Sean Carroll's Mindscape: Science, Society, Philosophy, Culture, Arts, and Ideas - Holiday Message | Hits and Misses

Episode Date: December 23, 2024

It's the end of the year, and time for our annual holiday break here at Mindscape. But as usual, we wrap up with a Holiday Message. This year, inspired by Joni Mitchell's "Hits" and "Misses" albums, I go through my scientific papers and talk about some of my favorites -- some of which were hits, in terms of making an impact on subsequent research, and some of which were misses by that standard. But I love them all! It's an excuse to talk about process -- how papers come to be, from the initial informal idea to sitting down and doing the work. Support Mindscape on Patreon. Blog post with transcript: https://www.preposterousuniverse.com/podcast/2024/12/23/holiday-message-hits-and-misses/ Here are links to the papers I discuss in the episode. S.M. Carroll, G.B. Field and R. Jackiw, 1990, "Limits on A Lorentz and Parity-Violating Modification of Electrodynamics,'' Phys. Rev. D 41, 1231. [pdf file; inSPIRE] S.M. Carroll, E. Farhi and A.H. Guth, 1992, "An Obstacle to Building a Time Machine,'' Phys. Rev. Lett. 68, 263; Erratum: 68, 3368. [pdf file; inSPIRE] S.M. Carroll, E. Farhi, A.H. Guth and K.D. Olum, 1994, "Energy-Momentum Restrictions on the Creation of Gott Time Machines,'' Phys. Rev. D 50, 6190; gr-qc/9404065. [arXiv; pdf; inSPIRE] S.M. Carroll, 1998, "Quintessence and the Rest of the World,'' Phys. Rev. Lett. 81, 3067; astro-ph/9806099. [arXiv; pdf; inSPIRE] S.M. Carroll, V. Duvvuri, M. Trodden, and M.S. Turner, 2003, "Is Cosmic Speed-Up Due to New Gravitational Physics?'' astro-ph/0306438. [arXiv; pdf; inSPIRE] S.M. Carroll and J. Chen, 2004, "Spontaneous Inflation and the Origin of the Arrow of Time'', hep-th/0410270. [arXiv, inSPIRE] L. Ackerman, M.R. Buckley, S.M. Carroll, and M. Kamionkowski, 2008, "Dark Matter and Dark Radiation," arxiv:0807.5126. [arXiv; pdf; inSPIRE] S.M. Carroll, M.C. Johnson, and L. Randall, 2009, "Dynamical Compactification," arxiv:0904.3115. [arXiv; pdf; inSPIRE] C. Cao, S.M. Carroll, and S. Michalakis, 2016, "Space from Hilbert Space: Recovering Geometry from Bulk Entanglement," arxiv:1606.08444. [arXiv, inSPIRE] C. Cao and S.M. Carroll, 2018, "Bulk Entanglement Gravity without a Boundary: Towards Finding Einstein's Equation in Hilbert Space," arxiv:1712.02803. [arXiv, inSPIRE] N. Bao, S.M. Carroll, A. Chatwin-Davies, J. Pollack, and G. Remmen, 2017, "Branches of the Black Hole Wave Function Need Not Contain Firewalls," arxiv:1712.04955. [arXiv, inSPIRE]

Hello, everyone. Welcome to the Mindscape Podcast. I'm your host, Sean Carroll. I'm not sure if I've ever mentioned it before, but one of my favorite singer-songwriters is Joni Mitchell, who everyone knows, of course, both because the singing and the songwriting are very good, but also the spirit. I like the way that Joni Mitchell approaches being a musician, being creative, and also dealing with the weirdness and nastiness of the music industry. I'll give you two examples. One is, there's a wonderful interview that I saw with her from the 70s where the interviewer said, I heard that you were mentioned as the female Bob Dylan, but you were not impressed with that. You didn't like that comparison.

Why not? He's great. And Joni Mitchell instantly says, have you ever heard him sing? Which I thought was very funny because they are, in fact, close friends or at least have been. The other is that after getting her start in the 60s and then having a lot of hit singles in the 70s, In the 80s, Joni Mitchell, of course, was told by her record company, it is time for a greatest hits album. And she said, well, my favorite songs are not necessarily the ones that sold the most copies that were the biggest hits.

So why don't we have an album that is just my favorite songs, that some of them are hits, some of them are not? The record company said no. And apparently the compromise, who knows how much of this story is accurate, but the compromise was they can out with two albums, one called hits and the other called misses. And the idea here is very, very important to emphasize that it's not that the misses were bad songs. It's the songs that Joni Mitchell herself had great fondness for. She really liked them. But for whatever reason, they didn't become as popular as the others.

I love this idea. And it came to mind when I was thinking about the podcast you're listening to right now, which is the annual holiday message. The holiday message is an unnumbered bonus episode. It's supposed to be short. They never end up being short. Sorry about that. But the original idea was maybe I would talk about, you know,

what had happened during the year or whatever. But the year in Minescape is always very, very eclectic and different. It's hard to find a small set of grand lessons to draw. So instead I've just been using it as sort of a free-for-all, something that is more frivolous and informal than a typical solo episode, but basically a mini-solo episode. And I've thought about this when thinking about the last podcast with Mike Wong, where he told a very charming story about the origin of this paper that was the inspiration for our episode, the paper about functional information and so forth, and how it came out of this group of people who were talking to each other. And it made me remember, I've said this before, but it is, I get a lot of questions about how a paper comes to be, right? How a certain idea comes out, how it shapes itself into an actual publication. In physics, that's the currency that we work in, right? We write papers. You don't

write books anymore in physics. You can write books, but those are not your, those are not the academic products that people care about. Let's put it that way. It's the papers that you have, especially in referee journals, that people care about. So your goals to write papers with good new physics ideas. So where do the ideas come from? How do you massage them into the shape that they're a paper? How do you get them published? How do you decide who to work with, what co-authors, what to include, when to publish? All those questions, right? And so I thought at first of maybe like picking out a favorite paper and talking about that, but then I have too many favorites. So I thought instead, since it's the holidays and I have a little bit of time, we'll do the hits or misses paradigm. And I will walk through some number, you know, let's put it this way. I'm going to talk about far fewer papers than I wanted to talk about. I now know how the rock star feels, who is four. forced to confront coming up with a listing for their greatest hits album. You know, there's always going to be edge cases. We're like, why is this one on there and not that one, right? But okay, we're going to talk about various papers that are both hits or misses in my scientific career.

Again, it's the holiday message. I can be self-indulgent as I want. And again, again, the idea is that I'm not going to talk about papers that didn't work out, that, you know, sometimes you write a paper, then you're like, why did I spend so much time doing that? But other times you write a paper and go like, no, I really, I really like this one. This is really good, but nevertheless, it doesn't make an impact. So making an impact matters. I'm not against making an impact. I'm someone who absolutely believes that you should aspire, not just to have true ideas, but to help other people understand those true ideas and have them be shared out there in the world. And in the way that scientific publishing works, that is quantified by how many people are

citing your paper. I don't think it's bad to hope that people cite your papers. I think that's part of the point of being a working scientist. So it does, however, help you quantify whether those papers have been hits or misses. So we're going to go through some examples of both. And as always, I want to thank everyone for spending the year here with Mindscape. It's been quite a ride. I'm always looking back over the people who appear during the year and I'm very impressed at the people I've been able to get on the podcast. This is the first year where we've had someone on the podcast and a couple months later, they won the Nobel Prize. That was Duran Asamoglu.

But we've had MacArthur Prizes. We've had Oscars. The Daniels won an Oscar after appearing on Mindscape. So we've been doing pretty well. And the audience matters just as much as the guests. So thank you, all of you. I hope you had a good 2024 and even better in 2025. Let's go.

My first ever published paper came out in 1990. It was not the first paper that I started writing, but as would turn out to be, true throughout my career. I'm very slow sometimes. So I had a paper that I worked on as an undergraduate on modeling and eclipsing binary star, Epsilon Araigy. And eventually we got a paper out about that in 1991. But by that time, I had already had another paper from my grad school days, my first ever published paper, was called Limits on a Lorentz and Parity-violating modification of Electrodynamics that I wrote with George Field and Roman Jakeef. Now, this is a weird collaboration in some ways. Romant-Chickev was a very accomplished quantum field theorist and

theoretical physicist. One of the pioneers of the idea of anomalies in gauge theories, sometimes called Adler-Bell-Yakkev Anomalies after Stephen Adler and John Bell, as well as Romon, who helped invent them. He also did a lot of work on the vacuum state of QCD and other ideas in, let us call it, mathematical physics. Romon loved to, he wasn't a mathematician. He didn't try to prove theorems or anything like that, but he loved to take new mathematical ideas and see how you could apply them in interesting physics contexts. And sometimes it paid off, right? It turns out, oh, it's actually super important for this or that physical application. Other times it was just kind of a cute math trick. That's how science goes sometimes. And George Field, of course, was my advisor, was my PhD advisor.

So you have to set the stage a little bit here. I was in a undergraduate at Villanova, and Villanova had no graduate school. No one there was interested in the kind of things I was interested. I was always interested in fundamental physics, particle physics, cosmology, gravity on the theoretical side of things. It was not a hotbed of that kind of research at Villanova. I applied to top-notch places to go. Some places just blatantly turned me down, Princeton. And Harvard turned me down. They literally said that Villanova was a lot of was just not up to snuff, that they'd never accepted someone from Billanova and weren't sure that I could hack it. But then I, these were the physics departments. I was awarded an NSF fellowship

and managed to use that to parlay my way into an acceptance in the astronomy department. So the reason I'm telling you this is just to know that all along I knew what I wanted to do was theoretical physics. But I found myself in an astronomy department because I figured Harvard's a great place, there's lots of great resources there. And I was somewhat correct. It was, it definitely hurt me not to be surrounded by other physics graduate students, et cetera. It's a different kind of vibe, right? But to some extent, I've overcome that. But anyway, the point is, you are randomly assigned an advisor when you get to the astronomy department at Harvard. And I was randomly assigned to George. George passed away this year. I wrote a little bit about that on my blog, if you want to read about it.

He was a huge figure in my life, one of the most influential people for me and a truly wonderful, wonderful person. So I got lucky because it was a completely random. random assignment of advisor and student. There just weren't any people in the Harvard Astronomy Department doing what you might call quantum field theory particle physics-y kinds of cosmology. George was the closest, and he was the closest for a very interesting reason. George was a theoretical astrophysicist, but his biggest work was in the interstellar medium and atomic and molecular physics and things like that, magnetic fields. Real astrophysics, right, gastrophysics, if you want to put it that way. He was stolen away from Berkeley by Harvard

in the 1970s to be the first director of the Harvard-Smithsonian Center for Astrophysics, and at some point in the 80s he stepped down from that and was sort of thinking about what research should do. Like he was always a restless intellectual person. He wanted to do something new, and he saw in the mid-1980s that there was a lot of excitement about particle physics and the early universe. So he said, well, I don't know anything about that. I will try to learn something about that. So in his very unique way, he was a student at a summer school in particle physics, the famous Leszouche summer schools, which I went to myself many years later. And he went as a student to this summer school. So he was surrounded by a bunch of other graduate students and himself,

a senior theoretical astrophysicist. And he sat on a bunch of lectures. And one of the lecturers was Roman Shakiv. And this was just before I got to grad school. And so Roman at the time was very interested in electro-magnetism and gauge theories more generally in three-dimensional space times. Okay, so two-plus-one dimensions, two dimensions of space, one dimension of time. Flatland, although if it's gravity, then gravity will make it curved land, but still a plane topologically. And it turns out there's, you know, in the spirit of Romanchiquef, there's a bunch of interesting mathematical things you can do if you imagine that you're doing electromagnetism in three dimensions instead of the four dimensions of the real world.

In particular, there are mathematical objects that naturally live in manifolds that are odd-dimensional. So like three-dimensional, for example, or five or seven, but not the four dimensions of the real world. And the most famous of these is the Churn-Simon's term, invented by SS Churn, and of course Jim Simons, who later left mathematics to found Renaissance technologies, became extremely rich and started the Simons Okay, so there's a lot of fun connections all over the place. So Romon had been working with his friends Stanley Desert and Gerrida Tuft on Chern-Simon's electromagnetism in 2-1 dimensions. Now, you can imagine being a condensed matter physicist and sort of confining things to a plane by using some material substrate, and that would be a place where maybe Chern-Simon's electromagnetism would be

relevant. Or you can imagine being a string theorist and having a two-dimensional brain or something. like that. But Roman didn't care. He was just interested in what would happen if you just let your imagination roam freely. George, on the other hand, as a student, was the down-to-earth astrophysicist, was like, why are we doing this? The world is four-dimensional. Space time is three-plus-one dimensional. How could you do something like this in the real world? That was his insistent question. And Roman was, you can't do that. It doesn't exist. And then, but eventually, because they're both very smart people, they realize there's a way to kind of do something. like it. But the point is you have to violate Lorentzin variance. That is to say, you have to pick

out a preferred frame of reference in the universe with respect to which you can measure your velocity, you know, in contradiction to the Michelson-Morley experiment and all the foundations of special relativity that Einstein sat on. But it was a very clever way of violating electrodynamics, violating Lorentzian variance, sorry. The idea being that, you know, in three-dimensional space around you, part of Lorentz invariance is rotational invariance. All of the different directions in space are created equal. If you draw a plane, right, a two-dimensional surface embedded in this three-dimensional space, you have to pick an orientation for the plane. So voila, you have violated rotational invariance, which is part of Lorentz invariance. So you can do the four-dimensional

version of that, and you can even do it in a relatively mild way. And this gets into mathematical niceties about invariance versus covariance and whatever. You don't to worry about. You don't to worry about it. But the point is, you can sort of still imagine a three plus one dimensional version of Chern-Simon's electromagnetism that picks out a preferred direction in space-time, but doesn't do anything else bad. In other words, it doesn't violate gauge invariance, or it doesn't make energies unbounded blow or anything like that, okay? It's relatively well-behaved in a whole bunch of ways. And basically what you're doing is taking a parameter that exists in the three-dimensional theory and making it a vector. Instead of a number, a mass scale, it is now a vector with a direction

in space time in the Lorentz violating theory. And then you imagine that this vector field fills all of space and is constant. Okay. So it's a vector field that is just the same direction everywhere throughout space interacting with the electromagnetic field that we know and love in a very straightforward way. And I think that George really at the time was not thinking about the deep implications for Lorentz invariance and whatever. From his perspective, you had some new equations. You had a modification of Maxwell's equations of electromagnetism. And that kind of thing just makes the theoretical physicist so happy because it's full employment. Every homework set that you ever did in electromagnetism when you took the class, you can now redo with this new version of electromagnetism.

To some people, this sounds horrible. To other people, it sounds like the most fun ever. So George sat down and got, you know, plain wave solutions and dynamo solutions for this modified version of electromagnetism and so forth. And that is exactly when I came on the scene. George had sort of played around with these equations. And both George and Romant had come back to Cambridge, Massachusetts, where both Harvard and MIT are located. And they said, let's keep talking about this. Maybe there's something interesting to do. So I met with them as the new grad student, George, basically. said, you know, why don't you come along and listen to us talk? Maybe it'll turn into something. And what we realized was, mostly George realized this, there was a way to experimentally test this idea of violating the Renson variance in this particular way, because it would cause what we now call cosmic byrefringence. I've talked about this before on the podcast, the screwy universe idea, a photon interacting with this vector field stretching throughout all the universe would rotate its polarization. And if only you knew the direction of polarization when it left the distant source, you would be able to tell how much it rotated by. And George was enough of a

real astronomer to know there were radio galaxies who had magnetic fields stretched along the direction of a jet, and they would be polarized perpendicularly to the jet. And you could take a picture of the jet and then take a picture of the polarization and compare them. Are they at 90 degrees or not? So that's where I come in as the new young student. You know, I don't recommend if you want to become a theoretical physicist doing things like quantum field theory or gravity or cosmology to go to an undergraduate institution that doesn't have any graduate classes. It was always a story of catching up for me because I didn't take quantum field theory until my second year in grad school, which is much later than people take it nowadays. if you're a good undergraduate, you'll take quantum field theory in your senior year as an undergraduate, generally. So I was lost.

A lot of the mathematical manipulations going on. I had to pick up the lingo, et cetera. But what I could do was collect the data. Now, I don't mean collect the data in the sense of going out to the telescope. I mean going to the library where you would pick out a paper version of the astrophysical journal, bring it to the Xerox machine, photocopy it, and then go to your computer. and type in the tables of data that other people had collected. So what I was doing was looking at polarization data, position angles, and of course the distance, the redshift for various radio

galaxies that I was able to find. And then I could do a little bit of something slightly more scientific, which is to do the statistical analysis on, you know, how good a fit is it if the vector is zero or if the vector is big, you know, what are the restrictions we could put on it? And the answer is we can put on very, very good restrictions. So we, we can put on very, very good restrictions. So we wrote a paper. None of us, neither Georgian or Roman or I, thought anyone would care about this paper because who wants to violate the Renson variance, right? What all of us had failed to take into consideration is precisely that joy of playing with new equations that physicists have. So that paper, as far as I know, that paper, other people had absolutely looked at, can you violate the

ransom variance and how can you experimentally test it. But we basically pioneered a new way of doing that based on terms in a Lagrangian, the Lagrangian being the foundational thing you write down, we define a quantum field theory. So this was guaranteed to be otherwise relatively well-behaved. There's issues, but it's relatively well-behaved. And so that opened up a floodgate of possibilities. You know, we basically had written a paper about one particular way to violate Lorenzen variance, but you could then start asking the question, what are the other ways?

What is the most general way that you could violate the Rensinvariants? And coupled all sorts of different fields, not just electromagnetism. And then you can ask, how do we experimentally test them? So Alan Costalecki, who was a later collaborator of mine at Indiana University, became the world's expert in this of figuring out all the different ways to violate the Renson variants and how to experimentally test them. And this idea led to new experimental tests that otherwise wouldn't have been done. So we got a lot of citations out of that one.

That was a hit, and it was a hit mostly because we opened up new possibilities. That's a lesson. As much as I can, I'm going to try to give people lessons from the hits and the misses. So the next one I wanted to talk about was a miss. Again, misses are things that I love dearly myself, but for some reason never took off out there in the citationalosphere. This is a collection of two papers. One is by myself, Eddie Fari, and Alan Gooth called An Obstacle to Building a Time Machine. and the other was with Eddie and Alan and myself and also Ken Olam called Energy Momentum Restrictions on the creation of Got Time Machines.

So what happened here was, time machine, of course, is just fancy science fiction talk for closed time-like curve in general relativity. The idea of a closed-time-like curve was an old one. The idea is time-like means you are always moving slower in the speed of light. Okay? in special relativity where space and time are fixed, you always move slower in the speed of light, you move on a time-like trajectory, and all the time-like trajectories basically move upward

in the space-time diagram, from the bottom to the top. So going forward in time means going upward in the diagram, that's all she wrote. In general relativity, now that you can curve space and time into each other, you can imagine that the overall geometry of space-time has the characteristics that locally you can move on a trajectory that is always moving slower than the speed of light, a well-formed time-like trajectory, but the global geometry of spacetime means that you zoom off in some direction and you come back before you left.

That would be a closed time-like curve. And the idea here is that it's 100% easy to write down spacetime geometries that have that property. what we don't know is if they appear in the real world. Does it actually happen, right? Can you build a time machine is the question. And around that time, I don't know, you know, sometimes these things just pop up around the early 1990s. This became a semi-hot topic in theoretical physics. This is when Kip Thorne and his friends used wormholes to show that you could make a time machine, close time-like curves, and eventually that led to interstellar and a whole bunch of other things. But there was another one, sort of a quirky little paper, that Richard Gott, an astrophysicist from Princeton, University came out with, where he showed how to construct a space time with closed time-like curves using cosmic strings. Now, cosmic strings are not necessarily known to exist, but theoretically, they're very easy to describe. They could be leftover topological defects from the cooling of the early universe. Just like you can have fractures in ice or crystals when they cool and try to settle into an ordered state, you can have fractures in the universe

itself, which would show up as cosmic strings. And you can then go and actually solve Einstein's equation to find what is the gravitational field around a cosmic string. And the answer is super interesting. If you have a single cosmic string that is perfectly straight, okay, and remains perfectly straight and infinitely long, then you can stand right next to it, even if it's very, very high energy, and there's no gravitational pull of the string on you. So in other words, in general relativity terms, the space time outside the cosmic string is perfectly flat. There's no gravitational field. How can that be, you ask, given that you're positing that the cosmic string itself has an enormous amount of energy, and energy creates the curvature of

space time? The answer is that there is curvature of space time, but only exactly at the location of the cosmic string, not outside. And what that means is the following. Ordinarily, if I have a gyroscope and I carry around, there's a little vector, and you know, the gyroscope, saying where the axis is, around which the gyroscope is rotating. And if you take, in flat space time, if you take a gyroscope and you move it around a circle, it comes back to exactly the position it was in when it left, right? And this is actually a mathematical operation called the halonomy of the vector. How does it rotate as you travel around a closed loop? If you take that gyroscope and you do a holonomy around the cosmic string, it does not come back

to where it started. Because basically, it is sensitive not just to the curvature of space time along its path, but the total amount of curvature of space time inside the path that it describes as a closed loop. Okay. So there is curvature in the space time. In fact, in much more lowbrow terms, it's a cone. It's a conical singularity in space time. If you take a big piece of paper and you put a dot on the piece of paper and then you cut a little wedge, a little angle out of the piece of paper that leads to the dot, so it's a perfectly two straight sides with an angle in between them. And then you, if you know general relativity or if you know your differential geometry enough,

the intrinsic geometry of the piece of paper, other than at the point where you is at the center of your angle, the intrinsic geometry of the paper is still flat, no matter what you do to it. If you crumple it or whatever, if you crumple the piece of paper, you're changing its relationship to the outside world, but you're not changing its intrinsic geometry, which is still flat. So I can take these two straight lines that I've cut out at an angle from my center point, and I can glue them together, and the rest of the piece of paper makes a cone. That is the geometry of a cosmic string. It's flat outside and a conical singularity right there.

So that's great for theorists because you can basically solve equations exactly when the solutions are that simple. So anyway, what Richard Gott had shown is if I have two infinitely long cosmic strings that are both perfectly straight and they're parallel to each other, but they're moving, they're moving past each other at a super high velocity, then you can solve all the equations exactly and you find that there are closed time-like curves in that geometry. So that's the got time machine named after Richard Gott, okay? On the one hand, super interesting.

On the other hand, you absolutely furrow your brow because, where in the world are you going to get two cosmic strings that are infinitely long, perfectly straight, parallel to each other, and moving at high velocity? Well, you know, maybe it's just an approximation to something deeper. So at this time, when God came out with his paper, I was taking some classes at MIT, including a class on quantum field theory and particle physics that Eddie Farie was teaching. And Eddie was on the lookout for a student to talk to, and so he asked me whether I'd be interested in talking with him about the Got Time Machine. Like, tried to understand what it was there. It was very vague

at the beginning. It was like, you know, what is going on here? Can we think about it in some clever way? Can we show how to make one or that you can't make one or whatever? And so we tried and we, you know, we made some progress. The super important, helpful insight here, and it harkens back to something we said before, is that because the cosmic strings are perfectly straight and parallel, nothing happens along the direction of the strings actually extending, right? So in other words, all of the action is basically in the directions defined by a plane perpendicular to the cosmic strings. In yet other words, the theory of perfectly straight parallel cosmic strings in three plus one dimensions is the same

as the theory of point particles in two plus one dimensional gravity. So said all over again, forget about the 3 plus 1 dimensional world and just do gravity in 2 plus 1 dimensions and ask, what is the gravitational feel around a point particle? The answer is there's no space-time curvature around that point particle, but it deforms the overall space-time into a conical shape, which is flat outside but an overall deficit angle if you make a loop around it. So we could analyze the whole problem, instead of two cosmic strings moving past each other, as two point particles in three dimensions moving past each other, including their gravitational field. So that was very helpful. And we did make progress, but we didn't actually crack the problem.

And eventually, Eddie was talking to his good friend, Alan Gooth, Alan, of course, the pioneer of the inflationary cosmology paradigm. And Alan had some very, very good ideas for how to make progress on this, including he did some numerical simulations, which was a little bit overkill, as far as I could tell. But basically, we figured. out what was the statement we wanted to make. So this is, again, sort of a lesson for you young scientists out there. We didn't even know what we wanted to say, what we started the paper, right? We just said, this is cool, this is interesting, let's think about it, let's see if we can come up with something that would be interesting to say. And eventually, here is what we

came up with to say. If you start in a space time that is a two plus one dimensional space time with some point particles that does not already have a got time machine in it. So the point particles are moving slowly with respect to each other, not fast enough. God showed that given the masses of the particles, they would have to be moving faster than a certain velocity in order to make this time machine. And so we proved, well, that's not true. Prove is too strong. We came up with an argument, let's put it that way, that said that if the particles aren't already moving fast enough, you can't get them to move fast enough to make a got time machine. And we had to be a little bit clever about that, and we all did contribute about, you know,

how do you propel a particle in two plus one dimensional gravity while conserving energy and things like that? And, you know, we figured that out. So we wrote a paper, basically saying you can't build a got time machine because you don't have enough energy. At least it seems that way. But it was very like we did an example and it didn't work. It wasn't an airtight proof. By the way, it was like slightly awkward. situation, because as I mentioned, Romant Jakiev, who is also at MIT, and Stanley Deser and

Gerarda Tuft, had been like the bosses of two plus one dimensional physics for a while, and they had also pioneered two plus one dimensional gravity, and they read the Gottime machine paper and were outraged. So like, no, this can't work. And they wrote a paper against it. But honestly, I think their paper was just not that convincing. They just said, we don't like it. It doesn't seem physical to us.

Whereas what Eddie and Alan and I tried to do was, you know, forget about whether you like it or not, we're saying, if you start with these boundary conditions, you can't get to it. And then we thought, you know, okay, but we want to do a little bit better. It's going to be a little bit more serious, a little bit more rigorous in proving that you can't do this. And the, and again, we sort of bang our head against it. You know, how do you make this work, et cetera? And the breakthrough came when I was traveling to give a talk at the University of Alberta. and Don Page, the famous cosmologist and quantum physicist, was there, and also one of his students or postdocs, Alex Lyons, was there, and the three of us were talking together. And offhandedly, Don says, well, of course, because I was talking about the group of Lorentz transformations in 2 plus 1 dimensions, which is S.O.2.1. And Don Page casually mentions, of course, that is anti-de-sitter space. And I said, what are you talking about? That is anti-de-sitter space. And he explained to me, that Lee groups, I didn't know this, but these continuous groups of transformations,

all the symmetry groups you've ever heard of, S.O3, SU2, et cetera, they're all manifolds in their own rights, and they have a natural metric on them. And the Lorentz group in three dimensions, the group of Lorentz boosts and rotations and so forth, has a geometry that happens to be exactly that of three-dimensional antit-sitter space. This is long before the ADS-CFT correspondence or anything like that, and I didn't know anything about antitistiter space. I knew that it was a solution to Einstein's equations

with a negative cosmological constant, but I didn't really know anything more deep about that. So he said that, and it was just sort of a toss-off remark, but it stuck in my brain. And on the plane ride home, I was thinking about, and I realized we could use that insight, that fact, to make a much simpler proof of the claim that we wanted to.

to make. We could make basically a proof that you can't build the time machine without starting from one using nothing but drawing pictures of trajectories in anti-decidder space. And it was very lovely, and I got to come back and talk to Alanetti and explain to them that I had done this, and they instantly got it. And yes, it was much, much cleaner than the, this is, you know, I love equations, but I really like diagrams better. And so when I was able to translate our equations into a diagram. I was much happier. Let's put it that way. Okay, but what happened was Alan and Eddie and I, we got a little, we got a little full of ourselves. So we wrote a paper with some title, something like, you know, time machines cannot be created in an open two plus one

dimensional universe with time by total momentum or something like that. And because we were feeling it a little bit, the title of our paper was that declarative statement. And then the abstract was simply four words. We prove the title. And we were very pleased with ourselves in doing this. So anyone who's ever seen a TV show or movie knows what's coming next, we put the paper on the archive and people pointed out to us that we had not proven the title. There were loopholes in our argument. And we, again, we sort of, you know, you bang your head against it. How do you close the loopholes and whatever? And as often happens, we started talking to people. And we talked to Ken Olam, who was another grad student of Allen's at MIT at the time. And we said, and we said, and

Ken has now been a researcher in cosmology at Tufts for a very long time, super smart guy. And Ken came up with some very good suggestions for fixing our proof, basically. And it took a while, and it was interesting because, you know, the reason I'm sort of going into the details is because who are the authors on a paper, right? This is always a good question. What kind of contribution counts? And Ken's contributions went from, you know, meriting an acknowledgement in the paper to meriting a very very important. strong acknowledgement in the paper to being a co-author on the paper. And that can happen, depending on just how your conversations go. So in the revised version of the paper, Ken was a co-author,

we changed the title to simply energy momentum restrictions on the creation of got time machines, and we had a real abstract explaining what was going on. So, but I was very proud of that paper, both because I thought that the question was really interesting, and I thought that I was happy with the cleverness of the way that we could do it. It was a miss. It was not a hit. Nobody cared. It got very few citations for either one of those papers. I guess the, well, of course, there's a lot of interest in closed time-like curves and close time machines, but where do you put your interest? So in the wormhole world, in the world that Kip Thorne and its friends were moving in,

you couldn't solve the equations exactly, okay? It's too hard. A wormhole solution in general relativity in three plus one dimensions is interesting, but very, very hard to exactly solve the equations, you have to sort of go on things you think are physically interesting. In our world, appoint particles in three dimensions. You can solve all the equations exactly, but it's not the real world, right? So what are you interested in? Are you interested in the real world where you can only kind of solve the equations or the fake world where you can solve them exactly? There's good reasons to be interested in both, but in this case, people thought that

the real world was more interesting. Good for them. And also, I didn't actually expect that this would happen, but it did happen. People who we talked about this result to were, you know, looked down their noses at it just because we were writing about time machines. It was really that level of snootiness. You know, there's a famous acknowledgement in one of Kip Thorne's papers saying, you know, usually in the acknowledgement section you say you talk, you acknowledge the people you talk to, but then you also acknowledge your funding sources. So Kip in one of his time machine papers wrote, this work was not. supported by the National Science Foundation because I've been told that I cannot use my National Science Foundation grant to support work on time machines. And I thought that was very funny, but it happened to me. I remember going to, you know, apply for postdocs, and I interviewed at the Harvard Society of Fellows. And one of the people there was like, really, you wrote about time machines? And literally, he said, what would Richard Feynman say about that? Well, you know, Feynman, in fact, had thought about closed time like curves himself, so he probably would have been fine with it. But

I was just surprised that people were really like that. I mean, if we had called it classifying the space of violations of global hyperbolicity in three-dimensional solutions to Einstein's field equations, no one would have objected, even though it was exactly the same content to the paper. But if you call it an obstacle to building a time machine, suddenly they cop an attitude, you know, what can you do? Anyway, so I love those papers, but they were not really hits. Moving on. Moving on is important here because I took a postdoc at MIT where we finished up that second paper. The first paper was written while I was still a grad student at Harvard. And then I took a second postdoc at what was then the Institute for Theoretical Physics is now the

Kavli Institute for Theoretical Physics at UC Santa Barbara. And I was making sort of career-oriented mistakes right and left. I was very bad at guiding my career. I was basically working on quirky things that I thought were interesting and no one else cared about. And it was not going to get me a job. I was not a hot property on the job market. And so by the end of my second postdoc, my second postdoc went from 1996 to 1999, halfway through, let's say, I realized like if I'm going to continue in this physics thing, I have to write some papers that people care about, right, that actually have an impact on the field. Again, I am not one of those people who thinks that it is bad to try to have an impact on the field. I think that that's a good thing. That's why we do this. So just writing my own little

that I thought were cute, but no one else cared about, was not really the only thing I should be doing. You spend some of your time doing that, but it can't be the only thing. So sadly, I was just not an expert in anything that the rest of the world was interested in at the time. You know, the mid-80s, people were super interested on the theoretical physics side of things, in dualities and M-theory and the second superstring revolution and things like that, none of which were really my bag. Or on the cosmology side of things, we discovered the temperature antisotropies

in the cosmic microwave background, and we were learning cosmological parameters from them or were beginning to, so there was a huge amount of work in figuring out how best to extract the information that would be coming down from the new generation of cosmic background experiments and satellites

and plug it into cosmological models. Also, it was like super important stuff to do and not what I would do for a living. So I was kind of stuck in between. Happily, the accelerating universe came to my rescue. So in 1998, astronomers announced that they had evidence that the universe was not only expanding, but accelerating. The easiest explanation for which would be the cosmological constant that had been

proposed by Einstein back in 1917. Now, I was for no especially good reason of my own the world's expert in the cosmological constant, or one of the world's experts. I had, along with Bill Press and Ed Turner, written a review article on the Cosmautical Constant in 1992. Well, we didn't even think that it was real, but we thought, well, yeah, okay, we'll write down some equations, give you some options here. I had also written a paper with Greg Anderson, which was a, you know, what we would now call an early model of dark energy before anyone had come up with a term dark energy. And I was also very close friends and frequent communicators with both of the supernova teams that were actually measuring the acceleration of the universe.

Saul Promotor's team from Berkeley and Brian Schmidt, Adam Rees, Bob Kirchner, that team, Nick Sunsiff, lots of people that measured the cosmuchal constant from the high z supernova team. And so I was friends with them. Adam has been on the podcast as a previous podcast guest. Brian Schmidt was my office mate in grad school. Saul and I had talked before they ever wrote their first paper about, you know, because he knew that I was a co-author on the review article. So anyway, I had an inn with the accelerating universe. And Brian even sent me some of the plots before they became public. And I didn't, you know, I was not

allowed to release them to the public. But when the news became public, I could, you know, give talks and use the plots and things like that. So it was great. But it didn't help me any, as far as writing papers until I could say something interesting in the form of a physics paper. So literally I was saying, like, what do I have to say about this? And there was a lot of effort by people like Paul Steinhart and Rob Caldwell and others on dynamical candidates for the dark energy. That is to say what they were calling at the time quintessence fields, like a scalar field that would have very, very slowly changing energy density. So it would look kind of like a cosmological constant, like a true vacuum energy, but it wouldn't really be a vacuum energy and maybe

you have some interesting astrophysical effects. And this was popular, and I could have written about that, but it bugged me, to be honest. Like, the whole discourse bugged me. And the reason why it bugged me is because by 1998, unlike, you know, eight years earlier, but by 1998, I knew some quantum field theory, you know, I was still not a super expert, but I knew a little bit. And I knew that you couldn't just write down scalar fields with absurdly small masses. The mass of the scalar field that you need to be quintessence is something like 10 to the minus 33 electron volts. Just for comparison purposes, the electron is about half a million electron volts, and the lightest massive particle, which are the neutrinos, are thought to be about 10 to the minus

3 electron volts. And this quintessence field that you're positing is 10 to the minus 33 electron volts. Where in the world did that come from? Ordinarily, in quantum field theory, if we have a mass parameter that is very, very small, there's a reason why. There's a symmetry or something like this that makes it that way. and these people, these cosmologists, were just writing it down because it fit the data, which is also a fine thing to do, but you would like to be a little bit more respectable than that.

And furthermore, once you have that light scalar field, it can couple to other fields, and you can even estimate how big the coupling should be and say, should I have seen this scalar field already in the experiments? And the answer was certainly yes. And I knew this very informally, like in my head. It wasn't like a detailed calculation. It was just sort of background knowledge. But what hit me was, I knew a loophole to this whole argument.

Because remember that first paper I wrote with Roman and George about violating the Renson variants, there was something about that that did always bug me when we were first writing the paper. We start with the idea that you have a constant vector field filling all of space time, right? Well, that sounds very innocent and innocuous, but there's no such thing as a constant vector field in a curved space time. The mathematical criterion that a vector field be constant doesn't make any sense once you're in a curved manifold. So what do you even mean?

Like you can make it make sense in cosmology, which we did. That's all we looked at in that first paper. But in a more general situation, there's just no way to do it. So there's different strategies you can have. Basically, there's two strategies. One is the vector field is not actually constant, but it's constant length, and it wants to more or less line up so that it becomes essentially constant or pretty close. This is called an ether field. Ted Jacobson and others have worked on this, and I later wrote papers about it. But in the particular case of the vector field that George and Roman and I use, there's a simpler way to do it.

If instead of a vector field, you have a scalar field, that is to say, a field that is just a number at every point in space time, rather than a vector with a magnitude in a direction, but that scalar field is changing. So the scalar field has a derivative. It has a gradient. It has a direction and a magnitude in which it is changing. That gradient of the scalar field is a vector field. So rather than the vector field itself being the thing that violates Lorentzian variance, you could just have a scalar field that is changing gradually throughout the universe, and that would pick out a preferred reference frame, the rest frame of the scalar field, and there would be a vector that would be the gradient of that scalar field. And it turns out that you can couple it naturally to electromagnetism. And this is all, compatible with symmetries that mean that you can't couple this scalar field to other fields in any way at all. At least, well, there's some loopholes there, but that's the basic idea. So basically what I'm saying is if you wanted to have a scalar field that could be the dark energy, and that scalar field has a natural symmetry that both keeps its mass low and prevents it from coupling to other fields,

then there's a natural way to do it. And I knew what that natural way. was. So I wrote a paper in 1998 called Quintessence and the rest of the world. And the idea was to say, here's how you can have your quintessence without it violating all the usual rules about experimental bounds with other fields. And the cherry on the top of the Sunday was, of course, there was one experimental effect. It was cosmological bi-refringence. It was exactly that photons traveling through this quintessence field, this pseudoscaler field. It's a pseudo-scaler because it's odd underpens. parody transformations, they would rotate their planes of polarization. And you could search for that in the data. And, you know, George and Roma and I had put a limit on that, but the limit wasn't

as good as possible. Maybe there was still some room under there. And in fact, in the quintessence in the rest of the world paper, I estimated what you might guess for the parameters you knew about dark energy, what you might guess the rotation is. And the answer was about one degree, which was smaller than the limits. We had a limit of about five degrees, or I think, yeah, five degrees, two degrees. I forget what it was. It depends on what data source you used. But the point was, it was on the one hand, below the limit, so we were not incompatible, and on the other hand, reachable if you improved the data. And so these days, people like my colleague Mark Kamienkowski and others showed that you could do even better if you use the cosmic microwave background,

and people are trying to do that. And so that's an ongoing, interesting thing going on. So that paper was a hit. That was the time, 1998, where the whole accelerators, writing universe thing, was new and exciting and sexy, and all the ideas, you know, the low-hanging fruit had not been picked, you could write down a model, you could point some things out, you could point out mistakes other people were making, and would all have a big impact. So that paper went very well and has gotten a lot of citations since then. So now we can move on to the next phase when I was at the University of Chicago, and I'll tell you, I was looking back for this podcast at my CV, looking for the, you know, the list of favorite papers. And it's, I can't find any

real misses when I was at the University of Chicago. There were some misses in terms of not getting citations, but the papers I loved when I was there also were very big hits, got a lot of citations overall. Like, very roughly, I'm counting over 100 citations as good. It's not super good until you get over 1,000, roughly speaking, by physics standards. Everyone's standards are different. I should mention, by the way, especially for those of you out there who have your own podcast or are doing your own research on important questions of scientific moment, you can find out who has written papers. They get a lot of citations and what those papers are and who has cited them. Just go to Google Scholar and type them in. So if you are trying to book someone for your

podcast and they claim to be a biologist and have an important new theory about the origin of COVID or something like that, plug them in. And it doesn't, the fact that someone has a lot of citations doesn't mean they're sensible. There's Nobel Prize winners who are no longer sensible people. But it is a good first pass at saying, like, is this a real scientist who's written papers and has made an impact on the community or not? It is not airtight. Don't get me wrong. There's highly cited papers that are nonsense. There are papers that have no citations that are great, but it is correlated. Having a positive impact on the rest of the field is correlated with being a good paper, and it's easy to check by anyone by going online. So anyway, yes, I wrote a bunch of papers.

I kind of, they did well when I was at the University of Chicago. In terms of the Joni Mitchell analogy, this would be the blue for the roses, quart and spark period of my output, as it were. I know what you're thinking. At the end of that period, I was denied tenure and had to leave. Why did that happen if all my papers were getting all these citations? Yeah, good, good question. I don't know. Sometimes the academic wheel is a little conundial. infusing in how it moves. But anyway, let me pick a couple papers. Again, what I care most about here is being informative about the process. How do you come up with ideas? How do you come up with papers, choose collaborators, things like that? So it's still the aftermath. My years of the

University of Chicago are still the aftermath of having discovered the dark energy in the celebration of the universe. And I was thinking about that a lot. It was obviously an important question to think about. It's only kind of an interesting question if it's not the cosmological constant. The cosmological constant is the best, most likely candidate for what the dark energy is. It's the simplest. It's the most robust. It is not subject to these experimental tests I was just telling you about. It's a puzzle why it is small. But even if you have a non-cosmological constant candidate for what the dark energy is, it is still a puzzle why the cosmological constant is small. That's just a puzzle one way or the other. You're not getting rid of that. In the very,

very early days of dynamical dark energy models, there was a hope we could pick the dynamics of the scalar field, so it would somehow explain why the cosmontrial constant is small, but that basically never works. So we're basically looking around for alternatives just because there may be, either, number one, they're sort of interesting two physicists, whether or not they're more robust and simpler than the cosmotical constant, but also number two, two, maybe something good will happen. Maybe by playing around with different ways of making the universe accelerate, you'll realize, oh, you know, in step five of thinking about it, you'll go, this actually does help solve the cosmological constant problem or something like that.

So especially in those days, the early 2000s, it was absolutely perfectly sensible to think hard about all the different ways you could make the universe accelerate. And there was, it was also, you know, we also knew that dark matter existed, right? There was evidence for dark matter. And there was this ongoing debate about whether or not dark matter could be replaced by modifying gravity. Okay. In fact, you know, there was this nice numerical coincidence that if you look at a galaxy like the Milky Way or other large spiral galaxies, Mond, modified Newtonian dynamics from Mordecai Milgram, pointed out that there was a radius around the middle of the galaxy, around the center of the galaxy, interior to which you don't need dark matter, and outside of which you do. And that radius is different

for different galaxies. It's not a fixed distance, but the acceleration due to gravity, in the good old Newtonian sense, is approximately equal in all the different galaxies that Milgram originally looked at. And numerically, the acceleration due to gravity where the data from rotation curves in spiral galaxies stops fitting, and you need to invoke dark matter, is numerically approximately equal to the Hubble constant today, which is numerically approximately equal to the cosmological constant today in appropriate units, where you have to take the right powers and divide by Newton's constant and things like that. So these things are all numerically similar to each other. It is very, very natural to ask if that numerical similarity is related to some underlying

physical common origin. Is there so? some reason why this feature of the dark matter, namely where it is in spiral galaxies, it makes perfect sense that there's more dark matter at the edges of galaxies than at the center because ordinary matter naturally falls into the center in ways that dark matter doesn't, but the specific place where that crossover happens is less obvious. And why it's connected to the Hubble constant, maybe it's just because there's not that many numbers it can be, but maybe there's a deeper physical understanding. So I thought about that, and I was trying to think, I was very sympathetic to the

the idea that we would come up with a way of replacing dark matter by modifying gravity. Right? I thought that was a very interesting idea. Today, 20 years later, I'm much more down on that idea because it's basically been ruled out by the data. I know that people are hanging on to it, but once ideas are ruled out by the data, I lose interest in them. At the time, though, in 2004, I was very interested.

And so I specifically was focusing on this similarity, right? The similarity of the acceleration scale where dark matter kicks in in spiral gas. galaxies and the acceleration scale where the universe starts accelerating because they're numerically similar to each other. So I said, what is common between these two features, these two parts of the universe, these two regimes of space time? And the answer is that gravity is weak, right? If you think about the gravitational field of a galaxy, there's more stuff near the center of the galaxy than near the edges. So the gravitational field becomes weaker and weaker. And it is where the gravitational field becomes sufficiently weak that you need to invoke dark matter or modified

gravity. Likewise, for the expansion of the universe, at early times when the universe is dense and expanding rapidly, the curvature of space time is relatively large, and it's late in the history of the universe when space time is becoming more and more flat overall, that you have this new thing kick in, and you need to have the universe accelerate. So I said to myself, okay, can we make money out of that? we make money out of the fact that in both the dark matter case and the dark energy case, the new effect seems to be kicking in when gravity is weak. That's a weird thing, right? That's not what you would expect, but that's okay.

You're trying to fit the data. Sometimes you try to fit data. You have to go to weird places. So is there any way to modify our favorite theory of gravity, Einstein's general relativity, in such a way that it is still general relativity in ordinary circumstances, but when space time becomes nearly flat, you do. deviate from that. And again, I know a little bit of quantum field theory, so I was able to think about this in terms of how would a quantum field theorist, this is all classical, in fact. So how

would a classical field theorist think about this? You know, Einstein and his friend David Hilbert figured out that you could derive Einstein's equations from an action principle, an action, the principle of least action says that there's this quantity you can calculate that is minimized when you solve the equations of motion. And the question is, what is the action? The action turns out to be an integral of the Lagrangian. I mentioned Lagrangian before that I learned about when we were writing our paper on Lorenz violation in cosmology. So could you write down an action which is ordinary when space time is curved and weird and different when space time is nearly flat? Well, the simplest thing to do is just to add a constant to the action, but we already did that with the cosmological constant.

The next simplest thing to do is to write something that is inversely dependent on the curvature, right? You have an easy number called the curvature scaler, capital R. For those of you who have read space, time, and motion, the biggest idea is number one. Capital R, the curvature scalar, that appears in Einstein's equation. R all by itself is basically the Lagrangian that gives you general relativity. So what about something that is a number that it gets bigger and bigger when R gets smaller and smaller? Like one over R is the simplest thing you could possibly do, okay? So what if you modified gravity by just writing down R plus 1 over R instead of just R all by itself as the action for gravity?

So, you know, then it's a homework problem then, right? You have your idea and now you have to solve the equations. I knew how to go from that kind of proposal to equations of motion and try to solve them and things like that. Eventually I learned, I think it was Ted Jacobson who mentioned this to me, but I would have stumbled across it myself just in, in, you know, searching other people's papers, whenever you have a theory of gravity that is some modification of general relativity just by doing weird things with the curvature scalar, you can, you basically bring a new degree of freedom to life. Einstein's original theory by itself has only the metric, as its only dynamical degree of freedom. But if you do, if you try to

mess around with it, generically, you will bring to life other degrees of freedom. That makes perfect sense once you know little quantum field theory. In particular, this kind of theory, R plus 1 over R, is actually equivalent to what is called a scalar tensor theory. You have a tensor field, the metric, and you also have a scalar field that you just brought to life with this kind of new action. And you can then show that in such theories, the Schwarzschild solution, the solution that you get in ordinary general relativity around the sun or something like that, is also a solution to your scalar tensor theory. So what this means is that you're not going to expect anything new and weird

when you're far away from a gravitating object like the galaxy. So I realized that this approach maybe it would help the universe accelerate. I mean, I showed that, yes, there are solutions where the universe is accelerating, but it did not help with dark matter. So my dream, my aspirations of unifying dark matter and dark energy into one modification of gravity failed. And therefore, my response was to put it in a drawer and forget about it. Like I said, okay, well, it didn't work, too bad.

And I didn't think anything more of it. And what happened was I got an, I forget the order of operations here, but two things happened. One is I got an email from Mark Trotten, who was a good friend of mine and frequent collaborator. And this was months later, and he said, has anyone ever written or looked into a theory of gravity that has a one-over-R-term in the gravitational Lagrangian, just like the ordinary R-term. And I said, well, I did. I found this and this and this, but I didn't really get very excited about it. And like almost at the same time, Vikram DeVorey, who was a grad student at the University

of Chicago at the time, working with Mike Turner, came into my office and said, has anyone ever thought of adding a one-over-R-term, the Lagrangian for gravity, to change the equations of motion? And I'm like, well, I guess I did. and I thought it was not interesting, but clearly it is interesting because people keep knocking on my door or sending me emails saying, let's do this. So we ended up doing that. And it ended up being me, Vikram, Mike Turner, and Mark Trotten on a paper called Is Cosmic Speed Up due to new gravitational physics. And again, it's, you know, this is a lesson that I never really learn, but I should learn. I thought it was a fun little model. You know, at first I put it in the drawer, but then eventually the team. ended up pushing it out the door and into the physical review, and it blew up. It's by far my highest cited original research paper by now, in part because it's full employment. It gives theoretical physicists a new toy to play with. We write down a way to modify gravity, and we don't

talk about dark matter at all. We're not trying to explain dark matter, but does it explain the acceleration of the universe? Well, you know, maybe, but guess what? Someone writes a paper saying, oh, actually it's incompatible with the following experimental bound. And someone else writes a paper saying, oh, but there's this twist that we can put on it that helps it escape that experimental bound. And you go on and on. And you try to constrain it against large-scale structure

and come up with two variations on the theme. You open a new kind of set of research questions by suggesting that. So I've done that twice in my life successfully so far with the Lorenz-violating stuff and with the modified gravity stuff. So give people a new playground to play in. That is the lesson for getting songs on your hit record there. Okay, so then I'm going to, like I said,

most of my papers did pretty well during that period, but I'm going to classify this one as kind of a miss, even though it really wasn't. And this is the well-known paper, spontaneous inflation and the and the origin of the arrow of time that I wrote with Jennifer Chen. So Jenny Chen was a grad student at Chicago at the time. This did get, this crossed my hundred citation threshold, but it didn't get as many citations as I think it should have. So I'm going to put it in the Mrs. album here. The idea here was, you probably know the story. Many of you know the story, but not all of you. So I'll tell it anyway. There is this question about the arrow of time. Why does time have an arrow? Well, we kind of know the answer, and the answer is because entropy is increasing.

Why is entropy increasing? Well, there's two parts to that answer. One is from Ludwig Boltzmann, who said what you mean by entropy is the number of one of the possible things you could mean by it. There's a footnote here. There's many different definitions of entropy. The one is relevant here is the entropy is the logarithm of the number of ways you can arrange the system so that it looks macroscopically the same. The logarithm of the number of microstates within a macro state. That's half the answer. The other half the answer, why is entropy increasing, is because it started in a number of the number.

a low entropy, microstate, okay? The past hypothesis, there's an initial condition that is crucially important to explaining the second law of thermodynamics. That's obviously a job for cosmologists, right? And this has been pointed out that this is a job for cosmologists by many, many people. Richard Feynman writes about it in the character of physical law and the Feynman lectures on physics and so forth. He thought that Caltech first-year undergraduates should understand this, even though most modern cosmologists still don't. We need to understand and why the early universe had low entropy. And I learned about that fact from Roger Penrose. Penrose in the 1970s really emphasized the fact that the early universe had low entropy, and that was a mystery.

That was very, very strange. In the 1980s, inflationary cosmology comes along and pretends to explain this problem and doesn't really succeed. It might be part of the solution, but by itself, it simply asserts an initial condition just like anything else. So as far as I was concerned, in the 2000s, this was still unanswered. And for me, the tipping point was, well, there are two tipping points. One was I read a paper by Hugh Price, the philosopher of science, who coined what he called the double standard principle. There were a lot of cosmological models at the time.

So before we discovered dark energy especially, Price was writing about models where we didn't even know whether the universe was open, closed, or flat. So it could be, in principle, that if you have a universe with enough energy in it, it will expand for a while, stop expanding, and then recalapse, right, as a closed universe. There's no reason, if you have a model

that has a big bang, expands, cools, and then starts recalapsing and crunches again, just because you put initial conditions on where entropy is low, there's no reason you should put last conditions on so that entropy is low, final conditions. The entropy should just grow if you don't do something, if you don't impose something to make it do something different. So you could easily have models where the universe expands and then recalapses. The big bang is low entropy, but the big crunch is high entropy.

What Price pointed out was that in cosmologists' attempts to account for the low entropy of the early universe, they cheated. They cheat over and over again. They invent principles. They don't even necessarily talk about entropy, but they talk about the simplicity or whatever, the naturalness of the initial conditions. But they don't apply those same criteria of simplicity or naturalness

to the final conditions. And that's fine if you think that there is some intrinsic direction of time, some intrinsic difference between the past and the future. But the laws of physics don't have that, and most of the cosmologists who were writing these models down,

didn't believe that there was any such intrinsic directionality to time. So they were just cheating. So Price's double standard principle is, if you think something is natural for the early universe, you should think it's natural for the late universe, okay, for the beginning and for the end. Now, he was writing this paper before we knew about the acceleration of the universe. So his conclusion was the universe probably does have a big bang and a big crunch, and they are both low entropy. We don't know why. Either one is low entropy, but at least it's playing fair. At least it's using the same criteria for both the future and the past.

So to a physicist, this was not the right direction. Like the laying out of the problem was perfectly sensible, et cetera. But basically, for the sake of being playing fair, you're imposing equally weird ill justified conditions on both the past and the future. That does not make things better. That makes things worse. So I was very, very interested in, could you solve this problem without sort of making things worse, without putting any fine tuning in there. And at the time, so 2004 is when we wrote the paper, I was certainly thinking a lot about the accelerating universe.

So the accelerating universe will eventually become decider space. So let's put it this way. And this is this sort of, I can't even tell you exactly when which idea appeared. This is something that Jenny and I were talking about back and forth for a while. and I was also spending time at a program back at KITP on super string cosmology at the time. So I was talking to people there too, David Gross and Tom Banks and a bunch of people, Joe Polchinski. And decider space is, like anti-desider space is the solution to Einstein's equations with a negative cosmological constant, decider space is the solution to Einstein's equation with a positive cosmological constant, a positive vacuum energy.

And that has a, if you draw a picture of it, very, very roughly, it looks like a hyperboloid, right? So there's a throat, there's a middle, and that's kind of a fake because we can't really embed things in a very clear way in the universe that we see. But anyway, it kind of looks like a middle out of which it grows bigger and bigger toward the future, and to the past it also grows bigger and bigger. So there's like a narrowing in the middle, and then it expands again. And so both in the far past and par future, it's getting bigger and bigger. That's DeSitter's space all by itself. The Big Bang model, as we conventionally understand it, starts with obviously something totally different than that. It starts with a singular moment, and then after that it's hot and dense and rapidly expanding.

And with the positive cosmotional constant, it would eventually open up and cooled off and turn into this sort of endlessly expanding and accelerating DeCitter phase in the future. And the entropy version of that story is that the universe starts out with low entropy, and as it expands and cools and empties out, its entropy increases. And in fact, that was the time when I started thinking that this process of the universe emptying out and becoming closer and closer to de sitter space reminded me of the second law of thermodynamics, reminded me of the approach to equilibration of, of a thermal system. Okay? And so I thought like there must be, and then I did stumble across an idea called the Cosmic No Hair theorem.

The Cosmic No Hair theorem was, I think, first put forward by Bob Wald in the 1980s. If you have a universe with nothing but a cosmological constant, eventually it will empty out into DeSitter space. All the perturbations will go away. The universe becomes emptier and emptier forever. That sounded like an approach to equilibrium.

So eventually many years later, with Aidan Chatwin-Davis in 2017, I wrote a paper called Cosmic Equilibration, a holographic No-Hare theorem for the generalized second law, where we established a connection between the cosmic no-hair theorem and the second law of thermodynamics. But back in 2004, I didn't know about that. All I knew was that the early universe had low entropy and the future would have high entropy, and the future looks like to sitter space. So I was enough, and this is where talking to philosophers helped a little bit, reading some philosophy papers. I hadn't been doing that much of that back in 2004. I literally got engaged in discussions with professional people who work on the foundations of physics only because I wrote this paper with Jenny about the Arrow of Time. That's when I hooked up with that whole group of people and found my happy home. But I've been reading a few of their papers, and I was philosophically adept enough to be able to tell what is cheating from what is not cheating.

So we are very, very biased by the fact that we live in a universe that is in the aftermath of the Hot Big Bang with low entropy. We think it's natural because it's what we see around us. But if you step back and ask like what really is the natural universe, arguably the answer would be decider space, an empty universe with nothing in it. Why? Well, because that's the high entropy configuration. And from Boltzmann's original definition, high entropy means there are many, many states that look like that. That's the one you would get, if you randomly asked. So everyone else in cosmology was asking, you know, why did the Big Bang have this property or that property? Jenny and I started asking, why don't we live into Citter space? Why don't we live in an empty universe? Why is there a Big Bang at all? Okay. And what we realized is that

there's various ways. It took us a few tries, but we realized, okay, there's various ways to be into sitter space, but not stay there. And one way, the way that we sort of focused in on, was actually first studied by Eddie Farie and Alan Goof and their collaborators back in the 1980s, the creation of baby universes. If you get exactly the right amount of matter and energy in a very tiny region of space, then as far as we know, we don't know for sure because quantum gravity is hard and it's tricky, and the calculations are not completely well-defined, but it seems plausible that you can make a little self-contained baby universe that buds off and goes its own way out of basically nothing at all. You need some initial energy,

but you can get that from a quantum fluctuation, if you like. You don't need to actually assemble it in your laboratory. So you could think that you were into sitter space, but you could be constantly at a very, very low rate, but nevertheless inevitably, because the universe last forever, be budding off new baby universes, which would start very small, which would naturally look like they were ready to inflate, and then they would look kind of like the big bang. They would expand and cool and become universes of their own and approach a decider phase. So the universe that we are in could be a baby universe from a pre-existing universe that was just empty and to sitter space. And indeed, it evades Hugh Price's argument about the

double standard principle because you can play the same game backward in time. You can evolve backward and you could butt off baby universes and they could increase in entropy and they would have an arrow of time pointing in the other direction. So the specific cosmological details here about baby universes and de-sitter space and whatever are not the most important point here. I think that they're a good hand-wavy suggestion as to maybe what can happen, but the underlying rules are sufficiently loosey-goosey that it's hard to really make them careful and rigorous to the point where, for example, you could use that idea to make a prediction

for the inflationary density perturbations that you could test in the cosmic microwave background. That's an absolutely plausible thing to think about doing, but we don't know how to do it quite yet. But the general idea that the universe could be infinite and restless, that there's always a way for the universe to expand and make more and more universe with more and more entropy. and along the way, the way that it makes more entropy is by making universes like ours, and it does that in both directions of time, past and future. I still think that, you know, 20 years later, that is the only attempt at explaining why the hour early universe has low entropy that doesn't cheat.

I'm trying to phrase that as carefully as I can. I don't think it's necessarily right. It's highly speculative. There might be something completely different out there. but it doesn't cheat, it doesn't fine-tune anywhere. It plays by the rules, in other words. So, you know, people can disagree with that. Like, there have been some citations.

People had disagreed. That's great. That's how science marches forward. But I still think it's the most promising general framework to go forward. So that's one that is very dear to my heart, even though it didn't get nearly the citations that many of my other papers about dark energy and so forth back from those eras got. Okay, then I moved to Caltech, and there's only so many things you can say about dark energy.

So I started thinking about dark matter a little bit, among other things, while I was at Caltech. And again, the story is interesting. By the way, there's something I should have mentioned back when I was talking about the quintessence and the rest of the world paper. Like I said, the idea that, you know, light scalar fields can be coupled to all sorts of other fields and therefore be experimentally testable. That was in the air. People knew about that. and I just knew that there was a way out, there's a loophole if you had a specific kind of pseudoscaler field, etc. But basically the whole idea and much of the outline of the paper occurred to me as I was traveling from Santa Barbara to Chicago to give a talk at a conference.

There was a talk at Fermilab that was invited to give on dark energy in the accelerating universe, and I wasn't sure what to talk about. and so I sort of put these ideas together in my head on the plane right over and wrote up the talk, and it was a short paper that I wrote after that. So even though I think that there is a correlation between how many citations you get and how good the paper is, far from a perfect correlation, but there is a positive correlation. As far as I know, there's no correlation between how much work you do on a paper and how good it is or how important it is, you can work really, really hard on a paper, and it's all solid and good. but at the end, like, it's, eh, okay, well, you prove something, but I'm not that interested in it.

Or you can just have one little flash that you can write down over a weekend, and that's a highly cited paper. So either way happens. Anyway, I was reminded of that because the next paper I want to talk about is called Dark Matter and Dark Radiation from 2008. And it started when I was once again, I was not sort of flying to a workshop needing to give a talk, but I was visiting someplace. I even forget where I was visiting, honestly. And as happens when you visit your fellow cosmologists, like we were talking about different things, and we were talking about dark matter. And at the time, people were interested in self-interacting dark matter. Maybe some people still are.

Probably they still are. It's an interesting idea. So the simplest dark matter models, and again, it's always good to sort of base your starting point on the simplest models that are robust and work, right? And for dark matter, that's the cold dark matter model. when you have dark matter particles that for whatever reason are created in the early universe with very low velocities, so they're cold, and then they almost don't interact. Maybe they interact a little bit, but like weakly interacting massive particles or axions interact completely negligibly in the late universe. And that basic idea, that's the cold dark matter idea, and that basically works. But it doesn't work exactly. And probably it doesn't. It doesn't. work exactly. In the sense of working, I mean fitting the data that we have from galaxies and clusters and large-scale structure. Probably it doesn't work, not because the dark matter is weird, but because ordinary matter is weird. Ordinary matter has magnetic fields and makes supernovae and has

dynamical friction of all sorts, and, you know, it's very, very complicated. But when it comes to the centers of galaxies and also satellites around galaxies, substructure and things like that, there's an argument that the predictions from a simple cold dark matter don't exactly fit the data. maybe you can fix that by having dark matter interact. Okay? That means two things. Number one, you have to come up with a model of how the dark matter interacts. Is it just, you know, some new force or something like that? And then number two, you better get the relic abundance, the amount of dark matter in the universe. You better get that right. And that can be kind of tricky. Okay, but so for whatever reason, we were talking and I think it was me, but I can't 100% promise,

but I think it was me who said, you know, I could even imagine a copy of electromagnetism, you know, like a version of electromagnetism, that is to say a photon-like field, a magnetic field, an electric field, but not the ones we know and love, but a new one that only coupled to dark matter. So there would be a charge in the dark matter sector. You'd have positively charged dark matter, negatively charged matter, but it wouldn't interact with ordinary photons. It would interact with dark photons, right? And presumably, I remember very vividly that presumably it would have to be a super-duper-weak interaction, like the strength of dark electromagnetism would have to be very, very small, otherwise you would have noticed it a very long time ago. It would have a, like, ordinary

electromagnetism has a very big effect on the dynamics of ordinary matter. Therefore, it's not so weird to suppose that dark electromagnetism would have a big effect on the dynamics of dark matter, and we haven't noticed that yet, right? So it would probably be negligible, but you know, it could be there, who knows. Anyway, the idea sort of stuck in my brain. I kept thinking about it. When I got back to Caltech, I started talking with Lottie Ackerman, who was my grad student there at Caltech at the time, and we said, yeah, let's figure that out. So like, your guess is you could have a new copy of electromagnetism that only interacted with dark matter, but only if the dark fine structure constant, that is to say, the strength of the dark electromagnetic

interaction, was very, very small, small enough that you wouldn't have noticed it. So, but okay, let's figure out exactly how small it could be. Like, what are the limits? What is both the particle physics and the astrophysics that you would do to put limits on this idea? So we started working on that, and Matt Buckley, who was a postdoc there at the time, is now a professor at Rutgers. He was a postdoc working on sort of particle physics and cosmology things. So we started talking with him about the particle physics side of it. How would you use these new interactions to predict the total abundance of things like that? And so we all got moving forward on that. And then we realized that we were worried that there was some clever

astrophysical, cosmological phenomenon that would actually totally rule this out that we didn't know about. So we started talking to Mark Kamienkowski, who's a theoretical cosmologist, who actually now is like me here at Johns Hopkins. And Mark, indeed, was the one who came up with the most stringent constraints on this idea. But again, it's a fun idea to have because it's once again, you get to do all your homework problems, right? You know, what is the effect of this on the cosmic microwave background? Can you make dark magnetic fields? Can you make dark radiation being given off that cools things down? All these things. You get to remember all of your homework problems from undergraduate in graduate school, which is a comforting thing. You're in your comfort zone a little bit there.

And interestingly, the answer we found was that if you did have dark electromagnetism, it wouldn't have to be that weak. Because there's a trade-off what matters for the questions like how much dark radiation do you give off when two particles scatter off of each other. It matters, and this is not at all surprising to real astrophysicists, but it wasn't sort of deep into my knowledge base. It depends not only on the strength of electromagnetism, but also on the masses of the particles. Okay, heavy particles don't move as much when you give them the same force as a light particle, and therefore they don't radiate as much. The fact that electromagnetism is so hugely influential for ordinary matter

is only because not only is electromagnetism not too weak, but the electron is pretty light. Okay, it's 1, 1,800th the mass of the proton. So as the particle that is charged gets heavier and heavier, even though dark electromagnetism might exist, it becomes less and less relevant. It becomes less and less noticeable. And once you put the dark particle, the dark matter particle, and this is a model where you have both a dark matter particle that is heavy and a new dark photon that is zero mass, just like the ordinary photon, if the dark matter particle is up there at a trillion electron volts, which is completely plausible, then the dark electromagnetic. isn't that noticeable. It is completely allowed. There's one possible, we did point out in the paper, one possible loophole. If there's an instability where you make strong dark magnetic fields, that could cause trouble in dark plasmas. So guess what? There's different ways to get around that as well.

So we wrote this paper, dark matter and dark radiation. And the only regret I have, it did well. It's still cited a bunch. People work on the idea, et cetera. For some reason, the first, the first, phrase dark photon was co-opted by other ideas. So we called our paper dark matter and dark radiation. We should have called it dark particles and dark photons or something like that, or dark matter and dark photons, because the ordinary photon is a massless particle that is based on a U-1 gauge symmetry. There is something called the Z boson, which is a massive particle that is also neutral and based on an SU2 gauge symmetry. for some reason the phrase dark photon has been adopted by models where there is a new U1 gauge boson, but is massive. Okay, so that is not our dark photon. Our dark photon would be truly massless.

There would truly be dark magnetic fields in the whole bit. But there is a burgeoning industry right now in searching for dark photons. You can Google dark photon and find a bunch of people looking for them. They're not looking for our particle. They're looking for massive new U1 gauge bosons that are out there doing other things. So still, it was a hit. People liked it. I was proud of it having worked it out, learned a lot.

Again, made a mistake in the original version of the paper had to put forward a revised version because there was, no, is that true? No, I made a mistake in a different paper. Never mind. There were Feynman diagrams in these papers. Even though I love Feynman diagrams, like I only actually used them in my research once every 10 years. so I have to completely relearn what to do, get the formulas right, and I tend to make mistakes if my collaborators

are not keeping a sharp eye on me. So in the dark radiation paper, I don't think we made any mistakes. There's a couple others that we goofed, and that's okay, you goof, people tell you, you submit the revised version. As long as you eventually get it right, I think I'm happy with that.

So let me move on to a miss. That was a 2008 paper. There's a miss. Again, the miss means I love this paper, but it didn't quite set the world on fire. And this was called dynamical compactification from decider space. You see, DeSitter Space is a theme that appears again and again here. So this is a paper I wrote with Matt Johnson, who is now at Primiter Institute and also Waterloo, I forget, the University of Waterloo, and Lisa Randall, who of course is a famous physicist.

Lisa was visiting Caltech at the time, and I had known Lisa for many years, and Matt was a postdoc at Caltech at the time. he was a graduate student in Santa Cruz with Anthony Aguirre, former Minescape Guests. He always got to point out the connections to former Minescape guests. So anyway, Matt and Lisa and I wrote a couple papers together, one on Extremel Black Holes, which was fun, and that actually did get some citations. This one I thought was really interesting and important, and yet didn't make a big splash. So you tell me why. I don't know.

Here's the question. Imagine you believe that there are extra dimensions of space. Okay, in these extra dimensions, in addition to the three that we know and love, are somehow curled up, compactified, and hidden from us. What is the cosmological evolution of that story? How do they become compactified in the first place? The usual answer is something like the following. In the early universe, perhaps all of the dimensions were compact, right?

And there is a famous mechanism, the Brandenberger Vafa mechanism, named after Robert Brandenberger and Kermann Bofa, another previous Minescape guest. And they showed that if you had nine plus one dimensional space time, which is what string theory wants, you could imagine if all nine of those dimensions were curled up, that three of them would become uncurled and start expanding and make a big bang like ours. It's kind of a very cool cosmological mechanism. It's one of those ideas when I heard it. I was like, I'm really sad.

I didn't think of that idea first. That was an awesome idea. it's also from my, you know, current perspective as someone who cares about the early universe and the arrow of time, entirely cheating. Like, why were any of the dimensions small? What you really should ask is, if none of the dimensions were small, could you make some small, right? Rather than starting with them all small and asking, can you make some big? If you start with all of them big, can you make some small? No one had apparently addressed that question as far as I could tell. And we didn't address it. We, so we wrote down a model.

in which we showed that you could indeed make extra dimensions small. Well, make ordinary dimensions small. This seems really hard to do from a simple visualization perspective. If you think about a piece of paper, but a piece of paper that is infinitely big, so a plane, and you want to curl it up into a cylinder so that one dimension is still long and the other dimension is small because it's the circle dimension that's wrapped up around the cylinder. How do you do that? The paper is infinitely big.

The plane goes on forever. It seems like it would take an infinitely big conspiracy for all of space time to go from a plane to a curled up cylinder, right? That just seems hard. Of course, the answer is, if you start with a plane, you don't curl up the whole thing.

You dig a hole. What you can do is take a region of that plane and you can sort of extrude it so that it looks like a cylinder that is attached to the plane in the shape of one of these pictures I'm sure you've seen of what a black hole space time looks like, right? And indeed, there are space times that are black hole

like or black holes, but you put extra things in there, extra gauge fields and things like that, where rather than things curling into kind of a funnel and then stopping at a singularity, they curl into a funnel, and then, as we showed in our paper, you can smoothly match that on to a cylinder. That is a generalization of a cylinder, so that the extra curled up dimension is not just a single circle, but a two-dimensional sphere. I had previously written a paper with James Gettis and Bob Wald, where we talked about compactifying and stabilizing two-dimensional spheres. So that's something that I knew how to do. So anyway, that is a way that you could have an n-dimensional space generate a region dynamically, which was n-minus two-dimensional in macroscopic size,

and then two-dimensional in the little sphere that is wrapped around. Okay, so you take a region of n-dimensional space, and there's a quantum fluctuation, and it turns into an n-minus two-dimensional space times a two-dimensional sphere. I'm sorry if this is getting too technical, but, you know, I can't draw pictures. It's an audio podcast.

What do you want me to do? And what we showed is that the ingredients you need for this are kind of minimal. You start with dissitter space, again, a space with a positive cosmological constant, and you start with an electromagnetic field. That's it. A good old U1 gauge boson,

a good old electricity and magnetism. If you have six-dimensional decider space and you just allow for quantum fluctuations, this is actually an area where we mostly do have control over the equations. It's not 100% because it's still quantum gravity in some sense, but it's in a regime where we think we understand what's going on. And there will be dynamical quantum fluctuations

into little tubes that look like four-dimensional space time with a compactified two-dimensional sphere. So to me, that's like really cool and plausibly even part of reality, as far as I know. You would have to do a lot more. We talked about it in the paper. One mistake we made in that paper was it was too long. Like it was really, it should have been two papers.

It should have been one paper on the classical solutions and a separate paper on the quantum fluctuations into them. But I don't know. we just got happy writing the paper, and it got too long. And a lot of this was done by Matt, I should say. I should give credit to the people who actually do this. You know, Lisa and I absolutely contributed the ideas, but a lot of the calculational heavy lifting

came from Matt in this one. And I think that people just don't really like decider space. I think that the modern view of quantum gravity, which is dominated by string theory, is one where anti-Dissiter space and even Minkowski space, to a lesser extent, make perfect sense, and D-sitter space seems weird to us. Even though it's close to where we live, it's something that we don't understand nearly as well. And also, we didn't do any, you know,

we didn't show how you could dynamically compactify onto some six-dimensional collabial manifold or anything like that, which is something that string theorists might be very interested in. But the general idea of starting from a big universe and making one with fewer spatial dimensions, I think is very interesting, and I'm surprised that was a bit of a miss, citations-wise. Now we're going to move on to two final examples from, I guess, the late Caltech period, if you want to put it that way. At that time, you know, I had, in the beginning of my Caltech period, I was really sort of looking for a better research direction, sort of still moving in the momentum that I had built up from Chicago doing things like extra dimensions

and dark energy and inflationary cosmology and stuff like that. But I was, becoming less and less into that and trying to become more foundational, right? Trying to think about how to really think deeply about the laws of physics and how to be more fundamental and innovative and creative about where they could come from rather than just writing down more scalar fields and having them push around the universe. And fortunately, that was becoming a thing, right, in theoretical physics more generally. And honestly, like the five years before the pandemic, we had a great little group built up with myself and a bunch of graduate students, Kim Boddy, who is now, I'm not going to start

listing everyone who's now faculty members. All the students there did very well in terms of getting faculty jobs, so that's good. But Kim Boddy was there, Jason Pollock, Aidan, Aidan, Chatwin Davis, Grant Remen, Tony Bartolada, Charles Tzow, Ashmeet Singh, as well as postdocs like Stefan Likinauer, Ning Bao, Spiros Mikalakis. So a bunch of people, and we all had these weekly group meetings on, I forget what we called it, something like modern quantum cosmology or something like that, the emergence of space and time, and other people came from other groups to sit in. And so we had this ongoing, rambling conversation about the emergence of space time, especially on the basis of quantum information, right? The whole it

from qubit paradigm or idea was growing in interest in that time. And mostly it was in the context of ADS-C-F-T, the anti-descitor space conformal field theory correspondence. And my always angle has been, well, I don't know, this is giving myself too much credit, but I've never put any effort into the single thing that everyone else was trying to do at the same time. So it's important to do things that have an impact and are considered to be interesting by the rest of the field, but it's not important to, you know, chase bandwagon simply for the sake of being on the bandwagon. So I love the idea that was emerging from ADS-E-F-T that quantum information and entanglement were somehow at the heart of space-time. That comes from people like Mark Van Romstank and Brian Swingle and so forth, as well as a bunch of people doing tensor networks.

But I wanted to do it more in the real world, right? More in the decider space side of things, rather than anti-de-sitter space side of things. So we did a bunch of different things. and the hit that came out of that, maybe a couple hits came out of that. This is another hit that I could have mentioned would have been my paper with Chip Sibbins on deriving the Bourne Rule in the many worlds interpretation of quantum mechanics, but I don't want to talk forever. So like I said, I'd have cut some of my favorites.

But thinking about that one, which I guess was from, what year was that from, like 2014? That sort of set me on the path, but from thinking about, this philosophy question, where does probability come from in the many worlds interpretation of quantum mechanics, I had started thinking more deeply about the ontology of the many worlds interpretation of quantum mechanics, which is just there is a wave function and it obeys the Schrodinger equation. As anyone who has heard me talk about this, has read something deeply hidden or has seen any of my videos about it, knows that is the essence of the many worlds interpretation. And there's plenty of philosophical questions that pop up from that. But I think there

are also physics questions. You know, if the world is just a wave function evolving in Hilbert space according to the Schrodinger equation, why does the world look like space and time and stuff and all that, right? So that became really the fundamental driving question in my research, and now 10 years later it still is. I'm still trying to figure out. Yeah, there's other questions that have gotten add into that, but that's still a very deep question. And so we had this group of people who would just meet and just talk about all sorts of things. Where does space come from? Where does time come from? Where does gravity come from? Where does entanglement come from? Where do fields come from, right? And we ended up writing lots of papers about lots of different things. And the biggest hits to come out

of that were, of course, one paper I wrote with Charles Tau and Spiros Mikalakis on space from Hilbert space, recovering geometry from bulk entanglement. And then a follow-up that Charles and I did by ourselves called bulk entanglement gravity without a boundary towards finding Einstein's equation in Hilbert space. Okay, these are all big buzzwords. What is going on here? Well, the idea was that if you didn't put the metric of space time in by hand, that is to say, let's back up even more. The usual way that in physics we derive a quantum theory of something, the quantum theory of the hydrogen atom or the harmonic oscillator or the electromagnetic field or whatever, is to start with a classical theory and quantize it.

So doing gravity, doing quantum gravity, you would ordinarily start with Einstein's general theory of relativity and quantize it. If instead you're doing something like string theory, you're just taking a different classical theory and quantizing. You're still writing down some classical degrees of freedom. There are strings traveling through space time or the curvature of space time itself. in general relativity, and you're trying to quantize that classical thing. So the thing that hit me by thinking deeply about many worlds and so forth was, you shouldn't really be doing that. You should be starting with the vector in Hilbert space, the wave function, the quantum thing,

and you should be deriving a classical image, whatever that image is, from that quantum thing. So the space from Hilbert Space program, as it were, was to say, how could you have a quantum state that didn't have space and time built into it? Or we actually had time built into it. We just kept time as a fundamental variable for this particular work. That's a separate set of questions we could also ask. And we did talk about that. Not a lot came out of it.

By the way, a whole bunch of papers came out of this group, many of which didn't have my name on it because, of course, everyone else is also talking to each other and writing papers, which is good. That's great. That's when things are going well. That's how it is. So Ashmead, I know, wrote a paper on Emergent Time that I was not part of. So this paper with Charles and Spiros was about emergent space,

and we use the entanglement between some abstract quantum degrees of freedom to figure out whether or not you could turn the entanglement structure into a metric structure. The basic idea just comes from quantum field theory. In quantum field theory, it is a known fact that if you're in the ground state, if you're in the vacuum, nothing going on, then there is entanglement. between quantum degrees of freedom in different parts of space, and the entanglement is very high when they're nearby, and it's very low when they're far away.

So there's a relationship between the amount of entanglement and the spatial geometry. So we just had the idea, let's turn that on its head. Rather than saying, here's the distance, I can calculate the entanglement. Let's say, here's the entanglement. Let me assert that I can treat that entanglement as a measure of distance. Does it work? Does it hang together? And so in our first paper, we said, well, if it hangs together and you can make these extra assumptions,

here's how you can actually derive an equation that should be obeyed by that emergent geometry, and the equation in the linear regime where gravity is weak turns out to be Einstein's equation. It's kind of, I like to emphasize this. It's not as impressive as it sounds when you put it that way, because there aren't that many equations for spacetime curvature that you might possibly want to pause it, getting Einstein's equation out is actually pretty natural. What's impressive is that you can get it out without even starting with a metric at all, right? With starting with completely quantum degrees of freedom.

And in the follow-up paper, in both papers, we used ideas from Ted Jacobson. Ted had written some papers, he wrote a very famous paper called the Einstein equation of state, where he said if instead of positing Einstein's equation in space time, you posit a relationship between entropy across a surface and the area of that surface. And of course, you can derive the entropy area relationship for a black hole in semi-classical general relativity. But Ted, again, turned it backwards and said, let's posit the entropy area relationship and derive Einstein's equation. Of course, he worked in a framework where you had a space-time and a metric, right? And so we were saying, you don't have that. All you have is entanglement, but can you do the same thing? And we argue that

the answer was yes. And it's not, so it's not going to be ever a super, well, it's not right now going to be a super popular approach because we are just in the bulk of space time. We are working in the regime where there's no black holes, there's no cosmology, there's no boundary at infinity. We're trying to ask why the earth goes around the sun and apples fall from trees, right? In that regime, you can treat gravity as sort of an ordinary local field theory, and that's the thing you want to get derived from your underlying quantum structure. So that's important, but it's not for many people as sexy or cool as doing the holographic thing in the ADS-CFT context. And so it has gotten a good amount of attention later on, but is not yet swept the attention of the entire rest of the community. I think that's actually perfectly okay, like I said before. I'm slow, and both of these papers, one from 2016, one from 2017, they were a little hand-wavy, to be perfectly honest, right? We were suggesting, well, if this is true, if that's true, then we can show that the following things will happen. But there are many, many steps that remain to be filled in. So, you know, in the best possible reading, this approach to quantum gravity is in the state that, you know, string theory maybe was in,

in 1972 or something like that, where you had a basic idea. There was some vaguely plausible aspects to it, but there were some crucial steps you had to demonstrate would work before other people would say, oh, wait, that is a promising approach. Let's sort of jump on that and see how far you can go. So me and my collaborators are still thinking about that, how to sort of make it more respectable, fill in some of the gaps, so maybe other people can jump on a bandwagon that we start.

That is the ultimate goal. And then the final paper I want to talk about, in terms of the misses from that period, again, I'm looking for ones that are I personally love, but have not made a huge impact. So I'm going to talk about a paper called Branches of the Black Hole Wave Function Need Not Contain Firewalls by Ningbao, myself, Aidan, Chatwin Davis, Jason Pollock, and Grant Remen. So the idea here was, this is 2017. It's a little bit past, but it's still in the period where people were super into this thing called the firewall paradox. The firewall paradox is put forward in a paper

called amps, AMPS, A-M-P-S, Omerie, Marolfe, Polchinsky, and Sully. And it purported to be a puzzle, paradox in our understanding of black hole information loss, okay? And the idea is, of course, people argue over whether or not black hole evaporation really does conserve information, right? black holes radiate, Stephen Hawking says this back in the 1970s, but they radiate in a way that is completely the same no matter what went into making the black hole. You can throw in books full of information. If you trust Hawking's calculation of how the information gets out, how the radiation gets out, the outgoing radiation knows nothing about the specific information that was in the book you sent into the black hole. So that information seems to be destroyed. Now, maybe it is destroyed. That's absolutely possibly. That's what Hawking himself, said, but most people, especially those trained in quantum field theory, are just used to the laws of physics not destroying information. Modulo, interestingly, the fact that when you measure a quantum system, its wave function collapses and information is destroyed, right? I don't think that's really destroying information, because I think that there's unitary, smooth, reversible, deterministic evolution of the wave function according to the Schrodinger equation. There is apparent loss of information, because the wave function branches, and you find yourself on one branch or the other, not being able to know which one ahead of time. And that's not what everyone believes. Like, some people believe that the information really is lost when you make a quantum measurement.

I'm not, it's weird because there are some people who think that information is lost when you make a quantum measurement, but they're very bothered by the idea that the black hole radiation would destroy information. That doesn't quite make sense to me. But on my side of things, I think that neither one of those really destroys information. So we should try to understand how the information gets out. And we've talked about that, about that, with people like Netta Englehart, for example. I should actually name-check Netta Englehart and Raphael Buso, two former Minescape guests, teamed up on a paper on entropy in curved space times that was crucially important to the paper that Aiden and I wrote on the Cosmic No Hair theorem and the Second Law of Thermodynamics.

So like the Netscape family tree is everywhere. here. Okay. Anyway, as Rafael Buso, in fact, who said to me, soon after the firewall paradox came online, he said like, oh yeah, you got to drop everything and start working on this. This is the most important thing. I didn't immediately drop everything to start working on it, but eventually I became interested. So here's the paradox. You think that entropy is, that information is not destroyed. I'm not going to debate that, but maybe information is not destroyed. Let's assume that it's not, okay? But you think that otherwise somehow radiation is emitted from black holes. The trick is supposed to be that you are imagining that the radiation that comes out has entanglement

in such a way is to not destroy the quantum information that originally went into the black hole. So the entanglement between different photons emitted as part of the radiation coming out due to hawking radiation has to be exactly precisely arranged so that it contains the same amount of quantum information as the stuff that went in. Okay? Now, there's a whole separate problem about how it actually gets there. That's the real black hole information loss puzzle. How does the entanglement quantum information that went into the black hole get to the radiation that's going out?

But let's put that aside for the second. Let's imagine somehow it does, okay? That was the state of the art in the mid-20 teens. And here is the puzzle pointed out by amps. They said, to get the information out requires that a, photon in the hawking radiation that is emitted relatively early after you've made the black hole. There's a lot of radiation that comes out early. There's a lot of radiation that comes out late when the black hole is smaller. And in order to make all the information comes out,

those two bits of information have to be entangled with each other. Early photons have to be entangled with later photons, okay, in order to keep all the quantum information coming out in the right magnitude. Okay, that's fine. I can get that. But also, if you go back to what Hawking said originally about the origin of Hawking radiation and you think about any one photon of hawking radiation be emitted near the black hole, the story that you're told is that one photon escapes and becomes hawking radiation, another photon falls into the black hole, and that ingoing photon from the point of view of an external observer has a negative energy, which is why the black hole eventually shrinks and evaporates away.

Third, you're told that when you are near the eventorizon of the black hole, just falling in, you see nothing. There's nothing special, right? In classical gener relativity, if you buy my general relativity textbook and you read about black holes, you will be told there's no special signposts there at the eventorisen of the black hole. And what that means is that there's a certain amount of entanglement between the ingoing photon and the outgoing photon. In fact, they have to be as entangled as they can get. The phrase that is banied about here is the monogamy of entanglement. If you have an outgoing

photon that is maximally entangled with an ingoing photon, which is what you need for everything to look like empty space, nothing special going on at the event horizon, then that outgoing photon cannot also be entangled with anyone else. Black holes degrees of quantum information do not cheat on each other. They are monogamous. If you are maximally entangled with one other degree of quantum information, then you can't be entangled with anybody else. But we just said you should be. We just said that the outgoing photon at late times has to be entangled with an outgoing photon at early times, but it can't be because it's maximally entangled with an ingoing photon in order for everything to look smooth at the event horizon.

So how do you get out of this? And the AMP's paper said, well, we don't know what actually happens, but look, one possibility is that the information does get out. So the early photons are maximally entangled with the late photons, and we just have to bite the bullet and say that the late photons, that none of the photons are maximally entangled with ingoing photons, which means that at the event horizon, it is not. empty space. It does not look completely like there's no black hole there. Rather, there is a

energy barrier right there at the Eventorizon because the Quantum State is not that of empty space. It's not that of the Minkowski vacuum, as we would say. And so that is the so-called firewall. They said, in order to get the information out, without losing information, there needs to be firewall at the Event Horizon, apparently. So of course, many people argued about this, Lenny Suskin, who was another Minescape guest, did a lot of work on this question, and Raphael did, of course, and others. And I'm not sure, this is the beginning, by the way. This was the inspiration, ultimately, for the ER equals EPR suggestion

by Suskin and Juan Maldesana, that there's a relationship between entanglement and wormholes in space time, ER being the Einstein Rosen paper that proposed wormholes in 1935, and EPR being the Einstein-Podolsky Rosen Paper that proposed entanglement back in 1935. So there's been a lot of work inspired by the firewalls paradox. But I, of course, was bugged by this thing that I've already mentioned, that, you know, measurements already collapse the wave function and seemingly violate information conservation. We know they don't really, if you believe in many worlds, but would it help at all to take

that seriously? The fact that when you do a quantum measurement, it makes the wave function apparently collapse and apparently lose information. So just by thinking about that and by talking to my friends who were mostly grad students of mine, Ning Bao was a postdoc at the time, and thinking about what it meant, here's what we realized. So if you have two particles that are entangled, you have the traditional Alice and Bob set up, right? So Alice has a particle, Bob has a particle, the particles are entangled with each other, and the usual thing you would say is if Alice measures her particle, Now you know what happens to Bob's particle. Okay, so if Alice's particles spin up and the two particles are entangled in such a way that the spins are opposite, you instantly know that Bob's particle is spin down.

But there's another thing you know, which is that after you do the measurement, there's no longer any more entanglement between Alice's particle and Bob's particle. You started out in a state where it was one over the square root of two, Alice's particle has spin up and Bob's has spin down, plus one over the square root of two, Alice's particle has spin up and Bob's has spin down, plus one over the square root of two. or two, Alice's is spin down, and Bob's is spin up. So that's an entangled state for the two particles. After you do the measurement, you have Alice's is up, Bobbs is down. That's not entangled. That's two separate quantum states, okay? Where did the entanglement go? The answer is that what is entangled with what else in the universe depends on what part of the wave function you're looking at. Are you looking at the whole wave function? Or are you looking at the whole wave function? Or are you at a branch of the wave function. So in the many-world story, when Alice measures her particle,

there's part of Alice that measures spin up on one branch, part of Alice that measures spin down on the other branch, and that whole shebang, Alice and her particle, are in the global wave function of the universe still entangled with Bob and his particle. But when you specialize to being on one branch or the other, by decoherence and things like that, on each branch, it looks like they are not entangled anymore. Okay? So there's a very, very elementary, simple thing about quantum mechanics, nothing fancy about quantum gravity,

but whether or not two subsystems of the universe are entangled with each other can have a different answer depending on whether you're saying, do you mean in the global wave function of the universe, or do you just mean on a branch? And remember, the global wave function of the universe is what obeys the Schrodinger equation and is where everything lives, but branches are where people live. Branches are where observers live.

Branches are what you measure, okay? And so what we realized is, when you're saying the late photon has to simultaneously be entangled with an early photon and with an ingoing photon, and that's not okay. But those entanglements are relative to two different questions. The question about the entanglement

between the early photon and the late photon is a question about the global wave function of the universe. Overall is information conserved. Nothing about branching or decoherence

or measurement outcomes or anything like that. In the overall wave function of the universe is there entanglement between the early photons and the late photons. Whereas the question

about what happens near the horizon, what is the entanglement of the outgoing photon and the ingoing photon? Is that enough to be restoring the sort of boringness, the no-drama condition, as it was labeled in the

Amps paper, near the event horizon, that's a question about a branch of the wave function, not the global wave function. In particular, you send in an observer. You throw an observer into the black hole, and you're asking the question, do they see a firewall? Which is a question that can be translated operationally into do the quantum measurements that those observers do, reveal the existence of a firewall or does it look like empty space? Now, we're not able to sort of definitively answer that question in a very precise quantitative way, but we tried our best to make the argument that it was possible as far as anyone knows that there are enough branches of the quantum wave function that no one of them contains a firewall. In other words,

that there are so many branches, because branching happens all the time, there's so many branches you can throw in as many observers as you want, and they would not see any firewalls when you went into the black hole, even though all the external outgoing photons are entangled with other photons so that all the information is eventually conserved. I know I'm talking this is very high-level abstract stuff for people who are not physicists, but as late is a holiday message anyway, I'm not working too hard. I could probably make it even more understandable, but that would take a lot more words. I don't really have that many words in me right now. Sorry about that. Anyway, so we suggested that maybe there wasn't, well, what we suggested was there was a logical loophole in the argument for

firewalls that had been given by amps. Whether the universe actually takes advantage of that loophole or not is much less clear to me. And this paper, yeah, you know, it got a few citations, but it certainly didn't count in anyone's mind as a solution to the firewall paradox or get nearly as many citations as it would have, if it had. I think we were a little bit on the tail end of the firewall paradox discussion. And also, I think the people were, you know, when this happens in physics also, when there's a bunch of people who are working in an area and they're thinking about a problem, they get a feeling for sort of what kind of solution will look reasonable to them, right? What is the kind of solution you'll expect the cosmological constant problem or the

problem of quantizing gravity or what the dark matter is or whatever? And when you suggest something that is kind of orthogonal to that a little bit, saying, well, maybe it's a different angle of attack that you should be taking, you have to work harder to convince people that you're on the right track. And I think that our paper, you know, suggested there was a loophole there, but it didn't quite close the loophole or really argue that the loophole was taken advantage of by the universe, enough to convince many people. So I thought the paper was really good. Didn't make as much of a splash as I had hoped. But you know, so what used to do in that situation, young scientists out there, this is probably going to happen to you too, that you write a paper you're very proud of,

and people don't quite pay attention to it as much as you want. Your job is to work harder now. Write a follow-up paper. Right, other papers develop the ideas further, show that they really do, solve the problems that you care about, figure out what the implications are, the consequences of this, advertise it widely. So I've been thinking about this paper again recently. This is one of the inspirations for a paper I think I told you that is still hasn't come out yet, but we'll come out soon by myself and Chris Shaloo at Harvard on what hawking radiation looks like when you fall into a black hole. It was really following up on this firewalls paper that started us asking that question. And I've been thinking since then about how should we think

about quantum systems that are outside our past light cone. Does the wave function of the universe branch everywhere throughout space simultaneously, or does it only branch within our past light cone if you're a believer in ever-ready in quantum mechanics? I'm not sure exactly how to ask that question in the context of quantum gravity, but I think that it's a question that deserves asking. I think that in other words, the reason why I think is important is we physicists, despite the fact that we learn quantum mechanics, we always think of the world classically at the end of the day. We think of the world as classical physics plus some occasional jumps, right? Now, not always, not strictly speaking, but like in

our heart of hearts, we do that. And as evidence for this, when you think about either the Black Hole Information problem or cosmology, eternal inflation, things like that, people are constantly turning quantum wave functions into realizations of stochastic processes. So if you have a quantum wave function that is a superposition of spin up and spin down, and you have a thousand of them and you measure, you're going to get some number of spin up and some numbers of spin down. But you know, anyone who's been listening this podcast knows, there's a difference between the wave function before you've measured it,

and then the wave function after you measured it, and you got all that measurement outcomes. It's collapsed onto some particular possibility. And yet, we're constantly talking about other parts of the multiverse as if their wave functions have collapsed. This is another paper I wrote. Actually, with Kim Boddy and Jason Pollock, we wrote a couple papers, one on Boltzman brains, one on eternal inflation, where we tried to be a little bit more respectable about the collapse

of the wave function in cosmology. But I think that we haven't quite taken that lesson to heart more generally in terms of black holes and eternal inflation and things like that. People have sort of nodded at it. Tom Banks has written some papers about things like this, but I think that taking the quantumness of the universe that we haven't yet observed seriously is something that we haven't done. Now, should we have done it? Does it matter?

Maybe it doesn't matter. That's absolutely possible. So you have to actually get people interested in it by saying, okay, not only should you do this, not only can you take this aspect of physics more seriously, but here is why you will gain a benefit from doing that. And that's what we're trying to do right now. That's how science works. There'll be both hits and misses along the way.

I guess that's the thing to keep in mind. Anyway, thanks very much for indulging me. This went way longer than it should have. I'm not surprised it went on this long, but it's longer than it needed to be. I'm sure that this was only of interest for the fraction of listeners who are really into the physics side of things. But hopefully you get an idea of the very different ways that some papers come together. It's some are just, you know, single authors, some are with a group of people, some you have the idea and other people work it out, some vice versa. The list of authors changes and grows and shrinks as time goes on. You make mistakes. You have to revise them. It's all very messy and human and wonderful. And I love it. Doing science is just a great thing. And so looking forward to more hits and misses. Thanks again, everyone, for listening to the Mindscape podcast and for your support. Have a great end of the year. See ya in 2025.