollar sign in front of them and talked about aesthetics, they wouldn’t be diverted from.

Steve: Well no, it’s not the dollar sign. The dollar sign is bringing the physicists to, say, Wall Street. The aesthetics are bringing them to CERN.

Corey: Well no, the dollar sign is building this new collider, right? So you have this fancy machine, you can pursue these very, very beautiful topics, and that may divert you from doing something else. I mean, as Sabine’s been saying, it’s quite possible you build this very large machine and nothing is found. And although there may be side results of this, you still have taken, you know, smart person ‘A’ who could have gone into a field that may have actually produced some concrete results, and send them into the field and say, well, there may be some side spin-offs that are successful. So I’m just saying, any sort of person who is more of a free-market oriented person as far as knowledge creation or economics, would find this presents a huge distortion of human capital, right?

Steve: I think it’s not as simple as you describe it. So to give you an example, I know many people from my generation who left physics — often against their will, but maybe not always — and went into finance; and so in terms of, if you were an economist and you said what was their contribution to GDP, it was ginormous, because the amount of taxes they pay every year dwarf what any university professor pays, okay, just the taxes. But if you actually ask them, looking back, well, did I create value for society, do I feel like I got a lot dumber doing this stuff? — yes, yes.

Corey: And society feels that way too about many people, about these talented people. That’s another distortive phenomenon. Finance was another distortive effect on the human capital market.

Steve: Okay, you could take another example — not finance, but they went into some applied area of research, but they were kind of bored by it, and weren’t as, didn’t realize their full potential as minds, because they were kind of doing something else but ultimately weren’t that passionate about it, so… To answer the question of which of these two regimes outperforms the other, you have to fix a certain set of parameters, and we don’t really know the values of those parameters.

Sabine: On this issue of spin-offs, that’s certainly a possibility, but this is again an argument that is not specific to building a larger collider. You can make a similar argument about other large-scale experiments where you hire a lot of smart people and actually give them the time to think. And so if that’s what you want to achieve, then you might as well invest that money in the most promising experimentable. And that’s also if you look at particles, for instance, you say you have this benefit that you have smart people and they have time to think, and who knows what they will come up with — congravity or something. Well, it’s not working, as we have already discussed. The only thing they come up with is predictions that are wrong.

Steve: One view of that is just that there is some low-hanging fruit that’s relatively easy to pick, and then, you know, when you confront something ultimately as hard as quantum gravity and you don’t have the right experimental tools, you know, one might expect that theorists, theoreticians would tread water for really a long time without good experimental probes of quantum gravity. Do you have an opinion on that?

Sabine: Yeah sure, so that’s certainly true, the easy things get done first. And you expect progress to slow down — that I think is natural — but it doesn’t really explain why theorists make all those wrong predictions and continue to make them without actually changing their methods. So that’s the thing: they’ve been using the same methods to make predictions ever since the completion of the Standard Model, and the only thing they’ve gotten when they went out to actually test those predictions are non-results, so it did not work out — but they still haven’t gotten the message, they’re still doing the same thing. And I think there’s something fundamentally broken in that system, that they’re not learning from their failure.

Corey: So I think this was actually a very interesting part of your book, the way you believe that the scientific method has been sort of damaged by this focus on naturalness and aesthetics, that physicists we think of as extremely rational and dedicated to kind of carrying out science in its most precise way are in fact not following the method. If you could elaborate on your critique and how you think they’ve deviated from scientific method?

Sabine: Yeah, it’s not only arguments from naturalness, it’s generally this method of developing models by paying attention to criteria from beauty. As I already said, naturalness is not the only criteria, and you also have this belief that it has to be simple in an absolute way, and there’s also a lot of attention been paid to it having a lot of symmetries, just because that has previously worked. So it’s a reasonable thing to try, you know. In the ’80s, after they had the Standard Model, they were trying to see if maybe gradual unification works, and there is one larger symmetry group that is broken, and that was a reasonable thing to try. But they didn’t learn the message — like that didn’t work, then they tried the next larger symmetry group and that didn’t work either, and then they tried fiddling around with the theories rather than wondering what went wrong there. And it’s the same with those arguments from naturalness, that we know from the cosmological constant, for example, that they don’t work. You know, the cosmological constant is not natural, it just isn’t natural. They have, as you already said, there’s this issue about the prior — or depending on what interpretation of your probabilities you use, the initial probability distribution — that you assume, you must make this assumption to argue that an unnatural theory is somehow problematic, and yet there is no way to justify this assumption. This knowledge has kind of gotten lost. So you know it, and I know it’s there in the literature; but a lot of people seem to have forgotten about it, because the others, they’re just mathematical formula that you can use to calculate how natural a theory is, where you can just apply it. I think what is happening here is that people are not correcting those methods that don’t work because they can still get it published, you know, there’s no reason for them to change their method. It’s generally accepted procedure, everyone does it. They think it’s good science.

Steve: So I think you touched there on the issue of local incentives. So what is the incentive for an individual theorist to either completely abandon their earlier research program and start something new, or just kind of incrementally keep publishing the papers and get the next promotion, keep their grant money flowing to fund their graduate students. And so I think it’s no surprise that there’s sort of psychological or institutional inertia in those incentives. So even though I think any thinking person — and maybe this is usually the younger people entering the field — would say hey, naturalness doesn’t work, it actually misguided, it caused tens of thousands of papers to be written over the last 30 years that turned out to really have nothing to do with TeV-scale physics; so we should just kind of abandon it and loosen up and just maybe take the prior that we don’t know anything about the probability distribution for the parameter space. If that were the case, would you then say the scientific method is kind of operating okay, or are there other issues that you could point to?

Sabine: So, certainly that would be progress, and I think it’s right what you say, that the young people are going to bring in change, because they just see that this didn’t work and they don’t want to waste the time of their life making the same mistakes as the previous generation. I kind of hope that now that the data, I think, is pretty clear and says well, that does not work, they will eventually be forced to give it up. But now the thing is that — unless they figure out what was the underlying cause of the problem, why could it be that all those ten thousand people believed in the same nonsensical thing — the problem is bound to recur in some other form. You know, they might throw out naturalness as a stupid criterion, but they will come up with a new stupid criterion and then use that to fabricate their models for the next larger collider, and then they build the collider and they don’t find anything. It’s the self-reflection that I’m missing here. They don’t seem to really have an awareness of what went wrong.

Steve: Yeah, I agree with you, there should be some meta-learning about this, but it’s just hard for people to do it. I would actually point to some — again, the mysteries of humanity — some fundamental psychological herd mentality that people have, that if you enter a field and everybody else is agreeing that yes, X  is a right way for model selection, you just, it’s very difficult to be a maverick and reject that in the face of everybody else’s acceptance of that idea. And so that’s why I think if you look at the historically really great scientists, they often tend to have this very maverick nature, or some ability to resist social pressure makes them an oddball in human society, but it makes them more able to reject a herd mentality in their own discipline.

Sabine: Yes, I think that’s certainly true, but it’s also true that we know of that problem, right? And so I think that the way that scientific research is currently organized, it makes those problems worse rather than make them better, for example, by giving people an easy opportunity to get out of the field if they feel that this is really not leading anywhere and they’re just wasting their time. And that’s, presently it’s pretty much impossible to do. You will know that yourself, you know: if you’ve done your PhD on a certain topic and you did your first post doc on that, you’re pretty much stuck, because no one’s going to hire you to work on something entirely different. You can’t get any grants either. You will basically be forced to convince everyone else that what you’re doing on is the right thing to do, and chances are you will also come to believe it yourself. And so there are just systemic problems with the way that we currently organize research that we could solve, but we don’t.

Steve: I agree with you. I mean, I’m an example of somebody who switched fields on multiple occasions, and every time is extremely hard, so I have scars all over my, at least my psychology, from each time that I’ve switched fields. But in a way I think the problem that you’re describing is kind of similar to, in financial markets, the problem that you will all the time have bubbles. And there will even be people inside pointing to the bubble and saying hey, houses are totally overpriced, this is insane. But they’re kind of helpless to correct the bubble, and then suddenly you have a kind of catastrophe and then everyone says well, I believed that it was a bubble too, I was never fooled. And then we forget why we have these bubbles. But in a way it’s, to me it’s a kind of difficult thing to change about human psychology. Corey, I think you want to say something.

Corey: Yeah, I think it’s even perhaps a little more extreme than that. Again going from your book, I find your comment about the failure to find anything but the Higgs as the nightmare scenario. And it seems that, if that’s right, that it’s striking that people haven’t absorbed that message. And I’m kind of curious to find out whether you think other people in the field have sort of, are they thinking okay, this isn’t working, I don’t know quite know what to do, but I’ve got to keep writing in this vein to keep my job? Are people aware that there’s a serious problem and just not really changing their behavior because they’re locked in their career, or is it kind of denial? Because it’s as if the financial crisis had happened and people just are pretending it didn’t happen. It seems like the crisis has already occurred.

Sabine: Yeah, so I think the current situation is kind of a mixture of denial — like that that can’t possibly have happened, what the hell’s going on here? — and also mixed with hope, because the LHC will still have the next round and maybe the particles will be there, and everything will be good, it could just be a more complicated version of naturalness. Of course, I can’t rule that out, maybe it’s true, right? So there’s always this hope factor. There are also a few people, I know a few people who have actually started working on something different, who have stopped working on supersymmetric models and now work on more general models, basically — you know, some do more astroparticle physics now than collider physics, so there’s a little bit of a change is taking place — but yeah, as you say, there is this amnesia that is taking place, that people forget what they even did, and what was going on, and “Didn’t we ever talk about the nightmare scenario?” “No, I don’t think, because it’s totally great that we have not found anything besides the Higgs, that’s teaching us so much, right?” [laughter] And so they’re kind of rewriting history, I think — which is sad, in a sense, because it’s all documented in the literature, of course, you know, that all those people who’ve made those predictions, they can’t even be bothered to even say that yes, that was wrong.

Steve: Yeah, almost no one is even fastidious enough to just go in the literature and see okay, who voted with their feet and spent 10 years exploring SUSI parameter space, and was quoted as saying they were absolutely sure we would see SUSI — I think you interviewed such people in your book, I don’t know if they ‘fessed up to what they said 10 years, 20 years ago. But let me just comment that the discussion we’re having right now is really focused more on the theorist community, the theoretical physicist, because ideas like naturalness and what is the prior on your parameter space for a model, those are notions that theorists are familiar with, but experimentalists who comprise the bulk of the physics population generally are not. They’re focused on much more practical things, like how to really make the detector work, or how to analyze the data. I just want to relate a story that occurred in this office that we’re sitting in right now. When I first got to Michigan State, I met with a very prominent senior ATLAS physicist, the head of our group experimentalist here — ATLAS is one of the big detector collaborations here at the LHC — and when I told him, I said well, you know, I don’t feel so bad about taking this administrative role or doing more stuff in AI or genomics because, after all, particle physics is in such crappy shape. And he didn’t actually understand what I meant by that. He literally was, he looked at me like I was crazy, because in his mind they had completed the construction of this ten billion dollar machine, they had successfully got it to work, they had discovered the Higgs boson in the face of incredible backgrounds that they had to suppress down by statistical analysis, so they had accomplished a tour de force of human scientific discovery. And he just couldn’t understand what I was saying. And I tried to explain to him that, well, if we don’t see anything more than the Higgs, our field is more than likely dead [laughs] — basically I said something like that to him, which I think you’re sympathetic to — but he literally did not understand what I was talking about.

Sabine: Yeah, it’s like they walked over the edge of the cliff and haven’t yet looked down.

Steve: They’re taking satisfaction solving the specific technical problems necessary to make the experiment work, and you have to respect that. They’re not responsible for these sort of highfalutin ideas of theory creation and stuff like that. So that’s the bulk of our field, actually.

Corey: I’d say this is actually rather consoling to me, because I’ve been in a number of fields that have almost precisely this problem, like linguistics, where people made all sorts of claims about theoretical linguistics is gonna discover the innate basis of language, it’s gonna become a model for neuroscience and cognitive science, and none of it happened. And yet people will continue to do research in the field using the same kinds of concepts they did 30 years ago, and they just seem oblivious to the fact that the field hasn’t gone anywhere.

Steve: But think of incentives: I make a big claim, so I get a lot of attention, I get a lot of resources, I become an endowed chair professor, I win some big prizes in my field, and I’m actually retired by the time people figure out that my bold claims of 20 years ago are not true. That’s a very bad system to be in, but it’s a little bit hard to change our system, like it’s hard to avoid that, because it takes so long to verify these scientific ideas.

Corey: And their research program: you can publish papers in them, you can go to conferences, you can get grant funding, so it’s like an institutional support. I thought this was a pathology of the things I just happen accidentally to study as a graduate student, but it looks like it’s broader.

Steve: In the golden areas of physics, it happens that the technology allows very fast checking of the theoretical ideas, where fast could be a couple years. You know, in the early days of particle physics someone would have an idea, and then very quickly they could run the experiment and check it. My view is, once it becomes like, it takes 10 years to plan and build the experiment and another 10 years to run it, that’s basically the bulk of somebody’s career, and then at that point all kinds of shenanigans are going to be difficult to root out.

Sabine: You are right, of course, that experimentalists have entirely different motivations to work on that kind of machine. They’re happy if they get the job done, basically, and I’m very sympathetic to that. But I also think that they make their life a little bit too easy, because it’s perfectly obvious that they kind of use the theorists with their mediocre predictions to advertise their research. So there were all those big promises for what the Large Hadron Collider was supposed to find, none of which has happened; and now the experimentalists are like, you know, they pretend that they had nothing to do with it, while at the same time they said nothing against what cannot be described as other than hype in the media. And they still don’t, right, because they’re still trying to sell now the next larger collider with this reference to the big questions, like what has 95% of the universe been made of. And this again, they pretend they didn’t see it, or I don’t know. And that’s just, it’s not okay. So I blame the experimentalists for either they didn’t know what was going on, which is bad because they should have known, or they knew but they turned a blind eye on it.

Steve: I would say for most of them, they say well, if Steve Weinberg says this is the right way to go, I really trust this guy, he’s so brilliant, he’s been right so many times in the past, let’s just do what he says; and meanwhile I’ve got this horrible problem of actually how to miniaturize these electronics and get them to be radiation resistant so they’ll run in the detector. I guess I  feel more of the blame should go on the theory community than on the experimental community. But I do agree with you that we’re basically in a pickle right now in particle physics. And the thing that I’ve been watching for a long time, really since I was a young professor, is the sort of bleeding off of the best talent away from our discipline and into other disciplines. And, you know, my son is 13 now, and he’s pretty good at math and… I would probably advise him to work on AI, not necessarily — well, of course it all depends on what he’s interested in — but physics doesn’t seem like a discipline right now that’s really charging forward. Now maybe some areas like quantum computation and quantum information are poised to make some big breakthroughs, but particle physics to me doesn’t seem like it’s in a particularly good state.

Sabine: Yeah, I agree with that.

Corey: How do you go forward now? I mean, you’re still a theoretical physicist. With your awareness of the kind of biases in the field, what lessons have you taken for your research to try to avoid getting sidetracked by concepts you think are kind of damaging research?

Sabine: Yeah, so that’s a very interesting question. So one thing is, of course, that in my own research I try to avoid relying on arguments from beauty. I will admit I did use them in the past, so it’s not like I’m a saint or something, I had to learn the lesson too. One of the reasons why I now work on dark matter, for example, is that there you don’t rely on those naturalness arguments, you actually know that there is something that needs explanation, so for me that’s kind of on the safe side. I also, so for a long time I worked on the phenomenology of quantum gravity. I already mentioned that, because I think that in that case one has a really well-defined problem. I’m no longer working on that just basically because I couldn’t get funding, but I still think that it’s a good problem to work on. And I’m also thinking about other areas where arguments from fine-tuning come in, if you know there’s something to be learned from it. So I’ve recently been reading a lot of papers about inflation — so that’s the space in the early universe that we believe led to an exponential increase of scales — and it is usually motivated by arguments from fine-tuning, which is very, very similar to arguments from naturalness. And I’ve been trying to make my mind up about whether that’s a theory that one can trust or not — and it’s complicated, let me summarize it that way. I don’t want to get into it too much, but… So it’s certainly something that has influenced my own thinking, this inflection of arguments from beauty. Yeah, so for what this issue is concerned with the social reinforcement and the cognitive biases, I try to do what I can. When it comes to emergent sociological trends in the community, there is really nothing that an individual can do something about. But you can certainly try to avoid obvious mistakes, like making arguments from authority — like you just said, “If Weinberg said it, then certainly there must be something to it” — so that’s just an argument that, you know, raises an immediate red flag, where I would say well, don’t make it. To some extent, I think you can learn to become more aware of those pitfalls of logical argumentation. I try to do that, you know. I’m probably not the best person to judge myself, [laughs] but I’m trying.

Steve: If I could make a comment on inflation, I think I agree with you that whether inflation “solves” certain problems in cosmology depends a lot on your, again your prior belief on initial conditions and arguments about entropics, what is the most likely state of the early universe. So I think you’re actually asking reasonable questions there. But for Corey’s sake I would say that, if it turns out that inflation is correct — and there are actually non-trivial predictions from inflation which have now been confirmed in our observations on the Cosmic Microwave Background — if that turns out to be true, then you’ll have a case where, in this case, theorists in the early ’80s, basically, understood some very unbelievable phenomena that happened just in the first instance of the universe and actually caused the universe to have its sort of gross morphology or gross shape, spacetime shape. if that’s true, that would be a huge victory of theoretical physics — I mean, I’m not saying that the inflation is right, but if it turns out inflation is right and did actually happen and we become convinced of that, reasonably convinced, then that would be an example of an incredible forward advance or victory of really pure thought, actually, in trying to understand what the history of the universe was.

Sabine: Yeah, sure. So as I like to say, physicists sometimes do the right things for the wrong reasons. I kind of suspect that inflation may be a case like that. It may have been conceived for the wrong reasons, basically to solve the monopole problem — which, if you ask me, is a problem that doesn’t exist because maybe there are no monopoles, so what’s there to solve? — and then there’s the flatness problem and also the horizon problem. I think those were originally the three motivations to look at inflation. And I don’t think those are good motivations. But now this, the data situation I think actually speaks for inflation, though I will admit I am not able yet to make this a very convincing argument, so it’s kind of weak. I don’t think if you want to make a case for inflation you actually need to rely on fine-tuning arguments. And since I think those arguments are not good arguments, I believe that it would be helpful for theory development if we could focus on the sound arguments, where you don’t have to rely on this hand-waving with the prior, stuff like that.

Steve: Yeah. absolutely. I mean, whether it solves any cosmological problems, there’s just the question of did it happen. There is this dynamical phenomenon that could have happened in the early universe, and it leads to very specific signals in the microwave background which we seem to be observing now. When I was a graduate student in the late ’80s and I first learned about inflation I thought, this is amazing, incredible that Guth and these others came up with this; but the idea that we would ever be able to test it, I thought, seemed just like science fiction back in the late ’80s. But now, actually, I would say the experimental situation is pretty strong, I would say, personally, the evidence that we went through an era of inflation is actually pretty strong. Whether it actually solves any of these cosmological problems is a separate issue. It may be just that theories of quantum fields in curved spacetime allow for these periods of quasi de Sitter growth, and we happen to have gone through one. So anyway, so Corey, I would say it’s not at all the best of times in high-energy collider physics, which is the glamour area of our field where most of the money goes, but I would say it doesn’t mean that there hasn’t been progress in theoretical physics in the last 30 or 40 years. Even string theory — which I don’t know if we have enough time to really get into, Sabine, I know you have, you know, very specific opinions about it — even if string theory turns out not to be the right theory of quantum gravity, not to apply to our universe, it did produce lots of really beautiful mathematics and non-trivial insights into areas related to physics. You know, it’s not like people have been completely spinning their wheels. But in the way that she describes — which is, theorist makes prediction of new phenomenon, new particle, and then that is verified by experimentalists, you know, sometime in 30 years — that didn’t happen. In that sense it’s been it’s been a bad 30 years.

Corey: Yeah, I think everyone can see this as far as string theory from the outside. I mean, string theory’s won the Fields Medal, it’s not won a Nobel Prize in physics, and it may never, actually, it sounds like.

Steve: Right. So maybe we should close by, if you want to riff a little bit about string theory. I know we’re running out of time, but Sabine… So you worked in quantum gravity, but primarily on non-string models of quantum gravity, and we could spend a whole hour talking about the sociology of what happened with string theory and particle physics groups and how it took over the whole field, and maybe either has or has not produced great results. But maybe you can just give us as much as you want on that.

Sabine: Well, I did work a little bit on string phenomenology. I worked on models with extra dimensions that were largely motivated by string theory, but I never really worked on the theory development or something like that. So a lot of people tend to think that I must be a hater of string theory, but let me assure you that isn’t so. I do think that string theory has really good motivations. We already spoke about quantum gravity, so we know that we need such a theory to fundamentally make sense of nature, and string theory is an approach to do that. So I think it does have really good motivations. But then the devil’s in the details, right? So I feel like this theory has run into conflict with experiments so many times and then had to be fudged, that at this point it’s so artificial one can’t really trust anything that comes out of this field. You said that yes, there have been a lot of mathematical insights that have been derived from string theory. Those have also, to some extent, informed certain parts of physics. The people who actually work on those areas, mostly condensed matter physics, are not terribly enthusiastic about it — at least that’s my interpretation when I talk to them. But yes, you’re right, it’s not that nothing came out of it. There have been, a few things have been coming out of it, but what has come out of it really has told us nothing about this question of what is the fundamental theory of spacetime. It’s more general insights about the structure of quantum field theories that have come out of it.

Steve: All right, so I think we’re out of time. I want to thank you for spending this hour with us, and I hope we can bring you back on the show at some point. Would that be okay?

Sabine: Yeah, that would be fine with me.

Steve: Great. Well thanks a lot. Bye.

Sabine: Okay, I wish you a good day.