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Credit: Brigitte Lacombe
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Interview of Surjeet Rajendran by David Zierler on May 4, 2022,
Niels Bohr Library & Archives, American Institute of Physics,
College Park, MD USA,
For multiple citations, "AIP" is the preferred abbreviation for the location.
Interview with Surjeet Rajendran, Associate Professor of Physics at Johns Hopkins University. He provides an overview of his current research activities with David Kaplan in black hole physics, new short distance forces, and modifications of quantum mechanics, and he shares his reaction on the recent g-2 muon anomaly at Fermilab. Rajendran explains why he identifies as a “speculator” in physics, he recounts his childhood in Chennai, India, and he discusses his grandparents’ communist activism, his Jesuit schooling, and how science offered a refuge for rebellion from these influences. He explains his decision to transfer from the Indian Institute of Technology to Caltech as an undergraduate, where he worked with Alan Weinstein on LIGO. Rajendran discusses his graduate research at Stanford, where KIPAC had just started, and where Savas Dimopoulos supervised his work on PPN parameters and solving the seismic noise problem on atom interferometers for LIGO. He describes his postdoctoral work, first at MIT and then at Johns Hopkins, when he began to collaborate with Kaplan on axion detection and the electroweak hierarchy problem. Rajendran explains the rise and fall of the BICEP project, and his Simons Foundation supported work on CASPEr. He discusses his interest in bouncing cosmology and firewalls in general relativity, and he conveys optimism that LIGO will advance our understanding of black hole information. At the end of the interview, Rajendran reviews his current interests in the Mössbauer effect, and explains how nice it was to win the New Horizons in Physics prize, and he prognosticates on how the interplay between observational and theoretical cosmology will continue to evolve and perhaps resolve fundamental and outstanding questions in the field.
Okay. This is David Zierler, Oral Historian for the American Institute of Physics. It is May 4th, 2021. I am so happy to be here with Professor Surjeet Rajendran. Surjeet, it's great to see you. Thank you for joining me today.
It's wonderful. Thank you for the opportunity. I'm looking forward to talking to you.
Surjeet, to start, would you please tell me your title and institutional affiliation?
Yeah, sure. I am an Associate Professor of Physics at Johns Hopkins University.
When did you come to Hopkins?
I moved to Hopkins from Berkeley July 1st, 2019, about a couple of years ago.
Did you come with tenure, or you achieved tenure at Hopkins?
I came with tenure. I was not tenured at Berkeley, but when they hired me here, they gave me tenure.
A question we're all dealing with right now, in the pandemic, how has your science been affected one way or another?
I would actually say that I'm one of the probably small number of lucky individuals in the country where the pandemic has actually been positive in terms of my productivity because I don't have kids or anything, and I get along very well with my spouse. I have a pretty large house where I have lots of space, so I've actually been very productive, I think, overall. It's been one of those things where my colleague, David Kaplan and I, we work together a lot, and we decided to form a pod, like over a year ago. So, we've been regularly meeting, and we've managed to get a bunch of things done that we're very happy about. This includes sort of a new direction to look for new short distance forces; more understanding of black hole physics; some modifications of quantum mechanics. Things of this kind. But it's been much harder on my students and postdocs, who basically had the problem that they don't really have as many projects going like I do. I think for them it has been more of a challenge in terms of actually staying productive. So, we do have group meetings regularly, and I try to keep their spirits up. But I can see it in their faces that they've not been having a good time. So, actually, they're all finally fully vaccinated now. So, finally, after a year and a half, we're going to meet in person tomorrow and have lunch, and sort of get things rolling again. So, it's not bad.
That's great. Surjeet, an even more contemporary question, given your interest in pursuing physics beyond the Standard Model, what is your instant reaction to the g-2 muon anomaly that everyone is so excited about at Fermilab?
Oh, yeah. So, I would say the g-2 is one of those things where I don't know how progress in that topic will be made. Let me put it that way. Of course, as you know, this calculation -- there's a very difficult theory calculation, and then there's the experimental results. I think the experimental result is correct, that they measured the value correctly. I don't doubt that. The question is, is that what the Standard Model predicts or not? There are two different methods. One of them is more data driven than the other, but they don't agree now. So, I don't really know exactly how we make progress at this point. How do we determine whether the theory answer is correct or not? It seems like kind of a messy situation. So, I'm personally not super enthusiastic that this is the right direction in the sense that -- for me, I always ask the question: when there's a controversy of this kind, how do you make progress? And I don't see an answer here. It's also the case that if you think about the kinds of new physics that would be necessary to explain this anomaly, there's a huge range of possibilities. Some of them would require building a new collider. Some of them may require doing other kinds of experiments. So, of course, in my opinion, all of those experiments are independently motivated anyway, so maybe people will just do that. It seems difficult on the theory side how we can get better progress on this front. So, it may just be that you have to do these other experiments, and then see what you get. Maybe I'm much more measured about this than many people. I don't know.
You're suggesting then that there's more to learn about what the Standard Model actually predicts.
Yeah. The fact that there's a lot of QCD that shows up in this calculation -- QCD is something where we don't really have very reliable calculation methods. So, it's fundamentally kind of a messy situation, and people work very hard on these problems, but they're just difficult problems. So, it's hard to know what that actually means.
Another sort of state of the play question, given your interest in the interplay between experimentation and theory, and that is, broadly for the projects that you're working on right now, where do you see which leading which? In other words, are there experiments that are really leading the theory, or are there theoretical advances that are really advancing or informing the experiments and observations? What's your general sense of where things are now?
You know, my specific interest in all these things has been the fact that I would say in all these cases it's been the theory that led to a new experiment. It is kind of, I would say, for example, I've worked on trying to detect gravitational ways. Of course, the idea of detecting gravitational waves obviously preexisted me. LIGO did amazing things, and all that. So, I would say what I brought into play would be the statement about, well, here are some other technologies that have been developed. Could we use them to detect these kinds of things? So, that was true for gravitational waves where we thought about how to use things called atom interferometers, atomic clocks—that were independently developed—and try to see how those could be used for these purposes. In the dark matter game, it was really more the statement about those vast parts of dark matter space that just were not being experimentally probed. Nobody had any idea how to do it. And I spent many years thinking about these problems. Eventually, I would say it was really theoretical insights in terms of looking at all those signatures that nobody was looking at. So, that was really a statement about the fact that I realized the dark matter could be doing these other things, and nobody's looking for those. Let's now figure out, if the dark matter had these other effects, what is the best technology to see them, and do those technologies exist at the level of sensitivity where we can find it? And we found that the answer to those questions was yes, and that's why those fields now exist, basically -- well, were created, to some extent. There are of course also situations where experiment does drive theory. That is more in terms of cosmic ray physics as well as physics from colliders. So, it's sort of more in the past, but I've certainly spent quite a bit of time thinking about data from these experiments. Occasionally, they have anomalies and then you think about -- I mean, it's a little bit like the g-2 kind of thing, where you see some result that is interesting, and it makes you think about what parts of theoretical space have we not explored? But my personal research has been more the other way around. I've really been driven more by thinking about the theoretical ideas first, and then figure out what experiments one should do.
Surjeet, a nomenclature question: the boundaries between cosmology and astrophysics, and then particle physics that has astrophysical or cosmological implications, where do you situate your own research within these subfields?
I would consider myself sort of a -- it's a funny sort of thing because I do work on a number of these areas. I've certainly worked quite a bit on cosmology, per se, but my definition of cosmology may be different from the cosmologists' definition of cosmology. A cosmologist's definition of cosmology would mean that they are thinking really about cosmological data, they are looking at how it is that structure evolves in the universe, that kind of question. My definition of cosmology is questioning more like the theoretical aspects of cosmology. Saying things like, what kinds of universes are possible? What kinds of new phenomena may exist? So, I'm more of a person who's on the speculative side of these kinds of things. So, if you look at every one of these fields, astro-particle physics, or particle physics applied to astrophysics, and then there's astrophysics per se, and then there's cosmology, in all of these cases there are the professionals who really just deal with the real data, and they look at what's actually something that's in the world. They try to look at these things. In all of these cases, I'm more of a speculator. I'm someone who comes in and says maybe there could be this new effect here, or this new thing you could be looking for. So, I consider myself broadly as a speculator in all of my research, actually.
Is there an intellectual tradition that you identify with, given your self-identification on the speculator side of theory?
Yeah, I mean, you know, a lot of physics really is driven by people being speculative. In a sense, pretty much every major advance in physics has been the result of someone speculating. So, to some extent, yeah, I would consider myself to be -- I don't want to sound too grand or something, some guy like Planck, or Niels Bohr. These guys were just speculating, right? I mean, Niels Bohr had a problem. He was trying to understand why the hydrogen atom was working the way it was working. He had no idea about quantum mechanics, none of that. He was trying to figure out some rule that would make sense, that would explain the data. So, I see myself very much along the lines of those guys. People who sort of come up with rules ad hoc, trying to parameterize what could be there in the world. Yukawa is another person that I really admire because he was asking this question -- we know that the atomic nucleus exists. He asked the question, why isn’t electrical repulsion breaking apart the nucleus? So, you realize there should be a new force that should be in there to hold up that nucleus together, but you don't see that force at long distances. So, basically, Coulomb, when he brought two charges together, he saw electromagnetic repulsion, but he did not see this new, strong force. You certainly don't see it at big distances. So, he's just asking the question, how can I modify the theory so that I have a force at short distance, but I don't have a force at long distances? And then he comes up with the so-called Yukawa potential. It was guess-work, speculation, but it happened to be right. So, I guess one word for this is called phenomenology. I'm certainly a phenomenologist by spirit, for sure. Actually, even by training. I'm definitely not one of those guys who thinks about the math and then claims insight from it.
Well, let's take it all the way back to the beginning. Let's start first with your parents. Tell me about them and where they're from.
Oh. I grew up in India, so my parents were in the city of Chennai, in India, which is a city in the southern part of the country. My mom was actually born in New Delhi, and she was there for a few years and then moved to Chennai. My dad was basically in Chennai all his life. That's where we lived back when I was a kid.
What languages or major cultural or religious observances stick out in your memory from your childhood?
Language-wise, the state where I grew up in, which is the state where Chennai is, is called Tamil Nadu. That's the state where Tamil is the language that people speak. But actually, my family -- my grandparents don't actually come from Chennai. They come from the neighboring state of Kerala. So, my native language is Malayalam, which is the language spoken in Kerala. So, I actually grew up speaking a little bit of Malayalam, a little bit of Tamil, and then quite a bit of English. That's what people sort of spoke in those days. In terms of religion, I have an interesting past. So, my parents -- and more than my parents, my grandparents were serious communists. So, if you look at it, my grandparents grew up in the 1930s and 40s when communism was fashionable. And you can see a lot of that as a response to colonialist rule, because India was still under British control at that time, and the Soviet Union was the one country that was opposed to colonialism. I don't think these people knew very much about all the atrocities Stalin was actually committing on his people. So, the Soviet Union was actually held up in this very high esteem. So, my grandparents were like serious, serious commies.
On which side? Which grandparents were the communists?
Oh, both of them. My father's parents as well as my mother's parents. In fact, that is kind of how my parents even met. It's a funny story. In 1975, Indira Gandhi imposed an emergency in India. She essentially declared martial law because her election was challenged. Actually, the high court in Allahabad set her election aside. So, she essentially declared martial law and declared herself Empress of India. So, my paternal grandfather was an active member of the Communist Party, so he was actually being pursued by the Indian authorities. So, he had to hide. He had to stay away from the police. Now, my maternal grandfather, he was actually an employee of the Soviet printing press. The Soviets had these consulates spread around, and they had a printing press there for the publication of their propaganda, and he was one of the printing press operators. So, since the Indian government was officially an ally of the Soviet Union, my maternal grandfather was basically off limits to the police. So, my paternal grandfather basically hid in my maternal grandfather's house during this time, and my father was a courier between him, and I guess the outside world, or whatever. So, that's basically how my parents began dating. This is kind of unusual in India, because a lot of Indian marriages are arranged marriages, and my parents had what is known as a love marriage, which is just basically like a normal dating style relationship. But this is kind of how their relationship matured. I mean, they knew each other before that socially, because they were all in the same commie circles, but this was one of the things that added to their relationship, I suppose. So, I grew up in this very weird household. It was an interesting time because I grew up in the late '80s and early '90s, which was kind of when Communism totally crashed. So, people around me were in this world where they were shocked by this whole possibility, especially seeing citizens of communist countries celebrating their newfound freedoms. Somehow it never occurred to them that it was odd that the supposedly wonderful Soviet Union had to build a wall to keep its people in. So, I would say I had a weird upbringing where at home, I was surrounded by all the “Red” talk, and at school -- they sent me to a Catholic school because a lot of the schools in India are run by Jesuits. So, my school was very, very Catholic and what not, but at home I was an atheist, because communists are atheists. So, fundamentally, both these experiences made me distrustful of authority. Both the parental kind as well as the schooling kind, which has been very helpful in my career.
Yes. Enter, science. Science is very useful in this regard.
Yes. Science is about rebellion. So, I rebelled against both these things, and became a free market loving atheist.
Surjeet, when was it physics specifically that you became interested in and thought you might pursue a career?
Oh, very early on. My mother told me a lot of stories about Galileo, so when I was in first grade -- I remember this -- she actually used to feed me and one of the things that she did was tell me stories to keep me interested. It sort of fit with the “Red” sentiment that you wanted to be opposing religion, in general. So, I heard a lot of stories about Galileo and Da Vinci, and people like that, who were essentially persecuted by the church for their scientific opinions. I would say, all of that ultimately did not make me a communist; it made me a physicist.
Were there any Indian physicist heroes, like Chandrasekhar, for example, that you thought about when you were younger?
Not particularly. I mean, Chandrasekhar, of course, was someone we all knew as a person we all heard about, and C.V. Raman, of course. But I was actually much more inspired by people like Feynman because the first thing -- it was kind of a cool thing where if you read Feynman's books, you sort of get the feeling that doing physics is fun, which is something that you don't realize when you learn about Galileo and Isaac Newton, right? You just learn about Galileo’s political problems and persecution, or how famous Newton became. You don't really learn that the day-to-day of physics is actually very enjoyable. And that's what really drew me to it even more, was the fact that it seemed like you could be a naughty kid, and have fun, and play around with these things, and make progress. So, I was much more inspired by Feynman than anyone else.
Were computers a big part of your childhood?
Not in the beginning, but they did become a very big part, I would say, in the mid '90s, like '94. I got my first computer when I was in eighth grade. I remember that because it certainly opened up the world a lot to me. I actually benefited in some sense from growing up in India around that time, because basically prior to 1991, India was a very, very closed economy. We didn't actually have a whole lot of money, and there wasn't a whole lot of technology to go around. The country opened up quite a bit in the early '90s, and as someone who belonged to the middle class at that time, I benefited a lot from that opening up, in terms of both seeing what the world was like, as well as the opportunities out there. So, yeah, I would say like '94 was a pretty important moment in my life, in terms of -- I actually remember it in terms of the change in how I felt about the world.
Did your high school offer a strong curriculum in math and science?
Yes. I was privileged to go to one of the best high schools in India. I went to a religious school, as I said. All of my schools were religious, funnily enough for a person who is from an atheistic background. My early childhood was kind of in this Christian tradition, Jesuit and what not. My parents were unhappy with the level of English instruction in that school, so they wanted to switch me over to a more -- a school where English was more prominent, more commonly spoken among the students. The Jesuit school largely served children who were not particularly wealthy, so their English knowledge wasn't that good, generally, just in terms of what they spoke around. So, they switched me to another school which was a Hindu religious school but had students from a wealthier section of society, and so English was more commonly spoken there. It also happens to be one of the best schools in the country. We had a very, very strong math and physics preparation.
What undergraduate colleges were within range for you, in terms of geography, in terms of your grades, in terms of how far you wanted to be from home? Where did you apply?
So, like many Indian kids, when I was finishing high school, my immediate goal was to go to the Indian Institutes of Technology. These are these institutions that are very hard to get into. There is a very competitive exam that you need to take. It is some insane thing. Something like 200,000 kids apply, and they admit 2,000 or something like that. There is an exam, and it's basically one of these things where in the hottest day in May -- May is the hottest month in India. The hottest day of that time, you spend the whole day taking physics, math, and chemistry exams, and that determines your future. It's a very high-pressure contest. In fact, the schools where you take these exams don't even have air conditioning. It's really a test of endurance more than anything else. So, I got into IIT. I spent a year at the Indian Institute of Technology in Mumbai pursuing physics. But I was very unhappy there because Indian education is very, very structured in terms of what you can and cannot do. You can't really pursue anything you want. There's like a fixed program. You've got to follow it. You can't fool around and do things. I didn't like that. I wanted more exploration.
Did that include both settling in on experimentation versus theory? Did you need to make that choice early on?
No, no. It was just the fact that the physics program just simply said, “Yeah, these are the courses you have to take.” You are correct that -- it's actually a big difference between the United States and India. In the United States, you get into a college. You're not admitted to a specific program. You can do anything you want. But in India, you are admitted to a specific program, and the program that I was admitted to was a combination of theory and experiment, but there was absolutely no flexibility at all. You just had to do everything that they told you to do.
What do you think are the advantages of this system versus the American style of take whatever you want?
I don't -- look, the thing is, I think it is probably helpful for people who have not spent a lot of time thinking about what they want to do. It gives them a certain level of structure. But at the end of the day, I am of the opinion that you're 18 years old. You better figure out what the world is like, and there are certain things that you may really like -- this is true even within physics. There are certain areas of physics that I really like, certain areas of physics that I really don't like, and certain things that I'm just good at, and certain things that I'm not good at. So, why force me to do all the things that you think I should know rather than letting me figure out what I want to know? So, I've always been a fan of the United States from a very early age, and for me, the American system spoke to me much more in the sense that, look, I'm old enough. I want to make my decisions. So, I transferred from IIT to Caltech as an undergrad. That was pretty unusual for people to do, in general, and I was very happy that I made that transition.
What year did you make that transition, both in terms of your level in college, and what year it was chronologically?
Actually, I transferred at the end of my freshman year. So, it was the beginning of my sophomore year, and that was 2001. It was actually an interesting time to be in the country at that time, because I was scheduled to fly to the United States on September 12th, 2001.
Oh boy. When did you actually fly? When did you get in?
The 19th. I was one of the very first flights allowed back in the country at that point.
Why Caltech? Did you get any specific advice? Did you apply by reputation? Were you enamored of Feynman? What was it?
Well, I applied to a small number of elite institutions in the United States that could provide financial aid. My parents were not wealthy enough to finance an American education, so I had to find places that would give me a scholarship. It was very, very hard as an international applicant to get scholarships from United States universities. The graduate program provides a lot of fellowships, as you know, but at the undergraduate level, it's very difficult, very competitive. So, Caltech was a very small number of institutions that actually would do it. So, I applied to about six places. I got into two of them, and Caltech gave me the best deal. I guess it was a combination of both California as well as Feynman that sealed the deal, and the money as well, at the end of the day. Essentially, it didn't cost my parents very much for me to go there. So, that's how I ended up there. And plus, it is a place that I fundamentally resonated with in terms of the fact that I'm very much a science person, and Caltech was just about science. So, it was a good fit for me.
What were your impressions of Caltech when you first arrived in Pasadena?
Well, I was blown away. Being a person who is drawn to science, and I like to do it a lot -- pretty much most of my time is spent about thinking about physics puzzles -- it was incredible being with other people who felt the same way. Everywhere else, you're kind of a weirdo. Why are you doing this? That kind of thing. And here, it's normal. So, I fit in very well. I had a grand time, actually. I was very impressed with the whole student crowd and how friendly they were. Again, it was an unusual time to come to the country given the tragedy of September 11th. So, I was suddenly very nervous about coming in because I looked like one of those guys. Some people have these kinds of opinions. So, I didn't know how I would fit in. So, I felt extremely welcomed, and people went out of their way to make me feel very comfortable. So, that's something that I would -- it's something that is very different from -- growing up in India, it's a country where there's a lot of political violence. Something happens, some number of people go crazy, and people get killed. So, I was actually very nervous coming to Caltech immediately after September 11th, because I was concerned about how people would react to my race, and things of that kind. But I found that not to be the case at all. I was very welcomed on campus, and it was a very, very supportive environment.
Did you have opportunity to develop relationships with professors in the physics departments, people you would consider mentors?
Yeah, to some extent. Professors are busy, so I wouldn't say I really had a whole lot of close relationships. Certainly, John Preskill was someone who endured a lot of my questions. I'm very grateful to him for that, as well as Professor Alan Weinstein, who was a professor who works on LIGO. He also dealt with me. The person that I perhaps had the closest relationship with was actually a professor of English, John Sutherland. We had long conversations about many, many things. Questions about life. And also, Professor Alan Hájek, who was a philosopher. So, it was interesting that I ended up at Caltech, and really talked a lot more to the people in the humanities and social sciences than I did to the physicists. But with the physicists, it's a thing -- with a physics professor, you go in, and there's sort of this aura of here's this great man. Why am I wasting his time? But the people in humanities were much more friendly, so it was a lot easier to relate to them, I felt. Also, in a humanities class you talk to people. You're not just getting lectured at, and I think that sort of broke the barrier between the professor and the students. In a physics lecture, you sit there like a good kid, and they lecture at you. So, I think the conversation helped quite a lot.
Did you have any summer internships that were relevant to physics?
Yes. I worked in my sophomore year with Alan Weinstein at LIGO. So, I actually spent a bunch of time analyzing what LIGO could do to search for supernova. Gravitational wavescould be produced by supernova, and it was possible that LIGO could see those. So, basically, I was doing some work on that front. And then in my junior year, I worked with John Preskill's group, doing some quantum information stuff. That was more of a theory project, but it was actually fun, and I learned quite a lot. One never really learns quantum mechanics properly from books, because the books are written in this very confused way. So, I spent a lot of time thinking about quantum mechanics during that summer. It was very useful in helping me understand the story.
And you got to see John right at the beginning of IQI.
Yes, I did. Yes.
Were you involved in that at all?
Well, I was part of his empire there. I mean, like, one of those guys in the corner who would sit quietly while he had all these people around him discussing stuff. So, it was fun to see all the activity there at that time. Of course, back then, quantum computing wasn't as hot as it is now, but it was certainly a lot of energy in the group around that.
What kind of advice did you get about graduate school? Did anybody encourage you specifically to stay at Caltech, or was that not encouraged?
People generally encouraged me to go somewhere else, and I think it's a good idea because every university group ends up over time developing its own theology. Physics is fundamentally a speculative field, and I think it's good to get different perspectives on what's interesting and what's not interesting. So, at Caltech, there was certainly a sense in which people felt that you should really go somewhere else just to get a wider view of what's going on in the world. So, I got that advice. I also got advice from Marc Kamionkowski, who is actually my colleague now at Hopkins. He was a professor at Caltech back then. I kind of asked him about what I should do in terms of theoretical physics, and in his very funny way, he heavily discouraged me from doing string theory. Implied it was a waste of time, and I'm very grateful to him for that advice.
I'm sure David Kaplan is very happy that you didn't pursue string theory also.
Oh, yes. Our opinions on this matter are very aligned.
Where did you apply for graduate school, and did you do that with the understanding that you were already making a life for yourself in the US and you'd not be going back to India?
Yeah, I certainly wanted to stay in the United States. I felt it was just the fact that my ambitions as well as just the scientific infrastructure is considerably better than it is in India. I also felt like, I would say, more in tune with the American ethos about the world that I ever did with India. It was pretty clear to me that I would be in this country for the long haul. I only applied to institutions in the United States. Stanford, Cornell, Princeton, Harvard. Sort of the standard places. I got into a couple of them, and I decided to go to Stanford for my PhD at the end of the day.
Were you thinking about professors specifically that you would want to be your graduate advisor?
I did not know enough about the field back then to make an informed decision on that front. In fact, actually, when I applied to graduate school, I thought I'd be applying mostly to do astrophysics, because that's what I was most interested in at that time. So, I kind of applied to places where astrophysics was strong, or things were happening. Stanford actually had just started this center called KIPAC, the Kavli Institute over there. And they had just stolen Roger Blandford who was a big-name professor from Caltech to go there. I had taken classes with Roger, and I knew he was a friendly guy, and things of that kind. So, it was really stuff like that. I didn't know enough at that time to really make an informed decision. I certainly got good advice from Marc, suggesting string theory is a waste of time. I generally was just drawn more and more to astrophysics and cosmological kind of questions, and Stanford's in California too, and that was great. And the fact that Blandford went there really, for me, was a pretty significant part of that decision. It certainly helped that I'd been visiting East Coast schools the week before. It was cold and miserable, and then I land in California. San Francisco, blue sky. That certainly helped.
How would you describe the Stanford Department of Physics versus Caltech? Obviously, you're coming at it from the perspective of a graduate student and an undergrad, but in what ways were the departments similar, and in what ways were they different?
Yeah, it's really hard for me to compare the environments because as an undergraduate you're not really plugged into the intellectual life of the department. You're just sort of taking courses. Stanford was a place where I really built up a lot of meaningful relationships. In fact, people that I've now known for 15 years. The relationships that you tend to build during your graduate career are much more enduring because they're people that you work with professionally for a long time. So, I think I pretty much made my first long-term, deep relationships at Stanford. It was a very friendly environment. I really liked the fact that many of the professors would talk to each other. There was a lot of communication between various groups. So, there's a sense in which in some departments people get very siloed. You do X, you just do X. Stanford was very, very interactive, and I'm an interactive guy my nature, so it actually helped a lot.
Who ended up being your graduate advisor?
What was Savas working on at the time you connected?
At the time, he was working on what is called split supersymmetry, which is sort of a modification of the theory of supersymmetry to account for the fact that supersymmetry does not solve the cosmological constant problem, and the fact that supersymmetry at that time was already very constrained by data from previous experiments, like LEP and stuff like that. But really, this is what he was doing when I started working with him, but around that time he himself was trying to make a switch into this idea of trying to do new experiments, things of this kind. So, to me, that was kind of the major thing, because I had never realized until then that thinking about new experiments is something that a theorist can and should do. In fact, Savas was pretty much the only person doing that sort of thinking. Nowadays, it's much more popular for young theorists to think about new experiments, but back then it was extremely uncommon. Savas was the only person who was doing that. So, to some extent, it was interesting being part of that environment in the very beginning, because it's the thing about life in general that you want to get into a field and if you're a young person and this field has been around for a long time, what are you going to add that the old guys haven't thought about in 30 years? Usually that curve is very, very high. You need to know a lot in order to go past the old guys. But when you're entering into a field at ground zero, the old guys have no advantage. They don't know anything more than you do. And for me, that was very, very interesting because I could be just as good as them. So, it was a very fertile environment for new ideas and new directions. It was risky because the whole thing could not have worked out, but I was drawn to it.
Did you realize in real time how lucky you are to have a graduate advisor who was both so nice and so eminent in the field?
I did not, actually. Actually, something that I've valued a lot about Savas is the fact that there are many, many graduate advisors in physics who dominantly view students as labor. Your job is to go and do what your advisor wants you to do to make the advisor more prominent. Savas was never about that. He gave me complete freedom to do whatever I wanted to do. Extremely supportive. I was incredibly lucky that I happened to find a person who was as supportive as he was and fully allowing me to grow into my own person.
What was your background in GR by the time it came to choosing a thesis topic? Had you taken classes?
Yeah. As I said, I was interested in astrophysics even at Caltech. GR was the bread and butter of that stuff, so I was really drawn to GR from the very beginning. I would say I had a pretty strong background in general relativity by the time I began working on gravitational waves more seriously.
Did you interact with Kip Thorne at all while you were at Caltech?
I was lucky to take a course from Kip. I don't remember its name, but yes. The LIGO guys used to teach two courses. One was a GR course and that was taught byLee Lindblom, who was also a LIGO professor, as well as Kip, who taught this course called Applications of Classical Physics which I kind of audited. It was really Kip's way of thinking about classical physics, and how he viewed it, and you kind of got this intuitive perspective on physics, which is very, very valuable.
How did you end up deciding what your thesis would be?
So, the story is that I was thinking about -- Savas and my colleague Peter, with whom I worked for many, many years, they were thinking about atom interferometers as a way to test gravity. So, they had come up with these proposals on how one could test general relativity. There's something called the PPN parameters. They're just sort of deviations from what general relativity could be. People typically do these experiments by looking at how the moon is falling towards the earth. There were some satellite experiments as well. So, they were thinking about how to use this new technology, atom interferometry, to just do these standard GR tests. And I had worked in LIGO before as an undergraduate, and I was aware of the fact that LIGO looks for gravitational waves at frequencies from about 40 hertz to about a kilohertz. The reason why they can't go below 40 hertz is because of seismic noise. The world shakes so much that the mirrors just shake too much, far more than what the gravitational waves do. And when I looked at the atom interferometer, I immediately realized that you could instantly solve this problem of seismic noise. The key idea is the following. To detect a gravity wave, you need two objects, and you want to try to measure the distance between them extremely accurately. You need to make sure that the distance between the two objects does not change by anything else other than the gravitational wave. So, if you use the mirrors of LIGO, the problem is the mirrors are 40 kg of sapphire, so you've got to hang them on the ceiling, and the ceiling is attached to the ground, and when the ground vibrates, the mirror will also vibrate. Now think about the following experiment. If I could take the two mirrors of LIGO, and I drop them, as they're falling, if I keep measuring the relative distance between them, a gravitational wave will come in and change that distance. That is something you can measure, but now that the mirrors are actually falling, if the ceiling or the ground shakes while they are falling, the mirrors are not coupled to it. They're not going to shake because the ground shakes. So, you've basically built the world's best vibration isolation system. Of course, you don't want to drop 40 kg of sapphire. There is no way to get money from Congress to do that. But what you can do is you can drop atoms, these ultra-cold atoms. So, that's how an atom interferometer really works. You take some cold cloud of atoms and you're dropping them, and as they're falling, you're trying to measure the distance between these two guys. So, I realized this part of the story, that when they were describing it to me and what they were working on, it just occurred to me that this solves LIGO's big problems. You can go below 40 hertz on the ground because you've gotten around LIGO's seismic noise problem. So, it was my idea, and that's kind of how I began working on it. Nobody really thought about how to use atom interferometers for gravitational waves in a serious way. There had been some prior work which really didn't realize the importance of the concept. So, with my colleague Peter, who was a graduate student at that time, we spent a couple of years going through all the fundamental sources of noise, the systematic problems that could exist, and how to combat it. So, I learned a lot from that project. It was really the project that I would say made me a scientist. It made me -- this is something I tell my students, that when I give a problem to them, their work on it might be very good, but they don't have ownership. That means, they don't wake up at 3 a.m. thinking about it and worrying about it. Solving LIGO’s seismic noise problem was an ambitious thing to do, and at the same time, it was entirely my baby, in the sense that I thought of the original idea. So, the ownership was so strong that I would literally just think about it all the time, thinking about problems that could come in, how they could be solved, what could be done to fix them. I've certainly spent sleepless nights worrying about this aspect or that aspect. So, it really trained me essentially on my own on how to be a scientist. How to be that paranoid person who worries about every possible thing and what could go wrong.
So, this essentially is what your thesis became.
What was your point of contact within the decisionmakers of LIGO? You had this great idea. What's the mode from your idea as a lowly graduate student, all the way up to Barry Barish, Kip Thorne, Rai Weiss? How did that happen?
Well, this is an education that I received later on in the politics of science, unfortunately. Look, it's this thing where I come up with this idea, and then all of us -- Mark Kasevich particularly-- contributed to it. In fact, they had many important insights. So, we built this up. We thought we really could do it. I was naive to think that if a new idea comes up, people will welcome it. This turns out not to be true. So, the politics is a little -- okay, so, here's what we should have done, and here's what we did not do. LIGO was a well-established program, and we were never going to compete with LIGO at LIGO's frequency. LIGO is the best instrument to do there, no doubt about it. So, our natural space is really between, I would say, .1 hertz and 10 hertz. That's really where we are really good at. There's also something called the LISA experiment, which is at like 10^-3 hertz to about a tenth of a hertz. Now, LISA is much more secure now. They had this LISA Pathfinder experiment that proved some fundamentally complicated technology. This was not true when I was thinking about this in 2006. LISA Pathfinder successfully flew and did what they needed to do in 2016. Around that time, 2015-2016. So, back then, there was a very real technological possibility that LISA Pathfinder would fail, and because some of the technologies that they were relying on was very similar to a program called Gravity Probe B that was germinated at Stanford. It took 50 years of development and [it] ultimately failed. It didn't do what it wanted to do. So, there was a reasonable chance that LISA itself may not work. So, instead of specifically tailoring our proposal to .1 hertz to 10 hertz, we started also thinking about how we could also do LISA territory. 10^-3 hertz, which was honestly more difficult for us, but it was certainly within the range of possibility. So, the way this project came out at the end of the day was not so much that hey, here are these guys with this new idea. it was more like this is direct competition to LISA. We certainly encouraged that perception as well. And then, we were going against a very large community of people who were invested in it for a very long period of time. So, there were a lot of political battles, which at the end of the day I think was just a waste of time. It took us a long time because of these battles to get ourselves off the ground. So, it was an education, both in terms of how to do science as well as the politics of it, which I think we dealt with much better when I began proposing experiments in dark matter which suddenly took off much more quickly than the gravitational wave experiments, and it was largely because I learned my lesson on how to deal with this.
Besides Savas, who else was on your thesis committee?
Mark Kasevich. So, Mark Kasevich was, in fact, the guy who built the fundamental technologies that actually make gravitational detection possible, but with atom interferometers. So, he was the main guy on the technology side. We had a couple of other guys. I think Shamit Kachru was on it; Steve Shenker may have been on it; also Tune Kamei, who was an external member, was on it as well.
What postdocs were available to you? What was most compelling to you after you wrapped up at Stanford?
Ah. I actually did not get a job in the first round of applications. This was an unusual thing where I thought I had done this very interesting thing that nobody else was doing, so I should be hot, or something. But it wasn't, because the point is everybody else is working on supersymmetry because they thought that was going to be right. I had explicitly not worked on it because I was fairly convinced it was going to be a dead end. So, in the first round of postdoc offers which actually happens in December, I didn't get an offer. I was very upset about it. December is a very lousy time when you're looking for jobs. This was also 2008, the financial crisis, a depressing time in general. But MIT did make me an offer in the very beginning of 2009. So, it wasn't for too long. So, the first round happens early December through the end of December, and then once people figure out where they want to go, the second round, you end up getting the next round. So, I got an offer in the second round of offers in January, and I got an offer from MIT. That was the only offer that I got, so I ended up going there for a year.
Was the LIGO possibility, going from your work at Stanford to MIT, particularly exciting? Was that part of your consideration?
Not at all, because the LIGO guys didn't like us very much, and I certainly wasn't going to go -- I wasn't personally useful to LIGO. LIGO is a serious experiment. They need serious people who can build serious things. I'm the speculator guy telling them on the side, “Hey, you could do XYZ.” So, I would not actually be a natural fit at LIGO at all because I'm not an experimentalist. So, for me, I was drawn to Boston because it seemed like there was MIT, and Harvard, and BU, lots of universities in the area, and certainly a reasonably nice town to live in. And also, I didn't have any other offers, so that's how I ended up at MIT. It was an easy choice.
Who did you work with at MIT, both at your level and among more senior people?
I didn't have very many collaborators there. I talked a lot of physics with this guy John McGreevy, who was actually a string theorist, who was at MIT and he moved to San Diego. But John I actually knew from Stanford. He was a postdoc back when I was a graduate student there, and I would bother him with all kinds of things. He was very, very nice to put up with me. So, I continued bothering him even though he was a professor at that point, and I was a postdoc. So, we talked a lot of physics, but our interests were a little bit not aligned because we was more of a string guy, and I was more of this speculative kind of person. So, I didn't really have any close colleagues there at MIT, and I sort of reached out to David Kaplan at Hopkins, who I had known from his time at Stanford before, to see if I could be stolen from MIT to go to Hopkins. I also had a personal situation where I was dating this girl at that time, and she had a position with the World Bank here in Washington, DC. So, it made more sense for me to be in Baltimore more than MIT. So, I actually moved -- again, a little bit unusual because people typically don't leave postdocs. I actually transferred from MIT to Hopkins in 2010.
Did you start working with David Kaplan then?
Yeah, that's right.
What was David doing at that point?
He was making a movie.
Yeah, he made this movie called Particle Fever.
Exactly, exactly. What has always impressed me about David is you can talk to David about anything. He's a very open guy, he's very comfortable to talk to, and you can discuss anything you want with him. And there's not a whole lot of hierarchy between him and me. Even back then, he was just very, very chatty -- it's how I like to do physics. I'm a chatty guy, and I just want to go and talk physics. With David, it was very, very clear that you could pursue ambitious and interesting projects with him.
So, what were you working on then? What was interesting to you?
So, at that time, I had thought about how one could actually use -- this was something from MIT. I was mostly working on how to detect these particles called axions, axion dark matter, using very, very cold molecules. So, David was generally interested in trying to think about how to do axion detection with -- generally thinking about how one can detect new particles. That was the area that he was beginning to think about. I had more experience thinking about it because that was more or less my tradition of what I had been doing at Stanford for quite some time. So, David was very interested in that idea. And back when we were at Hopkins, we also began talking about how one might use these pulsars also to constrain particles like axions. It was something that we were brewing up at that time. But I was only in Hopkins for one year, because Savas ended up getting a lot of money from the European Research Council, and he decided to steal me to Stanford from Hopkins. So, I spent only one year at Hopkins, and moved to Stanford again at the end of that.
What happened to the World Bank job for your girlfriend?
Oh, so that relationship fell apart, and I acquired, actually -- I began dating another girl in California, who actually is my wife now. So, that certainly worked out very well. So, it was a combination of things that basically led to me moving back to California. To some extent, it was an unusual career trajectory, because it's normally not the case that people -- nobody leaves a postdoc midway, certainly not from MIT. And then, I left one postdoc, and I left another postdoc also midway to go back to my graduate advisor's home, back at Stanford. Many people counseled me against all of this and said this was risky because people will not view you in this way or that way. I've always held the opinion that the pursuit of happiness is not wrong, and it's the sole reason why we live. So, I've always chosen paths that would maximize my happiness. And I think it's the right call.
Did you remain in touch with David when you moved back to Stanford on the electroweak hierarchy problem?
Yes. The thing about David is that there are certainly people who would have been angry, or whatever, about me dumping them and going somewhere else. But David is not that person fundamentally at all. He's not a person who views the world in that sort of a zero-sum game. He's very much a blue-sky thinker -- he understood why I left, and we continued talking physics. We actually continued writing papers together, too, even though I'd officially moved to Stanford. In fact, I would come and visit Baltimore regularly, even when I was at Stanford. Ultimately, I would say he won the prize -- by convincing me to leave Berkeley and move to Hopkins permanently. So, it worked out for him.
Now, the electroweak hierarchy problem, in what ways was it connected or not to your interest in axion detection?
Ah. So, the story about this is that I had in 2013 figured out how to detect axions using nuclear magnetic resonance. So, we were very excited, and Edward Witten actually heard about this through my colleague Peter or something like that. And Edward Witten was also very interested in axion detection. He thought it was an interesting idea, and he thought we would benefit by having some funding for it, of course. He hangs out with famous people such as Jim Simons, and I guess he had lunch with Simons sometime, and happened to mention this possibility that Simons' foundation could support. I think Edward also told Simons that the axion is the physics analog of theChern-Simons term, which it actually is, which I think convinced Simons it was something he may want to fund. So, Simons invited us to his foundation to give a presentation for what we might do. This was in 2014, actually. Now, we were going to go to Simons' place in April of 2014, and March 14th, 2014, was the day it leaked out that this experiment called BICEP had seen inflationary gravitational waves. If that experiment was actually correct, and they'd actually seen inflationary gravitational waves, the kind of axions that we were thinking about would have naively been ruled out. Basically, if you took the naive cosmological story, these axions could not exist. So, there's no point in looking for them. So, we were in an awkward situation. We were going to go up to this guy in two weeks to get a few million dollars of his money to do this experiment, while this other experiment says it's actually ruled out. Also, I did not know this at the time, but Simons's godson, Brian Keating, was a big guy in BICEP. So, I think Simons was heavily invested in thinking that BICEP was right. So, the question to us was basically, “Why should I give you guys this money? You're ruled out. Go away. Do something else with your time.” So, I, at that point -- you know, it really changed what I was working on because I was thinking really about experiments a lot, and not so much thinking about the hierarchy problem, and things of this kind. But then I began really asking the question, is it really true that if inflation actually happened, and BICEP was actually correct, is it really the case that -- is its model independently the case that axions would be ruled out? And then I began poking at the results, and I came to the conclusion, no. You could actually build models of axions where this was not true. BICEP could still be correct, but it would then be the case that -- BICEP could still be right but we could still have axion dark matter without it being ruled out, which really depended on early universe cosmology, things that we have no access to. And the seed of that whole concept was that you somehow had to give a large enough mass to the axion at the time of inflation, or immediately after inflation, and then remove that mass later. So, that's what got me thinking about what else might be possible, in terms of doing this. So, I showed up to Jim Simons' foundation in April, and I told him it's not ruled out. There are these other models that you can write down. Simons wasn't very impressed. He was like, “Yeah, yeah, whatever. Go away. I'm not giving you guys money.” So, we didn't get money in 2014 from Simons. But the idea stuck with me that you could really do this, that you could in fact give a scalar field, like an axion, a big mass at some point, and then remove it cosmologically. And that idea matured over the summer. I traveled around a little bit, but I didn't have very much to do over a period of like three weeks, because I was on a safari in Tanzania where I would go and look at these wonderful animals in the morning, and I had nothing to do in the evening. So, I just sat and thought about physics, and the idea matured in that time. You could really use the same concept that you could give a scalar a big mass in the early universe, and then remove it, and maybe try to solve the hierarchy problem as well. That's really what led to the idea that the Higgs could have had a gigantic mass in the early universe, and you could remove it later on and make it small. So, David, at that point, had just finished working on his movie. Particle Fever came out as a big success, and he wanted a sabbatical where he was going to just get back into physics, as he put it. He of course knew me, and he also knew Peter Graham, my other colleague at Stanford, so he asked if he could come to the Bay Area for a sabbatical. We made it possible for that to happen. Actually, the very first day he arrived in California, we went out to have dim sum, which we both enjoy, and then we went to get some coffee, which he enjoys more than I do, but we began talking about what we were thinking about. I told him this was what I was thinking about, and David was immediately interested in the concept. He was of course much more familiar with other concepts people had played around with before, such as trying to do similar things to the cosmological constant, which never really worked back then. So, really, the day he got in, essentially was a good time, because I'd sort of developed enough thoughts on this myself, and David had also thought about similar problems with the cosmological constant. So, we spent his entire sabbatical essentially pushing this through. Of course, it is the usual thing in science, you think everything should be figured out in a month or so. Of course, that wasn't true. We spent about six months, I think, learning, and unlearning, and relearning, and making it work. But I think it was January of that year when we had our first working model. It was a little clunky at the beginning, and then by April, we had really defined it to a simple set of statements. So, that was the story there.
And obviously, the Simons Foundation did fund you for CASPEr.
They did, yeah. What happened was, of course, after we were rejected, the BICEP story kind of collapsed. People found various flaws with what their claims were. It turned out that actually when we were making our pitch to Simons in New York, there was a guy who was Skyping in from California, from the Bay Area. I didn't know who he was. They told me it was just Simons' son-in-law. Now, the thing is, Simons is worth over 20 billion. His son-in-law is a poor guy. He's only worth a couple of billion. So, Mark Heising listened to all of this and he was very interested. So, he reached out to us after the whole BICEP thing had collapsed. He sort of said, “Look, I thought your idea was very interesting. I don't have as big a foundation as Simons, but I'm not entirely a poor guy, so I too can pitch in and do something for you guys.” So, they essentially restarted the process of trying to reengage with us, and then managed to also bring the Simons Foundation on board. So, by the time this happened in 2015, BICEP had really collapsed, and I think there was an overall sense in which what we were proposing had made more sense to them. So, everything turned out to be good at the end of the day.
So, what were CASPEr's goals? What did it seek to accomplish?
The goal of CASPEr is to look for axion dark matter. Basically, axions can do a couple of things. What people had been looking for prior to our work was that an axion could come in and could convert to a photon. And you could build a really, really quiet cavity, and you could measure the conversion of the axion to a photon. That is what this experiment called ADMX does. ADMX is a great experiment, and they're very, very good at finding axions at frequencies of around a few gigahertz or 10 gigahertz. That's their range. If you think broadly about axions, it's possible to get axions of much lower frequency as well. Megahertz, kilohertz, things of this kind. And in that arena, the cavities just don't work very well. There are fundamental physics reasons for this, simply because if you think about the electromagnetic wave that corresponds to a kilohertz axion, for example, is gigantic. It's thousands of kilometers. So, it won't fit into a small cavity you can build in a lab. So, if you try to proceed in a small cavity, you get very suppressed, fundamentally, by the fact that your cavity size is mismatched with the wavelength of the axion. So, you need a new way to do it, and what I had recognized was the fact that one thing you can do is axions also cause spins to rotate. So, if you have an axion going through, and you have a spin, the spin can rotate. So, you can image an experiment where you take a whole bunch of nuclei, you align them in one direction, the axion goes in, the spins start rotating, and then you can put a magnetometer next to that set of nucleons, and if the spins rotate their magnetic field would change. That is something you can measure, so that's what CASPEr is doing. CASPEr is basically trying to do NMR for axions. So, in a typical nuclear magnetic resonance experiment, that's what you're trying to do. You have some sample. You're trying to measure some stray magnetic field, and what happens is that magnetic field causes some spins to rotate in some way, and you're trying to measure that rotation. That's what you're trying to do. So, here, also, we're trying to detect a new magnetic field. The magnetic field, you think about it as a fake magnetic field, because it's coming from the axion. So, the dark matter can be thought of effectively as a new source of a magnetic field causing a spin to rotate. That's what CASPEr is trying to do. It's trying to use the idea of NMR to measure the hidden magnetic field of axions, or hidden photons, particles like that.
Did you have interactions with Pierre Sikivie at all in this work?
No. I had really just thought about it on my own, and basically the people I talked to the most wereDima Budker, who was ourcolleague in trying to -- who is actually building the apparatus now in Mainz, as well as Alex Sushkov, who was a postdoc at that time, and now professor at Boston University. So, I'd really talk to these guys a lot more. The challenge for axion detection had been something that I'd been thinking about really from graduate school onwards. I was sort of maturing into someone who was thinking about how to detect new physics with new experiments, and gravitational waves was a big thing I was working on back then. But I always kept axions in mind, because axions were the other dominant dark matter candidate that people had thought about. ADMX could really only do from about a gigahertz, or 10 gigahertz, or something like that, or maybe 100 gigahertz now. But it was a pretty narrow range of frequencies they could look at. So, for me, the scientific problem that you wanted to look at as much axion parameter space as possible was very much a part of something that I had actively thought about for many years. But on this one, I would say that we played the politics right. In fact, it's even scientifically true that ADMX is the right experiment to do from 1 gigahertz to 100 gigahertz. So, I never tried to do better than ADMX in that frequency band. We just picked a different frequency band where nobody else was doing anything. And then it was all great, because everybody supported it, because it was clearly a good scientific case. And we managed to get off the ground very quickly.
Now, at some point, you joined the faculty at Berkeley.
Yeah. That was in 2014.
Was it an open position that you applied to? Were you recruited? How did that come together?
That was an open position. They had an open position that they advertised for in 2012, and the job interview and all that happened in 2013. So, I got my offer from them in 2013, I guess July or something like this. And then I sort of negotiated staying as a postdoc for another year at Stanford because I didn't want to be a professor and do all the work. So, I spent one year as a postdoc extra at Stanford, and I started officially in 2014.
When did you get involved in bouncing cosmology?
Ah. This began following our work with David and Peter Graham on trying to solve the hierarchy problem. We had this cosmological relaxation story, and then we were thinking about using the same ideas to solve the cosmological constant problem. What is it that prevented solutions to the cosmological constant problem prior to our work? There was an effort by this guy Larry Abbott who was a physicist, and then became a successful neurobiologist, or something, which was the so-called Abbott model, which does solve the cosmological constant problem. It does take a very large cosmological constant and eventually can make it very small, but it ends up with what is called an empty universe. By the time you solve the cosmological constant problem, the universe is completely empty, so it can't be our world. And the question was really like, how do you reheat an empty universe? And naively, you try to think about trying to reheat an empty universe, you have to violate energy conservation, because you've got nothing, and you suddenly have to get heat. That sounds like you violate energy conservation. Now, the key point is that there is in fact only one theoretically consistent, experimentally verified way of violating energy conservation in our universe, and that is through gravitation. It turns out that gravitation does not actually have a conserved energy. It's a surprising result to people who haven't thought about it, but when you think about cosmology you know this is true. Take for example the cosmological constant itself. You can take a tiny universe, put a cosmological constant in it, the universe will expand exponentially at the same density. So, you've now got a gigantic amount of energy density. So, where did that energy come from? You violated energy conservation. So, it is a statement about Einstein's theory itself, fundamentally. Gravitation does have a conserved energy in some cases, but generically, it does not. So, that was the main idea for me, that if you want to reheat an empty universe, you can only do it through gravity. So, the idea we came up with was the fact that yeah, let's say I've done something. I've solved the cosmological constant. I've made it very, very small, but now I will still have some particles in that universe that is still very, very cold, but how about I now start making the universe crunch? As the universe crunches, these particles will get hot. Just like how an expanding universe makes particles cold, a crunching universe will make particles hot. So, as you crunch, the universe will automatically get hot. And now, if you make it bounce, you're done. You've now got a small cosmological constant, which is what you already did, and now you've essentially converted a hot, crunching universe into a hot, expanding universe. So, if you could make a bouncing cosmology work, you could solve the cosmological constant problem. I was very excited about that possibility, and I began investigating bounces very carefully at that point.
Did you talk to Paul Steinhardt at all?
No. I'd known of Paul's work. I've talked to Paul since that. But this is one of those things where I felt there was a general attitude in the community about bouncing universes and the attitude was partly based upon mathematical results, but partly just based on the fact that certain people in the community did not like certain other people, and I thought that was ridiculous. So, I began looking into trying to understand fundamentally why the bounce is difficult, and what you can do to combat it. So, it actually helped greatly that at that time I was teaching general relativity at Berkeley, because at that time, I really began going through all these GR theorems. If I was going to stand before like 30 graduate students and talk to them about all these things, I better know what I was talking about. And while you are teaching and doing these things, you're thinking about all the loopholes that are actually there in these theorems, and I identified a loophole that we ultimately exploited, which is the following thing. You ask, why is it fundamentally difficult for a universe to undergo a bounce? What is the math theorem that forbids this? The real challenge is the following. What does a bounce require? A bounce requires the fact that if I have matter, the matter is collapsing. It's going towards each other. And then when you go through a bounce, this matter has to re-expand. Now, the intuition is that if you think about gravity, you're starting with a lower density amount of gas or whatever, the gravity is very, very weak. As the matter goes towards each other, the gravitational force gets stronger and stronger and stronger. So, it would be fundamentally weird for strong gravity to suddenly become repulsive and kick you out. That is the fundamental mathematical obstacle to creating a bounce. Like, how do you create repulsion in a contracting ball of matter? That is the main challenge. Now, one way of handling that challenge is to do what is called violating the null energy condition. This is a statement that somehow matter could have negative energy density. If matter had negative energy density, it would effectively have antigravity, in some sense, and that antigravity would actually cause this thing to expand. You can create null energy violation, but it turns out it's very hard to make it big. Because the typical ways in which people create negative energy in the world are either associated with quantum effects which tend to be very small, or they create disasters and instabilities. One way to get a negative energy would be to create particles with negative mass. That's one way you would create it. But if you have particles with negative mass, what would happen is that empty space can decay into particles of positive and negative mass, because that way you've conserved energy. So, you would not have a stable universe if you have particles with both positive and negative mass together. So, that's why violating the null energy condition is always viewed to be very difficult, and that's why nobody pursued it. But if you look at the theorems, there's another way in which you combat gravity, the attractiveness of gravity, and it's something that we do every day in our life. The earth goes around the sun. The earth does not fall towards the sun. It doesn't hit the sun. That is not because the earth has negative energy. It's because the earth has rotation. Centrifugal forces, rotational forces, are a trivial way in which you can avoid collapsing due to gravity. So, in the GR parlance, that is called vorticity. And I realized that this theorem clearly has a loophole, that if there was enough vorticity in the world, you could actually create a bounce. Of course, I'm not the first person in the world to have noticed that those equations have vorticity and there should really be a way in which one should be able to do this. In fact, Kurt Gödel had created what is called the Gödel Universe, which is a universe that spins. That's a universe that only has dust and a cosmological constant. And usually if you have a universe with dust and positive cosmological constant, that universe expands forever. But what Gödel actually showed is that if you have rotation the forces of gravity can be exactly canceled by this rotation. Now, the reason why Gödel built that kind of universe was also the reason that people had dismissed vorticity before. Gödel had built that universe primarily to mock Einstein. That was his actual goal. And that is because the Gödel universe has something very weird. It has something called a closed time-like curve. You start at a point in space in time, and if you just sit in that universe, you wait long enough, you will basically come back to that same point in time. Like a time machine, basically. And Gödel was basically telling Einstein, “Look, Einstein. You've created this theory of general relativity, but I just take a cosmological constant and dust and rotation -- all these three things are reasonable things to have -- and look, you get closed time-like curves. So, something must be wrong in your theory.” That was the idea that Kurt Gödel was going with. So, I don't particularly care about closed time-like curves, but we don't actually live in a world like that, so one should ask, what is it about vorticity that fundamentally causes closed timeline curves? The main problem is the following. If you think about it, if a universe is homogeneous and isotropic, it means there is no special point anymore. So, the only way you can create rotation is if every point in space is rotating around every point. Now, if you have an infinite universe, and every point is rotating around every other point, you can eventually go far enough out that there will be one point that will be rotating faster than the speed of light relative to you. Because you have a constant rotational velocity, and the farther away you go, the speed just keeps increasing. That is fundamentally how in the Gödel universe, you end up creating closed time like curves. So, if you wanted to create a homogenous universe, and you wanted to make the homogeneous universe undergo a bounce, without violating the energy condition anywhere, you would require vorticity everywhere. That was a challenge. How do you create vorticity everywhere without creating a closed time-like curve? So, that was a challenge that we set out ourselves to handle. The one thing that we introduced that people in the '60s did not think about was the possibility of extra dimensions of space. It was the fact that if you think about the Einstein's theorem, the theorems basically say I want some rotation. That's it. They don't care where the rotation is. You just need some rotation to combat gravity, and all the problems with closed time-like curves come because you're trying to rotate something that's very, very far away from you. So, the thought that we had was saying, look, what if, as I'm crunching this universe together, what if I create a rotation inside some extra dimension? So, basically, all these particles are going towards each other, and instead of rotating around each other in the large dimensions, maybe they rotate into an extra dimension. That was kind of the little trick that we played, and once we played that trick, it turns out you can get a bouncing universe because you've got vorticity everywhere. At the same time, you've eliminated closed time-like curves, because all the rotations are now happening inside some small extra dimension. So, we found we could build a viable model, so we were very excited.
And where are the firewalls in general relativity? Where does that come into this?
That really comes a lot from thinking about the physics of black holes themselves. So, if you had told me five years ago that I would be working on firewalls, I would have said, “No way.” But much of the last five years has been that way, where I can't believe this pandemic -- all these things. It's just crazy stuff. So, the firewall story really came about in 2012. I remember this very well. I was sort of dining, and I was, as usual, looking at the papers that had come out. The stringers had discovered some big thing that they had not solved the black hole information problem. I was like, “These people don't know what they're talking about.” Okay, I won't spend time attacking them. Let me just tell you my perspective on the topic. Here is the main thing. If you want to solve the black hole information problem, you want to get information from inside the black hole, outside. That's what you need to do. So, how can you get information from inside the black hole to the outside? Well, something has to physically go from the inside to the outside. The only way something can go physically from the inside to the outside is if you violate the rules of general relativity. That's it. The only way you can actually violate the rules of general relativity is if the energy density in the system is at the Planck density. So, if you could do all of that, then you could violate the rules of general relativity enough to actually go from inside the back hole to the outside. The key question becomes, how can you do this? How can you really create Planck densities everywhere inside a black hole, all the way to the event horizon, without actually violating energy conservation, and stuff like that? You might think, naively, if I take a black hole and at the surface, or everywhere inside of it, if I put it all with Planck density, the mass of the black hole would be enormous, gigantic. It would be way bigger than the official mass of the black hole that would be measured outside. So, this idea never made any sense. How could it ever work? But then I learned a lot more about a different problem inReissner Nordstrom black holes andKerr black holes. These are charged and rotating black holes. These black holes have what are called an inner and an outer horizon, and they have a very weird phenomenon going on, which is that on the outside of a charged black hole, if you jump in, you will cross the outer horizon. It's very similar to a regular black hole. You would just keep falling in. But once you cross the inner horizon, and you go to the region inside, it turns out that you can hang out there. You're no long required to continue falling towards a singularity. That's just a fact of the geometry. Not only that, but you can also try to leave that region and go somewhere else. There's nothing that blocks you. And if you look at the textbooks on GR, this is basically where they say something that's totally ridiculous. They will say that when you try to jump into a black hole, you go from the outer horizon, and you cross the inner horizon, and you try to leave the inner horizon, they will say that you will now actually go into a new universe. That is the official GR textbook answer, and that's totally ridiculous. Do you really believe that you can jump insideSagittarius A, the big black hole in the center of our galaxy, and you can jump into it and go into a different universe by crossing the inner horizon? That sounded ridiculous, and people know that it's ridiculous, so they have thoughts about this. In fact, Penrose who was one of the first people to think about it carefully, suggested a resolution. The idea fundamentally is that the inner horizon is a place of instability. You can actually calculate this. If you stand in the inner horizon, and then you calculate how some light from far away is falling in and hitting the inner horizon, you will find that the light gets extremely blue shifted. So, it turns out that even a tiny amount of energy from the outside can go to the inner horizon and become extremely energetic, because you've just gained a lot of energy from this gravitational in-fall. So, at the inner horizon, it's actually possible to build a gigantic amount of energy density. In fact, you could actually build up to Planck densities at the inner horizon without changing anything at all about the external parameters of the black hole. So, what David and I realized is that the same idea could also be used for the outer horizon as well. Outer horizons also have dramatic blue shifts. So, that's kind of what we constructed in this paper, where we basically said, look, I have a solution in general relativity where outside the firewall region, or whatever, it looks just like the regular Schwarzschild geometry, but as you approach the black hole, you think you're going to hit the event horizon, but just before you hit the event horizon, you actually hit a region of Planck density. So, what's really happening is that the dramatic positive energy densities in there are getting canceled by dramatic negative binding energies in the system. Hence, we've accomplished our goal, that we really have a Planck density region everywhere in the story without violating anything at all about the external parameters of the black hole. We are very, very excited about this, and in a sense, in just a couple of sentences -- here is our main point. Let's think about why people believe in black holes. What's the thing? The reason why people believe in black holes is the following. If you take some region of space, and you put enough matter in there, as long as general relativity is valid, and general relativity will be valid as long as the density of the matter is low enough, which is generically true, Penrose has rigorously shown that no new force can support this region against gravitational collapse. This region will collapse. David and I completely agree with this. There is no doubt that you cannot prevent gravitational collapse. But what general relativity predicts is that you will keep collapsing, you will eventually hit a region where the density hits Planck density. Nobody in the world doubts this. This is what is called a singularity. Now, the Schwarzschild solution is an assumption about the future evolution of this high-density region. The Schwarzschild solution assumes that this high-density region remains physically small, and thus, there is an event horizon outside of it, and then you end up getting the black hole information problem. I would say, nobody in the world -- string theorists, anyone included -- knows what actually happens to that region of high density. There's no reason why it needs to remain physically small. What we are positing is the fact that gravitation has this phenomenon where regions at high density can expand while remaining at high density. So, this is the phenomenon of inflation which is a small universe becoming very big at high density. Also, this phenomenon that you see in the inner horizons of black holes, where a small region can become as big as the inner horizon at high density. All of these are possible within black hole geometries. So, we are just speculating, as we are speculators, that this region of high density can expand, continuously violating the rules of general relativity, and get outside the horizon. To us, that is a viable possibility which people have ignored, and if you don't ignore it, you then think about what can be experimentally done to probe it. I believe LIGO will be able to experimentally probe it once they do some of these upgrades that they're planning on doing. So, of all the things I've worked on -- I will say this -- this one, I think, is correct. The black hole information problem cannot be solved as long as the Schwarzschild black hole is the right description of it, with the event horizon or whatever. You physically have to get information from inside the black hole to the outside. The only way you can do that is by violating general relativity, and the only way to violate general relativity is to constantly remain at high density. So, I believe that we have hit a kernel of truth here. It's a dangerous thing to say as a physicist, that you believe something without experimental proof. But this one, to me, it feels right. I am optimistic that maybe one day LIGO will actually go ahead and discover these things, and we will know the truth.
And it's LIGO and only LIGO that would be able to do this?
LIGO, I think, is the best bet. LIGO, LISA,MAGIS. Gravitational wave detectors will be the first, I think, most obvious place to look for. There might be signatures in the electromagnetic spectrum, but they're generally harder to get to. That is an unfortunate fact about the world, which is that we form solar mass black holes. That's the lowest mass black hole that we know how to form. And signatures from black holes would typically be at the size of the black hole. So, the frequency that they would produce would be at the size of the black hole. So, a solar mass black hole would produce signatures in gravitational waves as well as electromagnetism at 100 kilohertz. That's what the black hole size corresponds to. Now, electromagnetic waves at 100 kilohertz have a hard time getting around in the universe, because we have what is called a plasma mass from all the ions in our galaxy, and they tend to absorb low-frequency electromagnetic waves. So, it just happens to be an unfortunate fact about the world that radio signals from solar mass black holes will likely get absorbed in the galaxy before they get to us. So, gravitational waves are likely our best bet.
And then your work with Peter and David subsequently, on reconciling large cosmological constants to small cosmological constants, is this a continuation of the work, or is this something separate, would you say?
It is a continuation of our bouncing cosmology work. When I think about the cosmological constant problem, I sort of look at it in terms of risks. Like, what could fail? So, back in 2015 or 2016 when I was thinking about this, the biggest possible failure mode was that we would not be able to make the universe bounce. I would say we retired that risk by basically saying that if these kinds of things are possible then it would be the case that a bouncing cosmology can be created. So, I would say we've retired that risk. The second risk would have been that it would have been impossible for you to come up with a model where this sort of relaxation actually happens. And we've now constructed a model where that relaxation actually happens. So, I would say we've retired that risk as well. There are a couple more things we need to do before we get a complete solution, which is that for the bouncing model, we need to write down a source of matter that everybody can agree works. And actually, David and I figured out what that matter is. So, we are sort of writing a paper about that at some point. And once we do that, we will then need a story where we connect all the dots together, where the relaxation naturally hands itself off to the bounce itself. So, I think that will be the last thing that we need to do before we have a full story from the very beginning through the bounce. But once we do that, I would feel very confident that we've actually, on paper, shown a story that anybody who questions whether we've done anything can go and verify. But we've mostly now been extremely encouraged in terms of thinking about how to detect more signatures that might be on these scenarios. Could one detect dark energy in the laboratory? So, with Peter and David, I've been thinking a lot about new directions in terms of experimentally detecting dark energy in the laboratory. So, that's what we've been thinking about quite a bit.
Was it a difficult decision to leave Berkeley to come to Hopkins?
Not really. For me, it was the case that David and I have been effectively collaborating for a very long time. So, physics-wise, I felt this was a no-brainer. Hopkins was also nice enough to make it financially a no-brainer. And fundamentally, our lives in the Bay Area were actually strenuous because my wife and I worked in two different parts of the Bay Area, so we both had terrible commutes. I was commuting 3 hours a day, and she was commuting 2 and a half hours a day, so it really made no sense in terms of where we could comfortably live and do good physics and what not. My wife is not an academic. She's a teacher, but it was still that kind of thing where we felt that this place really would have made a lot more sense. In fact, I have absolutely no regrets now after moving here. I'm enjoying this area a lot more than I ever thought I would because it turns out that I really enjoy hot and humid weather, growing up in Chennai, which is the natural climate there. I enjoy Maryland much more than I ever enjoyed California.
Surjeet, just to bring our conversation right up to the present, you mentioned that in the beginning of our talk that in the pandemic with remote work, obviously no commuting whatsoever, you've been more productive than ever. So, what are some of the big things that you're working on in the past year or so?
Oh, good. So, there are two things that I actually am extremely excited about. One of them we've already published a paper on. One is actually -- this is a fundamentally new way to detect forces that are of very, very short range. There are a number of experiments that people have done to detect new short distance forces between matter -- it's essentially short distance in the sense that if you separate two objects by too much beyond the range, the force goes to zero. So, now you ask the question, there are extremely good bounds between new forces between matter that are separated a centimeter or longer. But as you bring the materials closer and closer, these bounds get really weak. The fundamental reason is because as you bring two sources of matter really close to each other, the sources of matter begin interacting not just through the new force, but also through electromagnetism. Electromagnetism is a very strong force, so even if the matter is neutral, what you could end up having is basically some stray charge sitting in some surface. So, there would be electromagnetic forces coming from surface imperfections, which rapidly dominate at distance below a micron. So, I was asking the question, how can one fundamentally beat this challenge, and what I stumbled upon was the possibility of using the so-called Mössbauer effect. This is an old technique, the Mössbauer effect, which is a statement that basically I can have -- in some crystals, I have some nucleus. A nucleus undergoes radioactive decay, and if the energy of the radiation is low enough, the nucleus doesn't recoil, but the entire crystal recoils. So, basically, the photon that goes out is the same energy as the decay itself. So, you could try to do what is called resonant emission and reabsorption. So, you basically have this crystal. It emits this gamma ray, and the gamma ray is at the same energy of the nuclear transition, and then you can try to see that gamma ray gets reabsorbed in the absorber in the top. So, this was used back in the day by Pound and Rebka, famously, to measure the gravitational redshift on the earth. So, they had this thing -- a plate here and a plate at the top, and they saw that the gamma ray, as it went up, the gravitational potential lost energy, which is what they ended up measuring. So, what is interesting about this is that first of all, if you think about it, nuclei are very, very protected from any electromagnetic noise, because they have the electron clouds around them. If we put a straight charge in the sample, the electrons do a great job of screening all that from the nuclei. Secondly, it is also the case that any correction, any shift on nuclear levels, fundamentally has to go through nuclear multiple moments. So, if you put a magnetic field, or an electric field, or whatever, the way they shift nuclear levels is by changing the nuclear multiple moment. You know, through the dipole moment, or quadrupole moment. And all of them are very small for nuclei. So, all of these electromagnetic sources of noise are fundamentally very small on nuclei. On the other hand, if you actually have a new force of nature, like a new scalar force or tensor force, those have the ability to directly change nuclear energy levels significantly. So, the idea basically is that Mössbauer is a way that you can dramatically decrease the electromagnetic sources of noise without changing your signal from scalar intensive forces. That's what we found. So, the idea would be the fact that we take two Mössbauer systems, set up a Mössbauer source and a Mössbauer receiver, and then bring in a new source of matter very, very close to the Mössbauer source, so if the new source of matter exerts a new force or whatever, it would shift the nuclear levels ever so slightly. And the gamma rays that are now being emitted will no longer be resonantly absorbed at the top. So, that would be a way for us to detect these new things. We worked with this guy Giorgio Gratta at Stanford on this, and he's extremely excited about doing it. Actually, I was just talking to him recently. He's all set up to -- he's got some Russians who have sent him some radioactive sources here and there. So, as soon as the pandemic limits on how many people can be in the lab are fully relaxed, he's going to build this. So, that's what he's been up to. The second thing, David and I are still working on this, but we believe we actually have a viable modification of quantum mechanics. There have been no, on paper, frameworks to change quantum mechanics and test it in the laboratory. So, in the past year or so -- I've been thinking about this concept for a long time, but in the past year it's really matured. What we basically have is we think a very sensible framework where one can actually deviate from the linear nature of quantum mechanics. So, there's fundamentally a nonlinear modification of quantum mechanics. People have thought about nonlinear modifications before, and usually those modifications have problems with causality. So, we essentially have a way to modify quantum mechanics in a causally consistent way. So, we are extremely excited, and we have a bunch of experiments that we've thought up that one could actually go and do. I've talked to a couple experimentalists who are all excited about doing it, so we'll see. The paper is not fully done yet, so I hope it survives our rigorous tests of reasonableness and all that, but I'm optimistic it will get there.
Surjeet, now that we've worked right up to the present, for the last part of our talk, I'll ask a few broadly retrospective questions about your career so far, and then we'll end looking to the future. So first, how did it feel when you won the 2017 New Horizons in Physics Prize?
Oh, I was very excited. I was very, very happy because in large part it was a recognition by the community that what we had done, which was basically go out there and talk about creating new experiments, was something that was worth doing. That felt very good because, as I said, the change is quite dramatic, because in 2009, when I was applying for a postdoc, people did not actually even think that this was a field. I didn't get a job in the first round, and people were doing supersymmetry. So, by 2016, it had become very clear that there was actually something important to do here, and to me that's very important because this sort of thing, more than the money that I got, it's a recognition -- it's a signal that it sends to young people that, look, there's something important that you should be doing. I think that message was received by the community. I'm very happy today that there are so many young people who are excited about thinking about new experiments to probe dark matter, dark energy, axions, whatever it is. So, it certainly led to a change in what people in the community view as an important thing to do. So, that was always the more important part of the story. I was also personally very, very humbled to receive this prize at the same time as Rai Weiss and Kip Thorne, because they won it as a special prize that year. To me, it was something that occurred to me when I was in this ceremony, with these very fancy rich people. You know, like billionaires and what not. And I asked myself this question, who was I jealous of in that room? And I was jealous of Rai Weiss. No one else. For a very fundamental reason. It actually spoke back to the reason why I became a physicist in the first place. Actually, I will quote a Tamil proverb for this. It's something that's stuck with me for a long time. The question that the Tamil proverb answers is basically, let's think about the various notions of wealth. Now, think about the fact that pretty much most sources of wealth that you know about would get destroyed by fire, by death, this, this, this. And the only source of wealth that is never destroyed is knowledge. Scientific accomplishment, largely. And I've been of the view that the reason why I pursue science is fundamentally that. I would like things that I do to be true, and they will be true for thousands of years. In fact, it's what we as humanity value. When we look back at human history, nobody knows the name of the richest guy in Greece. We know Pythagoras, the triangle guy. And for tens of thousands of years, as long as human civilization continues, Pythagoras did something that'll be true. To me, that was always what drew me to science, and Rai Weiss and Kip Thorne, they did something incredible. For the rest of human history, we will know, from this completely crazy time that we've been living in -- politics, pandemic, whatever -- 10,000 years from now, what Rai Weiss and Kip Thorne did will still be relevant. To me, it was incredibly humbling to be around them at that time because nothing I've done has been true. These guys did something great, so that to me was a privilege. Actually, Rai Weiss doesn't remember this, but Rai and I have had fights, ten years ago, with all this atom interferometry and gravity wave kind of thing. Of course, he was in a very different mood back then than he was after he had done all these incredible things. So, I had a lot of fun chatting with Rai Weiss about how he felt. This is the thing, right? This man, in 1975, was bold enough to go and say that I take two mirrors, I separate them by 4 kilometers, I want to make sure they don't move by 10^-18 meters. That's crazy. He had that confidence to push it through. And I was just thinking, what is the level of doubt that he must have had in the last 40 years? He spent $1 billion of the public's money, and how did he live with that? It is that confidence that you need to do science, that fortitude. So, I asked him that question. His wife answered. She said, “You don't want to know about this.” And then he told me, “Look, when I saw that result,” his personal sense was not happiness. It was relief. He felt like he had gotten a monkey off his back, that he finally was able to do it. So, to me, that was a lot of fun. It was a wonderful moment.
I can see why you liked to hang out with the humanities professors at Caltech now.
Yeah, indeed. There's a sense in which there is the human aspect of science, that people are -- it is funny that people forget the fact that scientists are humans, too. The fact that we are humans creates so much, both in terms of discord in the community, as well as I would even say fundamentally flawed ways of looking at the world, which fundamentally comes from the fact that we are humans. If we are blind to that aspect of ourselves, we tend to do wrong science, flawed science.
Surjeet, for my last question, it'll span both the past in your science career, and where things are headed. That is, given your laser focus on the interface between theoretical phenomenology and experimentation, what has been achieved observationally already that gives you a lot of optimism that the theories that you're working on will be demonstrated, and what are those areas where it requires a great amount of patience of foresight because the technology or even the imagination, or perhaps even the next Rai Weiss, the world is not yet ready for these things?
Yeah, I would say broadly the things that I've focused on, on the experimental front, have largely been things that I actually felt would be demonstrable in the next ten years or so, because we definitely do all of these things in very close association with experimentalists. Experimentalists need to get results. They can't just sit on an armchair and think about kooky things in the sky. So, all of the things that I have personally been involved in are all things where I'm very happy to say were proof of concept things are actually happening. This is the reason why I keep pushing them, because you can see actual developments going forward. So, I'm pretty optimistic that, scientifically, these experiments we've pushed like CASPEr, MAGIS—which is the atom interferometer for gravitational waves, which has now got secure funding—these are things that actually will happen, and that technology will move forward. We would have to play the political games necessary to get more funding, but okay. I think that is something that we are more adept at doing than we've ever been before. So, I'm optimistic on that front, certainly. I'm also optimistic that LIGO -- which has nothing to do with me. It's just the incredible work at LIGO that people have been doing. I think they will get a factor of ten or so more sensitivity than they have been doing before. So, that makes me optimistic that my more, let's say, radical, but in my opinion reasonable, opinions about black holes can actually be tested. You know, in terms of, what are things that are really ambitious? There's nothing that I work on in terms of active stuff, but I think things like a new collider, in my opinion. They're not going to build a new collider unless the costs dramatically get down. For that, I think you would need someone beyond the next Rai Weiss to get those incredibly ambitious experimental things launched. So, I've tended to work on those direction in close contact with experiments where we tend to push things that we think are reasonable, given resources and a lot of hard work, but achievable in the next ten years or so. I think on that front I'm pretty optimistic that the things we've talked about certainly seem like things that would see the light of day, should we continue getting funding. That's the one thing that is difficult to predict.
It's exciting to find out. We'll have to see.
Yeah, yeah. Ten years from now it will be interesting to look at this transcript and see how crazy I actually was.
We'll revisit. We'll see where we are in ten years.
It will be fun to do, for sure.
Surjeet, this has been a lot of fun. Thank you so much.
Thank you so much for your time.