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Interview of Savas Dimopoulos by David Zierler on April 27, 2021,
Niels Bohr Library & Archives, American Institute of Physics,
College Park, MD USA,
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Interview with Savas Dimopoulos, Professor of Physics at Stanford University. The interview begins with Dimopoulos reflecting on how the pandemic has affected his research, and he gives his initial impressions on the g-2 muon anomaly experiment at Fermilab. He discusses the push and pull between theory and experimentation when searching for physics beyond the Standard Model. Dimopoulos then recounts his early childhood in Turkey, where his family was part of the Greek minority. Due to ethnic tensions, he fled with his family to Athens as refugees. Dimopoulos remembers his early exposure to math and physics and being torn between the two. He describes moving to the US at age 18 for his undergraduate studies at University of Houston. Dimopoulos then recounts his inclination toward theory and his acceptance at University of Chicago to pursue his graduate studies under Yoichiro Nambu. He discusses his post-doctoral appointment at Columbia which then led to an offer from Stanford. He explains his research in baryogenesis and technicolor, as well as his brief time at Harvard with Howard Georgi. Dimopoulos talks about his return to Stanford, his work at CERN, and his research on large extra dimensions with Dvali and Arkani-Hamed. He concludes the interview with predictions for the future of physics beyond the Standard Model.
Okay. This is David Zierler, Oral Historian for the American Institute of Physics. It is April 27th, 2021. I am delighted to be here with Professor Savas Dimopoulos. Savas, it's great to see you. Thank you so much for joining me.
Great to see you. Thank you for having me.
Savas, to start, would you please tell me your title and institutional affiliation?
My title is Professor of Physics, and I'm at Stanford University.
Savas, I'd like to hear a little bit about how your science has fared during the pandemic. Remote working and not being able to see your colleagues and collaborators in person.
Yes, I can tell you, I had two classes of projects when the pandemic started. One class were projects that were well advanced. All the ideas were set, and it was a matter of implementing these ideas with computations. Those projects fared quite well. They, in fact, in some ways may have been accelerated because we had more free time. Everybody knew what they were supposed to do. We didn't rely very much on interactions, and those projects progressed perhaps more rapidly. Then, there were the projects which were either at the very early stage, or ideas that we were trying to develop. We're at the fishing stage, where we would brainstorm and try to come up with an idea solving a specific problem. Those didn't fare well. Those that relied a lot on continuous human interaction, and brainstorming, and daily changes of points of view, that rely a lot on random encounters with colleagues in different disciplines during coffee breaks, or during cookie time, or in seminars, those things didn't fare well at all. The obvious explanation is that those need these unplanned human interactions to spark progress, and those unplanned human interactions didn't exist. It's not possible to implement this by Zoom. Zoom is a very structured thing, and these unstructured interactions are very important components to what we call creativity. So, those projects are still ongoing. In the last few weeks that we have been allowed to go to our offices and work under more normal conditions the pace of progress has accelerated noticeably.
Savas, an even more current question. Because of your devotion to searching for physics beyond the standard model, I wonder what your take is so far -- of course it will be speculative -- but what do you think so far about the g-2 muon anomaly experiment at Fermilab. Do you think this will prove to be new physics or not?
There is a generic answer to these types of questions. Anytime there is a rumor of a new thing, the safe thing to say is, ah, it probably will go away. I'm hoping, of course, like everybody else, that this turns out to be a true anomaly, true Beyond the Standard Model (BSM) signature. The issue is that there are two classes of theoretical computations of the standard model magnitude of the effect that disagree with each other: The dispersive and the lattice computations. The lattice computations pretty much agree with the experiment, the dispersive do not. So, until this theoretical tension is resolved and we understand which is correct, we can't even call it an anomaly. It's only an anomaly if you trust the dispersive computation. If you trust the lattice computation, it agrees with the standard model and it does not indicate new physics. I think the most important front at the moment that can be pursued is to get the theorists to understand why these two different computational methods give such different answers. And only after this is resolved we'll know for sure if it should be called an anomaly or not. But I am excited. It will be a few of years before some of these issues are resolved because lattice computations take time to implement. There will also be more experimental data analyzed, so we'll know more. So, in a relatively short timescale by particle physics standards, this thing will resolve itself. But it's definitely exciting. And it's not the only anomaly that is out there. There are a number of other ones that are not quite as dramatic, but one can dream that somehow there will be a unified explanation of at least some of these anomalies that will point to some new direction. But I think it's too early to tell. And I also think that the generic answer is very unfair. At some point, the generic answer will be wrong, and we'll have a new discovery.
Savas, branching out from that more broadly, of course, as you well know, the story of building the standard model is an interplay between experimentation and theory. Where is the field right now? In other words, sometimes since the 1970s, theory has been leading experiment, and sometimes experiment has been leading theory. So, right now as a time capsule circa April 2021, which is leading which, as the community searches for physics beyond the standard model?
The word "leading" suggests that it's a winner. Nobody's a winner unless theory and experiment go hand-in-hand. And it's also fair to say that experiments, especially these days, are much harder to do and take much longer timescales than theories. So, in that sense, "leading" with quotes, yes, the theory is leading. The Standard Model became the leading theory back in 1978, when parity violation in electron deuteron scattering was observed at SLAC. I was still a student back then, and I remember that was a turning point. I said, "Oh, my god, my career is over. Now we know the model, and what do I do next?" That was the turning point when we transitioned from the “what” to the big “whys”. Like, why is the universe so large? Why is gravity so much weaker force than all the other forces of nature? This second question is called the hierarchy problem and has been a driving force of theory for over forty years. There were many theories proposed to address the question: Technicolor, supersymmetry, extra dimensions, split supersymmetry, and others. So, the theory is way ahead in that sense, but it's ahead and lonely because effectively, the experiments now take longer. In the '70s, when I was a student, it was a happy time in retrospect when there would be some theoretical development, and experiments within a few years, would catch up. But now, the time lag between the theoretical ideas and experiments is now on the order of decades - at least as far as collider physics is concerned. So, in that sense, the theory is ahead of experiment.
However, thinking of just collider physics as the only way to look for new physics is a limited point of view. A new point of view that I initiated over twenty years ago, was to think of small-scale experiments that can search for new phenomena, new particles, new forces, new dimensions of space. In this field, experiment and theory are going hand-in-hand. In fact, experiments, in some sense, have been ahead in this. That's why I started to think about these ideas. I noticed that, for example, atom interferometry is a field that had already five Nobel Prizes -- for very good reasons. These people can do miracles. They can measure things to many, many decimals. And the question is, with such precision, can you search for small deviations that are evidence for new physics? The answer is, of course, yes. For example, one famous is example is people can measure gravity now at distances as small as 50 microns, which is thinner than the width of a human hair. This was inconceivable as recently as around the 1990s, when I started thinking about extra dimensions of space that could change the laws of gravity change at short distances. I remember, at that time, which was only 30 years ago, gravity was measured at 1 cm, and now it's down to 50 microns, and will soon approach 10 microns. The tool of small-scale experiments is high precision, instead of high energy. They look for tiny deviations to low energy quantities that can signal new physics. g-2 is an example of a high precision probe of new physics. It's still an accelerator experiment, but it's not a high energy accelerator by the standards of the large hadron collider (LHC). It uses that infrastructure, but it is a high precision experiment at energies of the order of the electron or the muon mass.
So, there are two frontiers: the high energy frontier, and the high precision frontier. In the high precision frontier, theory and experiment are pretty much in lock-step. Now, experiment was ahead until around 2000. Then, myself and then many others have thought hard about the theoretical ideas that can be tested with these. So, now they are in lock-step, so it's very exciting, and the timescale for experiments there is short. It's again few years. In some cases -- if the experiment is already set up and you want to just measure something -- it's a few months. And sometimes you don't even have to take the data. The data are there, and all you have to do is analyze it. So, we are very much in lock-step, and that's a very healthy state of affairs.
Another tool that we have to probe new physics that has been around now since the '80s, is looking for evidence for new physics in astrophysical objects, or in cosmology. That field has been active for 40 years now. That is still going on. There observation -- I don't want to call that experiment -- astrophysics observation and theory are pretty much in lock-step because there is a lot of breakthroughs that happen in astrophysical observation, most recently with advanced LIGO. These things tie in very well with theoretical ideas for new particles, etc. So, there is really three different frontiers. There is the astrophysical searches for beyond the standard model, there is high precision frontier, and then high energy frontier. And the high energy, that's where the disparity between theory and experiment is, and theory is too far ahead. The other two methods are pretty much in good lock-step. That's why you see much more activity in those other fields than in traditional collider physics these days. As I said, even g-2, even though it's a collider experiment, it's really precision. You're counting on the precision of the experiment to look for evidence of deviations from the standard model. You don't necessarily count finding a new particle directly in the lab. You look for its indirect effects on g-2.
If you had asked me your question before 2010, when LHC was turning on, my answer for the high energy frontier would have been more optimistic. I would have said that finally experiment has caught up with theory. All the theories addressing the hierarchy problem predicted new physics around the TeV scale, the LHC energy, and theory and experiment are finally in lock-step. Theory had been ahead for a while, but in a decade or two, experiment caught up. And now, they'll be in lock-step and they'll be talking to each other a lot. Well, this did happen, and we didn't find any new physics at the LHC energy so far. There is still the possibility that LHC will make a discovery as it runs for over another decade or two in high luminosity mode. So, it'll become more of a high energy and higher precision machine. So, there is still hope that something will be found there, but so far, we haven't found any evidence. So, the general feeling is that we may not be looking at the right energy, that we need to go to higher energy to find new phenomenon.
Savas, I wonder if that puts you in a similar place as your colleague Michael Peskin, who is so focused on the ILC as the next energy frontier.
Now, the ILC -- now, there are many ideas for going beyond the LHC. That's what you're referring to. So, ILC is definitely one such worthwhile idea, and then there are other ideas like muon colliders. My favorite is something that will not happen: that the LHC, instead of pursuing a high luminosity option, that they will instead try to increase their energy, maybe double their energy if possible, within the present tunnel. Just upgrading their magnets, and that is technologically a challenge. Some people say it's doable. Some people say it's hard. So, that's part of the reason this is not being pursued. But that in principle was another option that will not be pursued, just doubling the LHC energy. The ultimate idea that is likely to happen in the far future is to go to a much higher energy collider than the LHC. Like some 100 TeV collider that has been under discussion both at CERN -- which may well be the long-term future of CERN -- and in China. These discussions have been going on for about seven years now. These plans are still very preliminary.
I'm in favor of all of these ideas for colliders. There is this idea that science is expensive, so a society cannot pursue all of the above. Of course, expensive is a relative concept. Expensive relative to what? Relative to one fancy bomber, or to the weekly cost of a war, or -- so, I think, somehow, given the long-term benefits of science and the applications that have led, I think society should be more generous towards supporting science, and supporting many of these ideas. There are advantages and, of course, challenges for all of these ideas. They don't all do the same thing. The ILC measures with precision the Higgs properties. The muon collider has other advantages. But the ultimate discovery machine may well be this 100 TeV hadron collider that I will not see. It will probably be at least three decades away, but I think for humanity, that's the direction. I doubt that any one of these colliders will be ready before 20 years.
If I had to choose only one, I would choose the 100 TeV collider because it has the best chance to find new physics and does not rely on an enormous technological breakthrough. But I think all of these ideas are good. For me, the ultimate question is what's the machine most likely to find new phenomena? I think colliders should go to the highest energy possible. That's because the way we -- the most convincing way we discover new physics, if you discover a new particle and say here it is. I saw it right here. I saw its decay products, and I know it is there. This is not doubtful. The other more indirect ways are of course possible -- we discovered several things indirectly, but it's much more involved, and at least in the early stages, much less convincing. It's not like something hitting you in the head like a bomb exploding, saying, "I'm here, I'm the Higgs." So, it's not as apparent. That would be my inclination.
Savas, we've been very forward looking in our discussion right now. Let's go back in history. Let's go back the eastern Mediterranean. I'd like to hear first about your parents. Tell me about them and where they're from.
They were born in Istanbul, Turkey, which was back then called Constantinople and was part of the Ottoman Empire. I was also born there. We belonged to the Greek minority in Constantinople. Then, there were ethnic tensions that were flaring up every now and then between Greece and Turkey. As a result of one of these ethnic tensions, we had to leave Turkey, leave all of our belongings, and go to Athens, Greece as refugees. This is where I grew up. I was 12 years old when I moved there.
How many generations back did your family go in Constantinople?
My grandparents came from Greece. However most Greeks that lived in Constantinople were descendants of the Ionians and have been in Asia minor for thousands of years, from a time before Homer and Democritos.
Savas, was your family assimilated into Turkish culture?
It's a complicated question. Not very much in the sense that at home we would speak Greek and we went to a Greek school. Most of our friends were Greeks, Jews, and Armenians. These three minorities tended to live together and interact, work, and socialize with each other. So, in that sense, none of the minorities were strongly assimilated at that time. That was perhaps a reason for the tension, but much of it had to do with politics. Our relations with the Turkish people were in general very good – they are kind and friendly. It was political tensions that led, for example, to the pogrom of September 1955 against the Greek minority – a peacetime pogrom against their own citizens. After the recent memory of the horrors the Second World War many Greeks decide to leave. We stayed a little longer, but then in '64, there were more tensions and many Greeks were expelled and given 24 hours to leave Turkey and give up all their possessions
Savas, to what extent was Cyprus a source of the tensions for your family?
Cyprus provided a convenient excuse for the Turkish government to expel the Greek minority – just as the fire in the house where Ataturk was born in Thessaloniki was the excuse for the pogroms of ’55. It was later proven that the fire was set by the Turkish government. The Turkish government did not want the ethnic minorities to stay in Turkey, and they made life difficult for them. For example, in the ‘40s there was an arbitrary tax only on minorities – a tax so large that several families were financially destroyed. There was a sequence of these catastrophic events, especially the pogrom of ’55, that led to a massive exodus of the Greek, Jewish, and Armenian minorities from Turkey. There is only about one thousand Greeks left in Constantinople today.
And Savas, even though you were ethnically Greek, did you feel at all like an outsider in Greece?
Partly, yes. First, it was a huge change of environment and standard of living, and I lost many of my friends. Second, my new classmates couldn't quite figure out what I was because I had a different accent than the Greeks from Greece. Sometimes they called me a Turk, which I found odd because the Turks would call me a Greek. So, yes, I did. All this ended soon when they realized I was a good student and in a few months I had many friends and I felt at home. In Greece I felt safe and free. I could go anywhere I wanted safely, and speak my language in the streets -- something officially forbidden by the Turkish government -- without fear of being punished or beaten.
Savas, when did you start to get interested in science?
It started soon after we were uprooted from our birthplace and we arrived in Athens as refugees. We transitioned overnight from a comfortable life to a tough life of refugees with minimal belongings. My parents and I were living in a basic studio apartment, my father was looking for work, and I had lost everything from my childhood -- including my siblings who had decided to go to America. My parents were very concerned about me and to make me feel better they started buying me books. In a few months after we moved to Athens, I had already a small library of books. They also made it a point to go to the main bookstore in Athens, which is still there, and tell them that if I go in there, to give me whatever books I wanted, and they'll pay for it later. So, it was a very clever thing because I immersed myself in books. I could not afford to have a real life, but through the books I created my own universe.
Among the books they gave me first were some scientific books that I still remember. One was an excellent layperson's book on physics book by Einstein and Infeld. It had a big impact on me. I still remember my excitement with the realization that waves on a wheat field can propagate and transfer energy over large distances without any correspondingly large motion of particles. That was one of the key moments when I realized how amazing science is and I that wanted to do it all my life. Another influential book was a biography of Einstein by Philip Frank. These and a few other books convinced me by the age of 13 that I want to devote my life to either physics or mathematics.
For another year or so, I had this dilemma: Should I become a physicist or a mathematician? And at that time, I started becoming interested in the concept of truth. I felt that science was perhaps the only way to really know the truth. The reason for that is when I arrived in Greece, it was time of great political tension. There was the left and the right. This was only 15 or so years after the Greek Civil War ended. So, there were still tensions between the left and the right. I would listen to speeches from the right, and I said, oh that makes sense, and speeches from the left and say, oh that makes sense. And they would reach opposite conclusions. So, I was confused. Who is right? How can you discover the truth in these instances? Then, I said, forget it. There is no way. You need a very precise tool, so that's where science entered.
So, I was struggling between physics and math because they both pursue the truth but with different methods. It took me over a year before I realized I want to do physics. The reason was very simple: I felt that in math, you have very clear, pristine logic that leads you from a few axioms to many theorems, many truths. And some theorems are very short to prove, and some theorems are very long. I wondered, how can you be sure, especially in a theorem that involves many, many steps? How can I be sure that someone didn't make a mistake in some step, or many people didn't make the same mistake, or some different mistake? How can I be 100% sure that there is not some bug in this proof? I argued that while in physics we also have a few axioms and theorems, you can test the result of the theorem independent of people. You can test it by experiment, by going out there in nature and finding what's out there and seeing if it obeys this theorem or not.
It's the best of both worlds. It has the truth of math, but the physical relation to nature.
Exactly, and that truth is out there independent of our existence. And somehow, nature tells you if you've made a mistake. So, now, the plus of math is math is a huge field. You can have many different axiomatic systems. So, you have more truths to explore. In nature, there is one universe. Well, there is at least one universe that we can test.
Don't tell Andrei Linde that.
I think he would agree that there is one universe that we can test, at least, now. So, there is one universe, so it's a smaller system. So, it's much more challenging to find the correct theory of physics, say beyond the standard model, because there's only one universe that we are testing. On the other hand, the truth can be double checked. It has to pass both the criterion of logical consistency, and it has to be cross-checked by nature, that this is indeed what happens in nature. So, I felt that it was a much surer footing for discovering the truth. So, by age 14 or so, I decided I would go into physics, but I would also -- of course, I would study math because it was a necessary tool. But I would focus on physics. So, that's when I decided.
But there were many other factors that played a role. For example, I was completely fascinated with the idea of calculus, that you could compute the motion of, let's say, the planets around the sun, at any time in the future, or at any time in the past, by using equations. It was mind boggling how these equations can keep track of the second by second motions of the planets around the star when they are so complicated and interdependent. So, the fact that there is one machinery that can keep track of all of these changes at the same time, and give you the correct answers, was just stunning to me. As soon as I decided to become a physicist, I started learning calculus and differential equations to prepare myself. By then I was fully immersed in science.
Savas, did you go to the United States by yourself, or your family moved?
No, I went by myself. My siblings too had moved to the US around the time of the ethnic tensions, around '64. They were significantly older than me, and they decided that Turkey wasn't a safe place for minorities. The plan was that when I would graduate from high school, I would do the same. And indeed, that's what happened. At age 18, I moved to Houston. They were in different cities. We were all in the States, but not in the same place. In fact, I first when to Houston because my brother was there, but then a few months after I went there, he moved to Boston, and I stayed in Houston to finish my studies.
How was your English before you go to the United States?
It was not good at all. Back then the foreign language taught at school was French, not English. So my mother actually sent me to an English Institute where you take English lessons three hours per week. But I wasn't too interested. I was more interested in socializing than going to the English lessons. So, I didn't really learn that much, and then I stopped. But I was reading physics books, and my English was essentially what we learned from physics books, which doesn't help a lot with socializing. In fact, quite the opposite. Some of my English I learned from English translations of Russian authors. Very famous ones, Landau and Lifshitz. These are not the best places to learn English. I knew some very basic things, but I couldn't really communicate. So, I had to learn English when I went to Houston.
Savas, did you go to the United States knowing that you would stay here? Was that the plan, or did you think you would go back?
No, I didn't think I would go back to Greece. Neither me, nor my siblings. America was a dream, the best place to be. So, we were not planning to go back.
You must have excelled in your undergraduate to have been admitted to the University of Chicago.
I did well. Actually, University of Houston was very good to me. First of all, I was a good student, and they treated me very well from the very beginning. Within, I would say, a couple of months, they figured out that I'm a special student, and they did everything possible to help me. As a freshman, they gave me an office on their floor, close to the faculty offices, so I could go and ask questions and interact with them. The other thing is, I had to work to support myself -- I was a busboy in a Greek restaurant for a short time. It didn't last very long because I was a horrible busboy. I'm surprised the restaurant kept me for as long as they did. I arrived in the U.S. in August, and around Christmastime I was fired from my job. I had to pay rent, food, and things like that. So, when my teacher Dr. Walker saw me depressed. He said, "I see you are down. Why are you down?" I said, "I lost my job." He said, "Don't worry, I'll take care of it. I'll make you a TA of my class." I was a freshman. This was the first quarter, and they made me a TA in a lab. This an example of America in action, and how generously it supported me.
Did you know in graduate school that it was theory that you wanted to pursue?
That's another interesting question. I had that inclination simply because I started reading books from and about Einstein. On the other hand, I knew that the ultimate truth has to be tested by experiment. So, I was interested in that, but I wasn't very good at it. I took classes, and I was usually the worst in experiment in classes. You know how when you do experiments, you're supposed to put dots on your dataset, and your dots are supposed to be on a straight line? Mine were never on a straight line. I couldn't figure it out. So, I wasn't very good at it. And then, I went to graduate school at the University of Chicago, and I had another year of taking experiment. It was required. And then, I remember, I stayed twice the amount of time in the lab. I would get a key and go at night, and I still couldn't get things to work out. So, I decided that experiment is not for me. I think there is some degree of meticulousness that it takes to do experiment that I didn't possess. But I never gave more than 10% chance that I would go to experiment, but I wanted to try because it would be exciting to make things actually work with your hands and your mind. So, I wasn't very good at it, but from the beginning I had theoretical inclinations.
Did you specifically want to go to Chicago to study with Nambu?
No, like with everybody else, I applied to several places -- I forget if it was 10 or 15. I was admitted by Chicago and by Columbia, and I decided to go to Chicago. I could happily have gone either way. Both are great universities.
I'm so excited. I've never interviewed a student of Nambu before. What was he like as a person?
Oh, he was a great person. He was exceedingly humble. He would meet with me about once a week every Friday afternoon to discuss physics. He was also the chairperson when I was his student in the beginning. So, he was really more busy than normal. We would spend an hour or two, and what interested me the most is first of all, of course, his brilliance goes without saying, but also his integrity. So, we would discuss a problem and he would go to the board, spend five minutes thinking -- five minutes of silence. When you're a young student, it feels like a century, with this great physicist. And then he would write something, and never tried to show off, and he taught me how to think from very first principles, no matter what question was at hand. He would start from basic principles, and he would slowly get to the heart of what we were discussing. So, he taught me a lot about methodology.
Savas, what was Nambu working on when you connected with him?
Well, what he was working on is not what he is best known for. He was working on, at that time, finding classical solutions of field equations. And he was very fond of doing clever tricks and how to find solutions. This was quite a topic back in the late '70s, because there were new objects that were discovered, new solutions to gauge field equations that were discovered, which were thought to be important for confinement, and some important problems of strong interaction. The idea that quarks are confined. So, they thought they might be relevant, and were called instantons and monopoles. So, he was interested in finding such solutions. We didn't work together; we didn't publish any papers together, but we would talk often. After he stopped being chairman, he was quite a bit more available. In fact, he went on leave and he took me with him. So, I went with him on leave, and actually, the leave was for about four months at Caltech, and then the remaining -- that was end of '77 at Caltech. So, I was at Caltech from August to January, essentially, and then from January to June, I was at Stanford, at SLAC, with him. During that time, we interacted a lot, both socially and physics-wise, because he was alone without his family, and I was alone, too. So, we interacted a lot, and that was a great year. I got to know him much better. He was a very gentle man. He was unassuming. He was shy in the beginning, but then he would open up, and his sense of humor would come in. It was always gentle humor -- he was an amazing person. And you know, he is one of the few people for which you can say everybody liked him. I remember Bruno Zumino starting his talk in Nambu’s 65th birthday fest by saying something like, "I've never met a person who doesn't like Nambu." It was really like that. This may also be correlated why it took so long for him to get the Nobel Prize, which he deserved quite a few decades earlier. He didn't mind staying in the background, avoiding politics, and just enjoying his physics.
Savas, what was the process for you developing your own thesis research?
The process was very interesting. It was quite solitary. As I mentioned before, Nambu was busy as a chairman, so I had to come up with my own ideas -- which is a good thing, the best way to train to become a thinker. So, the process was completely self-driven. I was thinking about, in fact, things that at the time were considered completely crazy. The first thing that I thought about in detail, leading towards my thesis work, was what is now called baryogenesis. Essentially, it's the idea of explaining why there is more matter in the universe that antimatter. This is now a very well-known topic. Back then, at least in the West, it was completely unknown. Some Russians like Sakharov, as we learned afterwards, had speculated on this. But back then it was the Communist bloc. There was not a lot of interaction between the Soviet physicists and -- because they couldn't travel in the U.S., and there was no internet, etc. So, at least in the west, there was not much work connecting beyond the standard models and cosmology. So, I started thinking, about the following thought. There is a concept called asymptotic freedom that says in strong interactions forces get weaker as you get into higher and higher energies or equivalently higher and higher temperatures.
So, if you go to high temperatures, strong interactions become weak and the theory becomes simpler, it can be mathematically treated with tractable techniques called perturbation theory. In fact, at very high temperatures a gas of strongly interacting particles behave like an almost non-interacting gas. In early universe as we go back in time the universe gets denser and hotter and therefore, according to asymptotic freedom, it becomes simpler – a gas of free particles. This means we can understand the early universe with simple mathematical equations! It is an enormously different view than the then prevailing view that the universe has a maximum temperature, called the Hagedorn temperature, that it can never exceed. So, I started thinking about whether you could use this asymptotic freedom to study things like the creation of matter versus antimatter. I had learned recently that interactions in grand unified theories, as well as electroweak instantons, can turn quarks into leptons. So, I thought of putting these ingredients together and finding out whether you could create the matter-antimatter excess from grand unified theories or from electroweak instantons. So, that's what I spent most of my time thinking.
Savas, when did you become aware of Alan Guth's work?
Oh, that was later. That was 1980, and that's another story. I'm talking now about 1976-1977. As I said, the last year of my graduate studies I was half the year at Caltech, the other half at Stanford and SLAC. When I came to SLAC, Sid Drell, the great director of the theory group, told me he had a so-called Drell Seminar, where only graduate students would show up, and himself. He was a very nice man. Non-intimidating. He didn't want other faculty to show off, so he wanted only students at the Drell seminar. So, the graduate students would be there, and every time one of the graduate students would give a talk. Drell would be the moderator, etc. So, he asked me, "You want to talk?" "Oh, yeah, sure. I'll talk." "What are you going to talk about?" I said, "It's unfinished work, baryogenesis." The title of my talk was How to Create Baryons in the Universe, something like that. So, I advertised this talk, and Lenny Susskind, who was at SLAC at the time, tells me, "You'll talk about that? I'd love to come because I've been thinking about the same ideas." I said, "Okay, that's great." Well, Sid Drell didn't let him in. He said, "No, we don't want any intimidating faculty". But then, I discussed this with Lenny. Lenny had thought about the same things, and so we got together and wrote a paper entitled “On the Baryon Number of the Universe”. This formed the basis of my thesis.
At Caltech, by the way, I also had a good time, but Caltech was a more intimidating atmosphere. Back then, Feynman and Gell-Mann were around, so it was quite different from Stanford and SLAC.
Savas, were you thinking about string theory at all in your work with Lenny?
No, no. Not at all. This was now 1978. Of course, Lenny had pioneered ideas of string theory, and Nambu had pioneered ideas of string theory back in the 1970s. But that wasn't the topic of our conversations. No, actually, it's interesting. I should tell you, Nambu could see ahead, and sometimes too far ahead. He did tell me when I was a student, because he saw that I was interested in grand unified theories -- he was very impressed because I would just pick up these ideas that were crazy, and he'd say, "Oh, okay. Maybe you can try to form a grand unified theory out of string theory." I said, "Eh." And he essentially told me the idea that -- and later on in '84 became the modern view of string theory, but back then, in the '70s, string theory was a theory of hadrons. How to explain hadrons bound together by string. And Nambu essentially proposed that maybe I should start thinking about building grand unified theory out of string theory. This would have predated the '84 string revolution, but I didn't pay any attention to it. I was doing my own things.
So, yeah, the atmosphere in Caltech was quite different. It was also very good, very educational. I had the office across from Feynman's, right across from his door. Of course, his was a fancy office, and mine was a windowless student office. But he was very friendly. He would come in and, "Hey, what are you up to today?" So, that last year when I traveled to Caltech and Stanford was a great experience for me, because I was exposed to other institutions, and I saw how different great people are. It was really fantastic. It was good luck to have that opportunity.
Savas, besides Nambu, who else was on your thesis committee?
Actually, I don't remember. I would have to check it out. All I remember, it was a very friendly committee.
Were you using the term "cosmology" at this point? Was that a term in use yet, or was it still too early?
It was. I can tell you what was a sort of breakthrough that I had to penetrate as a student, was back then, the majority point of view was that the universe can never get any hotter than 100 MeV. 100 MeV is like the mass of the pion. It's less than the mass of the proton. It's now considered very low energy in particle physics. And there were reasons for that, in fact, having to do with the theories of strong interactions, as they were understood back then. If you try to heat the system up, you need to put a lot of energy into it, and then the particles start moving faster. But there were arguments saying that when you have the strong interactions, particles don't get faster. You just produce more particles, but they don't get any faster. You just increase the number of particles, not their energy. So, this means that the temperature doesn't really increase as you put more and more energy into it. There was something called Hagedorn temperature, which said that the universe can never get hotter than 100 MeV. That's why people thought I was crazy saying, let's assume that the universe started at 1016 GeV -- stratospheric. What the majority had missed was that this idea of asymptotic freedom that had just been discovered in '74 says that, in fact, strong interactions get weak, so you can use essentially intuition from weakly interacting gasses, or weakly interacting fluids, to go back in time. So, the higher the temperature, the simpler the theory gets. I remember because I wanted to publish the baryogenesis paper earlier, but people -- many people, but for example the astrophysicists, like David Schramm, who was a great physicist and friend, would tell me, "No, no. You can never heat up above the Hagedorn temperature. There's something wrong in what you're saying." So, that was the breakthrough. The breakthrough came in this idea of asymptotic freedom, that things become simpler at high temperatures, or high energies.
What were your opportunities after you graduated? What was available to you for post-docs?
Oh, for post-doc, I got two offers. Actually, I wasn't in the first round of preference, or maybe not even in the second. I got offers in late January. Usually, the hot people get offers sometime in mid-December, and then there is the second generation, which is early January. So, I was a late January person. I got a few offers, nevertheless. I got one in late January. I got one from Berkeley, a three-year offer, and one offer at Columbia University. That was a two-year offer. And one offer at École Normale Supérieure in Paris, that I didn't go to because I wanted to stay in America. So, those were my only options. I didn't get any offers from the hot places back then were, of course, Harvard, Princeton, SLAC, and Caltech. So, I didn't get any of those. But I was still very happy with what I had gotten. I was more unhappy that it took so long for me to get one offer, that I thought, okay, maybe I'm not cut out to be a particle theorist -- by the way, this was sort of before I published my papers on baryogenesis, on matter-antimatter asymmetry generation.
Another thing I should tell you about Nambu is that he was not a very political person neither for himself, as evidenced by his Nobel Prize coming so late, nor for his students. And it's very funny, because people told me -- more than one person told me, "Your letter is the best letter from Nambu I'd ever seen in my life." Of course, he was the only big person that wrote a letter for me. The others were not as well known. So, anyway, I had an option with three years at Berkeley and two years at Columbia. And then, Lenny Susskind told me, "Obviously, you should come to Berkeley so that we are close together and continue working together." And I thought about it. I thought, maybe I'm not cut out to be a physicist, so maybe I'll go to Columbia, which is a two-year job, because if I fail, then I can go to Wall Street and make some real money. So, that was 1978. It would have been good time, by the way, to go to Wall Street then. In addition, my sister lives in New Jersey, so she would be close, so there was also family there.
So, I dropped a three-year offer at Berkeley to go to the two-year offer at Columbia. And I didn't regret it, actually. It worked out very well. I became a post-doc in September of '78 and in March of '79 I had an offer for junior faculty from Stanford, which was my dream job. So, things worked out very well. There was a sequence of papers, one I wrote with Lenny on the baryon number of the universe. There was another work I wrote with him on something called extended technicolor, and these two papers led to faculty offers from Rockefeller University, from University of Pennsylvania, and from Stanford. I went to Stanford. I was a post-doc for nine months. So, it worked out very well, but it's funny that I went to New York because I thought I would be forced out of physics so I may as well be close to Wall Street.
A backup plan.
Yeah. By the way, this idea gave me peace of mind. I said, look, I'm not going to succeed. Let's take that for granted. Let me have fun in the meantime.
Perhaps you could be more adventurous with your research.
Yes. These were very adventurous things. Both baryogenesis and technicolor them were absolutely adventurous and crazy, so most people would say. I'm not sure, probably I would have taken similar risks, but I definitely had peace of mind saying, okay, I'm good. Let me just have fun. By the way, it was the same attitude as a graduate student, the mid to late '70s. I'm talking about '74 to '78 were very difficult years. The funding situation was bad. As soon as I joined the particle theory group at Chicago, that was beginning of '75, three junior faculty didn't get tenure. In the particle theory group, three. And the post-docs couldn't get jobs. The graduate students couldn't get jobs. Things were really bad, not just in Chicago. So, I had already resigned to the idea that I would fail, so I better enjoy it while it lasts. Physics is my hobby. Just like hippies used to go and enjoy their life, and then join the real world in their 30s, I'll just be happy and enjoy what I'm doing for however long I can. That frame of mind gave me the peace to explore wild things without concern for the consequences.
Savas, I'll come back to the question about inflation, and when you first heard about Alan Guth's work.
Yes, of course. I can tell you; I was at Stanford as junior faculty in '79. I came here in September, and Alan Guth was visiting Stanford and SLAC back then. He was officially, I believe, a visitor at SLAC for a year. So, Alan Guth was, I forget, in his second or third post-doc. He was a post-doc, I believe, in Cornell. So, he came as a visitor. He was in a different field. He was working in a different field. I believe it was lattice gauge theories. So, he came and started learning cosmology, and he had many conversations with everybody that he started thinking about cosmology. So, he developed the inflationary idea through his attempt to learn cosmology. My interactions with him were just -- he was a very impressive, very sharp physicist. I kept thinking, how come this guy is not more famous? He's amazing. And sure enough he became famous.
It just took a few years.
It took a few years, but boy, it was worth it. So, he developed the idea -- I didn't hear about it. I witnessed it. I remember discussions that he had with Lenny (Susskind) and Bob Wagoner, while he was learning the field, and a lot of back and forth because what he was thinking about was obviously revolutionary. So, it was a lot of fun. And then, when it started crystalizing in his mind, it became this beautiful framework. It went from being impossible to inevitable. This is inevitably the right idea for explaining the homogeneity of the universe, and so many other things in retrospect. It was just fantastic. Witnessing it was even more fantastic than hearing about it. Another thing I remember, when I went to Harvard -- so, I was at Stanford in '79, and then…
Now, you went to Harvard on leave from Stanford, or you resigned your position?
On leave from Stanford. So, what happened is actually interesting. I mean, that's another story. As you get older, you accumulate a lot of stories. Yeah, so what happened is in '79 to '80, I was at Stanford, and then I was invited to go to what was called ITP, and now it's called KITP, in Santa Barbara by Frank Wilczek, to stay there a few months. And then I was invited to go to University of Michigan to stay there for a few months. Anyway, I wasn't inclined to say no to things, so I accumulated invitations. My wife was saying, "Are we going to be moving like nomads?" Yes, it turns out to be good for my career, so I went. And while I was at Stanford, I received a phone call, and I was working with my friends Lenny and Stuart Raby. I received a phone call in my office, and it was Howard Georgi, "I would like to offer you an associate professorship at Harvard." I remember what I told him on the phone was, "Well, no, I'm really happy here. I work well with my friends, and yeah, I don't think so."
What was your confidence level that you would achieve tenure at Stanford at that point?
Actually, it wasn't high, but the associate professorship at Harvard wasn't tenured either.
Yes, of course. These are two very iffy options you're considering.
That's right. So, this was a young person without thinking. I said no on the phone, and then at the end of the conversation, Lenny said, "Who was that? What was this conversation?" "Oh, yeah, just Howard Georgi," who I only met once before and we had a good interaction. At any rate, I told him, "Yeah, he just offered me the position." "Hm, you may want to explore that." Lenny insisted. Then, he explained to me that this at least may help me get tenure at Stanford, and perhaps at Harvard. So, I thought, well, since I'm going to be in a nomadic mode, I may as well go to Harvard, too. Anyway, I went to ITP, to Michigan, and to Harvard, and I also got job offers from ITP and Michigan. But I went to Harvard thinking I would stay there for at least five years. But then Stanford came back with tenure very rapidly. So, I stayed at Harvard only a bit over a year and a half. But it was great. This experience, just like as a graduate student experiencing Chicago, Caltech, Stanford, and SLAC, now I was exploring Stanford, ITP, Michigan, Harvard. It was great for my perspective as well as -- and I interacted with many different people. Collaborated with tons of people, wrote papers.
Savas, tell me about your work with Georgi on SU(5).
Ah, okay. Well, that was another fantastic experience. First of all, the original SU(5) was of course done by Georgi and Glashow back in 1974. So, in the early '80s -- in 1979, I proposed a theory with Lenny called extended technicolor, which was an extension of a theory Lenny had proposed before called technicolor. So, we thought this was going to address the hierarchy problem, but it turned out to have problems with observations, so-called phenomenological problems, that contradicted experiments. So, that didn't live very long, that class of theories. So, then we started thinking about -- by we, I mean Lenny Susskind, Stuart Raby, and myself -- started thinking about supersymmetry as a way to address the hierarchy problem. And while I was doing some aspects of that, I interacted with Howard Georgi when I was visiting Harvard with my wife to see how we liked Boston.
So, we started working, and anyway, it was an amazing experience with Howard. First of all, he's a great physicist, and he has a very sharp and quick mind. He has a way of being right about things for reasons that cannot be easily understood. So, that was a fantastic experience. So, he and I managed to find a supersymmetric version of the theory that he had proposed with Georgi and Glashow back in '74. And that turned out to be the most popular beyond the standard model theory for 40 years –from 1981 when we wrote our paper until now. This so-called MSSM, or Minimal Supersymmetric Standard Model, is based on that paper that we wrote. That paper laid the foundation for what experiment to pursue if you want to discovery supersymmetry. For example, when people plan colliders, they don't plan them in a vacuum. They have in mind that they want to test specific ideas and specific theories. This enters, for example, in the detectors. What type of detector do you want to build? What do you want the detector to be able to detect with high precision? All of these questions are dictated by theoretical ideas that one wants to explore. So, they are not in a vacuum. So, the supersymmetric standard model whose basis we proposed played a huge role in the future colliders, including LEP, as well as the LHC. The collider as well as their detectors, and all the details of the detectors. It was a great experience interacting with Howard. He was different than everybody else, and everybody is great in their own way. Howard had a peculiar way. It worked out very well.
Were you thinking specifically about supersymmetry with Howard?
Yes. First of all, I had started thinking about supersymmetry way before, with Lenny and with Stuart Raby. This was about a year before I worked with Howard. So, I had already been on that trajectory and had written papers with Stuart. In addition, a few months before I got Howard interested, together with Stuart and Frank Wilczek we explored the unification of couplings in the supersymmetric grand unified theories (SUSYGUTs) which led to the famous prediction of the weak mixing angle in these theories, which was subsequently shown to agree with experiments at LEP and SLC in 1991. So I together with my friends had already explored some aspects of the MSSM, but we had left some important questions unanswered, such as the issue of supersymmetry breaking and the spectroscopy of supersymmetric particles. The paper with Howard built a complete general supersymmetric framework, the MSSM (minimal supersymmetric standard model), addressing these issues. It had an enormous impact on the field. It largely “shaped theoretical research on TeV-scale physics and inspired a large range of experiments” (quoting from my 2006 Sakurai prize nomination).
Savas, at this point, in the early 1980s, was your sense that the standard model was complete, so to speak, and that you were starting to work beyond it, or was this still very much in the mode of building the standard model?
Well, it depends on what you mean by complete. As a theory by itself, mathematically, it may have been complete, but physically, we already suspected there was dark matter. Although this was very preliminary, but still, there was this possibility. But there were glaring questions such as, why is gravity so much weaker than electromagnetism? A question that a child can ask. My favorite way of describing how big the problem is that when I lift my iPhone, the electrical forces on my fingers are able to hold an object against the gravitational attraction of the entire planet Earth. So, the gravity of the whole planet Earth is counterbalanced by the electricity of my tiny fingers. And the only reason why I can do that is because the electrical forces (that are holding the iPhone) are intrinsically so much stronger than the gravitational force (that the Earth is pulling it with). This is called a hierarchy problem. Why is gravity so much weaker than electricity? It's hard to think that this is just an accident. This seems like a deep fact that begs for an explanation. That has been the issue of the last 40 years, the hierarchy problem. So, we never thought the standard model was complete.
There was another problem which was already apparent in around '78, which is called the cosmological constant problem, which is essentially the problem of why is the universe so big? If you look at all the fundamental length scales of the universe, they're tiny. In fact, for gravity, the fundamental scale for gravity is unimaginably small. It's 10-33 cm. So, how come we have a theory which has length scales in it that are tiny, can produce such a big universe? That's the central aspect of what's called the cosmological constant problem. We still don't understand it, and there is no theory of this. There is no mathematical theory of this. But it turned out there were mathematical frameworks to address the hierarchy problem, and that's what for the last 40 years many particle theorists have been working on.
What research were you doing when you got back to Stanford?
I was doing the supersymmetric standard model. And then I started thinking about many other things. One of them is what may be referred to as theories of fermion masses. I started thinking about whether I could build a framework where I could explain the parameters of the standard model. Just to give you a perspective, the standard model has about 20 parameters. Now, it's a little more than 20, because we discovered neutrino masses, but about 20 parameters. By parameters, I mean numbers that you have to input in your theory. For example, the value of the mass of the electron, or the value of the charge of the electron are examples of parameters that you have to input. You measure them, and then you input them in your theory. And your theory is a giant machine. You turn the crank, and you can predict, in principle, anything that you want from these 20 parameters that you input into the crank. So, I wanted to see if there was a way to relate these parameters, and to start with two or three, and predict the rest by some mathematics. So, that's what I focused on. It didn't prove particularly fruitful, but that was one of the many things I tried. And of course, every few years, one changes direction. It's very healthy to, after five years, change direction, for many reasons. One, it's more fun to learn new things. The other is that once you spend a few years with something your thinking is set. So, you are less likely to have a breakthrough that will lead to a revolution. So, it's better to move to something else.
Savas, when did you become involved in neutrino masses?
Neutrino masses I never really got involved in except in the context of what is called theories of fermion masses. I got involved in the sense that these theories that we were playing with could predict neutrino masses. Back then, less was known about neutrinos, so that was a prediction. In particular, with Lawrence Hall and Stuart Raby in the early '90s, we tried to build complete theories of all parameters, or all masses, including the neutrino masses. So, again, we had machinery that predicted things. It turned out that the theories have not been supported by data, to the extent that they could be tested, because they only made a handful of predictions. Let's say, you have 20 parameters. You have to input 15 to predict 5, or something like that. So, it was more of correlations of parameters, but they didn't pan out.
So, this was in the early '90s. The biggest success of a theory that I proposed is the theory of what's called supersymmetric grand unification, which as I said, I built together with Stuart Raby and Frank Wilczek first, and then with Howard Georgi. We made a prediction of what is called a weak mixing angle in supersymmetric theories. So, this means the following. You have three interactions. Strong, weak, and electromagnetic. These three interactions have independent coupling strengths, what are called coupling constants. Now, in grand unified theory, if you know two of them, the third is determined. If you know the strengths of two of the interactions, the third is determined. So, that's what is meant by the prediction of the weak mixing angle. It's a fancy name. If you give me two, I can tell you the third. In the standard model, all of these three are independent. In grand unified theories, they are correlated. Okay, so you can make this correlation either in the non-supersymmetric grand unified version of the standard model or in the supersymmetric version.
So, we pointed out in 1981 in these papers with Frank and Stuart and also with Howard that the value of the third coupling that you predict in supersymmetric theories is different than that of the standard model. That was in 1981. In 1991, this third parameter that we predicted was measured very precisely, and it was found to agree with the supersymmetric prediction, and not with the non-supersymmetric prediction. So around '91 I experienced the most exciting feeling of being on the right path: the precise confirmation of a prediction of the supersymmetric standard model that I had proposed ten years before. It's a good success because it's within a few percent. It gets the right number within 2%, whereas the standard model misses by a lot. That is the reason why in '91, the whole community started saying, "Well, it's probably supersymmetry, so let's look for supersymmetry." So, most searches at the LHC were targeted to look for supersymmetry for this reason.
Savas, what about the SSC? Were you following developments on the SSC in the search for supersymmetry?
Yes. The SSC is a sad story because it was canceled in November of '93. The US community started thinking about the SSC in '83. That's when the consensus in the community evolved that we should build the SSC. And the supersymmetric standard model was proposed in '81. So, between '81 and '83, there were only two years. There wasn't enough time for everybody to convert to the supersymmetric point of view. Although, the majority already was convinced that this was the direction to pursue. Furthermore, in '83, we didn't know what we knew in '91, which was that the supersymmetry gives you this third parameter correctly, this so-called weak mixing angle correctly to 2%. So the case for SUSY wasn't as strong in the SSC. Whereas for the LHC, it was really strong. At the end of '91, people were convinced that the next collider should look for supersymmetric particles. In fact, interestingly, after the end of '91, there started being several conferences on the history of science where people would go to these workshops or conferences and would start arguing about who said what, when, before who, etc., trying to prepare the ground for credit for the most important discovery. So, it was very funny. Before we even knew that supersymmetry was right, there was a lot of effort to start to get the history straight. So, that's how confident we were, and justifiably so. So, the LHC and the LHC detectors were optimized to look for supersymmetry. So, before 1993 there were two options, the SSC and the LHC, but in November of '93 the US Congress canceled the SSC, so LHC was the only collider, and much of the experimental community migrated to Europe, either physically or intellectually by sending the students and post-docs, etc. The whole world focused on the LHC which started running around 2010. And then in '12, the Higgs was discovered. That was pretty good.
Before we get there, Savas, tell me about your visit to CERN in the mid 1990s.
CERN made me a permanent staff offer in '93, so I wanted to explore it, although I was very happy at Stanford. I wanted to explore it especially because after '93 it was the only collider that was going to be pursuing high energy. So, I considered it seriously. I went to CERN to explore it and see if I want to stay there permanently or not. That was sort of golden years, because there was a lot of excitement and anticipation. LEP was already running at CERN then, and there was going to be the LHC coming up next. So, it was a very exciting place to be with lots of young people and visitors. So, I liked it a lot. I spent there three happy years, collaborated with countless numbers of people. But then I decided to come back to Stanford to continue here. It was a very hard decision because these are two fantastic places. What I would have preferred is to be able to create two parallel universes. In one stay at CERN, in the other go back to Stanford, and then be extremely happy in both. But they didn't let me do that.
Savas, during your time in the mid 1990s, what was the level of optimism about finding the Higgs at that point?
The level of optimism of finding the Higgs someplace, somewhere, was very high. It wasn't clear though whether LEP would have found it. LEP was running at relatively low energies, around 100 GeV, and mostly near 94 GeV, the mass of the Z boson. So, it was mostly running at low energies, but it was accumulating a lot of precision. In the end, it created millions of Z particles, so they studied a lot of quantities very precisely. So, the level of optimism for finding it somewhere was good, but nobody knew the mass of the Higgs, so it wasn't clear where it would be found.
Relatedly, were you following developments at the Tevatron?
Yes, absolutely. You caught me mid-sentence. There was the Tevatron, which was also an amazing machine and very much a player in the search for the Higgs. They almost found it. The Tevatron for a while was the only very high energy game in town and it discovered the top quark! That was officiated around '93, '94, although the evidence for it had accumulated since the early '90s. So, Fermilab was a major player.
Savas, tell me about your important collaboration with both Gia Dvali and Nima Arkani-Hamed.
Well, these are two great theorists. What exactly do you want me to tell you about it?
How did the idea of large extra dimensions come about?
Let me trace the ideas that led to our work and as an example of how synthetic the scientific process is.
It started with the idea of TeV-size extra dimensions that I began thinking about in the summer of 1988 with Ignatios Antoniadis, during a late evening swim in Crete at a conference in the orthodox academy of Crete. We continued thinking about this when we would meet in the summers of 88, 89, and 90, but did not get too far. Ignatios was brave enough to write an early paper on this in 1990. I felt that the ideas were not yet adequately developed and did not participate in this paper. In retrospect this may not have been the correct decision, my participation might have triggered earlier interest in these ideas.
Another breakthrough came in the early ‘90s when I learned from my Stanford colleague Peter Michelson that gravity had only been measured down to a cm. This was a stunning fact: one of the most important forces in the universe had not been measured at distances below a cm! I could not get this thought out of my mind and would mention it to any physicist that I met. It created a universe of possibilities for new physics that I started exploring. So in the years ‘95 to ‘97 I wrote papers showing how string theory could give rise to new forces with sub-cm range, mediated by particles called moduli. Then with Gia Dvali, at the CERN Cafeteria in the spring of ‘97, we had the key thought that perhaps gravity can spread in more than 3 spatial dimensions whereas electric and other forces are confined to our three dimensions. I decided to work exclusively on this idea after finishing some other projects, and arranged not to teach in the winter of ‘98 and go to Paris to learn about extra dimensions from Ignatios Antoniadis.
In the fall of ‘97 Nima Arkani-Hamed came to SLAC as a postdoc and we were having fun exploring crazy ideas. We talked about the extra dimensions ideas, and I invited him to join me in Paris in the winter to learn from Ignatios about extra dimensions. It took Nima a whole second to agree to come to Paris, for the sake of science. This started one of the most exciting times in my career, comparable to the early ‘80s. We had incredibly productive time in Paris but it was not obvious at the time. There were too many exciting new possibilities that took time to disentangle. The simplest possibilities had not crystalized yet. When we went back to Stanford I had also arranged for Gia to come visit Stanford for a month. This was when the simplest possibilities rose to the surface and for the next six months I had one of the most exciting time in my career. We all knew that we were working on something amazing and we were all alone on this, like being alone in a toy store. We were exploring all kinds of amazing possibilities -- like science fiction but on solid mathematical footing. Then Ignatios visited Stanford for a few weeks and showed us how to imbed these ideas in string theory on even more solid footing.
My first seminar on this, outside Stanford, was in the Institute of Theoretical physics in Santa Barbara in June of ‘98. There was a string workshop there, and many of the world’s top string theorists were present. The reception was enthusiastic. After my second talk at the SUSY ‘98 conference in July in Oxford interest in these ideas exploded and lasted for many years. It inspired new experiments, both small scale -- searches for new submm dimensions and forces -- and collider searches for new particles and energy leaking into new dimensions.
I'm intrigued by the manyfold universe. Who came up with that term?
It may have been me, but I am not sure. That was after the proposal of extra dimensions. The idea is if there are extra dimensions, maybe our three dimensional the space can fold onto itself, back and forth, like a long roll or paper rolling back and forth and back and forth.
At this point, Savas, are you operating on the basis that cosmic inflation is settled science, or is there still doubt in your mind?
I'm not a professional on this, but I find it difficult to think of an alternative.
Such as string gas cosmology, for example.
To compare two theories, theory A and theory B, on equal footing, they have to be able to make the same predictions. If theory A is very specific and makes many predictions, and theory B is a vague theory which maybe explains one thing sort of, and the rest is too complicated to compute, then it's not a fair comparison. Theory A in this case is inflation. Inflation has gone far beyond explaining the homogeneity of the universe etc. for which it was originally designed. It makes detailed quantitative predictions about the microwave background radiation distortions that we see in the sky and the fluctuations of the universe that eventually leads to structure formation, galaxies, etc. The alternative proposals are not as predictive to really compare them head-on. So, I don't think it's a fair comparison unless the alternatives come up with calculational schemes where they can compute the same or more things than inflation, and then compare them.
Savas, how did it feel when you were awarded the Sakurai Prize in 2006?
Oh, it felt great. I like the quote a lot, because when I learned I got the prize I jokingly asked, "Uh, why did I get the Sakurai Prize? None of my theories have really proven to be right." But then I read the quotation, and it was right on. It roughly said, "For proposing theoretical ideas that strongly influenced theoretical research and future experiments."
At the TeV scale.
At the TeV scale, yes. And I felt, oh, well, maybe I did deserve it after all.
Savas, now that we're 15 years out from this recognition, what has changed in experimentation, in thinking about energies at the TeV level?
Well, what has changed in experimentation? What do you mean by experimentation?
Advances, if we are working toward either an upgrade at the LHC, or we're thinking about the ILC, in what ways in the past 15 years have thoughts about TeV physics matured, become more feasible, become something that is not necessarily fantastical in the short term?
Yeah, you mean, fantastical to implement experimentally.
Yeah. Now, it depends -- as we were saying before, first of all, as far as probing the TeV scale, as we were discussing in the beginning, you can do it in two ways. If you want to probe the TeV scale, either you go there, you build a high energy machine at the TeV scale and then discover the particles themselves. The new particles that the new theory predicts, you produce them, and you look at them and you look at their decay products. So, that's one way, and on that front, there have been advances in detector and accelerator technology. None of them are revolutionary in the sense that they'll shrink the timescale for colliders from 30 years to 3 years. None of that -- oh, gee, now I can fit the LHC machine in my bedroom. So, these developments haven't been so dramatic to shrink the amount of time, or the size, or the cost of the project, to where it will be on the timescale of a graduate student -- five years. On the other hand, you can also explore the TeV scale by high precision experiments at lower energies. Again, g-2 could be an example. g-2 is sensitive to TeV scale physics. Or atom interferometry, which is a topic that I worked on. Atom interferometry can be sensitive to physics at much smaller distances than the size of an atom. That's why they have been five Nobel Prizes in just AMO physics (atomic molecular optical physics) within a couple of decades. The high precision frontier is improving by an order of magnitude every few years and promises to be an exciting probe of TeV scale physics or beyond. On the collider front we need a revolutionary new development that will shrink the cost, the size, and the time of the project. Somehow, we need to shrink it all. Well, we haven't had an idea of how to do that yet.
Savas, when the Higgs was announced in 2012, did you see that as a capstone to the standard model?
Yes. I think this was a completion of the standard model. It was particularly important for the Higgs, because it was still possible that the Higgs was not a point particle like it was discovered to be. In the standard model, the Higgs is a point particle. In theories beyond the standard model, it can be fuzzy. For example, the so-called composite models, it's not a point particle. It's sort of like a proton or an atom that it's made out of sub-constituents. So, until the Higgs was discovered, there was a possibility that it would be composite, not elementary. Similarly, there was no guarantee that there would be only one Higgs. It could be that there could be two Higgses, which is not an aspect of the standard model. If there was more than one Higgs it would be beyond the standard model. So, we are now pretty confident, as far as we can see from the LHC, that there is a single point-like Higgs. The standard model, as it was proposed in the '60s, has been completed.
Given what has and has not been seen at the LHC since the discovery of the Higgs, what does that tell you more broadly about the need for searching beyond the standard model for new physics?
Well, it tells me that we have to look both harder and elsewhere. By harder, I mean build more powerful colliders, higher energy colliders. And by looking elsewhere, I mean look at small-scale experiments. Tabletop experiments, or intermediate experiments like the g-2. Or look harder in astrophysical systems to see new physics. That is what is happening de facto. In 2016, there was an excitement for a few months, there was thought to be a discovery of a new particle at 750 GeV, which went away. After that went away, and another year or so of experimentation, the community became fairly confident that there's probably not another particle that we'll discover in the present run of the LHC. Now, it's possible that the high luminosity LHC that is starting soon will discover something. That's not excluded, but clearly, because the high luminosity will not go to higher energy the chances of a new discovery are limited. High luminosity means you'll have much more data, many more collisions, so more chances to discover more things. Also, qualitatively, the detectors will become much better. You can see things; you can see tracks better. So, you could discover some niche phenomenon. However, because you won't change the energy, the chances of this are not as high as we thought, let’s say, in 2008, before the present version of the LHC started running.
Savas, to bring our conversation up to the present, tell me about some of your more recent collaboration with experimentalists doing fundamental physics, such as the gravity wave detector that you're involved with.
Oh, yes. That was a great thing. Starting in the early ‘90s, I started thinking about small-scale experiments, because I was completely fascinated with the fact that gravity had not been measured at distances less than a centimeter, which I thought was just crazy, given how technologically advanced we were even back then. What was needed to motivate the experimentalists to look for new sub-cm phenomena was a paradigm that would predict new phenomena at such small distances. Eventually, a compelling paradigm was provided by the theory of large extra dimensions. You could have dimensions as large as a millimeter without violating anything that we know, and you could use the extra dimensions to dilute the strength of gravity and explain the hierarchy problem. So, I started thinking about that, and I benefitted a lot from the fact that Stanford is an extremely interdisciplinary institution that favors a lot of cross-talk. Even in the ‘40s it was interdisciplinary in the sense that the there was a lot of interaction between Engineering and Physics-- that's why a lot of companies started here. So, Hewlett-Packard, Varian, and Silicon Valley started here for that reason. So, this spirit is very much alive.
When I was young, I didn't believe this idea of culture -- it's BS I thought. Well, culture, there's something real about it that I still can't figure out. So, when I came here, immediately, experimentalists, like Bill Fairbank and Hofstadter etc., would come to my office. I was a mere junior faculty, and they would talk to me for hours about ideas. And Felix Bloch would come, and we would discuss all kinds of crazy ideas. Felix Bloch, of course, was both a theorist and an experimentalist. So, I started interacting automatically with many experimentalists. I didn't really start anything, I was just continuing the local tradition. But then, I started getting really serious, so I started collaborating with many of my friends. Aharon Kapitulnik, with whom -- we were thinking together about testing short distance gravity, and now he has tested it down to distances of about 50 microns, as has Adelberger, University of Washington, and others. These are great physicists that managed to make tremendous breakthroughs. And then, I started working very closely with Mark Kasevich, and several youngsters, like Jason Hogan, and my students, Peter Graham, Mina Arvanitaki, and Surjeet Rajendran. So, this was the group of people that for four years we were talking every day over coffee, a few hours a day, which is a lot of time for an experimentalist to be talking to theorists, but it was worthwhile.
So, we first worked out the idea of using atom interferometers to test new physics. For example, an atom interferometer -- you know, atoms go up and down, and you measure their positions very precisely. If there is another new force coming, let's say, from a wall, or from a piece of lead that is in addition to gravity, you would be able to detect it. So, that was one idea, but there are many others that we thought of how to test new physics beyond the standard model. But then we said why don't we use it to detect gravity waves? If there's a gravity wave, it will jolt the position of the atoms, and we should be able to see this jolt. So, then we worked it out, and we proposed what used to be called AGIS. Now it's called MAGIS, which is a big new effort that started at Stanford, and now it's being built at Fermilab as well as in Europe, to look for gravitational waves, not with ordinary light interferometers, but with atom interferometers.
The interactions were incredible, because -- in the beginning, I thought that if I had experimental colleagues, I would just tell them ideas -- here's the theory, and here's what I think the signature would be. And then they'd tell me, "No, no, no. This cannot be measured. Go back, come with a better idea." That's not how it works at all. In fact, you do tell them an idea, the theory, and sort of some sketch about how to go about measuring it, and then they'll tell you much better ideas of how to measure it, with much better setups, and how to cancel errors so you get a much better precision. So, it was much more interactive, to the point where some of my experimental colleagues would even be able to do theoretical computations. I had to learn a lot about experiments. Of course, I did this partly because, as I said, I very much believe that every few years people should change what they're thinking about, simply because in my case, I found it made my life interesting. On the other hand, I also think it's very fruitful to explore. I think much of human progress is actually synthetic. You synthesize different things that pre-exist, and pretty soon the new thing you synthesized gets a life of its own.
Perhaps like the standard model.
Perhaps like the standard model, if you're lucky. Yes, but it's usually synthetic. It's very rarely that you come up with a lightbulb inside out of nowhere. I don't think there is, especially at these times, anything out of nowhere. It's just synthetic. So, now, because knowledge is widely spread, having many different people to interact is essential -- is also accounts for why collaborations in general are growing. There's just too much knowledge needed for a project, to have an expert that knows everything. So, talking to experimentalists is amazing, but they contributed vast amounts beyond what I thought possible. I don't think we could have done it, because we simply would not know what is possible. By "we," I mean the theoretical subgroup of these -- the theorists just couldn't even imagine what is possible to do. Also, proposing an experiment is very hard because you have to think of what are called backgrounds, experimental noise that is everywhere. A good proposal must at least account for the obvious sources of noise ones before you get started, so that you know what not to do. These things are costly, both in money and time. So, there is a lot of thought there. Every paper would take at least a year to fully analyze. It was an amazing experience. And it continues, by the way. We still continue to talk to experimentalists and astrophysicists. In the building that I'm at, the experimentalists and the theorists mix together, and the astrophysicists are all together, and we all run into each other. There are common seminars, that's very healthy. I remember one of my complaints about Harvard was that all the astrophysicists were at a different building far away. And about CERN, by the way, one of the reasons why I ended up not staying after the three years, even though it was the obvious decision to stay, as the LHC would be there, was the breadth. I wanted to be at an institution which wasn't focused on one thing. It is an amazing institution with top people, but I felt I was ready to start learning other things. That's why, as soon as I came back to Stanford in '97, I immediately started working with experimentalists.
That's interesting how CERN had that influence on you.
Yeah, because I mean, the people there were great. The experimentalists were fantastic, but they didn't need me anymore. They took the proposals that I made in '81, and they were already far ahead of me in designing ways to detect these things. So, in a sense, it was a non-obvious decision. The best decision would have been to have these two parallel universes where I was in both institutions. The second best I felt was to choose the broader institution. It worked out well.
Savas, now that we've worked right up to the present, I'd like to ask, for the last part of our talk, one broadly retrospective question about your work, and then we'll look to the future. Looking back over the course of your career, all of the topics that you've worked on, all of the collaborators that you've written papers with, what stands out in your mind as being the most intellectually satisfying, where you started on a topic that was interesting to you, and in the course of that research, you really learned something about how physics or nature works?
Oh, I think the most important thing is what I told you before -- the thing that I told you is called the prediction of the weak mixing angle. This comes under the grand name of gauge coupling unification. The consequence of the idea is that even though there are three forces -- if you exclude gravity, there is strong, weak, and electromagnetic, these forces become one. One unified force. That idea leads to the prediction that these three numbers, the strong, weak, and electromagnetic numbers are not independent, and that if you know two of them, you know the third. Using that idea, we predicted what that number would be in supersymmetric theories versus the standard model, and that prediction, ten years later, was confirmed by experiment. The moment I learned that the prediction of gauge coupling unification works for supersymmetry, but does not work for the standard model, that was probably the highest moment in my career so far, where I said, "Oh my god, maybe the almighty has spoken and this may be the way the universe works. We should look full steam for supersymmetry." That was the one moment where I thought I touched a new truth -- very rarely, you feel that.
You know as a theorist you scribble on a piece of paper, and talk to your colleagues, and go to the board, and erase each other's notes, and argue endlessly. And it feels like a game. It's an intellectual game, and in some sense, it's a lot of cleverness. It's an art, what model is more beautiful. Beautiful typically means simple and elegant. Simple components, but it predicts a lot. So, you argue about these, but it never dawns on you that this may be, in fact, the route that Nature took. Somehow, it would be a scary thought to keep that continuously on your mind. It's a very heavy load to carry. First of all, because it's rare that what you do that day will actually be realized in nature in the future. So, when, around '91, I was informed that -- I think one of my friends either Howard or Frank and I were the first to talk about this over the phone. He said, "You know, I think we got it right. They measured the thing, and it's exactly our predictions in our paper." I got goosebumps, and I felt elated, oh my god, the almighty has spoken. So, we and the whole community said, okay, supersymmetry is the way to move forward. So, that was probably the top moment in my case.
Savas, last question, looking to the future. Given your devotion to looking for physics beyond the standard model, and given your innovation as a theorist in working with experimentalists, and thinking about experiments that will get us there, for however long you choose to remain active in the field, how optimistic are you that you will be a part of and witness to this major breakthrough in physics?
By breakthrough, you mean discovery beyond the standard model of physics?
Yes. How optimistic I am. I would have given a very different answer in 2008. In 2008, which was before the start of the LHC, I would say at least 20%. In fact, I would have believed more, but I would have been cautious to say. Now, I'm much less certain. And the reason why I'm much less certain is because these theories predicted -- the theories were addressed to solve a specific problem, the so-called hierarchy problem. They predicted most naturally phenomena below a TeV. The fact that so far nothing has been seen there does not make me feel confident anymore. I will definitely not quote a number like 50%. If you're implying in my lifetime, 20 years maybe, I would give it 10% but that's probably an optimistic version. What I said so far applies to the LHC.
On the other hand, if we're talking more broadly about all experiments and all phenomena that I have predicted, with all experiments, let's say, astrophysical observation, small-scale experiments, and colliders -- what's the chance that one of the things I've proposed there turns out to be true? I'm significantly more optimistic. An example I didn't discuss because I didn't have time -- there's too much to discuss -- is there is a very interesting phenomenon that is called blackhole super radiance (BHSR). It says that around a rapidly rotating blackhole, you can create particles (bosons) in a broad mass range. It relies on just having particles that have gravitational interaction, which every particle does, so it's a very general conclusion. Moreover, these particles do not to be present in the universe, it suffices that they are present in the theory. So, BHSR can be used to search for all kinds of particles proposed for good reasons. One you may have heard is the axion. The axion is a very popular particle. It can be produced by rotating black holes.
So, that's an example of a proposal that I was involved in that I think has a good chance of being seen. Now that blackholes are really being observed, both with the advanced LIGO and with the Event Horizon Telescope, we are entering the era where blackholes can be used as probes of new physics. BHSR is one of the most exciting and general phenomena: a rapidly rotating blackhole produces a new particle in a certain mass range and leaves signatures that you can detect with astrophysical observation, such as gravitational waves. So, that part of my work, I think, may well pay off, and it may well lead to the discovery of a very exciting particle. That would be amazing, because it would mean that axion can be discovered by BHs before it's even discovered in the laboratory. That rarely happens, but if that happens, it will be exciting. So, I'm optimistic about some of my work becoming directly relevant for nature, beyond inspiring new experiments at the TeV scale, as the Sakurai quote goes.
You mean, in the more immediate sense.
In the more immediate sense. Not only did it inspire experiments, but these experiments found the particles that I had mind, that may happen. I've made several proposals, and the chance that one of them works, I would be quite optimistic about that. But as far as TeV physics, electroweak physics, obviously it's a narrower thing, and we've already looked at it once. Is there a chance that we'll look at it again with high luminosity and it will give something? Yes. But the fact that there are no discernible anomalies in the present run of the LHC is not encouraging for the prospects of the high luminosity LHC. Personally, I feel that a more promising direction would be to stop the high luminosity LHC and immediately go to the highest energy possible within the present tunnel of the LHC. This is a controversial view both for technological reasons (differing views on attainable magnet technology) and for political ones (going back on the high luminosity commitment).
Another important change in attitude from before the '50s, before the big science era, is that physicists then were not thinking much about a deep theoretical motivation to look here or there. They would just do something because they could. There was new technology, and then they would apply it, they looked whatever they could, and they made discoveries. Much of what we knew before the '50s didn't come from a divine inspiration, or trying to solve a deep, fine-tuning problem, or hierarchy problem. They just looked where they could, and they found tons of stuff. So, I think we should continue with the same philosophy. Look where you can, and you may even find something far cleverer than anything humans conceived. Nature is infinitely more interesting, and smarter than humans, and we should look where we can. This philosophy is now re-emerging in the context of a large number of small-scale experiments looking for new physics.
The big science era -- that emerged after the success of the Manhattan project – necessitated a significant amount of planning, pre-conception, and “deep theoretical motivation” for what type of physics may be out there, and where. It has sometimes been successful, but it is not guaranteed to work.
Savas, you're a student of history to appreciate this fact.
The fact being?
The fact being that what has worked in the past in terms of basic science and sticking with it should continue in the future. That's how we're going to find new physics.
Yes. The best-case scenario is to find new physics nobody thought of. An extreme example is quantum mechanics. Quantum mechanics is so far removed from normal intuition that I don't think it could have been anticipated, and it was not anticipated by pencil and paper. It had to come from experiment. People thought they knew what was going on, and then they found out that they didn't. Who told them that they didn't? It was experiment. And I think the same thing may happen now. We have a crisis: we don't understand why gravity is so much weaker than the other forces of nature. We thought we could explain it, and the ideas we've had haven't panned out yet. Maybe this is an indication of something much bigger, that we'll learn a much bigger lesson. Perhaps as big a change as the change from classical to quantum physics, and that will have to come from experiment.
Savas, it's been an absolute pleasure spending this time with you. Thank you so much for joining me, for sharing all of your insight and explanation over the years. I'm so grateful we were able to do this. Thank you so much.
Thank you. It was a pleasure.