Sean Carroll's Mindscape: Science, Society, Philosophy, Culture, Arts, and Ideas - 245 | Solo: The Crisis in Physics

Episode Date: July 31, 2023

Physics is in crisis, what else is new? That's what we hear in certain corners, anyway, usually pointed at "fundamental" physics of particles and fields. (Condensed matter and biophysics etc. are just fine.) In this solo podcast I ruminate on the unusual situation fundamental physics finds itself in, where we have a theoretical understanding that fits almost all the data, but which nobody believes to be the final answer. I talk about how we got here, and argue that it's not really a "crisis" in any real sense. But there are ways I think the academic community could handle the problem better, especially by making more space for respectable but minority approaches to deep puzzles. Blog post with transcript: https://www.preposterousuniverse.com/podcast/2023/07/31/245-solo-the-crisis-in-physics/ Support Mindscape on Patreon: https://www.patreon.com/seanmcarroll

Hello everyone, welcome to the Mindscape Podcast. I'm your host, Sean Carroll. Physics. It is in a crisis. We are told this. I've been told this on the internet, on podcasts, even in books, the crisis that we're in physics right now. And that's sad to me to hear the physics is in a crisis. I grew up wanting to be a physicist. I am now a physicist, among other things. Physics is my life. I love it very much. It makes me worry to hear. that the field would be in a crisis. What does that mean? Did the laws of physics stop working? Did physicists go on strike? What exactly is going on? So I am here to do this solo podcast to tell you my particular views on the crisis in physics, which is that there is not a crisis in physics. That is what I think anyway. I will give you my reasons for thinking that. You can make up your own mind. I first want to say, though, that it makes me sad, that I have to be on that side. You know, when I was growing up thinking about being a physicist, I certainly imagined that in the fantasy future life I had for myself, I would be a radical physicist, a heretic, right?

tearing down the stuffy establishment notions and replacing them with my own creative impulse and so forth. And it took quite a bit of education and years and thinking to realize that being a heretic is super hard work. It's really, really very difficult. You know, the heretics who are out there will often point to people like Galileo and Einstein as their predecessors in heresy. What they don't tell you all the time is that nobody understood the physics of their time better than Galileo and Einstein. These people maybe had opposition from the establishment, absolutely, no doubt about that. They would grumble about that opposition sometimes. but if they did overthrow the established view,

it was very much from working inside the system. They first mastered what everyone else understood and they built upon it, and building upon it sometimes means tearing something down and building something better. It's not that they just wandered in off the street with their own kooky ideas and succeeded. In the real world of the history of science,

especially in fields that are mature fields, where we understand the basic ideas in many different ways, where there are a lot of established results, etc., it's really, really hard to be a good heretic, even though it is romantic and attractive. I would like to be the heretic. But then I look out at the information landscape, at what people are being told about physics.

And what I find is there is far too much heresy out there. It is far too easy for the person on the street who just wants to know, what the universe is like to hear the point of view of the heretical fringe rather than the establishment. Just the other week, we heard a paper that came out with a press release claiming that the universe is really twice as old as anyone thought it was. Complete and utter nonsense, sadly, but people who really should know better jumped on that as evidence that, ah, see cosmology, it's not really as settled as we think. Anything can happen. I've been skeptical all along. I have had my suspicions and now I see them confirmed, right? But it's,

it's just nonsense. It was just crack pottery. And so I feel that my own job is something different. You know, I've mentioned before that I've heard this podcast criticized for not being edgy enough. And I wear that as a badge of honor. My goal is never to be edgy. Maybe it will be edgy by mistake or because that's where we go. But my goal is just. to be correct. Or at least my goal is to help you, the listener, and me, the podcaster, in our mutual goals of becoming more and more correct, more and more right about the real world. Sometimes that involves being edgy and creative and rebellious and heretical. Sometimes it involves understanding why the establishment has the point of view that it does.

So in the solo podcast, I want to cover what I think about the claims that physics is in crisis right now. I'm not going to pick on individual people, because that's not what we're here about. I'm going to pick on individual ideas. And what I think is true is that because I do want to give you the ability to make up your own mind, whether or not you agree with me, in order to understand whether physics in crisis it's necessary to understand where physics is. So a lot of this, I predict overly long podcast, is going to be me trying to explain the basics of how we got here and where we are right now, which is a lot, but I think it's kind of worth it. So maybe the people who are experts in modern physics

will find this a bit of a review for most of the podcast, but hopefully we'll shed light for those of you who are not in the trenches here. Let me take this opportunity before we dive into it to mention that we have a Patreon. You knew I was going to say that, right? Patreon.com slash Sean M. Carroll is where you go to give support to the Mindscape podcast. I mentioned on Twitter, and I should mention again, that we've been experimenting with.

with this new thing where at the end of every podcast, I do a little reflection video. So video or audio, either way, you can listen to it, me just for a couple of minutes saying what I thought about the podcast or explaining why I had that particular guest on, et cetera. I have put up one example on the YouTube's. If you go to my YouTube channel, it's not hard to find, Sean Carroll, it might be Sean M. Carroll, who knows, but you can find it. You're very smart. You will find a little free sample. I showed up, I put on YouTube the reflection video I did after the Tim Maudlin podcast if you want to see the basic spirit of what it is like. I don't do reflection videos for the Ask Me Anything episodes. That would be too much of my own voice, but I

figure for this solo episode, maybe I will do a little reflection video. Maybe I will reveal some secrets that you don't get to hear if you're not a Patreon supporter. Who knows? You know, are you willing to take that chance? That's the real question. And, With that, let's go. A good place to start talking about the crisis in physics is in a tweet from Martin Bauer. Martin is a very good physicist and a very good Twitter follow. If you are still following people on Twitter before it completely dies, I encourage you to follow Martin M. Bauer. And what Martin says is he says, the crisis in particle physics.

He found an article which he thinks is accurate. and intriguingly portraying the crisis that we have in particle physics or fundamental physics. And so he goes over in what ways the crisis is manifesting itself. It is that high energy theoretical physics is in trouble because it's become too specialized, because there is no clear theory that is leading the pack and going to win the day, because physicists are willing to wander away from what the data are telling them, focusing on speculative ideas, that the system suppresses independent thought, that theorists are not interacting with experimentalists, and so on.

There's a long list. Now, I've been in this discourse too long for a long time, so I knew, by the time I was, you know, at the third or fourth tweet in this thread, I kind of figured out the joke. And the joke is, at the very end, Martin reveals that indeed, all these quotes are from a very long like 100-page article on the crisis in particle physics from the year 1977. That's the joke.

Because everyone always thinks that their field is in a crisis, right? Or at least there's a certain kind of person who will always think their field is in a crisis, no matter what state it's actually in. To many of us now, looking back, the mid-1970s are like the golden days of particle physics and quantum field theory, right? we were finally figuring out gauge theories in confinement and the standard model and chiral symmetry and things like that. And instantons, not perturbative, you can go on and on, like the 70s or the golden age. And here is this person making all of the same complaints about the state of physics that we are hearing about it now.

So how can this be true and how should we think about what it means right now? Because you are hearing people who are pretty respectable as well as, as completely fringy lunatics, complain about the current state of physics. And one thing I want to say is that, even though I am going to be a little bit of an apologist for the current state of physics, I'm certainly not going to be a complete apologist. I have my issues, and I would like to criticize physics and the physics community. I'm happy to do that, but I want to do it in a nuanced way. And when I, for example, let's take the foundations of quantum mechanics, right? You will have heard me say that it is a shame, an embarrassment, a scandal.

that the foundations of quantum mechanics are so thoroughly ignored by the physics community. But what you won't hear me say is it it's because there's a conspiracy, because they are afraid of their cushy positions, because even because they're not working in good faith, they're too afraid to face the truth. None of those things am I going to say. What I'm going to say is they're wrong. The physics establishment is wrong to not place more emphasis on understanding

the foundations of quantum mechanics. And here are my intellectual reasons why they are wrong. I'm not trying to question their morals or their intentions or their integrity. I'm trying to give a better argument. And that's fine. And so I'm going to try to give a good argument throughout this podcast about the ways in which I think that we can do better than what we're doing right now in contemporary fundamental physics. But most of it, I'm just going to be saying here is why we are doing it in this particular way. And it actually kind of makes sense. So the big, big, big, big reason why we're in so much apparent trouble in physics is because physics is too successful. This is the irony. Someone should come up with a fancy name for this particular

ironic situation we find ourselves in. Physics for the first time in human history is too good at understanding the physical world. And I want to be very, very specific about what that means because there's certainly plenty of things we don't understand, right? But we understand a lot, and that is getting us into trouble as physicists, because progress or even the illusion of progress is easier to perceive when we're not done yet, right? When there's things that we don't understand that are staring us right in the face and we can try to come up with explanations and test them right away. That's not the situation we're in right now. But let's be careful about this. In addition to my physics job, I am now a professional philosopher, so I am what, obligatory,

obligated to be careful about defining my terms and things like that. So when I say that physics understands things, what do I mean? You know, there's a certain kind of response that I'm just going to dismiss because it's a misunderstanding of what I'm trying to say. When I say, like, we understand gravity. Einstein in 1915 gave us general relativity. It fits all the data. It made predictions. They all came true. It's well understood. And there are people who will say, yeah, but we don't really understand gravity, man, like what is space time? Okay, you know, I get that. I'm not sure that there is necessarily a sensible answer to that one, but it's not what I mean, okay? So I'm just putting that aside. By me, talking about understanding what I mean is we have some well-defined

physical theory that fits all the data and we think is accurate and true in its domain of applicability. So let me be even more specific than that. We can distinguish between different levels of understanding that a physicist would recognize. We can talk about what you might want to label strong understanding. A strong understanding is what we have, for example, with general relativity. There's a unique, well-tested theory. It accounts for all of the data that we have within the purported domain of applicability of the theory.

So the theory might say, well, I just don't know what to say about something. So general relativity doesn't know what to say about the singularity at a black hole or the Big Bang or, you know, small-scale quantum gravity stuff. But in the regime where general relativity purports to make predictions, all of those predictions are 100% compatible with the data as far as we know right now. And there are no real competitors, right? There's no people working on alternatives to general relativity that would truly displace general relativity. There are plenty of people, including myself, who've worked on modifications of general relativity, extensions and so forth, or even theories that would

underlie general relativity in some sense, but general relativity will still be there. It will always be there. It is just like when we talk about Newtonian gravity or Newtonian dynamics, the fundamental ontology, you know, the fundamental deep-down framework of what that theory took to be real and important, turns out not to be there, right? We don't have an absolute space, absolute time, action at a distance, any of those features of Newtonian gravity. But the theory remains accurate in its domain of applicability. So Newtonian gravity didn't go away. If you want to fly a rocket to the moon or catch a baseball,

Newtonian gravity is the theory for you. So general relativity is like that. It's not going to go away. That is what I am labeling a strong understanding at the level of physics. Then we might talk about weak understanding. Okay, we have a weak understanding when there are situations, for which we have more than one theory. We have several theories that in principle can account for the data,

but at the moment we cannot discriminate between them. Plenty of examples of this, okay? You know, a really good example actually is quantum mechanics, the foundations of quantum mechanics. That's the conundrum we find ourselves in. Back in the 1920s, we didn't actually have any single very good theory of quantum mechanics. We had some ad hoc rules that grew into what we call the Copenhagen. interpretation. But starting in the 50s with Bohemian mechanics and many worlds and then also

objective collapse models, et cetera, we have now a handful of perfectly good physical theories that all give the same predictions in the data that we have so far collected. We can hope, and in some cases it's clearly true, that there will be deviations in their predictions down the line, but so far in the data we've actually made, these theories make the same predictions. So that's a weak understanding. We kind of have theories that might be right, but we don't know if any one of them is right, or we don't know which one is right or even if the one that will turn out to be right is one that we haven't invented yet. And that's also true not just for quantum mechanics, but for other famous examples like in cosmology, dark matter, dark energy.

These are things that cosmologists talk about all the time. And you have to be a little bit careful when you talk about how well we understand these things. It is too easy to say, well, 95% of the universe is something we don't understand at all. That's just wrong. That's not something that you should say. 95% of the universe, which is the 70% that is dark energy, the 25% that is dark matter, are things that we haven't pinpointed yet. But that is very, very different from saying that we don't understand them at all.

On the one hand, we know an enormous amount about their properties. We know how much dark matter and dark energy there is. We know where it is. We know how it behaves to a very good approximation. And we have multiple theories that could account for what is going on in both cases. For dark matter, we have wimps and axions and plenty of other ideas. For dark energy, we have the vacuum energy, the cosmological constant, which is the same as the vacuum energy. Also dynamical quintessence-like fields and so forth.

But we don't know which if any of those are right. So I would qualify that as a weak kind of understanding. There's something that we understand about the phenomenon. We have more than one theory that can fit the data, but we have not yet figured out which, if any, of those theories, is right? And then there are cases where there's no understanding, so neither strong nor weak understanding, right? We don't have any solid theories that account for the data. A classic example right now in modern physics would be what happened at the Big Bang. We just don't know. What happened before the Big Bang? Is there even before a Big Bang? bang. We just don't know. We have to be honest. We have kind of hand-wavy models. Again, I'm responsible for some of them, but we don't have anything that rises to the level of a completely convincing theory that, you know, if we discovered a wimp or an axi on tomorrow, you go, oh yeah, okay, good, that's the answer. We've been waiting to figure it out. Now we know it. There's no such theory on the market now, which even if we found evidence for it, when it comes to what happened at the Big Bang, we would instantly jump on that bandwagon because the theories are

half-baked. They're in the situation where maybe quantum mechanics was in 1925 or something like that. And the history is that most of the time in the history of physics, there were big, obvious things you could point to where we had no understanding, things that were very well within the realm of experimentally accessible phenomena. You know, today we say the Big Bang is something about which we have no understanding, but you can't see the Big Bang either. right? It's a very long time ago. And more importantly, there is the, when I've talked about the Big Bang now, I mean literally the moment, okay? Not the Big Bang model. The Big Bang model is what happens over the next 14 billion years as the universe expands and cools from an initially hot dense state and galaxies coalesce. All of that is the Big Bang. That's in 100% good shape. What happened at the moment of the Big Bang is something we have no understanding about. But it is precisely because of features right after the purported. initial moment that kind of make it hard to see what happened at that moment. The universe basically is locally in thermal equilibrium. It's not really in thermal equilibrium because the universe

is expanding, but the hot dense plasma is, you know, kind of featureless. There's not a lot there. There's a little bit there, of course. We look at the temperature fluctuations in the cosmic microwave background. We learn a lot from them, but not as much as we would like. And certainly nothing that gives us direct evidence about what happened at the Big Bang. What I'm trying to get at in telling you all this is to contrast it to what the story would have been like 100 years ago, right? A hundred years ago, we knew about protons and neutrons and nuclei, but we had zero idea what held those nuclei together. We had no understanding at all of what we would now call the strong and weak nuclear forces. A hundred years before that, we didn't know what light was. We thought it was a wave,

but we didn't have Maxwell's theory of electromagnetism to tell us it was a wave in the electromagnetic field with equations and all that stuff, okay? And of course, even easier claims to point to earlier in the history of physics. So the overwhelming story of the history of physics is there are certain things that we had some understanding of, but very obvious, pointable to phenomena that we did not have any understanding of at all, and we were working on that. We were trying to come up with theories to explain that. And the real weird thing about the present moment is that we have at least a weak understanding, in some cases a strong understanding, of everything that we are able to experimentally probe directly. Okay. We have a strong understanding of everything nearby. So as I very often said, the laws of physics underlying everyday life are completely understood. But what I mean by that is you and all the atoms you're made out of and all the forces holding them together and pushing them around, as well as everyone else you've ever met and the floor you're walking on and the air around you and the sun shining and the earth and the moon and the stars, all of that, we have a strong understanding.

We have a theory that is right that explains what's going on there. And we have at least a weak understanding of every experimentally accessible phenomenon. We don't understand, as I said, dark matter and dark energy at the strong level. We have a weak understanding of them. But there's sort of nothing that is experimentally accessible to which we have no understanding at all. That's new. That is a new feature in the history of physics. So I wanted to, if you will indulge me, explain how we got there a little bit.

This is going to be sketchy because it's basically the whole history of physics, right? Or at least of modern physics. Let me pause before I dive into it. to mention one other things, I don't want to forget to say it. You know, we had the 1920s in physics. It was a pretty remarkable decade. It wasn't just quantum mechanics that came together, but there were, you know, really important experiments

and radioactivity and things like that, not to mention the discovery of the expansion of the universe. And if, as a whole, you think about the first half of the 20th century, okay, between the years 1900, which very, very, conveniently was the year that Planck put forward his hypothesis of discrete packets of energy being given off in black body radiation, which launched eventually into quantum mechanics, to 1950, where, you know, we had built the atomic bomb. I forgot to mention in the intro, you know, if you've seen Oppenheimer recently, you know that physics does matter for our everyday lives, as well as

for our intellectual lives. That's an enormous amount happened over the first half of the 20th century. invented special relativity, general relativity, quantum mechanics, quantum field theory, particle physics, the big bang model, the expansion of the universe, all this stuff, okay? It was an absolutely unique era in the history of physics. It was so much stuff going on that in the second half of the 20th century, when we think about fundamental physics, let me pause once again, sorry about this. Again, something I forgot, I should write better notes for these solo episodes, but I forgot to say this also. To the extent, that there's supposed to be a crisis in anything, it's not in physics. It's in a particular little slice of physics, what you might call fundamental physics, high energy physics, particle physics, something like that, okay? There's plenty of other areas of physics that are going on just fine with nothing even arguably crisis-like about them, whether it's plasma physics or atomic physics or molecular physics or biophysics or even astrophysics, for that matter, condensed matter of physics, soft condensed matter, hard condensed matter, whole bunches of things

that are going along just fine, more, you know, fun discoveries than ever. So when people try to say that there's a crisis in physics, they're showing that they're a little bit favoring in their attentions, a certain kind of physics. Now, that happens also be my kind of physics, so I do care about that. But there's a simple glib answer to the crisis in physics question, which is you've got to pay more attention to the rest of physics. But still, it's important that fundamental physics be understood and hopefully moving forward. So that's what we're talking about in this podcast today. So as I was saying about the second half of the 20th century, in fundamental physics, it was a very exciting time.

Black holes were thought about and discovered. We put together the standard model of particle physics, and we built these giant particle accelerators and discovered all these wonderful particles. We found the acceleration of the universe. in 1998. But thinking back on it now, since we're no longer quite in that half century, an argument could be made. I'm not sure how good an argument it is, but I think it's a plausible one, face value believable, that all the excitement of the second half of the 20th century in fundamental physics was really cleaning up and finishing the project of the first half of the 20th century. You know, the first half the 20th century, we already had quantum mechanics and quantum field theory.

In some sense, putting together the standard model was just figuring out what is the right quantum field theory to actually describe the world. We already had general relativity, in some sense, figuring out that there were black holes and the cosmic microwave background and things like that, was really taking general relativity seriously and understanding what it predicted. It was by all possible measures and enormously exciting time in physics, the second half of the time. 20th century, but it was also very much building on the excitement of the first half of the 20th century. You know, we talked about the fact that people always find that their own era is in crisis or whatever. Richard Feynman, who we now think of as this, you know, brilliant, very important foundational physicist kind of lamented that he wasn't around for the real excitement in the 1920s,

right? But anyway, it was a very exciting time and a lot of progress was made in the second half of the 20th century. Now we're in the first half of the 21st century, and the going is getting a little bit slower because at the very simplest level, we finished cleaning up and putting the dots on the eyes and crossing the T's of the tremendous revolutions of the first half of the 20th century. And the reason why I want to emphasize this is because that first half of the 20th century isn't what we should expect. We were spoiled. It's usually not that much going on at the same. same time, not quite so many revolutions per decade in fundamental physics. I think actually, if we're honest, even though I have made and will continue to make this argument that we're in a

slightly special situation right now because we have a theory that fits all the data, if you put aside the actual theories that we have and just think about the rate of progress, I think that right now we're in a much more typical rate of progress in fundamental physics than we were in the 20th century, especially that first half. So we have to sort of, you know, accept that it's not always going to be like the first half of the 20th century. That was a very special historic time. Maybe there will be times in the future that are equally exciting, but my point is that you can't just rely on it to be that exciting every single half century. Okay, that was a little background, but now I want to go through the specifics. I want to be a little bit more specifics about what

this understanding is that we currently have, because that's going to be a important for understanding why it's so hard to move beyond that understanding. So we have space time, right? And again, we're very, very sketchy. You're not going to learn this in any comprehensive way from this particular podcast, but we have the idea that space and time are glued together to make space time. This was the theory of relativity. Einstein put, again, the finishing touches on it in 1905, arguably maybe the finishing touch was 1907 when Minkowski pointed out that you should think of special relativity as a theory of spacetime. Einstein was reluctant to go along with that, but he eventually realized that was a very good idea. But he was building, Einstein was building

on progress that had been made at the end of the 19th century and even before 1905. People like Lawrence and Fitzgerald and Pongruet and so forth had really shaped up a lot of what you needed. The ingredients were there to put them together into the theory of special relativity. And it was Minkowski who really said, think of this as a theory of space time. And then in 1915, Einstein, who would by that point very much come on the bandwagon of thinking about space and time as unified, rather than separate, as they were in Newtonian physics, said, and space time can be curved, and it's that curvature that is gravity. And that was the theory of general relativity. Both of these theories special and general relativity survive to the present day. Special relativity is the theory

of how space time is when gravity is not important, when the curvature of space time is essentially flat. General relativity is the theory that includes gravity, makes predictions like the Big Bang, black holes, and so forth. The next ingredient is quantum mechanics. Again, the first hints in that very turn of the century, but it wasn't really made quantitative in a convincing way until the 1920s. with matrix mechanics from Heisenberg and his friends, Wade mechanics from Schrodinger, the Copenhagen interpretation was eventually dominant. It came to be the way that people thought about quantum mechanics.

You've heard me mention that we're not done yet with quantum mechanics, as Einstein also thought at the time, but I'm not going to go into that here. I just point out that quantum mechanics, you know, if anything, it's super impressive how quickly people jumped on the quantum bandwagon. If you go from 1900 to 1927, 1927 is the year of the Fifth Solve conference, which is sort of the really solidification of our contemporary understanding of quantum mechanics. Given the absolutely revolutionary nature of what quantum mechanics is and how much of a departure it was from the Newtonian paradigm, which had been incredibly successful up to then, I give just immense credit to the physicists of the time who were willing. willing to throw out so much that had been successful, the whole paradigm of deterministic

Laplaceian evolution that have been set up by Newton and replace it with quantum mechanics. So anyway, kudos to them. I think the history will recognize that. They don't need my help. But then, of course, this quantum field theory, I have to emphasize that quantum field theory is not a successor to quantum mechanics. You know, sometimes this is a little bit confusing. So quantum mechanics is a replacement for classical mechanics. Okay, but it is a framework in which you can study many different kinds of systems, the harmonic oscillator, spins, what have you. Field theory is just one of those systems that you can study within the framework of quantum mechanics, and quantum field theory is precisely the quantum

theory of fields. It is a quantum theory. It is underneath the umbrella of quantum mechanics. It is not separate from it or a replacement to it. And quantum field theory is, 100% compatible with special relativity. It is marginally compatible with general relativity. I'll get to that in a second, but you know, sometimes people say, is it possible to reconcile special relativity with quantum mechanics? And you have to say, yes, that was done in the 1930s, basically, right? So you got to catch up. Yes, relativistic quantum field theory is our best current understanding of fundamental physics. And it 100% includes the lessons of special relativity. And the whole point of quantum field theory is to say that there aren't particles out there, right?

The world is made of fields fundamentally, whether you're talking about photons and gravitons from the electromagnetic field and the gravitational field, or whether you're talking about electrons and neutrinos and quarks. Those are all based on fields. That is to say, something that fills all of space time, takes on a value at every point in space time, and has some dynamics. They can vibrate. they can oscillate, and we perceive those oscillations as particles. Because why? Because quantum mechanics.

It is exactly the same kind of mathematical thing going on when you look at an emission of photons from an atom, right? The whole thing that inspired the original quantum revolution, one of the things, was that the wavelengths of light coming out of atoms are quantized, are discrete, certain kinds of frequency. are seen, others are not. You see spectral lines. Why? Because the electrons fall into orbitals that have different discrete energies. And what you're seeing when you see those emissions from atoms is an electron jumping from one discrete atomic orbital to another one. But the crucial thing here is quantum mechanics isn't a theory of pixels or quantum or anything like that, right? It's a theory of wave functions that are perfectly smooth. There's a equation for them, the Schrodinger equation, and when you saw the equation, just like there are

different frequencies or fundamental and then overtones when you pluck a string on a violin or a guitar, there is a discrete set of solutions to the equation that you get for the electron in the atom. That's why you see the discreetness, not because it's built in into the theory, but because it comes out in the particular solutions. Exactly the same thing is going on with quantum field theory. Why do you see particles? There's no particleness in the fundamental definition of the theory. It comes out because there are solutions to the theory that come in discrete buckets, one that has no energy at all, and we call that the vacuum and there are no particles. Then there's a set of solutions that have a little bit of energy, and we call that a one particle solution. Maybe the

particle is stationary, so it has as low as possible energy, maybe it's moving, so it's a high energy particle, but that's one set of solutions, and there's another set, which is two particle solutions, and so forth. All of the talk we do about particle physics and so forth is a language that we use to describe the solutions to the equations of quantum field theory. So the underlying language is fields, what you see when you observe them, are particles. And there's one more thing I want to say about quantum field theory that is going to be crucially important for our story, which is the idea of effective field theory. This came much. much later in the 60s and 70s from Ken Wilson and other people.

And the idea is the following, that as it was understood back in the 30s and 40s, if you just do quantum field theory, let's say quantum electrodynamics, right, QED, so that's the theory that has electrons and positrons and photons. Or more accurately, it has the fields underlying them. So it has the electromagnetic field, the electron field, the positron field, And QED, quantum electrodynamics, is a theory of their interactions. And people very quickly wrote down what they guessed such a theory would look like, and they very quickly ran into trouble.

You could do an approximation to what the theory was telling you, and it seemed to be kind of like the right answer. But then you go beyond that approximation, and you get infinity. You get an integral, and you do the integral, and the answer is infinitely big, and that sounded bad. So people like Feynman and Tominaga and Schwinger and Dyson in the 1940s and 50s figured out how to renormalize the quantum field theory. And this was something which, in my personal opinion, was always presented as more weird and mysterious than it should be. To me, it's just a particular way of taking a limit, which is a very standard calculus-based move.

If you do things naively, you get infinity. what you really want to do is subtract infinity from infinity and get a finite answer. Now that's by itself. If you just say, do that, say here's an infinity, here's another infinity, subtract them. Tell me the finite answer. That's an ill-defined problem. You can't do that. But under certain specific physical conditions, when you have a well-defined idea of what it is you're after, you can turn it into a well-defined problem. You can take the limit as one quantity is getting bigger and bigger, and there's another quantity that's getting bigger and bigger, and you let them go to infinity individually,

but subtract them off and get a finite answer at the end of the day. So I was never worried about renormalization as an idea, but nevertheless, it was a hint that there was something maybe sketchy going on at the foundations of quantum field theory. And so Ken Wilson in the 1960s, if you think about that moment in history, it was just the beginning of people,

trying to do slightly larger-scale computer work than they had done before. You know, there were computers, but they were used for pretty simple things. The idea of simulating a quantum field theory on a computer was not well-established at all. And that was one of Wilson's projects. He started thinking about this. And what he realized is, you know, you can just do this most straightforward thing. Or you take all of space time and you discretize it. So you say, rather than there being a smooth,

space time underneath my feet. I'm going to take a lattice, a series of dots with a certain distance between them. I'm going to approximate my quantum field theory by doing some finite difference mathematical manipulations rather than a smooth differential equation kind of thing that the theory itself tells you to do. So this wasn't supposed to be replacement. It's just a calculational tool. You can do what is called lattice quantum field theory as an approximation, and then you sort of do it for different sizes of the lattice, and then you take the limit as the lattice size gets arbitrarily small. It goes to zero, and then presumably you recover the smoothness of the original theory. What Wilson realized is that when you do this, when you do

the first step in putting the theory on a lattice, all the infinities disappear right away. The reason why there ever were infinities, you can think about in terms of Feynman diagrams, right? Feynman, one of the things he did was figure out a way to calculate scattering processes in quantum field theory by writing down these little cartoon pictures of particles bumping into each other. And one of the features of Feynman diagrams is they help you see where the infinites might be lurking. namely the infinities lurk in the loops in the Feynman diagram. You can imagine in your head drawing sort of different stick figure Feynman diagrams for electrons and positrons and photons bumping into each other and scattering and going off their separate ways. The simplest diagrams will be what are called tree diagrams.

They just have some lines and you cannot, with your finger, trace a closed loop in any of those lines. It looks more like a tree, okay, but then there are more complicated diagrams, more topologically involved ones, where somewhere in the middle of the diagram, there is a loop that you can go around with your finger forever and ever if you wanted to. And the rules that Feynman wrote down say that what the diagrams are are ways of representing individual numerical contributions to the final answer that you're trying to get. What is the probability that this electron is going to scatter off of that positron, for example? And so when you have a loop, you go through the math, when you figure out when you ask the question, well, okay, how much energy or how much momentum does this particular particle

in the loop have? The answer is it is not constrained. You can have an infinite series, an infinite sequence of different possible momenta that any one particle in the loop can have as long as you correctly balance it against all the other particles in the loop. At every vertex in the diagram, energy is conserved, but we think about a certain undefined or unconstrained momentum flowing around the loop, literally called the loop momentum. It's not very clever.

And what Wilson realized, people knew this, but he sort of appreciated the implications of it, is that the reason why you had infinity in the first place is because you are considering momentum in the loop of your Feynman diagrams that were arbitrarily large. You took the momentum from zero to infinity and you added them altogether. And in quantum field theory or in quantum mechanics more generally, high momentum and high energy correspond to short distances, right? Basically because everything is a wave at the end of the day and high energy waves are those with short wavelength.

So high energy waves are those that can probe short distances. And so when Wilson tried to put his quantum field theory on a lattice in order to do a computer simulation, all the infinities went away because he was not including arbitrarily short distances. He had gotten rid of those arbitrarily short distances by putting the theory on a lattice. And you know, you or I would say, okay, that was good for our computer simulation, so be it. What makes people geniuses is they can see the implications of these things that are put in front of their noses. And Wilson said, well, why was I ever of the opinion that I knew what was happening at arbitrarily short distances anyway? What right do I have to say that I understand physics as length scales go to zero?

I mean, after all, I don't know whether he said this out loud, but certainly this is something we would say today. there's something called the Planck scale, right? The length scale, I never remember what it is, 10 to minus 35 centimeters or something. A length scale that seems to be the length scale of which quantum gravity becomes important. Maybe space time itself is not really well defined on those scales.

So I don't know what's going on. I don't know what new particles are there. There could be very, very heavy particles. A heavy particle is a, so a massive particle has a lot of energy because it equals MC squared. So the wavelength associated with a very massive particle is very short. So maybe there are virtual, very high mass particles that I don't know about that could change things. And the brilliance of Wilson was to realize it didn't matter what happened at the very short distances, the very high energies.

That is both where the infinities were lurking, but also a place where we have no right to say we know what's going on. So Wilson says, let's be honest. Let's ask whether we can do physics at low energies and long wavelengths without specifying what happens at high energies. And, you know, maybe in some other possible world, the answer could have been you can't. You need to know what's going on to short distances to know what's going on to long distances.

But in our world, that turns out not to be the case. So Wilson says, let's just be explicit. it. Let's be honest. Let's say we have what we now call an ultraviolet cutoff. We have an energy above which we have no idea what's going on, below which we're going to try to have a theory that describes what is going on. So the ultraviolet cutoff separates the energy scales or the length scales that we do claim to understand low energies, long wavelengths, from those that we don't claim to understand, short distances, short wavelengths, high energies. And Wilson showed that this was sort of in keeping with the whole idea of renormalization, because you might

say, all right, if I ignore what's going on at high energies, well, I could get in trouble because things could happen at high energies that might be important. But Wilson was able to show that, yeah, things can happen. But all that they do, as far as the low energy dynamics is concerned, is give you certain definite numbers for what the low energy. equations of motion look like. So the mass of a particle, the coupling constants like the fine structure constant or the strong interaction fine structure constant, the expectation value of the Higgs boson, all these different parameters of particle physics, they do depend on your ultraviolet cutoff, but there's no extra information that comes in, or at least there's a little bit of extra

information, but it also can be absorbed into what we call irrelevant operators. There's a whole song and dance. This is the whole story, which is long and involved and beautiful, of effective field theory. The idea of an effective field theory is, you can do quantum field theory perfectly well at energies below the ultraviolet cutoff without knowing what the physics is above the ultraviolet cutoff, even if space and time themselves exist above the ultraviolet cutoff. You don't need to know that. It will not show up in your low-energy effective quantum field theory. So this and other things, and not exactly this, but related to things, won Wilson the Nobel Prize and the undying reverence of modern quantum field theorists. By the way, if you're interested

knowing why I am so hyped up on this, this will be a big part of volume two of the biggest ideas in the universe. Remember my book series, Volume 1, Space Time, and Motion is all about classical physics, including relativity. Volume two will be quanta and fields. So I do a little bit of quantum mechanics, but mostly it's quantum field theory and particle physics. And I place a huge amount of emphasis on effective field theory, vitamin diagrams, and renormalization. So remember the spirit of the book is I give you a little bit of the equations, so you can actually see them in action, and you can see what it means to say there's an ultraviolet cutoff, the dynamics don't depend on it. There is a renormalization that will tell you how to change your parameters so that

the physics is independent of the value of the ultraviolet cutoff, etc. Sadly, the book's not going to be out until early next year, but keep your calendars ready for 2024 when the biggest idea of volume two comes out. All of this will become much clear. Okay. This is what we call a good news, bad news situation in the game, okay? Because what's the good news? The good news is that effective theories are effective. In some sense, we were already using that fact before we knew it. You know, the first field theory, the first modern quantum field theory, is written down by Enrico Fermi in his theory of beta decay. And the fields that he was considering were protons and neutrons and neutrons. These days we know, number one, that protons and neutrons

are not elementary fields, you can still treat them as fields and the particles as vibrations in the fields, but we have a deeper picture in which they are quarks and gluons and so forth. And also we know that the beta decay interaction is an example of the weak interactions mediated by W bosons. Fermi didn't know any of that. Why was Fermi in the 1930s able to invent such a good theory without knowing about quarks and gluons and the W. bosons. The answer is that secretly he has an effective field theory. His theory is valid below a certain energy scale. The thing about effective field theories is they will be valid below the ultraviolet cutoff. They may or may not continue to be valid above the ultraviolet cutoff. When you go above

the ultraviolet cutoff, you are open to the possibility that very new physical phenomena kick in, maybe new particles, new fields, maybe even something that is not in the realm of quantum field theory at all. That's the power of effective field theory. It doesn't need to assume that the fundamental nature of reality is a quantum field theory. The low energy, visible nature of reality, will still be very well described by a quantum field theory. Even if it's strings or loops or triangles or whatever at the deepest level, quantum field theory at the effective level will be valid below the ultraviolet cutoff. And that's exactly what Fermi had stumbled upon. His theories valid up until you get to the scale of the W. boson, which is 80 billion electron bolts, which is way higher than they had

access to in the 1930s. That's the good news. The bad news is the same news. The same phenomenon that makes effective field theories so effective at low energies, and they're the theories that, you know, we test the large Hadron Collider, et cetera, makes our questions about what goes on past the ultraviolet cutoff very, very difficult to answer. Because unless you literally build a particle accelerator and smash particles together at energies, scattering energies higher than the ultraviolet cutoff, your effective field theory is going to give you whatever answer you want. Sorry, it's going to give you the answer you need. It's going to give you the correct answer. Okay? So there's a phenomenon called decoupling. You can very easily imagine that there are high energy processes, heavy particles, new symmetries, new forces, discrete spaceline, whatever you want above the high energy ultraviolet cutoff. And you can't tell. You can't distinguish between any of those possibilities just by doing experiments at lower energies. And by lower energies, we mean lower than the high energy.

energy experiments we've done, you know, several trillion electron volts now with a large Hadron Collider. So effective field theories are great because they help us describe the world very, very accurately. They sadly indicate why it is hard to move beyond our current best understanding, because indirect evidence is very, very limited in what it can possibly tell us. And direct evidence is very expensive to get. You have to build a giant particle accelerator. Anyway, that's a very important part of our story because that's an important part of why physics right now is having trouble making wonderful, fast, dramatic leaps in progress in fundamental physics because effective field theories are making it too accurate to describe the world right now at the energies that we have access to. Okay, let me zoom through the rest of the story I wanted to tell you about contemporary physics. So it's not just quantum field theory. That's obviously the centerpiece of everything, but there are particular kinds of quantum field theories.

Quantum field theory, as we see it, manifest in nature, does have that pleasant property that sometimes shows up that if it's allowed to happen, it seems to happen. The standard model of particle physics seems to do everything possible that we can think of a theory to do, maybe other than supersymmetry, which is a separate question we'll get to later. But the first step is gauge invariance. Okay. You may have heard that the standard model of particle physics is based on this idea of gauge invariance, gauge symmetry. And it goes all the way back to electromagnetism, to Maxwell, really. But let me say what gauge invariance is in a more modern language, in a field theory language, right? We have an electron and a positron.

So these are charged particles, but they both have their fields that they're really vibrations in. So there are these fields filling all of space, the electron field, the positron field. In modern quantum field theory, you'd actually join them together. You would join particles and antiparticles together into a single mathematical structure, but that's okay. It doesn't matter. Conceptually, there's an electron field and a positron field. And it turns out that these fields are complex fields.

What does that mean? A field is just at every point in space there's a number, a value for the field, or maybe some slightly more sophisticated geometric quantity. So like the electric field is a little vector at every point in space. A vector has both a magnitude and a direction. The electron and positron fields, and I'm also ignoring spin because there's too many things you've got to ignore, but that's okay. At every point in space, there's a complex number. That's what it means to say they are complex fields.

So complex number is just not a complicated number, it's just a real number plus an imaginary number. A plus I, B, where A is a real number, B is another real number, I is the square root of minus one, the imaginary unit. So the numerical value of the electron field at any one point in space is a complex number, A plus I, B, for some definite numbers A and B. Now, one of the things about this complex number, set of complex numbers is you can think of it as a plane, right? We talk about the complex plane.

It's almost like it is, in fact, a two-dimensional, vector space. You can think about one axis being the real part of the number, which we've labeled A, and then the perpendicular axis is the imaginary part of that complex number, which we've labeled B. So you have A plus IB, A is going horizontally, B is going vertically. The actual complex number, a plus IB, is some dot on that plane, and you can imagine drawing a line from the origin to the dot, which looks like a little vector. The reason why I'm saying all that is because, you know, if you've played around with vectors ever in your life, you might be familiar with the idea that very often

the vector itself has some intrinsic meaning, but the particular coordinates in which we express the vector don't have any real physical meaning. So if I set up a coordinate system here in my room, X, Y, and Z, so maybe X is going, I'm pointing in a direction right now, you can't see me, but that's X, here's Y, and Z is a bit, vertical, okay? Then I can tell you what the components are of, let's say, the electric field

at one point in space, because it will have a component in the X direction, a component in the Y direction, a component of the Z direction. But physically, the electric field doesn't know what components I've set up. It doesn't care. The physics of the electric field are independent of the axes I use to define the components of the field. It's the vector that matters, not the axes with which I define it. So in some cases, that will also be true for complex numbers. You have A plus I, B, but you could rotate those two axes, the real axis, what you're calling the real axis and the imaginary axis, you could just rotate them,

and the physical essence of the thing you're describing is unaffected, just like the physical essence of the electric field is unaffected by me changing coordinates here in the room, okay? So if you have a field that has that kind of invariance, that it is a complex number, but it doesn't matter how we choose to define what is the real part and what is the imaginary part as long as we do so consistently, then you have a symmetry. That kind of invariance is called a symmetry, and that is the kind of thing that pervades all of modern physics. And that might make sense, you know, that that kind of makes sense that it doesn't really matter which is the real part, which is the imaginary part. that's a human convention, okay, blah, blah, blah. And that's fine. But what's going on in modern particle physics is a little more subtle than that. It says that I'm picking at a point right in front of my nose right now. Again, you can't see it, but imagine a point in space. It says at that point in space,

there's a symmetry that says I can separately rotate the real and imaginary part of the electric field. No physical differences being made. But I can pick a different point, any different point I want. Fix a point in your brain. Look at that point. And I can, again, rotate the real and imaginary part of the electric field, the electron field. I can rotate the A and B components together in some different coordinate systems, some different basis for the vector space. And the magical thing, the important thing, is I can do that separately at each point. At every point in space, I can separately rotate the real part and the imaginary part of the electron field, and this turns out to be a symmetry of the theory. That's a gauge invariance. It's the idea that you can separately rotate the bases of your vector space, whatever that happens to be, at every point in space, and the theory as a whole is physically unaffected by it. Another famous vivid example are the quarks. You may have heard that quarks come in colors. They're either red, green, or blue, not real colors, just whimsical names that particle physicists have given

to them, it's not really even true that quarks are red, green, or blue. What really is true is that there is a three-dimensional vector space. And every individual quark field has a certain direction in that vector space. And the basis, the axes of the vector space are the red direction, the blue direction, and the green direction. And guess what? Nobody cares. There's no physical relevance to how you orient your red, green, and blue axes at every point in space, and you can rotate them independently all throughout space time. That is a different kind of gauge invariance. So for the electron, you were just taking one direction of rotation, and that is called U1. For the quarks, you have three different axes, and the rotations

you do are called SU3. That one and that three are literally, the number of dimensions you're rotating into each other. In a weird counting system, because the complex plane counts as one complex number, so you're really rotating one number into itself. That's a little bit of math. You don't need to worry about right now. The point is, even though you might say very reasonably, that I don't care how I set up A plus I B at any one point,

or red, green, and blue at any one point, I do care physically how to relate them. at different points in space. How do I know if the electron field at this point and the electron field at that point are pointing in the same direction? If I've changed my axes, A plus IB, right, then I need to compare them somehow.

So what I really need to do is a way to take the electron field at one point in space and walk it over to the other points that I can compare them. You can't just compare them at different points. They're not next to each other. You can't subtract them from each other. they need to be next door. So you need to move the field at one point to the field at another point.

How do you do that? The answer, which is, you know, the kind of thing that makes graduate students in physics just their eyes light up with spark holes when they finally realize this, because it's very, very beautiful and very, very compelling. The idea, the answer is you need another field. You need a different field. In addition to the electron field itself, you need a field that tells you how to move the value of the electron field at one point. point to another point in space, or the three dimensions of the quark color space to another point in space, or in real space time. You have curvature, right? How can you describe the value of a vector at one point in space compared to the value at another point? You need to carry it, and you need a field to tell you how to carry. And these fields are called connection fields for obvious reasons. They help you connect one point to another. They are also called gauge. fields. And in the case of electromagnetism, this gauge field is literally the electromagnetic field. What

you think of as the electric field and the magnetic field are the amount of rate of change, either in space or in time, of the underlying gauge field. In the case of quantum chromodynamics, in SU3, they are the gluon fields. In the case of curved space time, it is the gravitational field. There's a more subtle connection there because there's a metric and a connection, but it's another story for another time. The point is that over and over again, what you see, once you have a field theory, is the possibility of these gauge symmetries, which require a gauge field to make mathematical sense of, and that field has the dynamics of its own. You don't need an electron field to run around to have an electric field or a magnetic field. Likewise, you don't need a gluon field around to have, sorry, you don't need a quark field around to have a glue on field. they have a life of their own with their separate dynamics.

Maxwell, when he wrote down Maxwell's equations in the mid-19th century, some people will, some people today will say, you know, Maxwell, he had the electric field, he had the magnetic field. He didn't know that there was gauge invariance, that there was an electromagnetic potential field from which you could make that. He did. He totally knew that. If you look at Maxwell's books, he absolutely knew that you could construct

what we now call the gauge field for electromagnetism, and from them, by taking derivatives of them, make the electric field or the magnetic field. What he didn't have was the whole symmetry group idea. He didn't have the idea that the matter fields, like the electron, would also be fields with their own ways of changing under these gauge symmetries. But he knew about gauge invariants. And classically, Maxwell's electrodynamics is like the paradigm of a wonderful classical field theory, and it was soon developed into the paradigm of a wonderful quantum field theory, quantum electrodynamics, QED, was the first quantum field theory to be really, really studied in detail and phenomenologically successful. So people knew about

gauge invariants, and they knew that it was wonderful, and it was a very, very natural thing to say, well, maybe the forces that we don't understand. stand. So thinking now the 1950s, okay? We've done pretty well with QED, the electromagnetism, but like I said, we have these things called nuclei, where the protons and neutrons are hanging out together, and there must be a force holding them together because the electromagnetic force all by itself would push protons apart. It would not hold them together, so we need a new force. Maybe, people said, it's a force that is kind of like electromagnetism, but more complicated. And the first people to say this were Yang and Mills, and so they invented Yang Mills theories.

But there is instantly a problem with Yang Mills theories. So Yang Mills theories are theories with connections, with gauge invariants, but in a more complicated way. The technical terms are non-Abelian. The symmetry group does not commute with itself. It matters which symmetry transformation you do first and then second versus second than first. Who cares? We don't care about that. That's not our goal right now.

The point is, there was a generalization of the idea of gauge invariance that seemed maybe promising, but had a huge problem right from the bat, namely that the photon, the particle that carries the electromagnetic force, the particle excitation of the underlying gauge field in electromagnetism, is massless. It moves at the speed of light. It zooms across space very easily, very readily, okay? It gives rise to a long-range force, Kulam's low. law is just like Newton's law of gravitation. It's an inverse square law. It is very easy to extend electromagnetic force across great distances in space. This turns out not to be a weird, quirky thing. This turns out to be apparently a necessary feature of gauge theories. The field that is the connection that you get when you have a gauge theory seems from the math to be

necessarily massless. And massless particles. are easy to make and easy to see, but the 1950s, they didn't see any massless particles popping out of the nucleus. So what's going on with that? Okay, you might think I've been going on too long. I have, but I'm going to make it a little bit shorter now, so I'm going to really sort of shortcut how to get out of this problem, but I really want to highlight the problem of the massless gauge bosons, because it really bugged people for decades. And there's two forces that you might worry about the weak nuclear force and the strong nuclear force, and because nature wants to make life as hard as possible for graduate students in physics, it solves the problem in two totally

different ways for the weak nuclear force and the strong nuclear force. For the strong nuclear force, it solves the problem because the gluons, which are the gauge bosons of the strong force, interact with each other. And they interact with each other very strongly, so strongly that even though they are massless and they do want to move at the speed of light, in fact, they are confined inside strongly interacting particles like protons and neutrons and mesons and so forth. So that's a very interesting piece of quantum field theory, won the Nobel Prize for David Pollitzer and David Gross and Frank Wilczak under the name of asymptotic freedom. But the basic lesson is the quarks are mass, the gluons rather, are massless, but you can't

see them because they're confined inside collections of strongly interacting particles. In the weak interactions, the answer is the Higgs mechanism. This is why the Higgs boson was such a big deal. The first person to actually point out what was going on was Philip Anderson, who was a condensed matter physicist who passed away. He won the Nobel Prize separately for his work in condensed matter physics, but the idea is spontaneous symmetry breaking. If you have another feel that is invariant under this gauge invariance that you've invented,

but it gets a non-zero value in empty space, a vacuum expectation value, that will give you the impression that apparently the symmetry is being broken, and that will allow the bosons, the gauge bosons that were supposed to be massless to now be massive, which we know the W and Z bosons actually are. This is what actually happens. It never happens at a good time. The pipe bursts at midnight. The heater quits on the coldest night.

Suddenly, you're overwhelmed. That's when HomeServe is here. For $4.99 a month, you're never alone. Just call their 24-7 hotline, and the local pro is on the way. Trusted by millions. HomeServe delivers peace of mind when you need it most. For plans starting at just $4.99 a month, go to homeserv.com. That's homeserv.com.

Not available everywhere. Most plans range between $499 to $11.99 a month your first year. Terms apply on covered repairs. But the first investigations of this spontaneous symmetry breaking by people like Nambu and Goldstone and others saw that even though you could give a mass to, sorry, they didn't say that. They were worried, let me get it exactly right, they were worried about global symmetries, not gauge symmetries. So there's no gauge bosons at all. You could only do that rotation uniformly throughout space when you rotate the different axes together, okay? In these global symmetries, there's a theorem, Goldstone's theorem,

that says you will always get a different kind of massless boson, basically because it causes zero energy to move around this field that you have used to get the non-zero value in empty space. And again, you don't see any of these massless bosons. So people were kind of grumbling and like, well, it's a mathematically cute idea. It doesn't seem to work. It was Anderson who pointed out that the two problems cancel each other out, that if you have spontaneous symmetry breaking with a gauge symmetry rather than a global symmetry,

then the would-be goldstone bosons, the particles that were supposed to be new massless bosons when you broke the symmetry get eaten by the gauge bosons. And the gauge bosons, by doing that, get heavy. So rather than getting two kinds of massless bosons, massless gauge bosons carrying the force, and the massless goldstone bosons from breaking the symmetry, you get one kind of massive bosons. And that's exactly the scheme that was used in what we now call the electro-week theory. So Higgs, and even before Higgs, Brow and on Glear, and just after Higgs, Goralnik, Hogan, and Kibble, they followed Anderson and they really did the particle physics of it. Anderson was still thinking like a condensed matter person, but Anderson was trying to point out to his particle physics quantum field theory friends that they could escape this puzzle. If you spontaneously broke a gauge symmetry, there's no massless particles lying around. Interesting side light. Look, it's my podcast. I can ramble on as long as I want. Interesting side light about this. We're going to get to the crisis in physics soon. Don't worry. Why didn't

Philip Anderson, who's a very smart guy, push his idea harder. You know, in the history of physics, you get credit for coming up with ideas, but you also get credit for sort of believing your own ideas and pushing them. And Anderson didn't really quite follow through on his idea that spontaneous breaking of gauge symmetries gives you no massless bosons at all. And the answer, as far as I can tell, is the cosmological constant problem. This is worth talking about because it's going to come up more than once. The cosmological constant problem is the idea that ever since Einstein says that general relativity is a theory of curve of space time,

it was open to the possibility that there is a vacuum energy, that there's an energy density in empty space itself. And this is mathematically identical to Einstein's idea of the cosmological constant. They're the same thing. There's no difference. There's not like, this is the cosmotial constant. That's the vacuum energy. They're the same thing, okay? Just different languages used to describe the same idea. The difference is that, you know, long after Einstein by the 50s and 60s, people realize

there could be different contributions to the cosmological constant. So, in fact, Feynman, I think I understand this correctly, but, you know, it's not a common fact, so maybe I'm hallucinating a little bit. One of Feynman's motivations for inventing Feynman diagrams was to get rid of. of quantum field theory. You know, back in the 50s, you could be ambitious like that. Right now, quantum field theory works too well. That's, it's a harder ambition to have. But in the 1950s, you could have said, well, maybe I can get all the benefit of quantum field theory without all the downside like the infinities, right? And one of the things that he knew was a problem,

Feynman, was that if you have a field that fills all of empty space, even if there's no particles, right, even if it's in its lowest energy state, in the vacuum state, it can still have energy. It can have what we call the zero point energy. And naively, you calculate the zero point energy, and it's hugely big. In fact, it's infinitely big, but Feynman wasn't surprised by that. Lots of things in quantum field theory are infinite. So that's what we call the cosmological constant problem. Naively, in quantum field theory, there is a quantum contribution to the energy of the vacuum,

which is very, very big, maybe infinitely big, depending on your attitude towards high momentum, high energy, modes of the quantum fields. And Feynman thought that maybe he could invent a theory that was a truly particle theory, right? That was really a theory of individual photons and electrons and so forth that would replace quantum field theory. It didn't work. Nowadays, we know that what Feynman diagrams really are are a useful calculational tool for talking about quantum field theory, not a replacement of quantum field theory. So Feynman was motivated by the cosmological constant problem, but it ended up not being very relevant to what he actually did. Same thing is true for Phil Anderson and spontaneous symmetry breaking.

Anderson realized that if there was a field filling all of space that was breaking these gauge symmetries, it would carry energy that field, and he estimated the size that it was big, much bigger than was possibly allowed by cosmological observations. So Anderson said, yeah, that's probably not on the right track. I will spend my time doing other things. Since then, we have learned to mostly ignore this problem. Now, we don't ignore the cosmological constant problem.

We know it's a problem. But we state that it's a problem. We state that it's important to think about. We try to think about it. Except that when we're doing quantum field theory, we just say, yeah, for some reason, the vacuum energy is very, very small. We don't know why, but it is. That's the best we can do right now for the cosmological constant problem.

And again, that's going to, it turns out that in 1990, we discovered that the universe is accelerating. We had Adam Reese on the podcast. He was one of the discoverers of that. And that seems to be best fit by the idea there is a tiny amount of cosmological constant out there, a tiny amount of energy in the vacuum, much, much smaller than you would estimate

either from the zero point energy of the quantum fields or the extra energy you get from the Higgs field. So there's still a cosmological constant problem, but it's not why is the cosmological constant zero, it's why is it a small, not quite zero number? That's the current version of the cosmological constant problem. Okay, so then there's a whole bunch of more details about parity violation and non-perturbative phenomena

and confinement and gluons and generations and families and all these things that ultimately triumph in the 1970s in the standard model of particle physics. And as you know, sometimes I like to talk about the core theory. That was a name given by Frank Wilczek. What's the difference between the core theory and the standard model? The standard model is everything other than gravity. Because we say, oh, yeah, gravity does not have a full quantum field theory description

or quantum description yet, so it doesn't count. Which is true that we do not have a full quantum theory of gravity yet. But remember what I just told you a few minutes ago. go about effective field theories, right? If you confine your attention not to every possible situation, but to certain situations, situations where the fields are relatively low energy and long wavelength, then you can invent an effective field theory that is true below some ultraviolet cutoff. So it turns out you can 100% do that for gravity. No problem whatsoever in including gravity in your effective low energy theory below the UV cutoff that you personally favor.

And that's what the core theory is. The core theory is the effective field theory that includes both the standard model and the weak field limit of general relativity. So it doesn't include the Big Bang or black holes, but that's okay. We don't have the Big Bang or any black holes here in the solar system, as far as we know. So our lives are very well described by the core theory. again good news bad news situation an amazing triumph the core theory the standard model in the 1970s made predictions right the w and z bosons were predicted and then observed the generation structures of the quarks and the leptons so that when we discovered the bottom quark we knew there had to be a top quark we discovered that we predicted the higgs boson took a long time to discover that comes around in 2012 that's good news there's nothing but good news many Nobel prizes were given out for all the work that went into constructing this model.

The bad news is, several decades later, that model continues to fit the data. There were two tiny updates, right, around the turn of the 21st century. One is neutrinos have mass. That was not part of the original standard model, but everyone knew it was not hard to put into the standard model. Again, it's sort of this weak understanding situation where we don't know exactly what the mechanism. is responsible for neutrino masses, but it's easy enough to include them. So it's a modification of the standard model, but not an overthrowing of it in any sense. The other one was, of course, the discovery in 1998 of the acceleration of the universe.

Again, put one number, the vacuum energy, into the theory, and there you have it. Other than that, the theory we're using today is the same theory that we had in the mid-1970s. other than the vacuum energy and the neutrino masses, there had been no surprising experimental results in fundamental physics since the 1970s. By surprising, I mean something we didn't anticipate in our favored theoretical models. So enormous credit to people who discovered the Higgs boson or discovered gravitational waves and so forth. But these were things that were predicted a long time ago. The Higgs boson comes from the 1960s. We were talking about gravitational waves, not long after Einstein invented general relativity.

So tour de forces on the experimental side and the vision that was required to build the experiments and the observatories that would find them and then to do it correctly deserves all the credit, all the Nobel Prizes. I still think someone on the experimental side should win the Nobel Prize for discovering the Higgs. We all know that the issue there is that the collaborations that did it had thousands of people on them and the rules, the self-imposed rules of the Nobel Committee, are that no more than three individuals can win the Nobel Prize in Physics at any one time. I would still be happy if someone like Lynn Evans, who was someone who saw the construction of the LHC through, through various little crises, might be a very good person to win a Nobel Prize, but they don't ask me. I'm not on that particular committee.

Anyway, so that's the weird situation we're in. So I hope you can now, that's a very long exposition. I hope it's useful for some people out there. But the point for everybody is we have a theory that does really well. And not only that, we kind of know why it does really well. It's because of the magic of effective field theories. The field theory that we now have, if you take a cutoff that is up there, you know, somewhere around the large Hadron Collider Energy Scale.

so some trillions of electron volts. We've looked below that scale, and we've seen a bunch of particles, and they're the particles that we thought were going to be there back in the 1970s. We haven't seen anything new, and we don't need anything new to fit the data. So that's a weird situation to be in.

I'm going to be a little bit more specific about it, okay? The ways in which we nevertheless try to get some guidance as to where to go next, but I want to emphasize that it's a weird situation to be in, and it's not because we're dumb. It's not because there's a conspiracy or a cabal to keep the truth hidden or anything like that. It's because of how nature works. It's because physicists have been smart, not dumb. They've been able to develop a theory that is a completely effective quantum field theory up to a very, very high energy scale. And without building a giant particle accelerator to go beyond that energy scale, we have to cross our fingers and hope we get lucky if we

want to get experimental data to guide us in the quest to go beyond that. So it's not like if people were just, you know, more open-minded or smarter or more willing to challenge the man, then we could make huge progress. None of those attitudes change the fact that we have a good effective field theory that keeps the possible wild new physics at higher energies and shorter distances hidden from us in a very direct physical way. So whatever you may think about the current state of physics, you have to do so from a perspective that appreciates the barriers and obstacles that are given to us by nature, by the universe, by the world, by physics, not by, human foibles. Human foibles are out there and they're adorable, let me tell you, but we have to

understand what they are and we have to take into account the real obstacles that no amount of human thinking is going to let us run around or wriggle out of. Okay. So with that, all as very long prologue, let us consider what we're doing right now in physics. What are we trying to do to get beyond the standard model, the core theory, et cetera? Because I guess the other thing to say is, the other slightly weird thing is, it's not just that we have a theory that fits all the data because then you might just declare victory. You know, they're done, right? That's not quite the situation we're in. We have a theory that fits all the data, and yet almost every working physicist is convinced the theory is not right, or at least that it's not complete, okay? Just

like Einstein was convinced that quantum mechanics is not complete. And there's various reasons to think. that we're not done yet. So we have a theory that the data is not telling us, not giving us any clues how to move beyond, but which we don't think is right, which we think is certainly part of some bigger and better theory that we don't have yet. That's a very tough situation to be in. There's no direct experimental guidance. So why don't we think we're right? Why don't we just declare victory? Why don't we just say that we're done with fundamental physics and move on? Well, there's a number of different kinds of things going on here. One is, very, very directly, we have phenomena that we only weakly understand in the classification

system I offered. Most importantly, the dark matter and the dark energy, right? We have this pie chart of the ingredients in the universe. It's possible, I don't want to do my own horn, but we're like past an hour into the podcast now. It's possible I was the first person to make that pie chart of the dark matter, the dark energy, and the ordinary matter. Again, zero IQ points are required to do that first, but I was.

was just, you know, in that discourse that was going on when the dark energy was first discovered and settled down, I thought that this is clearly an example of why a place where a pie chart is the right way to express what we now know. And in fact, if you go to my website, preposterousuniverse.com, there's the little, you know, icon that you see in the tabs telling you which webpage you're on. And the icon on my website is that little pie chart. That's why it's called preposterous universe because it's a joke, right? The universe is not preposterous. It just eludes our understand. And the pie chart is 5% of the known universe is ordinary matter, which I mean all of the stuff in the standard model of particle physics, all the atoms, all the particles

you've ever made in a lab, 5% of the universe. 25% is dark matter, which is some kind of matter, right, some particle-like thing in some way, but is not something that any of the particles in the standard model can be. We've ruled them out using various techniques. And the dark energy, 70% is smoothly distributed. It's not matter. It does not evolve as matter. It does not clump. It does not move around like matter does. It's a good fit to the data to say that it's perfectly smooth, just like the cosmological constant. But in the case of both the dark matter and the dark energy, we're not sure what they are. So we have models that fit the data, but we don't know which if any of those models is the right one.

So let's think very carefully about dark matter because it gets a certain reputation that I think, you know, you want to think clearly about the dark matter. So the first thing to realize about the dark matter is it exists. We have enough data, enough information to say that dark matter is real, okay? that doesn't mean that gravity is not also doing something weird in cosmology. So those of you, I know that there's probably a heterogeneous audience out here. Some of you are hearing some of these vocabulary words for the first time. Others have been hearing far too much about it.

But there is the following very, very natural line of thought. How do we know there's dark matter? Well, you know, we look at some astrophysical thing like a galaxy or a cluster of galaxies. We know how gravity works, right? It's a fact of gravity in the observable universe that actually Newtonian gravity works pretty well. You know, Newtonian gravity fails when gravity becomes very, very strong, like near a black hole or something like that. It also fails if you want to have a source of gravity that is relativistic, like photons or whatever. But in the world around us, if you stay away from the black holes at centers of galaxies, for galaxies and per clusters and stuff like that,

Newton's approximation works very well for figuring out what the gravitational field actually is. And in Newtonian gravity, there's a very direct correlation between how much stuff you have, how much matter you have, and how strong the gravitational field is. So you can implicitly work out, for example, the mass of the sun by just seeing how the planets orbit around the sun, figuring out their gravitational force that makes that happen and inferring the mass of the sun. So you can also play that same game for galaxies and clusters. And what you find is the gravitational field necessary to account for the motions that you see in galaxies and clusters is substantially larger than the amount of stuff that you can actually discern, the amount of ordinary matter. So you have to be careful about that.

I mean, obviously, maybe you just missed some ordinary matter. Like maybe it's invisible. Maybe it's just not glowing at the wavelengths you like. And in fact, if you just counted stars, you would be well undercounting the total mass of galaxies and clusters. Most of the mass in a cluster, for example, the ordinary mass is in hot intergalactic gas. That is, turns out you can see it if you look in the x-rays because it's hot. So it's giving up x-rays. You can actually find it nowadays, but in the 1970s you couldn't find it.

So because the gravitational field is larger than what you see, and by the way, again, I should be very, very clear because it is worth getting this right. We have separate, completely independent ways of figuring out how much ordinary matter there is in the universe. We have that both from the cosmic microwave background, which implicitly has its patterns of temperature fluctuations depend on the amount of ordinary matter. matter, and also from primordial nucleosynthesis. The early universe was a nuclear reactor. It was fusing protons and neutrons into helium and lithium and deuterium in a way that depends on how much ordinary matter there is. So all of these lines of evidence, direct inventories, the cosmic microwave background, Big Bang nucleosynthesis, they give us the same answer. They all agree. 5%. of the matter density of the energy density in the universe is in ordinary matter. So the idea that

there's just more, you know, brown dwarfs or planets out there or so forth, that's not going to fly for the whole dark matter issue. So where is this extra gravity coming from that we appear to get in galaxies and clusters? The obvious simple answer is maybe there's more matter than you see. So it's not ordinary matter. Maybe it's extraordinary matter, which we call dark matter, something that has to be a different kind of particle, not in the standard model. But there's another very obvious thing to think, which is that all of our reason for believing in dark matter comes not from directly detecting it, not from putting our fingers on it and touching it directly, but from seeing its gravitational influence, right?

So of course, it's possible that what we're seeing is not that there's new matter, but that gravity is different on these cosmological scales than it is, let's say, here in the solar system, a theory of modified gravity. That is 100% a sensible thing to think about. So let me be very clear. There's no sense whatsoever in which the establishment is keeping people from thinking about modified gravity.

Everyone in the establishment has thought about modified gravity. I've thought about it. My most highly cited paper is on the idea of modified gravity. but nevertheless, the data have spoken. Gravity might very well be modified, but dark matter is still there. So let me be very clear about why that's true, because it's important for this. And let me first say before why the data have spoken, let's see what the theory has to say, right? We talked before about effective field theories.

Gravity is a field theory. Gravity is an effective field theory. The low energy limit of general relativity is the right theory. to use when describing these galaxies and clusters and so forth. And Ken Wilson taught us how to think about these effective field theories. And part of his catechism is that it is perfectly natural for the field theory that you know and love to change and be modified at small distances and high energies.

It is not at all natural for a quantum field theory to change. change and be modified at long distances and low energies. It is hard to hide new effects that would be important at very, very large length scales and not at medium light scales. So it is very hard to come up with new effects that will be relevant for galaxies, but invisible in the solar system. Now, just because it's hard, it doesn't mean you can't do it. That's why people try to do it. That is why people like me have written down theories. and they go to great lengths to say, well, okay, why haven't we actually seen these effects here in the solar system, etc. I'm just trying to let you know that in case you're saying, well, if we've only tested general relativity really well in like pulsars and the solar system or whatever,

why shouldn't it be different in galaxies and clusters? And there's an answer to that because effective field theory says it won't be. Again, it's easy to imagine changing it in galaxies and clusters, but very hard to imagine way. of changing it that don't show up in other experiments. You have to work to do that. You can, but you have to work to do it. So theoretically, it's already, you know, a few strikes against the idea of modifying gravity. And then what about observationally? Well, here is the test. When someone says, I want to modify gravity, I think I can do away with dark matter. And you say, well, how do you explain the observational evidence for dark matter? If they start talking about

galaxies and spiral galaxies and rotation curves, you can stop listening. You know you don't need to really take them seriously. Because historically, the first evidence for dark matter came from clusters and galaxies. Arguably, it came from clusters, Fritz Zwicki, as long ago as the 1930s, pointed out that it needs to be more matter, but Zwicky's observations and theories were not good enough to say that you couldn't just have ordinary matter you hadn't found yet. It was really Vera Rubin and Kent Ford with their observations of spiral galaxies and the 70s and so forth that really said, okay, here is forced due to gravity that is not accounted for by the ordinary matter, and so we need something new, okay? But now that is no longer

the best evidence for dark matter. It's true that historically that was the first evidence, but these days we have way better evidence. We have a evidence from large-scale structure and how it evolved. We have evidence from gravitational lensing, but mostly, most importantly, we have evidence from the cosmic microwave background. Those tiny temperature fluctuations in the cosmic microwave background evolve in a very predictable way and a way that depends on precisely how much dark matter versus ordinary matter you have in the universe. It is really quantitatively beautiful and precise. It is quantitatively much better evidence for the existence of dark matter and for the properties of dark matter than anything about

clusters and galaxies. And as I'll explain in a second, it's really evidence for dark matter, not for modified gravity. So if someone says they can do away with dark matter and replace it with modified gravity, they have to start by explaining the cosmic microwave background. They should start by accounting for the best evidence, not for the oldest evidence. Okay. Why is the cosmic microwave background the best evidence. Let's go back to the idea of Newtonian gravity, right? I said that Newtonian gravity was very straightforward. It said that the force due to gravity was proportional to the amount of mass causing the gravitational pull, right? And that's true. But there's another thing, which is that the direction of the gravitational force is pointing toward

where the mass is, okay? Or if in a more general circumstance when you have lots of stars around you or whatever, the net gravitational acceleration that you will feel in that Newtonian limit is just the sum of the individual accelerations from the stars, from the individual masses that are causing the gravitational field. So the Newtonian gravity, which is the limit in the weak field of gener relativity, is not just telling you the strength of gravity, but also the direction in which it points. So how would you go about changing gravity? How would you go about modifying gravity? without any deep theoretical superstructure, just the idea of how could gravity be modified?

The easy thing to imagine doing, and certainly something that was at the top of the minds of people who thought about rotation curves and things like that, when they tried to get rid of dark matter back in the day, is that you change the inverse square law. That is to say the inverse square law says the strength of the gravitational force is proportional to one over the distance squared

between the two bodies that are attracting each other, the inverse square law, right? So as long as you just imagine changing that, so that gravity falls off more slowly than one over distance squared, you might be able to imagine coming up with a theory that explains the spiral galaxy rotation curves, right? So but notice what you're doing. You're keeping the direction of the gravitational force the same as Newton had it. All you're doing is changing the magnitude of the gravity. gravitational force from 1 over R squared to something else. And even if you don't have a deep-seeded quantum field theory justification for doing so,

you can imagine it. You can imagine it fairly straightforwardly on the basis of just the phenomenology of gravity. No one would give you a hard time for letting your imagination roam free there. But what if you wanted to change the direction in which gravity pointed? That's much harder. If the game you're playing is, the source of gravity is just ordinary matter. There's no dark matter. There's no extra new sources of gravity there, okay?

And you're going to modify gravity, but the source of gravity is still ordinary matter. It's easy to imagine the strength of gravity changing. It's hard to imagine the direction changing because how does it change? In what direction does it go? There's only one direction which is toward the source, but there's lots of directions which are not toward the source. It's very hard to imagine just changing the theory of gravity so that the force of gravity points in a different direction,

points somewhere other than where the ordinary matter is. So if you go out and collect data and the data are showing you, not just that the force of gravity declines under a different pattern than one over R squared, but that the force of gravity points in a different direction than where the ordinary matter is, that's something that's going to be very hard to explain by modifying gravity.

Guess what? Guess why I'm leading you down this primrose path? Because that is exactly the data we have. I mean, maybe the most aesthetically pleasing version of it is something like the bullet cluster. The bullet cluster is this example of two clusters of galaxies that pass through each other so that the hot, dense intergalactic medium, which is most of the order, matter in the clusters hit each other, created a shock wave, and got stuck. The galaxies, which are actually like tiny little invisible things compared to the giant interstellar gas, the galaxies just pass right through each other, right? But the galaxies are also tinier. They don't weigh as much as the intergalactic gas. So in something like the bullet cluster,

what would you predict if you ask the question, where is the gravity? If you modify gravity but didn't believe in dark matter. The answer you would give is the gravity should point toward that intergalactic gas because that's where most of the matter is. But then you do the experiment, you collect the data, you do gravitational lensing and other things, and you show that where the gravity is is where the galaxies are, not where the two globs of hot intergalactic matter that bumped into each other are, but where the galaxies are that passed right through. And that sounds puzzling, but then you realize, oh, I know what's going on. There's dark matter. The dark matter in the clusters didn't shock against the dark matter in the other clusters, because dark matter is

collisionless. It just keeps going, right? That's one of the features that we've figured out about how dark matter behaves. It does not shock or bump into itself. It just keeps going along us very way. So the prediction of the dark matter model is that the gravitational field should be where the galaxies are. The prediction of the modified gravity model, so the gravitational field should be where the gas is in between in the bullet cluster, and the data say the gravitational field is where the galaxies are, or more honestly, the gravitational field is where the dark matter is. Now, I say that's the most aesthetically pleasing one because you can make these beautiful pictures, and it's kind of vivid, it's visceral, right? You feel it in your bones, like, oh yes, there's like a picture of where the dark matter is.

I get it. But they're clusters of galaxies. They're messy, right? I mean, it's the same reason why I'm saying, don't worry about people who put all the emphasis on individual galaxies and clusters when they talk about replacing the dark matter. Galaxies are messy places. Clusters of galaxies are messy places. There's a lot of astrophysics going on.

You might think that despite everything, there was some weird, known phenomenon going on. As in contrast, we have the cosmic microwave background. The cosmic microwave background, we know what's going on. And the reason why is because there's only a little tiny bit going on. The variation in temperature from point to point in the cosmic microwave background is one part in 10 to the 5, right? Tiny little difference in temperature from one point to another. And that makes it very easy to calculate. You're not calculating these giant nonlinear feedback mechanisms, you're calculating tiny variations on top of a smooth background. And so here's what happens. And I've told this story elsewhere, so I do apologize

if you've heard it before, but for these purposes, it's super worth it. And the purposes, remember, are explaining why we know dark matter exists. So in the early universe, there are deviations in density from place to place. Maybe they came from inflation, maybe they came from inflation, maybe it came from somewhere else, but somewhere early in the universe, we don't know. That's part of what we don't yet understand, no understanding, I would say. But there's some initial condition.

And then you can just say, once you get the initial condition, what happens to it? And what happens is, a region of the early universe that is slightly over-dense will start to contract. Gravity turns up the contrast knob on the universe. Over-dense regions become more over-dense,

underdense regions empty out. But this happens, you know, it can't happen on a scale larger than the Hubble radius, the horizon size at that time in the early universe. So basically as the universe expands and slows down, larger and larger regions are able to collapse, are able to come together and coalesce under their own gravitational pull. And so you see this cascade of different length scales

on which these dynamics are taking place, the smallest length scales come first, and they can, you know, early on start this coalescence, the larger length scales will only happen later. But in the early universe, it's, you know, a hot plasma, right? This is, we're thinking now not the first fraction of a second, but we're thinking the first hundred thousand years. It's still too hot for there to be atoms. There's electrons, there's photons, there's photons, et cetera.

So when that coalescence happens, you not only increase the density, of matter in a certain region, you increase the temperature. It gets hotter. It's like pushing a piston together. And what the higher temperature means is that there's a pressure, there's a restoring force. So literally, it bounces. This region that was initially over-dense starts to contract, but it heats up, pressurizes, and then pushes backward. It starts to go the other way. It actually becomes underdense compared to the surrounding medium. If this sounds a little bit like a sound wave in the air, you are exactly right. This is an acoustic wave in the early universe. So an initial overdense region coalesces a little bit, becomes a little more overdense, but then it

quickly bounces, becomes underdense, and then it'll collapse again. You know, it bounces back and forth. It's oscillating until the point where you hit recombination, where the electrons and the protons come together to make atoms, now the universe is transparent and things just collapse. But before that moment, things were bouncing back and forth. While this is happening, okay, so you have small scales which will bounce back and forth several times before recombination, larger scales which will bounce one or two or three times before recombination. There's one more important effect going on, which is damping.

This is damping that was first studied by Joe Selk, our recent podcast cast, in fact, is called silk damping. There's different kinds of damping, but one of the more important ones is silk damping. And the idea is that, sure, in one region, you're going to coalesce, collapse a little bit, heat up, and you're going to expand, you're going to bounce back and forth. But all along, you have photons passing through the regions, right? Photons moving the speed of light. And the photons, in some sense, want to smooth things out. In the regions where you're overdense and hotter, there are more photons, higher energy. They escape to the outside, which is less

dense, lower temperature. And so the photons damp the oscillations. If you had this ringing, it is very much like the ringing of a bell in the real world. It rings, but it eventually dies down. So those fluctuations, those oscillations, those sound waves in the early universe, on small scales will be damp compared to the larger scales. I'm going through all the story because this story leads to a prediction. It leads to a prediction for what you should see when you look at how much variation there is in temperature in the microwave background. Namely, when you look at small scales, there should be a little bit of variation. When you look at larger scales, up to about one degree on the sky, there should be more variation.

So you see this, if you've ever seen this famous plot that came out of WMAP or Planck, etc., there is the amount of temperature variation as a function of angular scale. And they plot it so that large angles are on the left, small angles are on the right, right. And what do you see is the, there's a curve that it goes up to a big peak, then it goes down, and it goes up again to a smaller peak, and then down, smaller peak, smaller peak, smaller peak. If that were the whole story, if you had nothing but ordinary physics, no dark matter, bouncing back and forth because of these thermal heating up stories, you make a very clear prediction that you and I can

understand even without running a computer simulation, right? And the prediction is that the smaller scale fluctuations are more damped than the larger scale ones, like we just said. Therefore, in all of these oscillations, these peaks that you see in the power spectrum, as we call it, of the cosmic microwave background, there's the big first peak at one degree, and then every peak at smaller scales should be consecutively smaller. But that's not what we see. That's not actually what the data say. When you look at the data, what you see is that even though there's one big first peak, the second and third peak are about the same size.

The third peak is not suppressed with respect to the second peak. They're about the same, and then the fourth and fifth peaks are both suppressed compared to the second and third. It's almost as if the odd-numbered peaks are somehow being boosted or the even-numbered peaks are somehow suppressed compared to what you might. naively expect. What is going on? Oh yes, I know what's going on. Dark matter. Because dark matter doesn't participate in this bouncing process. The dark matter, again, is collisionless. It's dark. It doesn't interact with photons or the bath or anything like that. But we do think, again, both theoretically and confirmed by observation, that those initial perturbations in the density

of ordinary matter and the initial perturbations in the density of dark matter were lined up with each other. So there is, these are what are called adiabatic fluctuations. So the places where there was slightly more density of dark matter are the same places where there's slightly more density of ordinary matter. Such a place begins to contract because of gravity. The ordinary matter heats up, pressurizes, and bounces. But the dark matter just keeps contracting. Then the ordinary matter has bounced so much that it is less dense than the surrounding regions, but it's an oscillating wave. So it starts to contract again. So those peaks that we see in the data from the cosmic microwave background represent the extremes of this bouncing

evolution, the highest density and then the lowest density, the highest density is a peak, The underdensity is a peak, the high density again is a peak, the lower density again is a peak. The odd-numbered peaks and the even-numbered peaks actually are physically different. The odd-numbered peaks are that first evolution to just the over-dense region. In that case, the ordinary matter and the dark matter are in lockstep. They are both evolving in the same direction, so they reinforce each other. but then the ordinary matter bounces and the second peak is it's underdense, but that is not reinforced by the dark matter.

The dark matter is still over dense, so there's a slight cancellation. And then it bounces back again and they're back in phase, the ordinary matter and the dark matter, and they reinforce each other again. The odd-numbered peaks see a reinforcement between ordinary matter and dark matter. The even-numbered peaks see a slight cancellation between ordinary matter and dark matter. So if you believe in dark matter, which many people did before they actually saw any of this, you would make a prediction ahead of time. And it would be very clear that you would not see a uniform damping of all the peaks in the microwave background. What

you would see is that the even-numbered peaks are more damped compared to the odd-numbered peaks. And that is exactly what is observed when you actually collected the data. This is a prediction made ahead of time, and the dark matter prediction came out smack on what you expect. Can you do this with modified gravity? Could you do this like you do the spiral galaxies? Can you explain it away? Well, there's a slightly complicated question here, because what do you mean by modified gravity? How are you going to actually modify gravity, right? Like in the galaxy, if you just change the one over R squared law, the inverse squared law, to something. more mild as you get to larger distances, okay, you can imagine doing that just by writing down

some equation out of your head. But now with the bouncing of the early universe and the radiation matters and the plasma and the internet, it's kind of a little bit more complicated. So at first, in the historical development of this controversy, the modified gravity people said, well, we just don't know. We're not exactly sure what to predict. There was one issue, which is that, you know, the modified gravity people, there's a community in the 80s and 90s, and they just had these phenomenological rules. They didn't have a deep down theory that was compatible with relativity and so forth. Finally, Jacob Beckenstein came up with such a theory, a fully relativistic model that would reproduce what is known as Mon. This came from Milgram, modified Newtonian dynamics.

It was the first idea of fitting rotation curves of galaxies by modifying gravity. And what Jacob Beckenstein did was basically put forward a fully blown, complete relativistic theory that predicted the same predictions that Mond would predict. In fact, I've heard the following anecdote. I'm not sure if it's true or not, but it's amusing. So I'm going to choose to believe that it's true. Before Beckenstein wrote down his theory, there was a story going around in the anti-modified gravity or anti-Mond community, which said that you can't write down a fully relativistic theory that gives rise to Mond.

And they called it Beckenstein's theorem. And it was just a joke because the theorem was based on the idea that Jacob Beckenstein had tried to write down such a theory and he had failed. And Jacob Beckenstein is a very smart guy, so if he can't do it, it can't be done. But Beckenstein heard about this and he said, I never tried to do that. And then he did try to do it and he succeeded because he's a very smart guy. So this theory in Beckenstein's original form was called Tevis, a tensor vector scalar theory. If you look at it,

oh my God, it is the ugliest theory you've ever seen. Because again, Begenstein is a smart guy. There's an enormous amount of constraints and restrictions that you need to have to fit all the data as well as to be theoretically respectable. Not even clear that it was 100% theoretically respectable, but it was apparently a theory that gave rise to the Mond phenomenology. And this happened before we actually collected the data on the cosmic microwave background. So now you have a theory that you can use to make a prediction. And people did.

It was a heroic effort because it's not easy to do this. They made the predictions. And guess what? You predicted a difference between the modified gravity theory and the dark matter theory. You would not get, there's no reason in modified gravity to get this difference between even-numbered peaks and odd-numbered peaks. And so they didn't. they got a smooth decline in the piece.

And they made a very explicit plot of what they predicted that the CMB would eventually look like. It did not look like that. The data came in and they were very clear that this particular prediction was wrong. Physicists are stubborn and smart and clever. They don't give up so easily. So is it possible to come up with a theory

that is modified gravity and science, some sense and correctly fits the cosmic microwave background data. If you are just shameless and bend over backwards and try to, you know, tweak your parameters, et cetera, yes, it is possible to do that. Now, if that's true, if it's possible to come up with such a theory and fit the microwave background, which is the best evidence we have for dark matter, why did I say earlier that we know that dark matter exists? Because, you know, you've lost a little sight of your original goal when you started doing this. When you look at these theories, even Beckenstein's theory, even the original Tevis model,

which was supposed to reproduce the modified gravity predictions. Why is it called Tebis? Tensor vector scalar. Well, the tensor is the good old gravitational field, the metric tensor that Einstein had. But the vector and the scalar referred to new degrees of freedom, new fields that Beckenstein had to put into his theory. And since then, every other person who has written down versions of modified gravity that claim to fit the CMB as well as other things also adds a bunch of fields into their theories.

How is it possible to make a difference between the even-numbered peaks and the odd-numbered peaks in the CMB if the only gravitational field is coming from ordinary matter? And the ordinary matter is uniform in its stamping from high, from small-scale, from large scales to small scales, why would there be a difference in the even-numbered peaks and the odd-numbered peaks? The answer, when you dig into it,

is that these other fields that you invented to supposedly modify gravity have energy. And they therefore create a gravitational field. And that gravitational field is not coupled directly to the ordinary matter. It is independent. In other words, it is dark.

dark matter. That is what it is. That's what dark matter is. Dark matter is some new degree of freedom, some new kind of field or particle or whatever that creates a gravitational feel. Other than the ordinary matter that we know and love. You, if you want, you can just stamp your feet and say, but I choose to call this modified gravity, not dark matter. It's a free country. Be my guess. But you're not going to be able to explain the cosmic microwave background with new sources of gravity over and above the ordinary matter that we know and love, because the ordinary matter declines uniformly, the data do not. In dark matter models, this is obvious and natural and immediate and very pleasing. In these other models, you can do it, but all you've done

is create a really weird and baroque and hard to understand a version of dark matter. Now, having said all that, let's be super duper fair here. There's a reason why people continue to pursue the idea of modifying gravity because there's something about the manifestation of dark matter in galaxies and clusters that is weird. This is what Milgram first seized on in the 1980s when he started thinking about Mond. There's a certain phenomenology in the sense of a certain way that we see things in the universe that keeps showing up in galaxies and arguably in clusters also, but that's maybe a little bit arguable,

but certainly in galaxies, there's a relationship between how the ordinary matter behaves and how the dark matter behaves. And it's not immediately explained by the dark matter hypothesis, whereas in modified gravity, you can just put it in as part of your modification of gravity. So this is what is called, the Mond phenomenology. What Mond, what Milgram's theory of modified gravity really does is it predicts a

certain feature of spiral galaxies that is absolutely seen out there in the universe and is not directly predicted by the dark matter theory. So that motivates people to pursue this dark matter idea. But note the difference here. The problem with dark matter, let's put it this way. The promise of modifying gravity is that you can explain a feature that is not yet otherwise explained by the dominant theory. But the problem with modified gravity is that it doesn't fit the data. It's ruled out. That's a bigger problem. It is important to try to understand why dark matter and ordinary matter interact the way that they do to give galaxy certain structures. This is absolutely a perfectly legitimate thing to think about and worry about and keep as a goal in your mind. But it's also hard because like we said at the start, galaxies are messy.

You know, galaxies by construction, or I shouldn't say by construction, but by observation, what we see is in a spiral galaxy, the centers of the galaxies, you don't really need dark matter to explain what's going on. It's mostly ordinary matter. That makes perfect sense because ordinary matter has. dissipation, it falls to the bottom of a gravitational well much more efficiently than dark matter does. And what Milgram points to in his phenomenology is that there's a certain radius in spiral galaxies inside of which you don't need dark matter outside of which you do, so that's what he tries to explain by modifying gravity. By all means, have as a goal explaining that in the dark matter

paradigm, but it's going to be hard, and you can't say, because you haven't explained it yet, dark matter isn't real. It's a paradigmatic difficult problem. It's like saying, you know, I don't understand consciousness, therefore let's change all the fundamental laws of physics. Why should we understand consciousness? It's hard. We'll get there eventually, but the fact that we're not there now is not strong evidence that we have to change the loss of physics, and the same thing is true for the rotation curves of spiral galaxies. So, you know, again, all of this is what in legal terms would be testimony against interest. I would like it if gravity were modified. I have written papers about modifying gravity. I've had many more thoughts about modifying gravity that

did not quite make it into papers because they didn't quite work. That would be cool. That would be fun. That would be awesome. But it would also both be in violation of our intuition from effect field theory, and in apparent violation of the data. And these days, there are plenty of plucky people who keep trying to modify gravity, but secretly, they're adding new stuff which does all the work that ordinary dark matter does. So they should be compared to other dark matter theories in terms of how natural the parameters are, how effective the predictions are, etc. One way or the other, dark matter exists. But we don't know what it is. Dark matter doesn't have to be a particle necessarily. It acts.

particle-like, but maybe they're microscopic black holes or something like that, completely allowed by the data. So that's a perfectly valid worry, right? The fact that we have very, very good evidence that dark matter exists and yet we don't know what it is. That's a puzzle. You know, that's not a crisis to have a puzzle we don't know the answer to. That's a good thing. That's the kind of thing that gets science going. When you have a puzzle that makes you think about things and maybe you can improve upon your understanding of the world. And it is not as if we are lacking in options for what the dark matter might be. We know, again, a lot about the dark matter.

We know that it's dark. In other words, it does not interact directly with electromagnetism, with light, with photons. And that's how we get most of our information about the universe out there. So that's an important fact about the dark matter. We know that it is cold. That's a new thing. We didn't back in my day when I started out. hot dark matter and warm dark matter. We're both very popular. What that means is how fast the

dark matter particles are moving in the early universe. Not so much today. They could be moving very quickly in the early universe and then have cooled off today. But if they were moving very quickly before recombination, then they would have smoothed out the density fluctuations that grow into galaxies and stars too much. So again, on the basis of data, we have excellent reason to believe the dark matter is cold as well as dark. We also know that it is collisionless, more or less collisionless, amongst itself. Now, in other words, dark matter, unlike ordinary matter, does not clump together. We think that the reason why ordinary matter dominates at the center of a galaxy is because ordinary particles, hydrogen atoms, for example,

can bump into each other. Even though a hydrogen atom is neutral, it's made of electrical, it's made of electrically charged particles, so in the bumping, the hydrogen atoms can give off photons and lose energy. They can dissipate. They can fall into the center of a gravitational potential well. The evidence is, from mapping out where dark matter is, the dark matter doesn't do this. Even though the galaxy that you see when you take a picture with JWST or something like that is this beautiful compact structure, the dark matter is in a big puppy halo, slightly concentrated near the middle, but mostly diffuse, because there's nothing to cool it off. There's nothing to allow it to lose energy and sink down to the bottom of the gravitational potential. It is mostly collisionless.

I say mostly because plenty of people, and again, myself included, I've been in this game for a long time, I've played with various different ideas, have explored the possibility that dark matter does interact, more or less noticeably with itself. Now, there's different ways to interact, The kinds of interactions that have been imagined for dark matter particles that would be of astrophysical interest have mostly been elastic collisions. In other words, the little dark matter particles, even though they rarely interact, when they do so, it's kind of like billiard balls bouncing into each other. There is no dissipation of their energy into emitting photons or anything because they don't interact under electromagnetism. Even there, my impression of the current state of the art is there's not a lot of parameter space in which that's allowed, but I think it is an open possibility still. Now, I did, with various colleagues including Mark Kamienkowski, Matthew Buckley, Lottie Ackerman, propose an idea where there would be an entirely new copy of electromagnetism, dark electromagnetism, so that you could actually have dark matter particles coupled to a mass.

lists U1 gauge field, right, a dark photon. And it turns out there's actually a lot of parameter space where that's okay, because if the interaction is weak enough, if the fine structure constant in the dark sector is sufficiently small, then you're actually not going to give off a lot of radiation. And then you can start thinking about dark atoms and dark chemistry and things like that, but it's more for fun because the data tell you that the dark matter is pretty smoothly distributed compared to ordinary matter. If there is any interesting chemistry, electromagnetism-level physics in the dark matter sector, it's much more feeble than it is in the ordinary matter sector. And the final thing we know is that adiabatic fact we mentioned before.

When you have the density perturbations in the early universe, the density perturbations in the dark matter track those in the ordinary matter. This is both exactly what you would expect from inflationary cosmology or something like that as a theory of where those density fluctuations came from and is also what is more or less insisted upon by the data that we have about where the dark matter is and where the ordinary matter is. So that's a good amount of constraint, right? The dark matter is dark, it's cold, it's non-dissipative, and it is adiabatic when in its density fluctuations. But that still leaves you a huge number of possible candidates. Martin Rees, Former Mindscape guest once said that there's so many plausible dark matter candidates,

it would be shocking if there wasn't dark matter out there in the universe. I'm not sure if that's true or not, but think of it this way. There's no reason why, in all the possible laws of physics, all the particles out there have to be easily noticeable to you. That's just not how the universe is set up. So there's a task to be done. If you're a particle physicist, invent, come up with plausible model, for particles that would be cold dark, et cetera,

and also have the right relic abundance. That's the crucially, crucially important point. You have a prediction from the early universe and the particle physics properties of whatever model you have as to how many particles are left over after the universe expands in cools. That's something you can calculate. That's something that every graduate student

who does early universe cosmology is trained to do at a young age, calculate the relic abundance of your favorite dark matter candidate. So you can do that, and the easiest thing to imagine is that your dark matter particle used to be in thermal equilibrium. So it's interacting enough, even though it doesn't interact by electromagnetism, it interacts by some other force, enough with ordinary matter, et cetera, that there was a time when they were interacting with each other relatively frequently, right? Dark matter particles were interconverting with ordinary manner. We don't know that to be true. I'm just saying that's the first thing that you might guess. That's a natural starting point. And then there's basically one parameter

that tells you on the basis of how strong those interactions are how many particles you have left over at the end of the day, the relic abundance. And the answer is that the strength of the interactions you need for a cold, dark, relic particle to have been. the right abundance to be the dark matter is basically the interaction strength of the weak interactions of particle physics. This is called the WIMP miracle. Wimps are weakly interacting massive particles. The miracle is just the idea that if you go backwards and ask how strong does interaction have to be to get you the right relic abundance of dark matter, the answer is roughly a known quantity, the interaction strength of the weak interactions of particle physics.

So the word weak in weakly interacting massive particle doesn't just mean not very strong. It means specifically the weak interactions that we know about from existing standard model particle physics. Now, that's a little bit of an exaggeration, this Wimp Miracle idea. It turns out there's a bunch of free parameters in there that you might not have paid close attention to, but actually do have an impact on what the relic abundance is. So there's room. There's more than a little bit of wiggle room. There's a couple of order of magnitude of wiggle room in terms of how much relic abundance you get. But roughly speaking, you know, that's a promising thing. Because if you think about where were our brains 50 years ago when the standard model was coming online, there's another puzzle with the weak interactions that we're going to get to in just a second, which is called the hierarchy problem. Why does the mass of the Higgs boson? Or, you know, Or more generally, why is the Electro-Weak scale, the energy scale characteristic of the Electro-Weak interactions, why is it so different from the plank mass or the Grand Unified scale or whatever higher scale that you might have?

So people imagine there's different physics that kicks in at the Electro-Weak scale to help explain that hierarchy problem. That would imply there are new particles at the weak scale, At this energy scale, which is roughly between 100 and 1,000 billion electron, so 100,000 times the mass of the proton, at that energy scale, there might be new particles that we haven't seen yet. They would be weakly interacting. They'd be associated with the weak interactions, and they would be massive. So, in other words, just on very basic general grounds, it's very natural to assume that

there are weakly interacting massive particles out there. Again, that's there's wiggle room here, right? You don't need to have particles that are, that qualify as wimps, especially because there's an extra property these particles should have that I should mention, which is that they should be stable, right? Not only neutral, not only electrically neutral and not interacting with photons, but they can't decay away very quickly. And it's pretty easy in particle physics to invent new heavy particles that decay away very quickly. You have to work a little bit to make particles that don't decay if they're very massive. So you can do it. It's not hard, but there's certainly no demand that there must be the particles there. They're natural, but they're not

necessary, okay? So this is a natural prediction, not prediction, but expectation that there are weakly interacting massive particles that would naturally be the dark matter. This is the reason why weekly interacting massive particles have for a long time been the favored candidates for being the dark matter because it's not just that you're inventing them to be the dark matter. They're something that pops out naturally of other theories that you invented for other reasons. Okay? That's a very common thing in particle physics. If you have all these puzzles around and you could, you know, invent new particle physics or

particles or phenomena or ideas puzzle by puzzle, but if you can get one idea that explains two puzzles, that's considered better, right? A little bit more elegant or parsimonious or something like that. And so new particles at the ElectraWeak scale might help you with both the dark matter problem and the hierarchy problem. And maybe other problems of ElectroWeak physics, who knows. So we have launched programs to look for these particles. It's not like we haven't looked. And there's a very big experimental program on the agenda. And it's ongoing. It's not like we're planning in the future.

It is going on right now. And in fact, we have not seen weekly interacting massive particle dark matter. And we could have seen it already. Okay? Let's be super duper honest. If you were asking people 20 years ago, I bet a lot of them would have bet at 50-50 that by now we would have detected weekly, interacting massive dark matter in experiments, and we have not yet. So that should decrease our credence

in the WIMP idea. How much it decreases it? Well, you know, that's going to depend on what your priors were and things like that. But I actually did the exercise of going back and looking at papers that were written 20 or 25 years ago about what we should expect the dark matter density to be and how much we can do with various experiments in ruling out the parameter space. And I compared it to what the current limits are. This was a couple of years ago, so maybe the limits have changed a little bit, but very, very roughly speaking, our current experiments have ruled out about 50% of the expected parameter space for weekly interacting massive dark matter. So 50%, again, very, very roughly. But it's not a lot of.

1%, it's not 99%, okay? So that's an interesting number because that means that, yeah, there should be some noticeable decrease in your credence that the WIMP idea is the right particle, the right model, the right hypothesis for explaining the dark matter. But you shouldn't have given up on it entirely. I mean, 50% of the parameter space is noticeable but not overwhelming, right? There's still a whole another 50% out there to be tested. And yeah, what could you do except build better experiments? Bigger experiments. The Xenon experiment has for a while now been one of the best out there at ruling out parameter space for dark matter. And they're going to keep going. They're going to build bigger detectors with more room to what they're doing is basically you have dark matter

all around you. If they are WIMS, then there are dark matter particles around you flying through your body right now, not interacting very much. But you build a detector which waits for those rare times when dark matter particles will interact with ordinary atoms, deposit some energy, and you detect that energy. That's what you're trying to look for. And haven't seen it yet. It's a very, very difficult thing to do because there are other things in the world that could bump into an atom and deposit some energy, things that have nothing to do with dark matter. That's why it's a very tricky thing to do. It's the backgrounds that really get you. But okay, so the WIMP possibility is very natural, very compelling.

We've ruled out much of the parameter space, but nowhere near all of it. Now, we also have other candidates, right? We've had other candidates for decades now. The traditional second place favorite candidate is the Axion particle. The axiom is an entirely different beast than the WIMP. It is much, much lighter. So a typical WIMP, again, it's going to be hundreds of billion, of electron bolts, hundreds of GEV or something like that. Of course, people are clever, so they

try different things with lighter, dark matter particles, and that's fun. That's full employment for particle astrophysicists. The axon is a much, much lighter particle. It has a similar, hypothetically, we don't know if it exists, but it would have a similar mass to neutrinos, right? Something like a tiny fraction of a single electron bolt, much later than electrons and things like that, maybe 10 to the minus 5 electron volts, 10 to the minus 4 for axions. And what is an axiom? It was a particle that came out of, once again, a completely different direction. It was not invented to be the dark matter. This came out of that, you know, those triumphant days in the 1970s were putting the standard model together. It was realized that there was a single puzzle. There's more than one puzzle,

but there was one puzzle that hadn't got a lot of attention called the strong CP problem. You may have heard that there are these symmetries in the standard model or would-be symmetries that are broken. They're called C, P, and T. C is particle-antiparticle symmetries. That's called charge conjugation, positive charges, turn to negative charges and vice versa. P is parity and T is time reversal in variance. individually, the physics and the standard model violates all of these symmetries, but the combination of them, C-P-T, is actually concerned.

And in the weak interactions in particular, you can see all these different things being violated in experiments. The strong interactions appear to preserve C-P-N-T separately, and that's okay, but it turns out, if you think about it hard, it would not have been difficult for the strong interactions to violate CP. It is very easy to write down a term in the standard model particle physics. There would be a strongly interacting term that would violate the combination of charge conjugation, which is particle antiparticle symmetry, and parity. Okay, but it's not violated.

So that's weird. Why isn't it violate? It would be too easy. Like in other areas of the standard model, if something is possible, it happens. but this particular term seems to be zero, even though, I mean, the experimental limits are that it's 10 to minus 9 or 10 to minus 10 or less or something like that. No reason that we know up for it to be that. So Roberto Peche and Helen Quinn back in the 1970s proposed a model, now called the Peche Quinn model, cleverly enough, that invented a new symmetry that would explain why there is no CP violation in the strong. interactions. And it was quickly realized by Frank Wilczek, former Minescape guest, and Stephen Weinberg, separately, that the new symmetry that was being proposed would come along with a new particle.

Frank Wilchek named it the axion after a laundry detergent that he saw in Europe. There is a relationship there with axial currents and things like that, but basically he was amused by the idea this laundry detergent sounded like an elementary particle. So the name has stuck, the axiom. So the axion is a spinoff, a spandrel, if you like, from an attempt to solve what is called the strong CP problem. And the axon has two parameters in it. One parameter is more or less fixed by physics, which is the strong interaction scale, what we call the QCD scale, the scale of which the strong interactions really become strong. But the other is the Pache Quinn scale. Peche and Quinn invented this new mechanism. A new energy scale comes along with it. We have no idea what that scale is. So we can therefore pick that scale

to be whatever we want based on doing experiments. Turns out that even though the axion is very, very light, the way it is produced in the early universe is completely different from the way that wimps are produced. The axion was never in equilibrium. It interact. acts so weakly with ordinary matter that it was never being produced and converting back and forth between ordinary matter. So it has never been hot. It was never high temperature. It is basically produced at zero temperature in the early universe. So it can be both light and nevertheless be cold, dark matter. And what you can do is you can say, is there a value of the Pache-Quinscale such that the relic density of axions is what you need to be the dark matter.

The answer you'll be unsurprised to hear is yes. You can absolutely do that. So that gives you a target to shoot for because you would like to experimentally detect these axions. Now, the axions are sort of, they have a smaller constituency than the wimps do, because, as I said, the wimps are often part of a much bigger structure that try to extend the physics at the electroweaks. scale. So we have not put as much effort into looking for axions experimentally. There have been, there are ongoing experiments to look for it. We haven't found it yet, but we also haven't ruled out as much of the viable parameter space, maybe 20% of the axon parameter space. That's very,

very roughly lit. That's literally me looking at plots and going, yeah, about 20% of the parameter space has ruled out. So maybe someone who's an expert knows more. But the point is, we have a been as successful because we haven't tried as hard to find dark matter axions. So that's still a completely viable theory. I mean, I literally just recently wrote a paper about how axions might help us create primordial magnetic fields. So the physics of axions is still very, very interesting and an ongoing concern. And of course, these two theories, Wimps and Axions, are not at all the only theories. Like I said, they're both examples of theories where the proposed dark matter candidate also solves another problem, which we like. But if you free yourself from that

constraint and just say, I'm going to invent a dark matter candidate, then go nuts. I mean, there are dozens, probably hundreds, maybe hundreds is a lower limit on the number of models that have been proposed for dark matter. Again, I'm responsible for some of them. Not that many. I've not done a lot of work on dark matter. But it, you know, it's fun. Propose a model. And then, of course, why do you propose a model? Not just because no one else has proposed it yet, but because it has some other interesting consequences, either experimentally or solve some other problem in the early universe or something like that. And sadly, some of the models that are proposed would imply that essentially we will never directly detect the dark matter. There are models of dark matter. There are models of

dark matter where the only interactions with ordinary matter are through gravity, basically. That would be sad, right? But the universe isn't out there to make us happy. So we're doing our best to find the dark matter to propose ideas that are experimentally testable, and we may or may not succeed. That's just the reality of it. So in terms of the crisis in physics idea, is this a crisis? I know it's certainly not a crisis. I mean, you can be sad that we haven't found the dark matter particle yet. You can be irked that nature is not being nice to us, but I think basically the strategies being pursued are exactly the right strategies.

You as a theorist put on your thinking caps and try to think of what the dark matter could be. As an experimentalist, you try to find it, and the experimentalist and the theorist talk to each other about the best ways of doing that. There are multiple prospects for what the dark matter might be. Again, unfortunately, their experimental tests are utterly different from each other. An experiment that is looking for wimps will not be able to find axions and vice versa. And if we're honest, there are models out there where no experiment is going to find them. So what are you supposed to do in that situation. I think that what you're supposed to do is what we're doing. And you're supposed to look, supposed to judge the different models on their relative plausibility, and you're supposed to spend

some money and some time and some effort in experimentally searching for these different possibilities relative to your expectation as to how likely they are. It makes perfect sense that we spend more money looking for whims than axions so far, because in the judgment of most physicists, they're the more likely candidate. Not by a lot, so we also do axions, and we're also doing other things as well. But I don't know what else people would want one to do, right? Nature is nature.

It's going to give you the experimental results when it chooses to, not when we demand it. We cannot just stamp our feet and say, find the dark matter tomorrow or else. That's just not a viable strategy. I think that's all I got to say about dark matter. There's also dark energy, but there's not that much to say about dark energy.

It is 70% of the energy density of the universe. It is less cut and dried about dark energy existing because in the case of dark energy, there's a lot less specificity in the data that we have about it. We know that how much of it there is, and we know that it doesn't evolve very quickly. We know that it's smoothly distributed through space, as far as we can tell,

and it's approximately constant in density over time. that's good, that's some information that really constrains things, but it's much less specific information than we have for dark matter. For dark matter, we can literally map out where it is, right? You can see these gorgeous maps that are made from gravitational lensing studies, and that's very, very specific info, whereas dark energy, we basically have a number, how much it is, and all the other numbers that might exist, like how much it changes from place to place, how much it changes from moment to moment. So far, all those other numbers are consistent with zero. So for dark energy, it's absolutely plausible that you could try to replace dark energy with modified gravity.

Again, this is something I have done, and people have followed up in many, many papers about that stuff. It's an actively pursued area. But I got to say, I think it's probably just a constant. And again, this is super duper testimony against interest because a lot of my papers, a lot of my most highly cited papers are about either getting rid of dark energy and replacing it with modified gravity or thinking about the consequences of some dynamical theory of dark energy. Most obviously, if you have an axion-like particle, but instead of 10 to the minus 5 electron volts, it's 10 to the minus 33 electron volts, some incredibly tiny mass, then that can be the dark energy rather than being

the dark matter. It can be a quintessence-like field where the field evolves very, very slowly over time, and you can make an experimental prediction based on that, which is called birefringence. The idea that photons traveling through this time-dependent quintessence field will slowly rotate their polarizations from the cosmic microwave background to today. And as I've mentioned, I did a solo podcast sometime back on the Screwy universe. So look that up if you're interested in these ideas, but there is a claim out there that you can kind of maybe see this by refringence in the known data that we have right now on the cosmic microwave background polarization. I think it's not yet to the level of statistical significance where we can

claim that it's really there. So I'm being very, very cautious about it. In fact, if I were to bet, I'd say if I were forced to bet to gun to my head, I think that the chances that it's, that the signal is truly a signal of bi-refringence rather than just some random fluctuation or experimental error is less than 50%. It's more than 5%. So it's absolutely worth following up on. I absolutely hope it's there. That would be great. But the simplest explanation for the dark energy is just that it's a cosmological constant. It's that vacuum energy that we were talking about before. It's the simplest explanation, and it fits all the data perfectly so far. So be very, very careful when people say, we know nothing about what the dark energy is. What do you mean? We know nothing. Again,

we know some of its properties, and we have a really good candidate for what it is. It's the cosmological constant. It's the vacuum energy. We're in this weak understanding phase where there are also other candidates. You could have some slowly varying scalar field, or you could modify gravity in some way. All of those are worse theories in the sense that they give rise to new problems you didn't already have without solving any of the other problems that the cosmological constant has, but they're viable experimentally, so we should take them seriously. But it's not that we are just clueless, you know, we have a perfectly good idea of what it could be that fits all the data. We're trying to pin down whether or not all the other theories are still viable or not. The more

data we get, the less viable they become, but they're still out there and we have to think about it. Again, not sure what else you would have people do. Like, that's what we got to do. We propose ideas and we experimentally test them. By the way, in both cases, in the cases of both dark matter and dark energy, you might roll your eyeballs a little bit at the tendency of theorists to just keep proposing models, right? Keep proposing theories of what the dark matter could be. the dark energy could be. There are many, many, many, many, many, many models out there. Doesn't it get a little tiresome? But the crucially important thing to realize is that when you say, let's do an experiment or let's do an astrophysical observation to test these ideas,

that idea of doing an experiment or doing an observation is not independent of your theoretical model. Different theories are going to be constrained by different experiments. Again, the Experiments that constrain whims are completely different from the experiments that constrain axions. So if you don't sit down and write down the explicit model, you can't experimentally test the idea. There might very well be some experiment that we could easily do for $100,000 that would instantly let us detect the dark matter. But we don't know what the experiment is yet because the theorists haven't yet invented the model that makes that prediction. Okay. So all of these theorists turning out new models, yes, it can look a little, you know, your eyes could glaze over if you're not actually one of these people, but it's crucially important because one of them might be right. And the right one might have some very clever, unusual, unique experimental signature that we don't know about yet. Theory and experiment depend on each other. And one of the ways they depend on each other is the experimentalists need theorists to tell them what to look for. So that activity going on is actually. actually crucially important. So I don't think that anything about dark matter and dark energy

represent crises in any possible sense. They represent good, old-fashioned physics, puzzles that we don't know the answers to yet. We have good ideas about what they could be. We're trying to test those ideas experimentally, as well as coming up with new ideas that might suggest new experimental tests. That's as healthy as it is possible for a field to be. Progress is, is slow, so what? That's not the physicist's fault. It's not the fault of the people trying to do the work. They would all like the progress to be fast. Nature does not always cooperate, and that's something we have to learn to accept. So that's one area that people get a little irked about, the whole dark matter, dark energy thing. Let's turn to the next area. I have three areas,

and I'm going to give them away. One is the dark matter, dark energy stuff. Another is naturalness problems within the core theory. And the third is quantum gravity. which I'm sure you've heard about. So let's talk about the naturalness problems. The naturalness problems in the core theory come about because we have this idea, and it's not a very philosophically respectable idea. I think there is a philosophically respectable idea buried in there, but I think that the philosophers and the physicists have not really sat down to hash out what it should be. But the germ of the idea is some features of a theory like the core theory look natural. to us, some features do not. What does it mean for a feature to look natural to us? And Gerard

Etowft, who is a famous physicist, one of the great masters of quantum field theory in the 70s and 80s and so forth, put forward a certain definition of naturalness in the context of quantum field theory, having to do with the existence of a small parameter is natural if a symmetry is restored, when that small parameter is literally zero. But there's other notions of naturalness that we use at a more informal level, and we can talk about why should we have some expectation that something is natural?

The rough and ready thing that we have in mind when we say that things in the standard model are natural or not is if you have a dimensionless number, so not like a mass or something like that, but maybe a ratio of two masses, that's a dimensionless number. if you have a dimensionless number that is very, very tiny, much, much smaller than one, or contrary-wise, its reciprocal is way, way greater than one, okay, if you find such a number for no good reason, like it's the combination of a whole bunch of things that really should

add up, we think, to something of order unity, but it doesn't. That's a naturalness problem. That's something that looks wrong to us. And I already mentioned the strong CP problem. and that's one of the naturalness problems. There's two other big, famous ones in the core theory. One is the hierarchy problem, and that's the ratio of the scale of the electroweak interactions, which is of order a couple hundred GEV, GEV's a billion electron volts,

to the plank scale, or if you think that there's some unification scale up there near the plank scale, then same thing. So very roughly speaking, the weak scale divided by the plank scale in the real world is something like 10 to the minus 15. keep, okay? That's a tiny number. And the reason why there's some meat on these bones is because

if you think of the Electro-Weak scale in the context of quantum field theory, it looks like it is a combination of various different contributions from various different things, okay? There are quantum corrections. If you start with a classical theory, there's quantum corrections to that classical result. You should add them all together, et cetera, and there's no reason for them to cancel, and they're generally big. So, very roughly speaking, we would expect the quantum corrections that we know and love from the standard model of particle physics would increase the Electro-Weak scale, if you just started with some classical value, and it would increase it all the way up to the Planck scale. There's no reason for it not to. But it doesn't. It's 10 to the minus 15 times the Planck scale,

very, very roughly speaking. That's the hierarchy problem. And why is there such a large hierarchy between the Electro Week scale and Plank Scale? The other problem is, of course, the Cosmological Constant problem. It's almost exactly the same story. The vacuum energy, the cosmological constant could very well be thought of as getting contributions from various different sources, classical quantum, et cetera. And it should be up there near the Plank scale. It is not. Depending on how you use units to measure it in, if you use units of energy,

density. The energy density in the vacuum is 10 to the minus 120 times the plank scale value. Now, that's the famous number that is supposed to be the largest discrepancy between expectation and reality in all of physics. I think it's perfectly valid to take the one quarter power of that. Take 10 to minus 120, raise it to the power 1 over 4. Why? Because dimensionally, this energy density that you're looking at has units of energy to the fourth power. Once you go into natural units when h bar equals c equals one, that's what particle visits is do. Everything is measured in energy to some power. Energy density is energy to the fourth power. So the actual discrepancy in energy scale between the vacuum energy and the plank scale is not 10 to the minus 120, but 10 to minus 30.

Okay. 10 to minus 30 is still a really small number. This is a giant discrepancy between, um, what we see and what we might expect. Now, in the case of the hierarchy problem, the thing is that the electro-week scale has been historically a little bit high for us to look at directly. That was the motivation behind building Large Hadron Collider would have been the motivation behind building the superconducting supercollider, which, remember, would have gotten to even higher energies than the LHC would have. We canceled it because in the late 1990, We were on a drive to cut the budget deficit. So the SSC was started but never finished.

And the tunnel was basically filled in. We're never going to do that. So the LHC, Large Hadron Collider at CERN outside Geneva, is our best look near the Electro Week scale. And because of the hierarchy problem, there was this very, very strong expectation that once we actually looked at the physics of the electrical week. weak scale, we would find some kind of new physics. There are specific examples of what it could be,

supersymmetry or extra dimensions or whatever, strong dynamics. There's various different options on the table, but there was a strong feeling that because of the hierarchy problem, there had to be something going on at the electroweak scale, and whatever that something was would give rise to a whole bunch of new particles. Maybe they'd be super symmetric particles. Super symmetry, if you know, is a hypothetical symmetry between bosons and fermions. From the mathematical quantum field theory perspective, it's an extremely natural thing to think about supersymmetry. And it turns out to have all sorts of nice properties. It helps make calculations easier. You know, it has very, very specific predictions, experimentally, and so forth. And it could help solve the hierarchy,

problem and it could give us a dark matter candidate. The neutraleino would be a super symmetric particle that would be a candidate to be a wimp, to be a weakly interacting massive particle. So it seemed, if you're thinking, you know, 20 years ago, again, you would have absolutely every right to think that by now we would have both found the dark matter in direct searches for dark matter, the weekly interacting massive neutrally no, and we would have found a whole bunch of particles at the LHC because the LHC looks at the electric weak scale, found the Higgs boson, right, and it's looking for more particles out there. Didn't work.

Didn't happen. We have not found any new particles. It could have been the case that we turn on the LACC and gluinos are just popping out of the detector and so many of them that it's hard to miss them, right? we haven't seen any not just super symmetric particles but any particles beyond what are already in the core theory.

Now, got to be honest, we're not done yet. We're nowhere near done. The LAC is still running, still looking for new things, always creeping up to higher energies, higher luminosities. But it wasn't the easy, nice thing that we might have hoped for, that we certainly had crossed our fingers hoping for.

There don't, so far, seem to be any new particles. at the Electra Week scale, other than the Higgs boson, which we knew had to be there. If most models of low-energy supersymmetry had been right, then we would have seen a bunch of new particles, and we haven't. So the hierarchy problem is just there. It's just staring us in the face. Now, in retrospect, you might have reasoned in the following way.

The hierarchy problem is a discrepancy between the Electro-Weak scale at 100 GV, and the plank scale at 10 to the 18 GEV or whatever. Whereas the cosmological constant problem is a very similar looking problem, but the energy scale of the vacuum is like 10 to the minus three electron volts. So that's what, 10 to the minus 12 GEV, which is very different than 10 to the plus 18 GEV. That's the 30 orders of magnitude difference. And we don't see any new particles near the vacuum energy scale that keep its scale. so much lower, so maybe that was not a right thing to think about the electroweweak scale either.

Fine, but we don't know what the right thing is. So again, we're just doing our honest best, right? We had a puzzle, the hierarchy problem. Still do. It hasn't gone away, okay, but it's been a major motivation for many years now. And we had good, plausible candidates to explain it. And so far there's no evidence for any of them, and that's a real fact that particle physicists have to face up to. So what do you do? Well, there's a couple different things you could do. Like, one thing to do is just bull on ahead. Just keep going. Just keep coming up with theories that would help to explain the hierarchy problem. And just imagine building even higher energy particle accelerators to test those theories. It is, you have to be honest, it is more of.

of a fishing expedition now. The LHC and the SSC that got canceled, they had a target to shoot for, the Electro Week scale, right? We didn't see, haven't seen yet anyway. I really hope that like the next month shows up a whole bunch of new particles and I can throw away this whole podcast, but right now we haven't seen any new particles at the LHC. So there's no very strong theoretical prediction that says, oh, just go one order of magnitude higher and you'll see a bunch of particles, okay? They might be there. The hierarchy problem is still the hierarchy problem, but whatever particles you discover will be have a little bit of extra energy themselves. They're not at the electric week scale. They would have to be at a higher energy, a higher mass. So it's a little

bit less clear that they would count as a solution to the hierarchy problem. But what are you going to do? Like again, nature is not being kind to us in this case. We have a puzzle. We're trying our best to solve it, right? I think that's what we're supposed to do. Now, there is another strategy besides just pulling on straightforwardly, which is rethink your assumptions, right? Take a step back, think about, okay, we have the cosmological constant problem, the strong CP problem, the hierarchy problem. These are all these puzzles that numbers that are in the standard model and could have been of order one are much, much smaller. What is going on with that? Okay, that's an absolutely. valid thing to do. It, in fact, is my preferred way of moving forward. I absolutely have tried. I have sat down. I have ideas. None of my ideas have been very good so far about really rethinking, you know, quantum field theory, effective field theory, naturalness, the structure of space time itself, to somehow make it more plausible that either the cosmoccial constant or the electric week scale should be much smaller than we naturally expect. But, you know, easier said than done. It's very easy to say, yes, rethink your deep assumptions. Okay, but the deep assumptions have been super productive and successful at explaining data up until today. So it's hard to rethink them without just breaking everything that represent all the successes we've had so far.

So by all means, rethink the assumptions, but that marching order is not very specific. It doesn't tell you what direction to margin, which assumption are we supposed to be rethinking. Again, I'm trying, other people are trying, but it's hard to know what to do. So this absence of particles, new particles at the Electro Week scale, is really concerning to the future of particle physics in my mind. I think that in my mind it's absolutely worth building a bigger, more energetic particle accelerator to look beyond what the LHCC is able to see, but in good conscience, I can't promise you will see anything. Anything new will rediscover the standard model, of course. I think it's worth it because it would truly expand our understanding of nature if we do find something, but I'm not the one writing the checks,

right? So I have to be honest about what the expectations are. I think this is a truly difficult problem. Is it a crisis? I don't know. Again, I don't think that nature ever said is going to be easy, Part of the joy, part of the challenge of this game is that the puzzles are hard. The things that we think about nature are tentative and subject to revision, and nature is tricky, and we're in regimes where our intuition is nowhere near good enough to make progress. So, again, I think what we're doing is what we're supposed to be doing. I don't see any crisis here. I see a sad situation where we didn't find as many particles yet.

as we wanted to, but that's different than a crisis. That's not because the physicists themselves have been doing anything wrong. And then the final thing I wanted to talk about is the idea of quantum gravity, right? Something that we don't understand perfectly well. I'm sure you've heard that. What should we do? We do have this effective field theory weak gravity understanding of quantum gravity that works perfectly fine, but we would like to understand the origin of the universe, the quantum nature of black holes, stuff like that. And here, you know, there's a slightly interesting story to tell because it's no doubt, I don't know what you've heard. If you're out there, if you're not within physics itself, there's a different feeling out there in the

public than there is within physics departments. Within physics departments, it is still true that string theory is very healthy. And it is, you know, is by far the most popular way of thinking about quantum gravity. You might have heard that string theory is dead, no one does it anymore, that's all completely wrong. Okay, now it might be wrong. Like string theory might not be the right theory. That's absolutely true. But within professional physics circles, it is still by far the most popular way of thinking about quantum gravity.

Why is that? Well, there's different explanations. We can go into the details about the history. But the main thing is that in, you know, The string theory was born in the late 1960s as a theory that tried to tackle the strong interactions, right? This is before we knew about QCD and quarks and whatever, and people realized that the experimental evidence of different particles that were strongly interacting might have well been fit by thinking about instead of particles, thinking about strings. In fact, what we now know is going on is that because the strong interactions are strong, because of confinement, if you have two quarks, it's not like an electron and a proton in a hydrogen atom where they have these electromagnetic fields that spread out in all directions around them. If you have two quarks, the gluon field that attaches them together is basically confined to a little tube from one quark to the other quark.

So it looks kind of like a string. You can imagine that little tube of gluons connecting the two quarks together could stretch and bounce. It could whirl around, right? It could have some angular momentum. There's various modes of vibration that it could have that are kind of like the vibrational modes of a string. So we understand why this collection of strongly interacting particles, not quarks, but the combined particles, the mesons and the barions, why you might have thought that thinking of them in terms of strings rather than quarks and gluons was the right way to go.

But when people thought about this hypothesis that the world was made of strings rather than particles, they kept running into the puzzle, the problem as they thought of it, that the theory kept predicting gravity. It kept predicting a spin-2 particle in particular, which has all the properties of the graviton. So eventually, they realized,

Well, look, gravity exists. Let's just take it seriously as a theory of gravity. So that was a research project in the 1970s. It was not a popular research project. It was like five people working on, I don't know, maybe more than five, but a very tiny number of people working on it very hard. And one of the reasons why it was not that popular is because, well, there's a couple reasons. Number one, no one in 1970s, very, very few people were thinking about quantum gravity. They were still having fun with the standard model and putting that together, right? Gravity seemed a little bit inaccessible. But number two, what we've learned by our studies of quantum field theory in the 20th century, especially these gauge theories that I told you about earlier, is they're very, very

delicate in some way. If you just write down a new theory and say, I have a gauge theory and here's some matter and here's some gauge forces, it's very, very easy for that theory to be ill-defined, for there to be reasons why it won't work, whether it's because there are negative energy particles or more commonly, there's something called the anomaly that you get when you quantize a gauge theory. You have a symmetry where the whole idea of a gauge theory is you're based on some symmetry, and it turns out that you can write down a symmetry of a classical theory, but then when you quantize the theory, the quantum theory no longer has that symmetry. You've broken the symmetry by the process of quantization. This is called an anomaly. And this is deadly if you have a gauge theory

in particle physics, the gauge symmetries are super duper important. So there is a requirement, if you have a well-defined gauge theory, that you not have an anomaly in it, that the symmetry is not broken by quantization. And everyone thought that string theory is just so complicated and all these random symmetries running around, that ultimately you would find some anomalies in it. and it wouldn't work. So in 1984, two things are happening in 1984. Number one, we had experimentally found the W and Z bosons. Okay, so it was pretty clear that what we now called the standard model of particle physics was on the right track. Basically, 1984 was around the year where particle physicists said, yeah, I think we got this one figured out. I think we have all the data to explain. We've made

predictions that we haven't yet tested. In 1984, we hadn't yet found the top quark, the Higgs, etc. But it was clear that the basic picture was on the right track. So where do you go next? What do you do? And the other thing that happened in 1984 is that Michael Green and John Schwartz showed that in string theory, all the anomalies cancel. There are no anomalies in super string theory. So it's super string theory because string theory, again, super symmetry, the symmetry, the symmetry, between bosons and fermions makes life easier in many ways. Whatever theory you have, if you make the supersymmetric version of it, it's nicer. The infinities go away, you can calculate things better.

So super string theory, it turns out supersymmetries, I don't want to say necessary, but super duper helpful in making string theory well defined. So in 1984, Green and Schwartz realized that super string theory is a perfectly viable theory of quantum gravity. It's finite. There's no infinities in the renormalization or anything like that. It's free of anomalies, and it predicts not only the existence of gravity, but the existence of other gauge forces, which might very well eventually end up being the electromagnetic weak and strong forces that we know about in the real world. There was a tiny problem that it only works in 10-dimensional space time. Okay, so that's no problem. Physicists are very brave.

they know what to do, take six of the dimensions, curl them up into a tiny little ball, and you can get an effective four-dimensional effective field theory, right? And it was soon realized after Green and Schwartz's breakthrough that there was a small number of different possibilities at the level of the 10-dimensional theories. There were only five different theories that were well-defined string theories. So the crucial thing, the reason why I'm going through that little bit of history is, at no point did the community of theoretical physicists say, let's do our best to think about quantum gravity. That is not a moment that ever happened, because they were already, like I said, very excited about field theory in the standard model.

And the string theorists were a tiny little minority that were trying something completely different. And it's not that the community said, let's think about quantum gravity. is that the string theorist said, here, you have a theory of quantum gravity right here that is very compatible with everything that we know otherwise, and might even be a theory of everything that also explains the standard model and so forth. So it wasn't that people sat around and said, what's the best way to quantize gravity? It's that this theory of quantum gravity fell in their lap.

People like Ed Witten said, this is a 21st century theory that somehow found his way into the 1980s, and we're going to spend decades figuring out what it's saying. Now, to be very, very fair, there was an enormous amount of overhype about string theory in the 1980s. Because it was potentially a theory of everything, people really got interested in this idea. Could you predict not just that there is gravity, which is nice, but also predict all the standard model and maybe some super symmetric version of the standard model and get the dark matter and figure out where all the parameters are and all those things. that was absolutely an ambition that people had in string theory in the 1980s. It didn't work. As you know, we would have told you if that had worked now.

It got worse over time. But also, since I was there, I can tell you that even though string theory was very, very hyped, there was a bandwagon that was launched in the 1980s, people were still quite skeptical or at least cautious about it. Many of the best physics departments in the world, didn't hire any string theorists at the time because they weren't sure whether the idea was just going to go away, whether it was just a fad. It really, the switch really flipped in the 90s when we had what is called the second super string revolution. We had the first revolution in 1984

with Green and Schwartz and the anomaly cancellations. In the 1990s, Joe Polchinski pointed out that string theory is not just a theory of strings. There are also these things called D-Brains, D-Rishley brains, which are not one-dimensional strings, but some of them are one-dimensional, but there's also two-dimensional brains, three-dimensional brains, four-dimensional brains, etc. This is brain B-R-A-N-E, a back construction out of membrane, okay? So Polchinsky pointed out the importance of these D-Brains for the fundamental way of defining string theory. That became very exciting, and then Witten quickly pointed out that, in fact, what was going on is that, what we thought were five separate string theories back in the 80s,

was just five different limits of a single theory. And in fact, there's a sixth limit called 11-dimensional supergravity, okay, which is not even a string theory, but it's a limit of this er theory, this overall theory, called M theory. And then Maldesana pointed out that this idea of holography that had been bandied about in the context of black holes

by Toft and Suskind, etc., had this wonderful property that you could implement it in what is called the ADS-CFT correspondence, where you have a five-dimensional anti-decidder space, which is a cosmological space time, that has a boundary at infinity that you can think of as flat space time in one lower dimension. And there is, you can imagine defining a ordinary, non-gravitational quantum field theory on the boundary that is holographically equivalent to the quantum gravity theory in the anti-de-sitter bulk. this is all amazingly, you know, exciting kind of stuff. So M theory, ADS, CFT, D brains, and this was the second super string revolution, and now people

got convinced, like a whole bunch of physics departments who didn't have any string theory suddenly hired string theorists. And that's the good news. The bad news is, you know, these D brains kind of threw a spanner into the works. Because back in the 80s, when you knew that string theory was naturally defined, in 10 dimensions and you said, okay, we're going to compactify the extra dimensions. We already knew there is a lot of different ways to compactify. And this is the subject of what are called Kalabi Yao manifolds, people like Brian Green,

who we had on the podcast. We're one of the experts, Andy Strominger, who we also had, were working on what kinds of Kolbiyal Manifolds could you compactify on? Once you had the d-brains, it turns out there's like a gazillion more ways to compactify. the extra dimensions. And it became very clear that you were not just going to start with M theory in 10 or 11 dimensions

and uniquely figure out why the standard model of particle physics in four dimensions is the physics that we observe. And in fact, you can have what is called a landscape of many, many different possibilities. And the number that is traditionally trotted out is 10 to the 500,

but that's a totally made up number. Some people think it's smaller, some people think it's infinity, but there's certainly not any obvious uniqueness in the way that you make the journey from string theory to the real world. Now, just because nature is mischievous, this was about the same time. Remember, this is mid-80s, okay, so Maldesana is like, I forget, 97 or 98. Then in 1998, we discovered the acceleration of the universe. Remember, those pesky astronomers told us that there is a cosmological constant. this rocked the world, as it should have, of theoretical physicists, because the idea that we had before for the cosmological constant was, you know, this number is way, way, way smaller than it should be. It should be at the plank scale. It's 10 to the minus 120 or less. In my mind,

this is how theoretical physicists thought at the time, in my mind, I don't know why the cosmological constant is smaller than I think it should be. But in the space of all possible theories that I don't know yet but I could imagine coming up with, it is easier for me to imagine some mechanism that takes this big number and squelters it all the way down to zero. Then it is to imagine a new mechanism that takes this big number and squelters it down to 10 to the minus 120 times its natural value, especially because that would be a weird, inexplicable coincidence with the value of the vacuum energy and the value of other energy densities in the universe, right? You know, we said right now, now that we know, we've discovered it,

it's 70% vacuum energy, 25% dark matter, 5% ordinary matter. So that's 30% matter, 70% vacuum energy. But these two quantities change with respect to each other rather dramatically as the universe expands. The density of dark energy stays constant. as the universe expands, and the density of matter goes down as the size of the universe cubed, because the volume goes up and the number of particles stays the same. So it's what is called a coincidence problem. Why in the world is the current ratio of vacuum energy to ordinary energy of order one, when it could be any other number. So most people before 1998 thought that we would eventually show that the cosmological constant is zero, we'd come up with some

theoretical explanation for that, but then it's not zero, probably, if the vacuum energy, if the reason why the universe is accelerating really is the vacuum energy. So guess what? There is this old idea that people have been bending around called the Anthropic principle and the multiverse, the idea that if you have in the universe different regions where the local laws of physics are different, then by a selection effect, we, complicated, intelligent, complex beings would only find ourselves in the subset of that ensemble of different possibilities that allowed for the existence of complex, organized life forms, right? It's a selection effect. It's environmental selection. It's the same reason why we're

not surprised that we human beings live on the earth rather than on the moon or on the sun, even though the sun is much bigger, because the conditions there are just not hospital. to us. In the solar system, there are conditions that are hospitable to life and conditions that are inhospitable. Of course, we're going to find ourselves in the hospitable region. So maybe, this idea that goes back to the 1980s or even the 70s, maybe if the universe is like that, maybe if the universe is an ensemble of many different local conditions, some of which are hospitable to life and some of which are not, some of the conditions that we observe around us can be explained by, environmental selection. We can only find ourselves in the regions that are allowed. And Stephen Weinberg

in the 1980s had pointed out that the cosmological constant was a ripe target for this kind of reasoning. We didn't know, said Weinberg, why the cosmological constant is so small, but if it were much bigger, we wouldn't be here to talk about it. It would not allow for the formation of galaxies and the existence of life and the long time span that the universe has and so on and so forth. So Weinberg pointed out that if that's the right answer, if there really is some kind of cosmological multiverse in which the cosmological constant takes on different values, then we would actually very naturally expect the value of the vacuum energy to be just big enough so that it's hard to find but not impossible. And so in 1998, that turned out to be what we found.

And the question became, are you going to take this anthropic idea seriously? And if so, you need a mechanism for making the cosmological constant different in different parts of the universe. And guess what? This idea of the string theory landscape fit perfectly into that aspiration, because with inflationary cosmology plus the string theory landscape, you can very easily make a multiverse where the cosmological constant takes on very different values from place to place. And so reluctantly, I don't think anyone was enthusiastic about it, maybe Andre Linday, but maybe no other people. Reluctantly, string theorists began to say,

maybe we're not going to find the ultimate answer to the cosmological constant problem. Maybe it's just we're in one of the 10 of the 500 ways of compactifying the extra dimensions that gives us the right answer. So a lot of people didn't like that. A lot of people still don't like that. Let me be clear. I don't want to go into too many details here, but string theory, whether or not it's right, we don't know whether it's right, but whether or not it's Right. It's led to a lot of exciting ideas that I think are very, very, very likely to be true. Even if string theory isn't true, some of the ideas that have been developed because of string theory, I personally think are extremely likely to ultimately find a place in our theory of quantum gravity.

These include ideas of holography, black hole complementarity, how to get information out of black holes as they evaporate away, the relationship between quantum information and immersion space time, many of these things have been developed within the umbrella of what we call string theory. And I don't think that they are going to go away. But there is a worry. Has string theory taken up all the oxygen? Has it prevented other theories of quantum gravity from getting the attention that they deserve? So again, I'll just give you my personal opinion.

No, it has not really. because there was never a moment. This is why I went through the idea that there was never a moment when the community of physicists said, yes, let's try to do quantum gravity. The time is right. Gravity is a very weak force. You can't make gravitons and detect them in a particle accelerator. Gravitons exist with almost 99.999% credence because of basic features of quantum field theory and general relativity.

But they're weak. They're weakly interacting, way, way more weekly interacting. than the actual weak interactions of particle physics. Because if you want, because the plank scale is a very high energy scale, gravity is correspondingly weak. So it is easy to do experiments on classical gravity. We do not know how to do experiments in the regime where both quantum mechanics and gravity are simultaneously relevant.

And because of that, it's very hard to make progress in quantum gravity. So as a problem, everyone agrees that quantizing gravity is important. But when physicists decide what to work on, they don't just say, well, what's important? They say what's important and what can we make progress on? Okay, this is a big reason why the foundations of quantum mechanics have been ignored for a long time because people don't know how to make progress on them. So string theory seemed to be an example of progress that we just got lucky with, right? A finite theory of quantum gravity just falling in our laps.

It might not be the right one. There are people out there, you know, one of my very first podcast interviews was with Carlo Rovelli. And later I interviewed Lee Smolin. These are both advocates of the loop quantum gravity approach to quantizing gravity. And I'm just not that excited about loop quantum gravity. It doesn't have the promise and the fruitfulness that string theory has. It's, you know, it's kind of a eat your vegetables. Here's a theory of gravity. Let's try to quantify. it and hope for the best. But, and other people will disagree, you're welcome to disagree. I have not seen any of the ideas that have been generated by people working in string

theory come out of loop quantum gravity or causal dynamical triangulations or Euclidean quantum gravity or these various other approaches that people think about. I think that string theory has been very fruitful in other ideas that may or may not be necessarily attached to string theory, but will still be very, very useful. So I think that string theory has been good for physics overall, whether or not it is overall, whether or not turns out to be the right theory of nature. And another footnote there that I want to add on, which is that there's an idea of unification, right, the theory of everything. That was the buzz phrase back in the 1980s, that we were going to take gravity and unify it along with the other forces. So what is the

backstory there. You know, Weinberg and Salam and their friends back in the 60s figured out, in some sense, how to unify electromagnetism and the weak force. It's kind of a clodgy unification because there's still, you know, different gauge symmetries running around, but it was super duper effective in terms of being right. It predicted all these things. The predictions came right. Nobel Prizes all around. And it was spectacularly successful. So that left out the strong interactions, right? The Electroweak theory is the electromagnetic and the weak interactions. It didn't, you can just tack on the strong interactions, SU3, QCD, but it's not unified with them. So a very, very natural thing to do in the 1970s was to try to unify the Electro-Weak interactions with the

strong interactions. And that was a challenge that people immediately took up. And the first famous example was George I and Glashow, Howard George I and Sheldon Glashow. proposed an SU5 grand unified model. And people were very excited because it seemed to be the way physics was going, more and more unification. And also, you made experimental predictions. One prediction you made was kind of unfortunate. You predicted that there were magnetic monopoles

that were much more dense than anything else in the universe. So that prediction was not borne out by reality. And it was a major, major motivation for Alan Gooth inventing the inflationary universe scenario in 1980. he pointed out you could inflate away all the magnetic monopoles that had predicted by grand unification. But the other experimental prediction was that the proton is not completely stable. You've unified quarks with leptons, right? Strongly interacting particles with non-strongly interacting particles.

As a result, you make a quantitative prediction that the proton will eventually decay. sometimes people talk about this as if it's like existentially worrisome like oh no even matter itself is not stable that never bothered me like the the lifetimes here we're talking about are 10 to the 35 years or something like that right we're not worried about this in a balance our investment portfolio kind of way but the nice thing is one decay every 10 to the 35 years isn't that often but what physicists know how to do is get a lot of particles together in the same place so you can

wait around and hope to see a proton decaying. And they did wait around and hope they did not see any protons decaying. So that was a blow, right? Grand unification. Grand unification is the label given to this idea of strong plus electro-week theory being unified. It does not include gravity. Grand unified theories or guts, as they were called, had nothing to do with gravity. They were a very big topic in the 1970s. They made a prediction that a proton would decay and it didn't. Again, as in many other cases, physicists are clever. You don't give up. You say, well, okay, we can still grand unify, but we can change around some of the parameters and some of the patterns and we can increase the lifetime of the proton so that you don't see it yet. Absolutely fair. People did that. But the

enthusiasm for grand unification has declined because it made a prediction that didn't come true. That's perfectly fair. That's what should happen. Again, no crisis going on. You're still trying because maybe it's true, but you're less enthusiastic than you were before. Then in the 1980s with string theory, there was the first well-posed theory that could unify, in principle, gravity with all the other forces, right? So that was very exciting, and people worked on that, and that was the theory of everything. So you still, to this day, now it's 2023, see a bunch of non-professional physicists thinking very hard about unifying things, unification, one form of unification or another. And what they've missed is that it's not the 1980s anymore. And it would be great to unify gravity

with the other forces of nature. That's a fine thing to think about doing, but it ain't enough. We know more now from thinking about the challenges of quantum gravity to realize that the real challenge, the real interest is not in unifying gravity with the other forces. You can play around with math and try to do that. The real challenge is that gravity seems to be a different kind of theory. It is not a straightforward quantum field theory. There's plenty of reasons to think that gravity is in some sense fundamentally non-local. It looks local in the weak field, effective field theory limit, etc. Local in the sense that if you poke the universe at one point, all the disturbances move away at the speed of light or light. less, right? But in gravity, in quantum gravity, you can imagine wormholes, virtual wormholes, or all sorts of weird spacetime geometries. In black holes, you have the idea that all the information is somehow encoded at the horizon, somehow in the black holes evaporate,

information travels from the inside to the outside, all of these non-local things going on. ADS-C-F-T is an example of an explicitly non-local connection between two different kinds of theories. So the challenge, the interest, the fun part of quantum gravity is not in unifying it with the other forces of nature. That's fine. Let's try to do that. That would have been a hot topic in the 1980s, still interesting. But now we have much more subtle, challenging features of quantum gravity that we would like to explain. So people are trying, but, you know, there's some fraction of people who are trying, right? What you will find, you know, I've interviewed a whole bunch of string theorists. They're honestly string theorists. People in that camp here on Mindscape. I almost don't want to forget anyone, but I already mentioned Annie Strominger. There was Clifford Johnson, Raphael Bousseau, Dada Englehart, right? Other people, Michael Dine has worked on the phenomenological side of string theory. And they don't want to call themselves string theorists. And it's not because they're embarrassed with string theory. It's because, you know,

sometimes they're doing string theory, sometimes they're not, who cares, they're doing theoretical physics, they're trying to understand the world, and the ultimate answers we get to how the world works might very well end up being inspired by string theory, but not being string theory, and that's fine. And those, I think that that set of activities is still very exciting. How could you not listen to the podcast I did with Natalie or Raphael or Andy and not be excited by what's going on there? So, I don't think this is a crisis either. You know, I think that quantum gravity is a very weird thing. It's experimentally very, very difficult to think about. But we've made sort of more progress than we really have any right to expect, honestly, in quantum gravity. And maybe we will continue to do that.

Maybe we'll continue to get lucky. But the fact that we're not done yet, the fact that we haven't completed it, that we haven't figured out exactly the path from M theory to the standard model particle physics, in my mind, is the least surprising thing in the world. That's one of the reasons why I don't do string theory myself. I think it is the best, most promising root we have to quantizing gravity compared to all the other roots. But it's hard. It's hard to make progress on it. And I think that there's other ways that we could think about. So that's my, I know, I told you at the beginning it was going to go on, right? But, you know, you're not forced to do this. You're not, there's no test at the end of it. You can listen to it if you want to. So,

I wanted to talk about those three segments, those three aspects of physics that were arguably, you know, crisis-laden. The fact that we have not yet pinned down the right models for the dark matter and dark energy, the fact that we have these naturalness problems and we keep coming up with theories to explain them, but they don't really seem to work. And the whole difficulty of quantum gravity and trying to find the right theory for that. So with that in mind, with that his background, what is the crisis? What is the purported, disastrous situation that physics is in? You know, I think that I don't want to be too unfair here, but I think a lot of the, if you dig into the specific arguments given by people who claim there's a crisis in physics, a lot of the time they come down to other people aren't working on my favorite ideas, which is fine. Like, everyone thinks that. Like if you, if you, you only have a finite lifespan, right?

And if you're a researcher, you only have a finite number of ideas that you can pursue, papers that you can write, et cetera. And if you, you're going to work on those ideas that you think are most interesting and promising. And when those ideas turn out to be in the minority, then you feel like everyone else is making a mistake. Why aren't they doing things my way? Why are they doing my favorite new theory of whatever? I get that. But it's, and this is, if there's a lesson to this whole long extended podcast, it's the following.

When we're in a situation where we don't know what the right answer is, or where we think that there is a theory that is better than the physical theories that we have right now, but we don't know which one it is. On the one hand, it's perfectly natural to spend your time working on what you think is the most promising way forward. but if you're honest about the health of the field as a whole, then you should hope that the field as a whole works on many different things, because you don't know what the right answer is. So if anyone is claiming there's a crisis in physics, and you dig down deeply into their justification for saying that, and it comes down to people are working on other ideas,

not the ideas that I like, I wouldn't take that too seriously. People are supposed to work on different ideas. And this whole situation is very hard, because, as we've discussed, we have a very good effective field theory. We have a theory that fits the data very, very well. There's some theories that we don't have pinned down yet, like the nature of the dark matter and so forth, and there we have more than one theory that is plausibly doing the job.

So what do you do in that situation? What is the healthy thing to do? And, you know, I was greatly impressed in the sense of an impression was made, not that I thought it was impressive, but an impression was made in a discussion that you can find online between Richard Feynman and Fred Hoyle. Feynman, you've heard of. Fred Hoyle, for those of you don't know, was a very successful astrophysicist and one of the primary proponents of the steady state model of the universe, as opposed to the Big Bang

model. But he was a brilliant guy. He just never quite let go of that steady state model. It's hard. This is something you see in science all the time. it's very hard to actually let go of your favorite theory, even when the data comes in and says that's not the way to go. This is why progress is made by people getting older and retiring as much as it is by people changing their minds. But the discussion, you might think, you know, Feynman was super duper successful.

Hoyle was pretty successful, but had some wacky ideas. You might think that the discussion between them would be, you know, oil haranguing Feynman about being too much in the establishment or something like that. But in fact, it was Feynman expressing great admiration for Fred Hoyle. And the direction of his admiration was not in any specific theory that Hoyle was proposing, but the style that they both used as successful theoretical physicists. Because Feynman points out that Hoyle was just fearless about putting forward speculative ideas, speculative new scenarios. whereas Feynman, in his own way of thinking about his own work, preferred to stick very, very close to what we already knew work.

His self-description, I'm not putting words in his mouth, he thought of himself as sort of reformulating things that we already know work to work better, right? And if you think about Feynman diagrams or the path integral or things like that, that is usually what he did. These are not overthrowing previously understood theories, renormalization, right? It's understanding theories that we already have. He had a couple of theories, which were, you know, speculative, but it was definitely not his usual mode of working. And this is a very interesting distinction because it continues on, right? I mean, Murray Gelman, Feynman's contemporary, was much more on the,

I'm going to propose a model side of things. But these are both very valid ways of. doing physics. You can both take what you already know and work within those paradigms. And I've written papers like that. You know, I've done papers on calculating things in the microwave background or large-scale structure or the Bayesian Second Law of Thermodynamics. I have also done the other thing proposing new models, right, being speculative. I propose models about Lorentz violation and quintessence and modified gravity in the arrow time and so forth. And you need to both, right? Even if an individual person wants to do one but not the other, the field needs both.

And you have to soldier on. And in different parts, different moments in history, one way of working might turn out to be more productive. And in other moments, the other one might be, and you might not know ahead of time. So we're in a situation now where people have been working within the known standard model and core theory for a long time to the extent that the improvements being made there are naturally going to get slower and slower. Like if you're tuning a car and trying to make it perform better and better, you can spend a lot of time tuning it and fixing it and whatever, but there is a maximum performance that you're going to reach.

And we're getting there. We're not there. There's still a lot of work to be done, especially when it comes to the strong interactions in QCD and so forth. There's plenty of things that we still need to understand about the good old-fashioned standard model. But a lot of modern fundamental physics is on the speculative sign, because we have the theory that works. We're trying to go beyond it. People propose new ideas, and then they try to test them. Most of them are going to fail. Sorry, only a few of them can be right. But that doesn't mean you don't need to do it. You have to do it anyway. You need to propose a whole bunch of ideas, even knowing that most

of them are going to fail. Now, there's another kind of worry, right? Not that people are just proposing a lot of speculative ideas, but they don't like the actual ideas that are being proposed, the most popular ideas. And that's, you know, perfectly intellectually respectable position to have. So I don't think it's intellectually respectable to be against the fact that particle physicists, fundamental physicists, are proposing a lot of ideas that are speculative and hard to test. That's just how we have to make progress. But the actual idea, that are being proposed, okay, you're absolutely welcome to think that it's the wrong direction to go in. So let's just quickly dance over some of the big targets here. There is supersymmetry.

As I said, supersymmetry, it popped up in, I think, maybe as early as the late 60s, right? But certainly in the 70s, it became popular. It has this nice feature. Super symmetry is this symmetry between bosons and fermions. It is both super highly constrained. in the sense that it is hard to write down theories of particle physics that are actually supersymmetric. Okay, it's much harder than non-super symmetric theories. That's a very sensible, generic feature of having symmetries in your theory. It constrains what you can do. And the other thing about supersymmetry is it makes life easier at a calculation, not a calculational level,

sometimes calculational level, but a mathematical level in terms of all these infinities that you worry about in particle physics. Ken Wilson said we don't have to worry about them in an effective field theory, but if your goal is more than an effective field theory, if your goal is a theory that covers everything, then you have to worry about the ultraviolet behavior of your theory. Physicists will often talk about whether a certain infrared theory, a theory of what is going on in the visible universe, at low energies, et cetera, has an ultraviolet completion, right?

Maybe you have an effective field theory that works perfectly well, low energies, but maybe there is no complete theory for which that is the low energy limit. That's an interesting thing to contemplate. And supersymmetry is absolutely indisputably helpful in trying to make a well-behaved ultraviolet theory. That doesn't mean it's necessarily true, but it's helpful. And the more supersymmetry you try to throw in, the more constrained things become, there's even a maximum amount of supersymmetry that you can put in your theory. once Joe Polchinski made the slightly lighthearted claim that if people doing loop quantum gravity were serious, they would undergo the following chain of logic.

They would say, okay, we have a theory of gravity, but it's not very well behaved at high energies, so let's make a supersymmetric version of our theory. That's fine. It's still loop quantum gravity but supersymmetric. And they would look at all the supersymmetries, and they would go, oh, you know, the way that you could have the most supersymmetry is if you were in 11-dimensional space-time, and then you would put a compactification of this 11-dimensional theory on a circle to make a 10-dimensional theory, and you would find that there are strings in that 10-dimensional

theory, and you would have reinvented string theory. Now, this is not exactly a plausible alternative history, especially because one of the things about loop quantum gravity is that it works best. In fact, it kind of only works naturally, let's say that. You never want to say something only works in physics because some clever person is going to find a way around it, but there's a natural living place for loop quantum gravity, which is three plus one dimensional space time, okay? I've heard string theorists, and this is, you know, now I've been apologizing and defending the status quo for a very long time here. Let me, let me tease the status quo a little bit. There's absolutely an idea that once you're embedded in the string theory world, you lose touch a little bit

with the real world, okay, with the world of three plus one dimensions and the quarks and leptons that we know about. The string theorists study these 10-dimensional, 11-dimensional theories so much in d-brains and compactifications that they begin to think, maybe casually, maybe in moments of weakness, they admit, they slip the tongue, and think that's right. That's clearly correct. And I've heard string theorists criticize loop quantum gravity because it only works in 3 plus 1 space-time dimensions. And people had to point out, well, that is where we live. That is the actual universe in which we live. You know, there's no obvious empirical necessity to have to live in 10 dimensions. It's a possibility, but we don't know. Anyway, I tease the string theorists. They're my friends,

too. So supersymmetry anyway, I don't think that it would necessarily lead you inevitably to string theory, but it is a perfectly obvious thing to try. There's a long history in physics of adding more symmetries and things get better. And it is phenomenologically interesting. You know, you literally double the number of particles in a supersymmetric theory from a non-superymmetric theory. You have a whole bunch of particles in the standard model, some bosons, some vermions. They don't match up with each other. But supersymmetry says that every such particle has a partner of the other kind of spin. So you have to double or more the number of particles in the super symmetric version of the standard model.

There's various supersymmetric versions of the standard model. And it's even, because it's constraining, it's even more specific than that in the phenomenology. You can't, in supersymmetric versions of the standard model, just take the Higgs boson and make a supersymmetric version of it. You need to take multiple versions of the original Higgs boson. You need to add more Higgs bosons to your regular non-superymmetric theory before you supersymmetrize. And so that's an interesting feature of the model that you could test at an accelerator and you could look at it, right? You could look for it. We did. We haven't found it yet. Again, it's possible that it's there, but we haven't found it yet. But let's be honest about supersymmetry. It's very, very helpful phenomenologically. It's very, very interesting in terms of predictions that it made. It also could have been found by now. And it's not necessary that it was found by now. Both of those things are simultaneously true. I don't want to be, you know, too pedantic or whatever, but sometimes.

Sometimes people pretend that one of those things is true, but not the other. It could have been found that it hasn't been. It could still be right. Because what happens is you know that supersymmetry is not manifest in the real world. When you look at the standard model, it by itself is not supersymmetric. You don't see this symmetry lying around. So you have to break the symmetry, just like Brow and Angler and Higgs and their friends broke the symmetry that we now know is the Electroweak symmetry, right? You have to somehow spontaneously break it.

So that means that there is an energy scale at which supersymmetry is broken. And you would predict, again, typically, normally, without working too hard, you would predict that the super partners that you don't directly see have masses of roughly that super symmetry breaking scale. And again, as I try to convince you for a very long spiel earlier, there was plenty of reason to think. in 70s, 80s, 90s, whatever, that there was something weird going on at the Electro-Weak scale, at the scale where the Higgs boson

gets its vacuum expectation value, and that gives masses to the W bosons, and the Z bosons, and all the fermions, and that scale is of order hundreds of GEV. So there was all the reason in the world, if you were a supersymmetry partisan, to think that the scale of supersymmetry breaking would be near that electro-smetry,

weak scale, maybe a little bit above it, okay, so that the effects trickle down and make the Higgs boson have the mass that it has. So weak scale supersymmetry was a very, very popular phenomenological prediction. Hypothesis, I should say. And again, you could have seen it by now very, very easily, and so you haven't. So what does that mean? Well, it means that there's lots of possibilities, but two possibilities suggest themselves very readily. One is that the scale of supersymmetry breaking, now imagining the supersymmetry is still real. Is it possible?

Super symmetry is true, even though we didn't see it yet? Yes. Either because the scale of supersymmetry is just a bit higher, for some reason, maybe there's some little mini hierarchy between the supersymmetry breaking scale and the Electro Week scale. So the LHC, which remember is not as high energy as the SSC would have been, just doesn't have the oomph to get there yet. That's plausible. You know, you begin to feel that you're grasping at straws a little bit, but it's certainly absolutely on the table as a possibility.

The other possibility is that the supersymmetry breaking scale is way up at the plank scale, that all of the dreams of new particles and dark matter candidates, etc. at the ElectraWeak scale were just misguided. Now, if that's true, supersymmetry would not serve as an explanation for the hierarchy problem. But it could still be true, right? We've lost supersymmetry as an explanation for the hierarchy problem if that scale, if that's true, if you have what is called high-scale supersymmetry breaking, but that it still could be true, right? And it's the job of the physicist to chase down what might be true. So I would say that given that the LHC has not found supersymmetry yet, it is 100% the right thing to decrease your credence that super symmetry is right from what it was, let's say, in 2005. If you had, whatever credence you had, the fact that super symmetry has not been found should, by

base's law, lower your credence because there was a prediction that gave you a chance that you would have seen it. You didn't. Your credence should go down. But it shouldn't go down to zero unless it was zero already. Okay? So you just have to be careful. You just have to really think it through. So I'm perfectly happy if people have lost their gungonness about supersymmetry, but you can't say that it's gone or has been ruled out or anything like that. Let me say just one more word about the hierarchy problem because I did mention it before. I alluded to it before, but maybe let me fill in a little bit. To me, the fact that the hierarchy problem didn't have some, doesn't have some obvious solution that popped in our faces when we turned on the LHC might, I'm kind

of cryptically optimistic that this means something really big. is going on. Okay? So what I mean by that is, you know, we already have the cosmological constant problem, and there's no easy way to solve that. We've been banging our heads about against the wall about that for a long time. There is the anthropic principle in the multiverse, but that doesn't really work for the hierarchy problem. You can easily imagine laws of physics that are compatible with intelligent life without having the Higgs boson be much later than the plank scale. So that's a different kind of thing. You know, in some sense, we have no good anthropic solutions for the hierarchy problem like we do for the cosmological constant problem. So people really thought

that they were going to find a whole bunch of new particles at the LHC to help explain the hierarchy problem, whether those were supersymmetric particles or particles from extra dimensions or strong dynamics or whatever. One thing or another would work. And they're not there yet. Maybe they'll be there tomorrow. Again, that's always possible, but let's imagine that they're not. Let's imagine that we run the LHC for several years, at higher energies and higher intensities and we don't see anything. Then you have two possible. responsibilities, right? One is there is no solution to the hierarchy problem. We just got lucky. The Higgs boson mass or the expectation value of the Higgs boson, if you want to think about it that way, just is much lower than the plank scale. It's a brute fact that we can accept, but we don't need to explain. You know, we've talked a

few times on the podcast with philosophers about what it means to explain something with Tonya Lombroso and with Simon Deo and most recently Katie Elliott. a little bit. Maybe there is no explanation for this. It's just a brute fact. That's a possibility. But the other possibility is that something way more dramatic and profound is going on, right? You know, when you say you have these expectations from effective field theory for the magnitude of the Higgs mass and the cosmontrial constant and they're way wrong, then it is very easy to say, okay, maybe something is wrong about your intuition about effective field theory. That's easy to But what is wrong about it?

And it could be something deep about the nature of space time or quantum field theory or something like that. Like I said, I've been trying to think of things. I haven't come up with anything very plausible yet, nothing, not even the least publishable unit, which academics like to talk about. No theory that even really came close to working there. But that's an exciting possibility because quantum field theory is so robust and so universal and so kind of hard to break that any way, that we can get a handle on ways in which our quantum field theory intuition just breaks down is potentially very, very interesting. On the flip side, it's a sort of negative result, right? I mean, if you just say, well, here's a calculation that doesn't work. Okay, that doesn't tell me

what does work. It doesn't give me much guidance as to how to go next. So I think that's something to keep an eye on for future progress, but it's hard to know what direction that future progress will be in. So I don't think there's any reason to be like, harshly negative about supers symmetry, et cetera. It was a very obvious thing to try. Now, you could be a little harsh about the precise amount of effort that has been put into supersymmetry. I'll get to that in a little bit. Let me, let's just put that on the table for a bit. String theory is obviously related to supersymmetry. Now, string theory, as I said, works best if you have super symmetry as part of it. So you get super string theory. You can absolutely have string theory and have

supersymmetry, we've broken at a very high scale, right? High scale super symmetry breaking at the plank scale, completely invisible to us at particle accelerators. So the fact that you didn't see supersymmetric particles yet at the LHC should lower your credence in supersymmetry, but shouldn't separately lower your credence in string theory, right? It lowers your credence in string theory because it lowers your credence in supersymmetry. It doesn't do it again. It doesn't sort of act twice. String theory doesn't really care if you have new particles at the LNG. LHC. As I said about the history of string theory, kind of fell in our laps. And it absolutely has not made direct connection with observation. And so I think that it's both true that it makes

perfect sense that we put a lot of effort into it. You know, when you get something nice dropped into your laps, then by all means, take advantage of it. It's also perfectly valid to say, you know, the progress has not been what we hoped. Let's broaden our horizons and think about other things. You know, I will say that the other options on the table are, for good reason, just not as attractive. It's not sociology, okay? It's not personality conflicts. It's not people trying to squelch the brave rebels or anything like that. There are physics-based reasons why people like string theory when it comes to quantum gravity. just to sketch out what is in the back of the mind of a lot of working string theorists. You know, as I said, string theory is a finite theory of quantum gravity.

You know, you can do your scattering predictions, et cetera. You get finite answers. That's semi-miraculous when it comes to quantum gravity. The other approaches, you know, there's probably many approaches out there. I shouldn't speak for all of them at once. But the popular alternative approaches to quantum gravity generally start by trying to to do just gravity. Okay? They're literally taking gravity as special and trying to quantize it.

And that's, again, a perfectly natural thing to try, but it's also perfectly natural to expect it won't work. Because if you think about what happens when you try to quantize gravity, that is to say, take some classical theory and apply it, the rules of quantum mechanics do it, and convert it into a quantum mechanical theory, whatever your approach is, you still have this Wilsonian distinction between what happens in the infrared at long distances, low energies, and what happens in the ultraviolet, short distances, high energies. And the structure of known physics is that there's really no regime in which what happens in the ultraviolet to gravity is independent of what happens to other things. Okay? I don't know. That was a kind of a tortured sentence,

but you know that you don't only have gravity in the world. You have all the other fields of nature in world, et cetera, and you know that they act as sources for gravity, right? Ordinary matter and energy and radiation create gravitational fields. So when you have a theory that has both gravity and it and other things, in that ultraviolet regime, in that high energy regime where everything is problematic and you're trying to invent a new theory of what's going on, there's no subset of that theory where you can turn on gravity and turn on everything else and get sensible answers. everything is important in the ultraviolet. Everything is, you know, energetic and bumping into each other and everything kind of matters.

That's part of why string theory seems a little miraculous, because it is a theory of everything. It includes not only gravity, but all the other stuff in the universe, and everything sort of miraculously conspires in the ultraviolet to give you a finite answer. So string theorists look at people trying to just quantize gravity, and they're like, what, What are you even trying that? There's no reason to think that that is going to work. Obviously, that doesn't imply that string theory is right. I'm just trying to give you a little bit of the reason why the physics community thinks that string theory is so much more promising than other approaches. It's not 100%, but it's a little bit of a reason. So, you know, should we be

critical of the fact that there was so much effort in string theory over the last few decades, even though it is not still connected with observations. You know, I have mixed feelings about that. I think that string theory has made progress. Like we've learned a lot about the structure of string theory itself, and we've learned a lot of lessons that sort of apply to quantum gravity more broadly, even if string theory itself turns out not to be on the right track, right? Things like, as I said, holography and complementarity and black hole information and things like that. All these insights as far as I can see came from people who were either string theorists or string theory adjacent. I don't know of any particular insights that came from non-string theory approaches that have

been that influential. The one possible counter example there is holography itself. Holography, the idea that the information contained in a black hole and maybe more broadly can be thought of as spread out over the horizon of the black hole rather than scattered through the interior. So something non-local and lower dimensional. Arguably, the first person to put forward that idea was Gerard Ettoft. He did it before Suskin did, but Suskin did in a way that was much clearer to the rest of the community and much more dramatic, and independently also, so they both get credit for it. But Toft was not really working within string theory.

He has worked within string theory, but he was actually, you know, ultimately, if you dig down, he was thinking about the foundations of quantum mechanics. he's interested in the foundations of quantum mechanics and that he had some discrete models and that led him to this holographic idea. But the development of those ideas has largely been within the string theory context. So that's one side of the story. I think that we've gotten some benefit from thinking so hard about string theory. On the other hand, I do think, as I, you know, alluded to in my joky story before, I do think that it has had an effect on the physical community, which is not entirely salutary.

There's the early generation of string theorists, if you're talking about the David Grosses and Ed Wittins, et cetera, of the world, those people grew up trying to fit the data, right? You can find papers by Ed Witten on dark matter candidates and predictions for astronomy, or papers by David Gross, obviously, in QCD, which was kind of a big deal in fitting the data, et cetera. So even though they were working on string theory, they were absolutely familiar. with the idea that the ultimate goal is to fit the data, is to come up with explanations for the real world.

And there's a whole generation, maybe by now two generations, of young string theories, who have only ever done string theory. And I'm thinking of string theory now in the broadest possible context where, you know, people who work on ADS-CFT and holography and all that stuff count as string theorists, even if they would know a string scattering diagram if it bit them in the nose, okay? The thing is that they're working in their little toy model space, where they have exactly solvable or at least, you know, very tractable situations like ADS-CFT that they can work like work in, they can take these d brains and they can overlap them, blah, blah, blah, blah, and they never need to worry about constraints from, I don't know, electric week precision tests or

Big Bang nucleosynthesis or whatever, because they're not even in that regime. They're not trying to explain the actual world. They're saying that, oh yeah, someday we'll get to the actual world, but right now we're trying to understand the features of super symmetric quantum field theories or d brains or ADS C of T or whatever. And I have very, very mixed feelings about this. I think I would personally be much happier if in addition to playing with those models, people kept front and center the idea that the ultimate goal is to explain the world of our experience, the world we actually see.

And there's absolutely a subset of the stringy community that kind of poohs that idea at this point, right? We're learning about the fundamental nature of string theory and guana field theory, not the dirty particularities of our world. I think that that is something that you can worry about. I think that, you know, you've got to keep your eyes on the prize. There was, you know, for a long time in the 80s and 90s a thriving string phenomenology movement. There's still people doing it, of course, but maybe the movement is a little bit less thriving than it used to be because it turns out to be really hard. But there's been almost a backlash or a backfire effect, I guess, where a lot of string theorists will sort of think it's just not their job to try to explain the messy particularities of the real world. And again, I think that that's, that is something I think you can legitimately worry about.

The real world should be the ultimate goal here. remember when we had Brian Green on the podcast, Brian is a very thoughtful guy and he was very honest and he says he absolutely can see a possible future history where string theory is only done in math departments, right? Where because people have not been focused on explaining the data and the real world, it becomes more, I mean, you do learn a lot about math by doing string theory. Edwiden won the Fields Medal, which is the highest mathematical prize you can win. And that might be fine. That might be what happens. But there is still also an ambition that string theory will actually explain something about the real world. So I think that's a difficult conversation to have within physics departments.

People don't like to be told that they're ignoring the real world. And so that's a tricky thing to get into. And I'll talk a little bit more about that in a second. But so I mentioned supersymmetry, string theory. And the last one I'll talk about very quickly is the multiverse. Again, I've talked about the multiverse a lot, so I don't need to go in a great detail, but just to emphasize things that I always emphasize, the current interest in the multiverse, to the extent that it exists, is not something that just came out of physicists saying,

wow, wouldn't it be cool that there was like a multiverse? There are all these universes. That's never been the motivation. You have pre-existing theories, namely inflationary cosmology, and string theory, and both of these theories are motivated by trying to explain features of the observed world. In the case of inflation, the fact that the cosmological universe we observe is spatially flat and very smooth on large scales. In the case of string theory, the fact that there is gravity and also gauge theories and also fermions in the universe. That, and they all have to fit together into some consistent framework. That was the original motivation for string theory. And then you follow your nose. You try to understand very well the predictions

of these theories, and you end up predicting a cosmological multiverse, at least in a large fraction of parameter space. Let's put it that way. Maybe you can avoid it. I don't even know, or maybe it's necessary. Maybe it's just optional. But it's certainly not that hard to get a cosmological multiverse in the combination of inflation plus string theory. You could also get a cosmological multiverse without inflation or string theory, but it's inflation and string. theory that sort of put it in front of you and you got to deal with it somehow. You can't just ignore the possibility, okay? And there are those who will say that even contemplating the multiverse is anti-scientific, because science should be about what we observe. And if you have a theory

that relies on things that you can never observe, that you can never see, even in principle, right, because they're outside our observable cosmological horizon, then what you're doing might be philosophy, but it's not science. That would be the argument. I don't think that argument is right at all, and I said so, said why many times, but let me very quickly review it, because it's relevant to this discussion. The thing about the multiverse is that it does matter. Just to say that the existence of other universes is not directly observable, therefore it's not scientific, I think is pretty obviously clearly wrong. It's a standard. example of bad philosophy, and scientists are not always well-trained at doing philosophy well.

The point is that it matters to scientific practice, whether or not there is a multiverse, right? The multiverse is something that could be true. It does not fit in to the things that Karl Popper was imagining when he invented the falsifiability criterion for separating science from non-science. What he was against are theories that really don't say anything that could be twisted to fit any possible empirical thing that happens in the world. The multiverse is not that. The multiverse absolutely says something. It says that the universe out there, far away, has different physical conditions than ours, okay? That is indisputably a thing that is being said, very precise and concrete.

It is not directly observable. That's an issue that we have to deal with, but it doesn't make it non-scientific. And here's the thing. The practice of science, as we've discussed, involves hypothesizing different models and trying to use them to best fit the data that we do observe. One of the puzzles we have, for example, is why is the cosmological constant so much smaller than the Planck scale? Well, maybe it's because there's a multiverse and the cosmological constant is just not a fundamental parameter. It takes on different values from place to place. And there's a selection effect that puts us in a region where the cosmological constant is just not a fundamental parameter. It takes on different values from place to place. And there's a selection effect that puts us in a region where the cosmological. constant is small. Or maybe there is no multiverse and there is a single unique predictive theory that tells you what the cosm partial constant is. Both of these possibilities are absolutely on the table as of right now. So as a theoretical physicist who is interested in this problem, what are you going to do? How are you going to spend your time? You don't know which of these possibilities is right. So imagine that you had an oracle or God or something who told

you indisputably that there really is a multiverse and that there really are regions of our space time where values of parameters like the cosmological constant take on different numerical values, okay? Then you would be really dumb if you just insisted on saying, well, I'm still going to work on a theory that predicts the cosmological constant taking on a unique value. You've just been told that that's wrong, okay? So of course, there is no such Oracle. There is no one who knows the right answer about this. But the point is that the work you do as a theoretical physicist will depend on whether or not there are regions far away where the cosmontral constant takes on different values. It matters.

You can't just say, well, I can't see those other universes, therefore I would ignore them. They play an explanatory role in what we actually do observe. And this is not like tricky or subtle. This is why it's a little frustrating for people like me. like it's not that hard to wrap your brain around this. You can't directly see the other regions of the universe, but they nevertheless play a role in explaining what we do see. Therefore, it is part of science, you know.

They're much like quarks and gluons. You don't see them directly either, or virtual particles or whatever your favorite example is. There's all sorts of examples of things you don't see directly, but nevertheless play a role in explaining what it is that we do see. the multiverse is just like that. So I don't think, I don't buy the argument that the multiverse is intrinsically anti-scientific in any way. I think that's just wrongheaded and bad philosophy, as I've said

before. Now, there's a more subtle version of this argument that I should give some credit to. It's that if you really have a multiverse where, you know, many, many, an infinite number of things happen. Okay, let's put it that way. An infinite number of regions that are all their separate universes and many different things happen, then it becomes hard. to make predictions, okay, even probabilistic predictions, because now the argument is not just, well, there's things I don't see, I don't like it, now the argument is you've lost predictive power because infinity divided by infinity is ill-defined, okay, because you're saying, well, I have an infinite number of regions of the universe, in an infinite number of them, the cosmontal constant

takes on a certain value, and in another infinite number of them it takes on a different value, how can you possibly predict what it is that you expect to see? Parenthetically, the way that these predictions are made is typically by assuming that we are typical in the set of all possible observers. I think that is a very, very bad, silly assumption, but that's a topic for another podcast. But anyway, the straightforward mathematical worry is that you just can't calculate anything, even in principle, because it's infinity divided by infinity. that's the argument that people like Paul Steinhart put forward saying that the current version of eternal inflation should not be taken seriously as a scientific hypothesis.

Now, that's a tricky one because there you have to say, well, maybe. You know, the thing about infinity divided by infinity is sometimes it's just completely ill-defined. If you just say those words, you can't actually pinpoint what the answer is. But in practice, for specific examples of infinity minus infinity, maybe there is a perfectly unique well-defined procedure for turning that into a well-defined number, right? And in the case of the cosmological multiverse, you just don't know. This is called the cosmological measure problem in multiverse study circles. And so what people like Steinhard is saying is, you can't ever solve the measure problem. And what people like me are saying is, how do you know that?

I mean, maybe you can't solve it. Maybe you just have to work harder. It's very hard because we don't have direct experimental guidance. But I don't think that the answer is to put your head in the sand and say, well, you just can't do it. Let's just think of other theories. If I had a convincing argument, it's hard to imagine what a convincing argument would be. But if I had a convincing argument that this sort of infinity divided by infinity problem was literally unsolvable, then I would take that as a very strong argument that he should not take the multiverse seriously. But I haven't seen any such

argument. And again, I don't even know what it would be like. It might be hard to figure out how to regularize this particular limit of infinity divided by infinity. And I'm not that convinced by any of the current proposals that have been put forward, but the fact is, there have been proposals that have been put forward. This is a question that you try to solve and you see whether you can answer it. You don't just insist that it is unsolvable question a priori. So anyway, I think that you can argue about the amount of effort that has been put into supersymmetry, string theory, the multiverse. That's a perfectly okay thing to discuss and to argue about. But none of these are pursued out of bad faith or conspiracy theories or, you know, some powerful person decides what is

allowed to be studied and what is not. They're pursued because they're good ideas. And I hope I've at least given you an insight into why the people who pursue them think that they are good ideas. Those people could be wrong. That's always possible. But they're trying their best. You know, every individual scientist wants to be right. I don't know if that's a dramatic, you know, wild claim these days, but the reason why people are working on these things is because they think that they're plausibly correct. Truly new good ideas, if you had an alternative to these ideas that had all of the promising features that the existing ideas have, would be very, very welcomed. It turns out that it's hard to come up with truly good new ideas. We're trying. Some people are trying, right?

But it is hard to do. Progress is slow. Nature is not being helpful at the moment. So that's the situation we are in. Okay. I want to wrap up. I've been going too long. I did predict it, right? You can at least say I made a falsifiable prediction that I would, I did, I promise you, I recorded the intro to this podcast before doing the podcast, but I knew I had a lot to say and I knew that I would indulge myself by talking a lot about known things, uh, about the standard model and things like that. But the reason why is not just complete self-indulgence. I really want to focus the idea that there are reasons why modern physicists think about things the way they do, okay? They're not just being lazy or group-thinky or whatever.

There's physics reasons why the currently most popular models are the most popular models. But there are also, the thing I want to wrap up with, perfectly legitimate concerns about how to handle the weird situation that we find ourselves in. By the weird situation we find ourselves in, what I mean is, as I said at the beginning, we have theories that fit all the data. Nature is not giving us clear, precise, experimental guidance about where to go from here. And that is a very, very tricky situation as an intellectual endeavor, okay, when you're really just left to your thoughts. you have the data like the data keep coming in. The experimentalist, don't blame the experimentalist.

It's not their fault that they haven't found data that is in wild contradiction to our expectations. It's nature's fault. The experimentalists are doing amazing things. And, you know, again, as I keep saying, maybe tomorrow we will find such a difference between theory and experiment. But right now we don't have it. So we are left to our thoughts in terms of how to go beyond it. And when you do have all sorts of new data coming in, and they're all surprising, you don't know how to fit them together and it's all a puzzle and it's all a lot of fun, then you can have people working on different approaches. And as soon as a new piece of data comes in, people's opinions can wildly change about which approach is more promising.

Okay. Like, you know, when you say, well, what if parity is not conserved? And then they go out and find that it's not conserved and, oh, okay, well, then everyone changes what they're working on? on, right? When the data is not flowing in, those rapid changes of direction driven by new experimental input are not there. So you're relying on people and their judgments about what is interesting and what is promising. Maybe string theory is the way to quantize gravity, maybe it's loop quantum gravity, maybe it's causal triangulations or something different than that. All the decisions about which to pursue, who to hire,

and there's a lot of levels of decisions here, right? Not only who do you hire on your faculty, but what do you teach your graduate students? What funding do you give? Who gets grants? Who gets to have a conference and who gets to get together with their friends? I mean, it would be perfectly legitimate to say, you know, progress in my subfield would have been faster

if we'd gotten more money to pursue it. You know, that's always a possibility. the trick is you have to convince the rest of the community that your approach is actually promising. So when data is not guiding you and when you just lean on human people deciding what is promising and what is not, biases can creep in. Everyone is biased, right? I mean, part of the bias is very simple and straightforward and obvious work on the thing that everyone else is working on, right? Because when you're a young person, there's always going to be some rogue genius doing whatever they want by. But most people are not geniuses. Most people are, you know, who are trying to be professional

academics. They're in grad school, their postdocs or whatever. They're trying their best. They know that most people in their positions are not ultimately going to be tenured faculty members. There is a very narrowing pipeline along the way from undergrad to grad to postdoc to faculty. Okay. So you can kind of puzzle away at your own little problems and put them on the archive and even get them published. And if nobody cares and what you've done, it's going to be hard to get hired or to get grant funding or whatever. There is, you know, part of the strategy you have to pursue, if you want to keep doing physics for a living, is to work on things that are on the one hand new and exciting, but on the other hand, relatable to the other people who are already out there.

So this is just a very natural, again, it's not evil or pernicious, it's just a very natural feature of the system, you know, what are you going to tell people who are hiring? Hire people who haven't done anything interesting? You know, you're not going to, that's not a very plausible strategy. You can't just say, like, hire everybody. There's a fixed number of jobs out there, okay? And there's a very natural, therefore, bias towards whatever theories are O'Coron at the time. But there's another, is a more subtle aspect of exactly this problem, which is that, okay, let's say that you're perfectly fair and rational. Okay. the hiring committee, some university are going to hire a new theoretical physicist, and you

know perfectly well that this particular theory might be right, this other approach might be right, people tend to do either one approach or the other, you're trying to figure out who to hire, and you think that there's a 90% chance that approach A is on the right track, and only a 10% chance that approach B is on the right track. You might argue, or you might naively expect, that 90% of the time you should hire a person working within Project A, which has a 90% chance of being right, and 10% of the time hire a person working within Project B. Here's the problem with that. You don't hire 10 people.

You don't hire 100 people or even 10 people. You hire a person every five years at best, maybe every 10 years or longer, depending how big your department is. you don't get a lot of chances at the prize, okay? You have to hire someone. And if you're a department like most departments where probably, you know, there's a big pipeline squeeze bottleneck between being postdoc and being junior faculty, but most junior faculty will eventually get tenure. So you hire someone, they're 30 years old, you're going to be with them for the next 40

years, right? So there's a, so a conservatism creeps in is what I'm getting at. You don't get to hire many people. When you hire them, you might very well be stuck with them as colleagues for the next four decades. And so it would be nice to take some chances, take a shot here and there, try, you know, roll the dice a little bit. But there is a natural conservatism that creeps in because you don't have that many chances to hire theoretical physicists and you want to be relevant and important department going forward. And, you know, maybe you can say, well, a very good person will start off. in paradigm B, but then eventually realize that it's not working and switched to paradigm A.

Sure. That's possible that it doesn't, it very often doesn't happen. I don't want to say that it doesn't often happen, but I should say that it often doesn't happen. How about that, right? People stick with the basic theory, the basic framework in which they've been working for a long time. The people who believe in the steady state theory kept working on the steady state theory for decades after we discovered the cosmic microwave background, okay? So what happens is that because you have individual departments doing the hiring and they don't get to hire many people, if there is a feeling in the community that one approach, approach A has a 90% chance of being right and approach B has a 10% chance of being right, roughly speaking, you hire 100% people working in approach A.

That's not always true because people are quirky and et cetera, et cetera, but there absolutely is going to be an enhancement of the bias against people working in approach A. B. It's exactly, this is very familiar from voting theory in a democracy, right? If you say, okay, we want to give everyone equal representation, but you have a bunch of states or counties or whatever where there's 90% of people voting for party A and 10% of the people voting for party B, every single state or every single county or whatever elects a representative from party A. You don't get 10% of party B in parliament, okay? The same kind of thing is happening. when you hire theoretical physicists. So as a field, it would be nice if we could give more representation, I think, to alternative ideas. I would completely agree with that critique of the

field as a whole. In my mind, when I have when I'm talking about alternative ideas now, I'm not talking about people wandering in off the street with their theory of everything. I'm talking about people who have come up, you know, understand all of modern physics very, very well, have done the work, have made a clear and conscientious decision that a particular minority approach is the best way forward and are doing their best, right, within that tradition. I do think that we have a failure of creating a mechanism for supporting and nurturing those kind of alternative ideas. And I think that's a shame. And some people, by the way, just don't want to have any support for alternative ideas. They think that they more or less know the right way forward.

You know, I started the thought experiment by saying, you know, imagine that you're perfectly rational and you distribute your credences. A lot of people distribute their credences 99.9% on one thing and 0.01% on everything else. So that also makes it hard. But what I'm trying to get across is there are a bunch of structural reasons why physics departments tend to be conservative. And they, conservative in the sense that they're going to hire people who are working in the areas that are sort of the sure things rather than the gambols. And the same thing goes for funding agencies and prize committees and so forth. Academia in general, not just physics departments. There's a lot of structural reasons why things are conservative. And I do think that's a problem.

I mean, you even see it in institutions like the Primator Institute, which is one of the world's greatest physics institutes right now. But when it started out, it was much quirkier. You know, Lee Smolin was there and Fotini Marco Pulu and a bunch of people and they were doing luke quantum gravity and weird approaches to the foundations of quantum mechanics. And as it grew and became more respectable, they turned into one of the world's great physics institutions, as I said, but they also became much more just mainstream and ordinary. It's a part of the life cycle of a physics department or institute. You have a plucky band of rebels and they kind of equilibrate and they become more normal and traditional. And you can't blame them. You can't blame

that particular institute because they're just trying to be a good physics institute, right? And their little part that they play turns out overall to make it harder and harder for small idiosyncratic research programs to flourish. You know, there are people who have tenure, you know, or senior people and they can work on their own quirky little ideas, right? That's part of the idea of tenure is that you're supposed to be shielded from the pressure to conform to everybody else's standards. But guess what? In a physics context, which is the one I'm familiar with, two things happen. Number one, you would like to have funding. You would like to get a grant to pay your summer salary, to pay your travel expenses, to pay for your new computer, to pay for your graduate students and postdocs.

And it's harder to get that grant. I know because not from applying for grants, but from being on the grant giving out committees. The grant giving out committees that I've been on are, I mean, if you had you been on them, you would actually be really impressed by how hard people try to do the right thing. Like, it's kind of like you see,

you hear stories about juries that go along the same directions. Like there's always terrible counter examples, but really people take their responsibilities pretty seriously. And they do want to support young people. They want to support daring ideas, etc. But it's just easier to give support to the things that are kind of sure things, right? Or at least the most likely thing to pay off in the eyes of the rest of the community. So that's one thing that happens. And the other thing that happens is, and this absolutely happens to me, like you might have as a senior person some quirky ideas that you think are interesting and fun, but the mainstream

doesn't really agree with your attitude on. But you need students, and you have students, whether you need them or not, they come to you as graduate students and would like to work on projects. And those students need to get jobs. You might be a senior person. You might be fine in your job. But they're at the beginning of their career.

And you can tell them, and I do, if you do this kind of thing, it might be fun and exciting, but it'll be hard to get a job doing it. And then they can make an educated decision about what to do. But oftentimes what they very, very sensibly want to do is, you know, please let me work on things that will allow me to be continually employed as a physicist. Okay. When you're a graduate student, that's not the time to take these giant risks,

unless you're the singular genius, in which case could be. But for most of us, you've got to be able to work in ways that other people recognize the value of your contribution. And that's, you know, it's not, again, it's not evil, right? It's not people trying to stamp down dissent or anything. It's just if I'm hiring postdocs, I'm going to want to hire someone who I can work with. That's not irrational or unreasonable. So if someone has their new, weird take on things that I have just no interest in,

it's very unlikely that since I rarely get to hire postdocs at all, that I'm going to spend my rare postdoc position on someone who I'm not going to. going to be able to work with, right? It's the system, it's the structure that forces you in this direction. It's not perniciousness or evil or some conspiracy theory. So even as a senior person, if you want to, you know, work with students and put them on the track to success, you are nudged in the mainstream kind of direction, whatever that mainstream is. So it just turns out to be really, really hard in the current system to say, you know, here is a minority, here's an unlikely shot. No one else thinks it's promising. I think maybe it has a chance. Let's put our precious finite

resources into it. So that, I think, I don't think that's a crisis, but I do think that it is something that is a failure or a shortcoming, let's put it that way, of the current system. I think that we absolutely need a mechanism to support diverse. reverse approaches. And it's, again, it's very hard to do because, I mean, it would be hard for me to say, okay, let's hire someone working on Mond or working on loop quantum gravity. I don't think that those approaches are very promising. But I do think that they're serious. You know, I think that they're like Tim Modlin when we had him on the podcast. He said, look, I don't, he's very anti-Everett, but he does think that it's a serious approach. It should be, it should be pursued by somebody,

even though not by him. So I think that we need. a better way of recognizing that kind of thing. We need a better way of separating out. Here is the approach we think is actually promising. Here is the set of complete crackpot theories. But here in between is a set of approaches that I don't think are personally promising, but they're serious and I could be wrong. Therefore, we should put some effort into supporting them. I have no idea how to actually make this happen. I'm not the boss of physics. But I do, you know, I want to be at least a little bit fair. I'm giving this very, very long spiel trying to explain why physics is the way it is, why it's not really a crisis, but I also do want to recognize that it's not perfect. It absolutely could be improved. And probably this is not just a deal with physics, right? This is probably a much broader feature of academia, whether it's economics or philosophy or history or whatever. There are bandwagons. There are mainstream views. People with their plucky minority views have a tough time. getting through. And we all know stories of the plucky minority view that turns out to triumph in the end.

Those are the very, very rare stories, to be clear. Most plucky minority views remain minority views. They become less plucky over time and eventually they fade away and you don't hear their stories. So it's hard to maintain a thriving and robust and diverse intellectual ecosystem. I wish we could do better than that. Does that rise to the level of a crisis? No, I don't think it really does. I mean, maybe 50 years from now, if we're still stuck with the core theory, then we might talk about crises in a more down-to-earth, you know, this is a real issue kind of way. But as I, you know, maybe this came across or maybe I need to say it more explicitly. It is true that the core theory works very well, and this is kind of frustrating. But there's no shortage of open questions that seem to be plausibly answerable.

What is the dark matter? energy evolve or not? What happens in black hole information theory? We didn't even mention why are there more barions and anti-barions? What is the origin of cosmic magnetic fields? Is there unification of the known forces? All of these things. Perfectly good questions. The hierarchy problem, the fact that it is not solved at the LHC, I mean, that is not very specific guidance, as I said, but maybe it's a hint. Maybe it's nudging us. And also, things come from out of the blue, right? You know, my particular response to the difficulty in coming up with plausible models that fit the data in modern fundamental physics has been to back up, right,

to step back, look at the foundations of things, rethink how we think about quantum mechanics and quantum field theory and the emergence of space time. And I certainly absolutely want to fit the data. You know, I absolutely want all of our speculations about quantum mechanics and gravity and version space time to end up with testable experimental predictions. I'm also, you know, perfectly well aware that that may or may not happen. I can't just insist on it, right? But you've got to try. You've got to keep it in the back of your mind as that's the ultimate goal and you have to keep asking those questions. So it's completely possible to me that even with just the current information we have, a theoretical breakthrough can really change our fortunes dramatically. If we're

actually able to come up with a theory that went from Everettian bare bones quantum state in Hilbert space to immersion space time to some particular prediction about the fluctuations from the early universe that we see in the microwave background or Lorentz invariance violations or you know something else like that everything could change you'd never know so this is what we signed up for you know we're trying our best nature never promised to be kind to us it's not because we're dumber. Now, the people doing theoretical physics today are just as smart as the people doing it 50 or 100 or 500 years ago. We have to take what nature gives us. And we're trying to do that. I do think we could be better at nurturing plucky minority approaches. Hopefully,

other people will, you know, think about that and try to come up with clever ways of doing it. I'm not like a build an institution kind of guy. That's not my strong suit myself. But I do hope, I do wish that there were more ways where people could pursue, especially in a situation where progress is slow. We're making progress in fundamental physics. We've come up with several wonderful ideas, but it's nowhere near the pace it was 100 years ago, right? You've got to face that.

That's a fact. And in that situation where progress is slower than it was before, that's the time to roll the dice a little bit, to take some chances. Everyone, every older theoretical physicist has a story about, you know, a story about how when they were younger, they had a cool idea, and they went to their mentors or their senior people and said, here's my cool idea. And they were told why the cool idea wouldn't work. And they said, oh, okay, I didn't know that. You're right. You're very wise and very smart. And then five years later, someone else actually wrote the cool idea and figured out how to make it work. Okay,

everyone has that story. I certainly do. It's so easy in physics to say why an idea won't work. It is harder to say, yeah, you know, I think it won't work, but let's pursue it anyway. Let's see. less like, you know, Alan Gooth, when he wrote his first paper on inflationary cosmology, had a model which clearly didn't work. And he publishes the paper and says, look, I know this doesn't work, but maybe someone will fix it. And of course, someone did and it went forward. That's a hard thing to do. I hope that we can become better at that. I'm completely optimistic about the future of physics. But I do think that we can do even better than we're doing right now. I think that we have to be, you know, this is not a time to be closed-minded to circle the wagons. It's a time to be expansive and

think about good ideas, take them seriously, and who knows, we might have a breakthrough that makes the second half of the 21st century just as exciting as the first half of the 20th century was.