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Interview of James Peebles by David Zierler on April 11, 2021,
Niels Bohr Library & Archives, American Institute of Physics,
College Park, MD USA,
For multiple citations, "AIP" is the preferred abbreviation for the location.
Interview with Phillip James Edwin Peebles, Albert Einstein Professor of Science, Emeritus, at Princeton University. Peebles describes his enjoyment in pursuing the issues in cosmology that are most interesting to him in retirement and he explains his appreciation for the importance of taking a sociological perspective to science. He describes his first exposure to cosmology as a field to specialize in during graduate school and he surveys some of the experiments and observational advances that have propelled theoretical cosmology. Peebles recounts his childhood in Manitoba, and he discusses his undergraduate education at the University of Manitoba. He describes arriving at Princeton in 1958 and how he became a student of Bob Dicke's. Peebles discusses his thesis research on the possibility that the fine-structure constant might be evolving. He describes staying at (and never leaving) Princeton for his postdoctoral work, and some of the exciting promises of infrared astronomy and radio astronomy. Peebles conveys the simple process of joining the faculty, and he describes the developments leading to the prediction of the cosmic microwave background. He discusses the trend of particle theorists pursuing questions in cosmology, and he reflects on the impact of the Vietnam era on Princeton. Peebles conveys the significance of the introduction of cold dark matter and his perspective on the inflationary theory of the universe. He explains why LambdaCDM has become standard in the field and why COBE was so important. Peebles surveys the many observational projects that are currently being planned, and he reflects on the "buzz" that he felt in advance of winning the Nobel Prize. He describes how his life has been affected by this honor, and he reflects on how the Department of Physics has changed over the course of his long career. At the end of the interview, Peebles emphasizes his interest in remaining close both to theory and experimentation, and he shares his sense of curiosity at what clues might be found from the epoch of light element production in the very early universe.
Okay, this is David Zierler, oral historian for the American Institute of Physics. It is April 11th, 2021. It’s my great honor to be here with Professor James Peebles. Jim, it’s great to see you. Thank you so much for joining me.
Jim, to start, would you please tell me your title and institutional affiliation?
Title, Albert Einstein Professor of Science Emeritus, Princeton University, New Jersey.
When did you go emeritus?
The year 2000, I think it was, two decades ago.
And did Paul Steinhardt immediately succeed you in that chair?
Oh, the chair, the department has quite a few chairs. They move around (laughter). I don’t pay any attention.
(Laughter) Okay. Jim, in what ways did going emeritus allow you to unburden yourself with administrative and other professorial duties, and be more involved just in the kinds of science that was most compelling to you at that point?
Well, you put it- that was my consideration. I loathed committee meetings, and I do not do them anymore. Another thought then was my looking at the courses we teach. I’d taught almost all of them enough times that I asked myself, “Do I really want to teach this one once again?”
And so, I decided to retire. Of course, an important consideration, never a guarantee, but I thought it would be true, was that I thought that I could keep my office. No one guaranteed that, but I have kept it for these past twenty years, and it looks pretty secure. So, I could continue doing what I liked to do, and refuse to do what I disliked (laughter).
Jim, a very in-the-moment question right now: we have some wobbling muons at Fermilab that are causing a lot of excitement right now.
From your vantage point, best-case scenario, if indeed this is new physics, what is the impact on theoretical cosmology as you’ve been working in this field?
I’m not at all sure. It’s no surprise that the Standard Model in particle physics is incomplete- they may have to add another field- I don’t know what. That will have an effect on the behavior of the early universe, but I expect it’ll be minor, and I don’t think it’ll change at all the big empirical clues we have from light element production. I imagine that’ll go on as before. The strength of the weak interaction that is needed there is pretty well nailed down.
It’s always fun to see a new phenomenon that suggests something- an improvement on our theories. You know, we have the big furor or the excitement about the Hubble tension, a similar situation. I was just talking to Stew Smith, who also went emeritus but worked in that field. He was a leader in B-bar at Stanford. He expressed mixed thinking about the muon magnetic moment. Surely, it’s a systematic error? But theory and measurements look good, so surely, it’s exciting.
Jim, another question a little farther back in time: over this past year in the pandemic, how has your science been affected one way or another? In other words, in the one chance, perhaps you haven’t travelled, so you’ve had more time or bandwidth to work on some problems. But on the other, to what extent is your theoretical work really reliant on in-person interactions?
Well, to begin, of course, on travel, I had a packed schedule. It abruptly stopped. I haven’t gone on a trip outside New Jersey for over a year.
It’s quite a change. That did offer me extra time to do other things. Nowadays I work mostly at home, and it’s convenient in some ways. I mean, I used to walk into the lab almost every day of the week. Now, I walk in far less often. A dramatic effect of that was that I lost ten pounds. Go figure.
The research I’ve been doing, I can do at home or at the lab. It’s more convenient at the lab because there I have two big monitors, and I can spread papers out all over the place. Here, I have only a laptop. I guess I could get a monitor of larger size, except we’re not in a large home, so it would be awkward to find a place to put it.
And, anyway, the exercise I get walking in, about a mile, I enjoy very much. It’s a walk past one busy street, and then it’s residential streets. I can let my mind wander. There was an article in The New York Times today. People spend forty percent of their time letting their mind wander. I think that’s great (laughter). Free association; thoughts come and go, and some stick and some are useful. So, in the end, my research has not suffered. My research these days is largely historical. I have just finished writing yet another book. It took me a long time. It’s just at the publisher now.
What am I doing now? I’m making a list of challenges to cosmology. Our present cosmology is remarkably well tested and established. But it is manifestly incomplete. So, where do we go next? The community has decided, rightly, to try to do better the tests that have brought us to where we are now.
The prototype for this, to me, is Euclid, an immense project. But what strikes me is that forty years ago or so, maybe more, I was doing that sort of thing. I was collecting data on galaxy distances and redshifts and positions. I was inventing statistics to measure them. Twenty years ago, people were doing that much more carefully and extensively. Euclid will do the same thing with exquisite precision. But I wonder whether we can broaden the tests.
So, I am preparing a document listing every oddity I can think of in cosmological tests, and things that could be investigated that aren’t that have some plausible chance of proving to be informative. So, that will be fun, and we’ll see how it’s received.
Jim, before we go back to the beginning, and develop your personal narrative, I’d like to ask sort of two broad questions right now that I think will shape much of our discussion; one centers on sociology and nomenclature, and the other is on the history of theory. So, with the first one, I would like to ask you to search back in your memory, and tell me sort of three landmarks in cosmology that informed where the field is now: first, when you- the very first time you came across the term “cosmology,” second, when you realized that cosmology could be a respectable field of study within physics, and third, as you said already, when cosmology achieved the level of maturity by whatever parameter you would use to make that decision.
Right. Actually, you mentioned sociology, and the book I have just completed has the title, On Reality: Lessons from Philosophy, Sociology, and Cosmology.
There you go.
Sociology, I’ve come to realize, plays a big role in our field. I don’t mean the sort of sociology that considers our subject a social construction. Some sociologists argue for that, for reasons I cannot understand. But there are other sociologists who make very sensible remarks about the way we do science, and I drew together the history of these ideas that fascinate me.
Anyway, I first heard the word “cosmology” used as a subject of science when I was a graduate student at Princeton University preparing for what used to be the graduate general examinations. At that time, around 1960, general relativity was an established part of the physical sciences. The general exams had questions on special relativity, and simple aspects of the general theory of relativity. Yet the empirical evidence for general relativity at that time was woefully meager. General relativity was, in fact, a social construction. I’m not complaining, that was just the way it was.
I remember at the time being shocked that people should pay much attention to this notion of a homogeneous universe. Who would have ever thought it’s that simple? If you had a question on general relativity in the general exams, you could be pretty sure it would be something spherically symmetric. You’d be given a line element. You’d be asked to interpret a few of its aspects. There was no empirical evidence of that situation. I remember we used to have a joke about finding the electrostatic capacitance of a spherical cow or finding the acceleration of a frictionless elephant on an incline plane, and I would add interpreting the line element of a homogenous universe. They were all artificial, problems you could work in an exam.
These were situations that can be put in an exam because they’re simple, but they’re not meant to be realistic. Bob Dicke, my teacher when I was a graduate student, was very interested in all aspects of gravity physics. He got interested in cosmology and advised me to look into it. I was, for the first few years of doing that, quite uneasy about spending much time on such an obviously poorly supported theory.
But I was fortunate because the theory then was wide open. There were very few people doing any research on cosmology, just a handful, and after a meeting or two, I got to know almost all of them apart from those in the Soviet Union. So, I had free play to think of ideas, to search around for whatever evidence there might be, and to compare theory and evidence. It was a lovely time for a postdoc to make meaningful contributions to a field, meaningful only because the field was so empty.
When did I decide that there was something to this? That was detection of the sea of microwave radiation. Of course, at first, we didn’t know that it’s radiation remnant from the hot early stages of expansion of the universe. But we did know one really striking property of this radiation, that it is close to isotropic, the same in all directions. That’s what you expect if this radiation were coming from a homogenous universe. Isotropy at our position means either we’re at the privileged center of an isotropic universe, or else we’re in a nearly homogenous universe.
That made homogeneity feel more real to me, and certainly was encouraging. It started encouraging others, too. The field got a lot less empty after the detection of this radiation, though it took many years before cosmology was really a fully active field.
One of the most dramatic moments for me in cosmology was the results from the COBE satellite FIRAS experiment that demonstrated that this sea of radiation has a very close to a thermal spectrum. It was marvelous. Until then, I could think of all kinds of alternative explanations for this radiation, but none of them would make it thermal except for the hot big bang.
So, this was to me a piece of evidence as tangible as the dinosaur footprints you can see in rocks that show these creatures actually walked the earth. We had close to tangible evidence that the universe evolved from a very different state, one that was hot and dense enough to have relaxed the radiation to thermal equilibrium. Also, you know, I was still kind of hung up on homogeneity. If the universe were microscopically very clumpy, while homogenous in the large-scale average, then you would expect this radiation to be a mixture of temperatures from hot and cold spots. That would make a spectrum that is not thermal. The fact that the spectrum is so darn close to thermal argued to me that, yes, the universe has to be darn close to uniform. The old assumption for homogeneity from philosophy or dumb hope changed to something empirically justified. It was a dramatic moment.
Then, in the late 1990s, when cosmology had become a more active subject, we had the cold dark matter that I introduced in ’82. In the 1990s cold dark matter was a firm part of cosmology; everyone “knew” it was there. But that wasn’t so. The dark matter I introduced in ’82 was just an ad hoc counterexample to the thought that the contrast between the very smooth distribution of the radiation and the very lumpy distribution of the galaxies was contradictory. How could the galaxies grow so clumpy without disturbing the radiation? I introduced cold dark matter as a convenient postulate to produce a counterexample to that challenge to our standard ideas. In the early 1990s I still considered it as just a convenient postulate. I could think of other ways to account for all the observations, and I was more than a little uneasy about the fact that the community was not more seriously questioning the reality of cold dark matter. The community was right because it’s there, but I wasn’t convinced of it because I couldn’t see much evidence to support it (laughter).
In fact, in the nineties, I was producing counterexamples that didn’t require cold dark matter, and would, more or less, fit the observations. The most widely considered, I called PIB, primeval isocurvature baryon, was kind of contrived, not as elegant as CDM, but, well, it was a different hypotheses, let’s say (laughter). I remember well when my best alternative to cold dark matter was shot down by the growing accuracy of measurements of the angular distribution of the three-degree sea of radiation left from hot early stages of expansion of the universe.
I was working out a new and more elaborate alternative to the accepted cold dark matter model just as the first evidence appeared that there is that bump in the anisotropy spectrum at around 1º. In my elegant new theory, there’s a dip at 1º. It was immediately obvious: first that my elegant new theory is just not right, and second that the old theory I introduced ten years back might be on the right track.
Certainly, the results from the satellite experiments WMAP and then Planck were exciting but, on the other hand, not that exciting because I’d more or less given up on my skepticism of cold dark matter. And it became a question of increasing evidence in increasingly persuasive detail that this is the way the universe is made. My present thinking is first, amazement that the measurements can be made so well; second, amazement that the measurements and data fit each other so well; and third, the hope that this is not the end of the story.
These days, people are asking two important questions: should I trust the extrapolation of general, and should I trust the idea of dark matter? Others rightly question the application of the rest of standard physics, but I would put that as less questionable at the moment. I used to be deeply concerned about the immense extrapolation of general relativity theory, but that no longer seems so questionable. We have tests of general relativity on the scale of the laboratory, on the scale of the Earth, on the scale of the solar system. Let’s toss in the evidence of gravitational waves from merging black holes. The cosmology built on general relativity passes demanding tests. That is, the theory has passed an impressive variety of tests on an immense range of scales.
It’s certainly conceivable that general relativity fails just on the scales of cosmology, and an alternative gravity would do better. But general relativity certainly has done a pretty good job, and I think it’s a reasonable bet therefore to say, “Well, it’s probably done an excellent job.” So, I would put my first thoughts on what’s gone wrong or what could be improved in the dark sector, the properties of dark matter and the cosmological constant. You know the latter has a new name: dark energy. But that doesn’t mean anything, it’s public relations. So, I’m now pretty convinced there’s going to be a better theory, but my bet is it’ll look a lot like LambdaCDM.
Jim, when Bob Dicke first invited you to join him on his cosmological inquiries, was your sense that, literally and figuratively, he was operating in a universe by himself, or were there peers? Were there contemporaries of his that were also thinking along those lines?
It is true that Bob was an interactive person. He traveled. He talked to people. He brought back ideas. But his search for a better empirical basis for gravity physics was not widely practiced outside Princeton. There were a few experiments at other places aimed at improving tests gravity physics. For example, Mössbauer announced the wonderfully narrow X-ray absorption lines by atoms bound in crystals. Bob Dicke recognized that Mössbauer’s effect could be used for a laboratory test of the gravitational redshift predicted by general relativity. Robert Pound at Harvard recognized it too. Bob wrote to Pound to say that he was welcome to take on this experiment, because there were many more for Dicke and his gravity group to look into. Jim Brault in Dicke’s group was already completing a different experiment to check the gravitational redshift. Prior to that measurements of redshifts of spectral lines of different elements in the sun were different, and there were different redshifts from different positions on the face of the sun. It was a mess. Brault showed how to straighten it out and got a five percent check of the prediction. At almost the same time, Pound was using the Mössbauer effect for a measurement of the gravitational redshift of gamma rays falling some tens of feet in a helium container in a tower at Harvard; a magnificent experiment. Their precision in their first result was similar to Braults’s. There were other gravity experiments, but not many. Bob Dicke was alone in making a systematic survey of all the different ways you could test gravity physics, not fettered at all by theory. If you can test it, test it.
A beautiful set of experiments came out of that that are not widely appreciated, though I did write a long article about it. Bob’s research program in the sixties and seventies was unique in gravity physics. It set the stage for a lot of PhDs, and quite a few Nobel Prizes. An example is Rai Weiss, an admirable physicist, who did a brilliant job in conceiving of the LIGO gravitational wave detector, making it happen, and getting those detections; magnificent. Rai spent a year at Princeton. He built a modifier LaCoste Romberg gravimeter while he was at Princeton, one of the kind that is used to detect things like earthquakes and underground nuclear explosions. At that time the standard gravimeter had a mechanical lever holding a test weight at almost unstable equilibrium. An observer used a microscope to examine the light reflected from that weight, to see whether the weight starts moving, as would happen in an earthquake. Bob led Rai to use Bob’s methods of synchronous detection to electronically monitor the position of that weight. Rai built one of the first devices that used electronic detection instead of the eyeball looking through a microscope. Synchronous detection figured in a lot of Bob’s elegant experiments.
Anyway, at that time Bob was fascinated by the notion of how you would build a gravitational wave detector. He had weekly meetings where we all gathered together. Sometimes one or another member would describe progress in their work or discuss an interesting paper. But often, Bob would simply describe his own thoughts, and quite a few of those meetings were devoted to how he’d build a gravitational wave detector. Anyway, and to take nothing away from Rai, I think Bob was instrumental in setting Rai off in a wonderfully important direction. He sent me off in another wonderfully important direction. He inspired COBE, and that produced a couple of Nobel Prizes. More may come. And, you know, his group is still in operation.
Jim, my second broad question would ask you to reflect on the history of theory, and particularly the history of the theory or, more accurately, the lack of a theory to truly under t=0. When was this something that cosmologists started to really seriously consider? When were there moments over the decades where there was real optimism that this may have been achievable? And where are we today on these things, and specifically what misapprehensions, even among physicists, stubbornly remained about theories or lack of theories relating to t=0?
I’m sorry, I’m confused. What do you mean by t=0?
The very beginning.
Oh, you don’t mean capital T, temperature?
No, no, time equals zero.
You mean little t, time.
The three minutes of the “first three minutes.”
Yes. You know, through much of my career, that question was wide open. We have a tentative idea now, inflation. But before this idea it was simply a manifest example of incompleteness. That didn’t stop us from doing research, though.
We said, “Let it be a postulate that the universe at some very early time, but after t=0, is expanding, hot, and close to uniform, and let us follow the consequences from there.” There was a lot to be done under that hypothesis, and, as we built tests, we gained confidence that the hypothesis is pretty good. Always there the question: what happened before the universe was expanding? But that didn’t stop us from doing good science about what the universe was doing after it was expanding.
Our cosmology still is incomplete. We have a popular idea about what the universe was doing before it could’ve been described by standard theory: inflation. We ask, “Do you trust inflation?” It’s popular, for good reason, but it has precious few empirical predictions on which it can be tested. I can mention just two.
First, a rapid expansion during inflation surely would stretch out the universe and remove space curvature. So, it seemed obvious, if you accept inflation, that the universe must be cosmologically flat; no curvature of sections of constant time. In the nineties, that was an article of faith, but it wasn’t a demonstration by any means. Now, I think the evidence is quite clear. The universe is awfully close to cosmologically flat. That arguably was a firm prediction from inflation, so we are impressed.
Second, the departures from homogeneity in inflation are frozen quantum fluctuations. They naturally are very close to scale-invariant, with a naturally slight tilt from scale-invariance. All that is now observed, which is a pretty impressive record. But, you know, these ideas don’t seem unique to inflation, so my thinking is that inflation is not very strongly supported. I can take inflation or leave it alone. That doesn’t make problematic all the research about what happened after inflation, of course.
What happened before inflation? There are ideas, but none that complete the theory. For example, eternal inflation can be eternal into the indefinite future, but it can’t be eternal into the past, or we’d have universes running into each other. My colleague Paul Steinhardt, whose office is just two doors down from mine, and I have different ideas about what this incompleteness might mean. Paul feels that it argues against inflation. I say, so inflation is not complete. All of our physical theories are incomplete. So, where were we? Oh, yes, the big puzzle about t=0 has, to me, always been a big puzzle, but not one that’s gotten in the way.
Is your sense that- is it possible that there’s something fundamental to t=0 that makes it resistant to either observation or theories that would inform the observations?
No, I don’t put any particular weight on t=0, though of course I resist thinking about t=0 because that sounds like infinite mass density, and I don’t want to go there.
So, to me, the theory is incomplete, and let’s leave it at that until someone has a bright idea about how to go about making it more complete.
Very good. Well, Jim, we don’t have to take it back to the ultimate beginning. Let’s take it back to your beginning. Let’s go back to Canada, and let’s hear first-
-about your parents. Tell me about them and where they’re from.
Where are they from? I was born and raised in the province of Manitoba, in the center of Canada. My mother and father were both born in and around the city of Winnipeg, which is the capital of Manitoba, and by far the largest city. My mother’s family came largely from south of England, they were Trefreys, and their ancestral home was near Lands End in the south of England.
On my father’s side, my great grandfather Peebles was a manager of an estate of the Duke of Northumberland. The Duke of Northumberland owned a good part of England in those days-maybe still does. The Duke’s main holdings are at the border with Scotland. And, you know, on the other side of the River Tweed, at the border, is the small town of Peebles. We visited once- a charming town. I checked the phone book, no Peebleses (laughter). Maybe it’s a name you acquired when you left. My grandfather Green, my mother’s father, came to Winnipeg as a pioneer, and worked at the local flour mill. In those days, wheat was ground here there in Winnipeg and he was a foreman at the mill.
Where are we? My grandfather Peebles, if I remember right, worked for the railroad. My father worked in the grain exchange. Winnipeg is at the edge of the Great Plains, and it is an important distribution point for the handing of grain shipped in by long freight trains from the west. The grain could go from Winnipeg north up to Hudson’s Bay, east to eastern Canada, or south to the States. My father worked, oh, as a clerk in managing all this. My mother was a homemaker.
I had two sisters, Audrey and June, both older than me. Audrey went to normal school, as it was called then, to become a teacher. She loved being a teacher. She even volunteered teaching after she retired.
I was the first in my immediate family to go to university, the University of Manitoba. I came from a small high school- I don’t know whether we had more than two dozen students in my class- really very small. We didn’t have such thing as a counselor, and, if there were one, I don’t think I would’ve paid much attention to the counselor. I was not very attentive to such things.
So, when I graduated from high school, I felt some vague need to continue with education. I didn’t know in what, but I was aware- one bit of self-awareness, that I liked to build things. And I had the impression engineers built things, so I entered engineering. I enjoyed the courses in engineering, I learned a lot. But one thing I noticed, again an example of my astute self-awareness, the courses I liked best were in physics. And I remember one of those singular moments in life, walking across the campus, talking to a friend from high school, Dale Loveridge. He asked, “How are you doing?” And I said, “Well, okay, but I’m sorry that I’m running out of physics courses to take.” And Dale said, “Why don’t you transfer to physics?” I assure you that had not occurred to me. So, I transferred. It was wonderful. I got along well with the students in engineering. We played a lot of card games, particularly hearts. I switched to physics, and we played bridge. But I remember wonderful hours spent debating mathematics and physics. I loved the courses. And, to my great good fortune, there was on the faculty at the University of Manitoba, Ken Standing, who had been a graduate student at Princeton University, in nuclear physics. He came back to Manitoba. He was ten years my senior and was just starting a wonderful career in precision measurements of masses of biophysical molecules. You know, these are data that biophysicists, and big pharma, really treasure.
Ken made quite a career of these valuable precision measurements. He also loved going to his cottage in eastern Manitoba, where you enter the Canadian Shield, a wonderful country of old mountains glacially ground down to smooth bumps and holes and bumps. Land about fifty percent water fifty percent in bumps and holes. Beautiful country. So, Ken had a good life. I managed actually to see him one last time just a few years before he died in his nineties. Anyway, Ken decided that I should go to Princeton for graduate study. Again, I hadn’t thought of graduate study. I was still a dopey kid.
Jim, did you take GR as an undergraduate?
No, none of that stuff (laughter). Ken wrote the appropriate letters, he pointed out the forms I should sign, and then, well, off Alison and I went off the states. When I arrived, there were two other graduate students from the University of Manitoba already at Princeton. That made three of us from one small university in Canada. How did that happen? To my deep, deep regret, I never thought to ask Ken. He must have (laughter)- he must have systematically sent students to Princeton.
Jim, what year did you arrive at Princeton?
Do you remember specifically if Sputnik really impacted things?
No, I don’t. I certainly remember Sputnik; it was all in the news. There was a later period of intense growth in physics triggered by Sputnik, but I think that happened near the end of my graduate study, when I was looking for a next position. There were lots opening up.
I remember a joke that used to go around. There was a scotch called Grant’s, and an advertisement, “While you’re up, get me a Grant’s.” And the phrase going around was, “While you’re up, get me a grant.” There was actually a very good system of funding for research in Dicke’s style. Industry and the military were very impressed with what came out of the Second World War, and they were anxious to learn about what oddball new ideas might come out of curiosity-driven physics. The many military branches were glad to provide funding for research in physics. Bob Dicke had research grants from the Signal Corps, ordinance, and the U.S. Office of Naval Research. Where was I? What did you ask me? (laughter)
Jim, when you got to Princeton, how well-
-formed was your identity in terms of the kind of physics that you wanted to pursue? First of all, did you know it was going to be theory at that point, or were you open to experimentation?
I had not given it much thought.
So, you were wide open?
Well, no, that’s not right. I had thought I would be a theorist. In fact, I had vague notions that I would be a particle theorist.
Of course. I mean, that was the big subject at that point.
Well, no, not really. The current algebra symmetries and all that were in the future. The big thing when I was a graduate student was dispersion relations. That’s still an important subject in particle physics, and in nuclear physics, but not particularly central. It was a low point actually in particle physics. That was one barrier to my going in that direction.
The other barrier was that I’m not well suited to particle physics. I mentioned that there were two other graduate students from Manitoba there. One was Bob Pollock. We were friends already at Manitoba. Bob, a brilliant experimentalist, later went off to Indiana and started building accelerators. He and his wife, Jean, who also is a Manitoban, and Alison and I were good friends while they were here, and then we visited back and forth when they moved to Indiana. Alison still often talks by telephone with Jean. I mention that because soon after I arrived, I was approached by Donald Hamilton, one of the professors of physics, who wanted to know whether I was another Bob Pollock and, if so, would I like to join his atomic beams group? It took a very short discussion to establish that “No, no, I’m not another Pollock.” And Donald and I parted as friends. It’s pretty clear that I was meant to be a theorist.
Jim, when you say that particle physics was at a low point at this time, is this a universal assertion, or are you saying this is specific to Princeton? In other words, would the same have been said at a place like Harvard?
I think so, but don’t know. What would they have been doing at Harvard? You remember QED had been well established. For the strong interaction you couldn’t use the same perturbative techniques, at least you didn’t think you could. Of course, you can, but you didn’t think so. There were the seeds of current algebra when I was a graduate student, but I think Gell-Mann was in the future.
Anyway, I said that it was clear that I’m not an experimentalist. It’s also clear that I’m not a theorist of the sort who would do particle theory, if there were a theory that’s interesting. But I had another stroke of excellent fortune. The other graduate student from Manitoba, Bob Moore, was working with Bob Dicke in his research group. Bob Moore said, “Why don’t you join me in one of his group meetings?” I did. And I discovered very quickly that this is the sort of physics I enjoy doing.
What were your initial impressions of Bob Dicke when you first met him?
Well, deeply impressed by the breadth of his knowledge of physics. Also, he was a very amiable person. He talked to the lowest of graduate students and the most senior of faculty in the same way. Full of ideas, and the ideas were elegant. So, an impressive person, but impressive in a very approachable way.
Was he working on anything in particular at that moment, or he always had a very diverse research agenda?
Oh, very diverse research agenda, though almost entirely in gravity physics. I arrived in ’58, and I think he has started his gravity research group in 1957. He worked fast. By the time I got there, the group was already large and active. Earlier, he had been doing what we might call quantum optics. He always worked well with graduate students, but I think prior to gravity physics the groups were smaller, one or two graduate students doing interesting laboratory experiments. The gravity group formed quickly and got going rapidly. There were lots of interesting experiments going when I arrived.
I would say his main interest in 1958, when I arrived, was the Eötvös experiment to check that the gravitational acceleration of a test particles is independent of the nature of the particle. The experiment was nearing completion when I joined the group. From there his interest continued to grow broader. His main focus later on was the question: do we trust the test of general relativity from the motion of Mercury? In particular, might the sun have a quadruple mass distribution that could cause an anomaly in the orbit of Mercury that would vitiate the apparent success of general relativity in accounting for the observed excess perihelion motion over the Newtonian physics prediction. His style often was that of focusing on the one experiment while allowing his research group to do their own thing, and only intervening when he saw people flagging or needing to be knocked off dead center.
It is striking that he liked to let each of his group members work on their own. It was a very different scene from what happens in a large research group these days, where you have to be directed to the community goal. But, of course, the gravity group’s experiments were much smaller, with less need to be organized.
Jim, coming from Manitoba, a small school, relative to your cohort who were coming from mostly bigger schools, more prestigious schools, how well prepared were you? What kind of catch-up did you need?
Modern physics was not heavily emphasized at Manitoba. But, on the other side of the coin, classical physics was heavily emphasized. So, when I arrived, I was shocked at the things I didn’t know, for example, about quantum electrodynamics. I saw people at the blackboard drawing Feynman diagrams. What are those? So, I had to play catch-up on that. But I was well-prepared on the classical physics side, so I had an advantage there. And, of course, in research in gravity physics in those days, a lot of it was classical physics, and that stood me in very good stead.
Did you respond well to Dicke’s style as a mentor to be hands-off, to let his students come up with projects of their own?
Yes, I tend to like to work alone; his style fit me very well.
And so, what did you want to work on, given that this was wide open for you? What was available? What was exciting to you?
Well, you know, I’d have to look at some of those old papers. Certainly, Bob’s invitation to think about the possibility that the universe began hot led me to lots of thought. Of course, the notion that the universe is homogenous was, to me, apparently an assumption of desperation. How could we check on it? For example, X-ray sources were known. The X-ray sky was known to be quite isotropic. Why is that? Is it because the universe is homogenous?
Bob was very interested in the notion that the strength of the gravitational interaction may be a function of time. That’s still a very topical question because in supersymmetry and then in superstring theory, or whatever it’s called these days, there is no physical scale, so you have to assume that the constants are nailed down by some unknown stabilizing effect, but you’re invited to imagine that the scale is not perfectly nailed down and that the physical constants of nature are evolving. There’s still no evidence of it. But in Bob’s day, that was an awfully attractive looking idea. He was very much taken with the point Dirac had made, and Eddington earlier, that the strength of the gravitational interaction, the form is down by some forty orders of magnitude from the strength of electromagnetism. Why that enormous difference?
Bob felt it could only mean- and, of course, he was not the first- that the strength of gravity has been weakening as the universe evolved. He wrote a lot of papers on that, and I was involved in quite a few of them. The evolution of the strength of the gravitational interaction would have interesting empirical effects. For example, it would mean that meteorites were moving around a hotter sun earlier on. The higher temperature of the meteorites would affect them. For example, potassium forty decays to argon forty, and the accumulation of argon since a meteorite was assembled gives a measure of its age. But if meteorites were hotter in the past, they would have lost argon more readily, a noble gas, by diffusion out of the meteorite. We wrote a paper on that.
I have a fond memory of the decay of rhenium-187 to osmium-187, at a very slow rate because the energy levels are almost exactly equal; there just barely enough energy to produce an electron and neutrino to decay from one to the other. If the strength of the electromagnetic interaction were evolving with the strength of gravity then in the past the energy difference between those two isotopes would be different, and the decay rate would be slower or faster, could even have reversed. And so, measurements of the history of decay of rhenium to osmium through their daughter products in meteorites was very interesting. I did flirt with the notion of an experimental thesis to get a better measurement of that decay energy.
Anyway, it’s the sort of thing I enjoyed doing. I got to read up on meteorites, and techniques for dating them, and for the measurements of isotope abundances, and the analysis of decay products, and work out what this might mean about the history these meteorites. It’s the sort of thing I enjoy.
Jim, was your sense that general relativity beyond Bob was a trendy field at this point?
Oh, no, quite the opposite. It was considered a dead field.
First, of course, from the experimental point of view of it’s very hard to do measurements in gravity because gravity is so weak. On the theoretical side, well, general relativity resists application to quantum mechanics, and so the theorists were saying, “Well, of course we’ll focus on the strongly interacting and weakly interacting particles because we know how to compute”- or at least they were learning. How do you compute quantum mechanics in general relativity? There were brave attempts, and I remember quite a few theorists passing through and lecturing on how to do it. Feynman was big on this, but he never got very far. By and large, the feeling was that gravitation is a dead subject.
Jim, was there anything happening at the Institute that was relevant for you? Would you go to seminars there, or was that really sort of outside of your orbit?
I went to them at the Institute for Advanced Study with Bob and other members of his group, and we had good conversations. For example, when Bob invited me to think about a Hot Big Bang, I hit upon the idea of light element formation. I’d no idea that George Gamow worked out so much of this, and so brilliantly, a decade earlier. But I remember realizing that in a Hot Big Bang it would be natural that there would be a considerable abundance of helium left over from the early universe. Maybe thirty percent of the mass would be helium; most of the rest hydrogen.
At the Institute, Bengt Strömgren was a true expert in astronomy. I remember a long talk with him about the cosmic helium abundance. Martin Schwarzschild was in the astronomy department at the university, but he too often went to the institute. I remember talking to him about helium. Both of them were polite and informative, but would not give me a simple answer to my question, could there be a lot of helium? I think both were pretty clearly thinking, “You’re going to have to read the literature and decide on that on your own. Make your own decision.” Anyway, yes, it was a place where we went, in fact, weekly, for lunch meeting. We exchanged views on what’s happening in physics and in astrophysics in particular. At the time, until John Bahcall arrived, Bengt Strömgren was the only astronomer at the Institute. John changed that, oh, in the early 1970s.
Jim, what was the process for you developing a thesis topic?
Well, I remarked on the measurements of the decay energy of rhenium-187. I came up with plans for how to do it. I remember the day I showed Bob my plans. He examined them with a glum look on his face and said. “Yeah, this is true. “You should consider staying a theorist.” How did he know? But he was absolutely right (laughter). My PhD thesis was on the possibility that the fine-structure constant, the strength of the electromagnetic interaction, might be evolving. I made up a little theory that was viable in which the fine-structure constant evolves. I looked into a lot of data on the empirical implications of an evolving fine-structure constant, largely its effect on radioactive decay rates. I don’t know who proposed that thesis, but it began with Dicke’s suggestion that I think about the possibility of evolution of the fine-structure constant. It was not as a PhD project at first, simply as a little paper to write. So, I produced studies, and the studies led me to other studies, and the project grew into a PhD.
Jim, what were some of the relevant experiments when you talk about the data, or observations that really informed the theories that went into your dissertation?
The Princeton Eötvös experiments told us that I would have to be very careful about coupling material fields to some other field that could cause an evolution of the fine-structure constant. But that was about it.
Other gravity group experiments were inspiring in the sense that they asked interesting questions by elegant methods. I’ll give you an example. One is interested in comparing the active and passive gravitational mass of a body to the inertial mass and the equivalence of mass and annihilation energy. The active mass determines how strongly this mass gravitationally attracts other objects. And the passive mass determines strongly the object is pulled on by other sources of gravity. The two are the same in general relativity theory, and you run into odd conundrums if they’re not the same. But, still, do the experiment.
So, Bob had a graduate student fill a large vat of fluid whose mass density could be very finely adjusted, by addition of salts, to agree with the mass density of a sphere with a different composition. The sphere in the fluid neither sank nor floated if the passive mass of the sphere is the same as the passive mass of the displaced fluid. So now place a Cavendish balance at one end of the tank and check its response to moving the sphere in the fluid toward and away from the balance. The Cavendish balance would be disturbed if active and passive masses differed. No one ever imagined they would differ, but let’s try it. It was a beautiful experiment, with elegant feedback techniques to control the balance and the fluid density. I came away from such experiences with a very well-developed appreciation of experimental checks of ideas. But they didn’t lead me to any particular idea.
Jim, who was on your thesis committee, besides Bob?
Tom Carver, John Wheeler, and there might have been one more I can’t bring it to mind. John Wheeler had far greater faith in general relativity than Bob Dicke did, and John’s opinion of my thesis pretty clearly was, “I don’t know why you’re going to all this trouble, but it’s alright with me.” Tom Carver was a condensed matter physicist, experimentalist and theorist. He was more sympathetic. He agreed that people should be asking these questions. You know, by and large, I had the impression that among the senior faculty the feeling was that it’s good I was looking into these issues, and Bob Dicke was looking into these issues, but that it was better you than me.
There was skepticism, but this is worth doing.
To go back to that sociology question, when you’re thinking about your next moves, you’re doing cosmology, you’re Bob Dicke’s student, how out there was your thesis topic in terms of the kinds of postdocs, the kinds of faculty positions that you can apply to, how the relevant people in the field might take you seriously or not? How much did you think about these things?
Not a lot. I mentioned earlier that this was a time not long after Sputnik when military and industry were very impressed by the products of physics,and wanted to have physicists around so that they might get hints to the great new ideas that are coming out of physics. So, government and industry were glad to fund research in physics at the modest levels we needed. There were not a lot of worries about finding a postdoc position supported by a research grant. Would my concentration on gravity physics have harmed me in finding a new position? I think not, because of this relative freedom of funding, which we should bear in mind was not big money.
-but it was there, the opportunity. I don’t think that my choice of research field had gave me cause to worry about whether I could find another position- in fact, I think quite the opposite. I never sought another position, but I got offers, at least two, on the table. And I had the feeling I’d get more if I wanted them. Fortunately, Bob said, “Why don’t you stick around and become a postdoc here at Princeton, and keep doing what you’re doing?” And, well, I never left.
Do you wonder what would’ve happened if you did, given the fact that you’ve been at Princeton all these years?
Yes, I do and, of course, I have no idea (laughter). A lot would’ve depended on when I moved. If after my PhD I left directly, I would’ve done something different in physics, and it’s hard to believe the outcome could’ve been as happy as it was by my staying at Princeton.
Was Dicke’s encouragement for you to stay, do you think it was- was he specifically looking forward to stay with you as a collaborator, or he just didn’t want to lose you?
I think both. I didn’t collaborate a lot with Bob once I’d got my PhD. But I didn’t collaborate a lot with anyone. As I say, I tend to like to work alone, and in those days that was quite appropriate in the subject of gravity physics and cosmology.
It was small enough where you could work alone?
Yes, it was indeed. Why Bob want me to stay? Well, Bob liked to see active people, and I was that. With me, he persuaded David Wilkinson to stay. David arrived as a postdoc, and then he stayed on first as a junior faculty member at about the same time I did. And, again, although David Wilkinson did write a few papers with Bob, they more or less worked independently, and that’s the way David- and Bob- liked it.
It was his style.
-what new projects did you take on as a postdoc?
Of course, many of them were continuation of the research on cosmology. I also did a lot of other things. For example, I’ve always been interested, since I was a graduate student, in galaxies, how they formed, how they evolved, what they might tell us about the nature of the universe. That was a time when infrared astronomy was just getting going. I was very interested in how infrared astronomy could aid explorations of the natures of galaxies.
Who was driving infrared astronomy at that point?
Not Princeton, although Bob of course had interest in it, and we had discussions of it. But, again, a name I can’t drag from my memory. I can’t even remember where the experts were based, but not at Princeton. I could look up some papers, but I’ve lost memory now. It was early days-
What was the promise of infrared astronomy? What could it do that it wasn’t able to do before?
Most directly, if you want to look at a galaxy that is very far away, it’s at high redshift, so you have to go to the infrared. And that certainly interested me a lot. Then, of course, there’s the question of whether galaxies are strong sources of microwave radiation. Will they get in the way of measuring the radiation from the early universe? But I think my main fascination was to see what young galaxies look like. And to do that, you’re going to have to go to the infrared because of the redshift.
The integrated amount of infrared radiation is interesting too because, for one thing, I was very interested in the mass density in baryons because that plays a role in the production of helium in the early universe. Given the temperature now, the higher the present baryon density, the more complete the conversion of neutrons and protons through deuterons to helium. On the other hand, if the mass density in baryons is low, you’ll leave more deuterons. That’s a very interesting difference.
So, I was interested in the baryon density. And one handle on the baryon density in those days was the integrated light from the galaxies. We needed luminosities of galaxies, but, you know, galaxies don’t have well-defined edges; their surface brightness just trails off with increasing distance from the center of the galaxy A related question: could there be considerable baryon mass in stars outside galaxies? A handle on all this is the integrated light from all of the galaxies.
So, I spent a lot of time looking into literature on- and looking into methods of determining- the surface brightness of the sky due to the integrated light from the galaxies. It would be redshifted toward the red. We even had graduate students devising experiments to measure the integrated light of the sky. How bright is the sky after you take out the galaxies? Turns out it’s not too bright. The galaxies don’t have sharp outer edges, but most of the light is coming from the parts you can see. But we didn’t know that in those days, and it certainly was interesting to find out.
When did you understand the importance of radio astronomy?
Oh, well, again, that was from the start of the cosmology I knew. Remember, I was nervous about the assumption of homogeneity. When I began there already were sky maps of radio sources, the extragalactic radio sources, and their counts as a function of flux density. The counts were heavily sought after as a test of Steady State theory. But more interesting to me was the maps of the distribution of radio galaxies across a good part of the sky. The distribution is quite smooth, which was one of the first indications I knew for homogeneity. I wasn’t aware that Hubble had done something similar with optical images back in the thirties. I learned that later.
But certainly, if you’re looking for microwave radiation from the Big Bang, then you have to worry about microwave radiation from the galaxies. I spent a lot of time looking up catalogs of extragalactic radio sources detectable at longer wavelengths and summing to get mean sky surface brightness-es. I extrapolated that to the microwave and was comforted to see that you’d expect this to be a factor of ten or more below the radiation from the Big Bang, so that was comforting.
Later, people objected that perhaps the radiation we were interpreting as being from the Big Bang was actually thermalized by dust at lower redshifts. If so, it removes the evidence that the universe expanded from an early dense optically thick state. An important test was that you would not expect high redshift radio sources to be observed if the dust in front of them were optically thick at these wavelengths. If the dust is optically thin, it’s not going to produce non-thermal radiation. So, I was very interested- we all were, in radio sources as probes of what’s in intergalactic space. The properties of radio galaxies are fascinating, but I never got much into that more than their use as a tool for understanding some properties of the universe.
Jim, were your cir- the circumstances leading to you joining the faculty at Princeton, were they as simple as when Bob asked you to say on as a postdoc?
Yes, as simple as that. Of course, it can’t have been simple in the senior faculty meeting. I know that, for sure, John Wheeler, a wonderful person, and very friendly, but he did wonder why we were continuing to question Einstein’s general relativity. But I also remember that John did get very excited about the idea of radiation from the early universe. That was while I was still a postdoc. And so, I don’t imagine the decision to admit me to the faculty as a junior faculty member was very controversial.
What was your sense of the culture of promoting junior faculty at that point?
Oh, well, the Princeton tradition was pretty clear: you don’t promote former graduate students to the faculty without allowing them to go off to other places for a few years. It’s a sound principle, I think, in general. Go away, do something else, discover what you really want to do with the rest of your career in physics. That was a pretty strongly enforced rule that wasn’t invoked in my case. I don’t know why. I never paused to think about it in those days. It just happened.
How parochial was your world, your physics world, by the time you became a faculty member? In other words, were you aware of what was going on at other top-flight universities? Were you going to all the conferences, meeting people across the field?
I certainly traveled a lot to give lectures and colloquia and attend meetings. People were interested in this radiation. And even before that, people did like to hear about what was going on in Bob Dicke’s group. So, from early stages as a graduate student, I got to meet a lot of people at other universities and learn what was going on there. So, I don’t feel that that I and our group were at all parochial. We were parochial in a sense of unusual research interests, but our research interests were well advertised.
Did you take on graduate students right away as a junior faculty member?
Yes, I did. My first one, Jer Yu, came to me. I guess it is part of my character that I didn’t actively solicit graduate students. Bob Dicke did. He created his research group by actively recruiting. I have never actively recruited. People come to me.
Not your style?
Not my style. And, you know, I formed the opinion that graduate students at Princeton, and I suppose as a general rule, talk to each other about what’s happening that’s interesting. When I had an interesting project, students would come around.
Jim, what classes did you teach when you first joined the faculty?
Oh, what did I start with? Thermodynamics for undergraduates. I taught that quite a few times. Physics of fluids, quantum mechanics many times. The hardest courses for me were the introductory ones. A more advanced course, well, you’re preaching to the choir, to be blunt.
But the introductory courses, well, you’ve got to be more skilled (laughter). They’re a lot more work. I certainly enjoyed teaching, and I learned a lot. I think it must be the rule. You learn a lot when you teach because you have to ask yourself all these questions that you fear might be coming from your students and you consider odd situations that perhaps hadn’t occurred to you earlier. So, teaching for me was valuable.
Jim, what were the most intensive years leading to the prediction of the cosmic microwave background radiation?
In what sense intense?
Like, this was the top of your research, this is what you were working on mostly.
But you know, prior to detection, this search for radiation from the early universe was a highly speculative endeavor; no guarantee that radiation would be present. I had assumed that, well, I’ll spend maybe a year on this, and then I’ll do something more interesting. It wasn’t intense. It became a little more intense after identification of the radiation, but even then, not very intense because I asked myself, what are the odds that this radiation actually is from the early universe, not from something local?
It was pointed out to me recently that in the first book I wrote- 1970 or ’71- I of course discussed the radiation at considerable length. But in the end, I wrote, “What are the odds that this is actually radiation from the early universe?” And I listed the pros and the cons. I wasn’t at all convinced that it’s real. During that time, you know, I don’t ever remember a feeling of intense concern about such things as, “Am I on the right track? Are other people beating us in some way?” For the most part, there was just day-to-day interesting research.
When the radiation- when the CMB radiation was predicted, what new questions could now be investigated as a result?
Well, I mentioned helium. The other big issue is what effect does this radiation have on the formation of galaxies? Pretty early on, I realized that in the early universe, when the baryons were thermally ionized, baryons and radiation would interact strongly with each other. That had some important consequences. It meant that prior to decoupling, at redshift about 1,000, when the temperature had dropped to 3,000 K, matter and radiation- of course, I didn’t know about dark matter then- matter in radiation would have acted as a fluid with high pressure from the radiation, meaning that gravity would not be capable of gathering matter, baryons, the plasma into clumps, the galaxies.
So, right off the bat, we had a very interesting result, a definite epoch at which structure could start to grow, after decoupling from the radiation. Furthermore, of course, during the early ages when plasma and radiation were acting as a fluid, any slight inhomogeneity in their distribution would oscillate as acoustic waves. Working out the effects of decoupling of those acoustic waves on the residual distributions of matter and radiation after decoupling became a topic well worth exploring. Earlier on, tidying up the theory of light element formation was very interesting, and the recognition that the amount of deuterium is an interesting measure of the baryon density- lots of aspects to consider.
Jim, you said earlier that dark energy, the term “dark energy” was a bit of a PR coup because it was a new name for an extant concept.
Was the same true at all for dark matter?
No, I think not. We needed a name. I didn’t give it the name “dark matter.” I don’t think I ever gave it a name. It was a new concept, that came from particle physics. In those days, the muon and its neutrino were just being discovered.
There was a lot of interest among particle theorists in non-baryonic matter, mostly focusing on neutrinos. Could the electron neutrino have a mass? A rest mass of about thirty eV would be very interesting for the mass density it would contribute. Or maybe there is a fourth neutrino family, with an interesting rest mass. So, there were ideas floating around about the notion of non-baryonic matter. I took them up and put them into cosmology.
In cosmology, there was no precedent for this. I don’t know that anyone prior to the introduction of dark matter gave thought to the possibility that the mass in the universe could have a form that doesn’t interact with matter and radiation. It was new, so there wasn’t a prior name. It was of course highly speculative. As I mentioned, I was a little unnerved and nervous about how popular the idea became. But it turned out to be productive.
Was there any notion some sixty years later than dark matter would still be fundamentally mysterious?
(Laughter) I didn’t worry about that. I did worry about the possibility that the idea would go away. But it also is striking to me that the first attempts at detection of dark matter began, by Bernard Sadoulet and others, when the idea was new and quite speculative.
The dark matter search began so early on. Why would someone mount a serious campaign to detect a wholly hypothetical particle? Well, it’s human nature, and Bernard is to be deeply respected for taking on this task that has lasted now for, oh, what, a half a century?
Approaching it, at least forty years, I think, from the eighties to now.
Jim, you mentioned already the value of particle physics at this point, which is very different, of course, than when you were a graduate student when it was a low point. Another sociological story, of course, and this comes later on, is the influx of particle theorists into cosmology. When-?
When did you sense that that trend started, and what were some of the advances in particle theory that may have precipitated this migration, if you will?
Yeah, I would have to consult old records to be sure. But I do remember very well Steven Weinberg taking quite an interest in this subject. He had been interested in cosmology well before the radiation. He wrote that elegant book, The First Three Minutes. He worked on the challenge of describing the physics of the plasma-radiation fluid that would have been present prior to decoupling. He had the disadvantage that he didn’t know the phenomenology. So, his work on the behavior of the matter-radiation fluid was good, but it didn’t carry us through to measurements of predictions of the patterns in the distributions of matter and radiation that we’ve since observed.
Other people: Sid Bludman from the University of Pennsylvania wrote an interesting paper. He was a particle theorist. There were others, but I can’t bring them to mind. But, yes, particle theorists saw that we were doing interesting things that were really not all that complicated. Why not try doing it yourself? So, yeah, people did.
Who were people who made a permanent transfer from particle theory to cosmology? Well, Dick Bond is a good example. He wasn’t in particle theory exactly, he was making supernovae, but he was interested in particle theory and its connection to the dark matter problem, which was new when he was a graduate student. He made a total transfer to cosmology. I’m sure there are other examples I can’t think of offhand.
Jim, while we’re in the chronological neighborhood of the late ’60s and early ’70s, were you aware at the earliest levels of what people like John Schwarz and Michael Greene and Veneziano were doing? Were you paying attention to the earliest iterations of string theory?
No, I was not. I do remember that these ideas might suggest that at high temperature there would be a flood of new particles, and that if there is a flood of particles, it’ll mean that the temperature can’t rise much going back in time because as the temperature rises it just creates more particles. So, the very early universe would not be as hot as we thought.
I remember concerns, does that mean that perhaps at the time of light element production, we might have overestimated the temperature? That was something interesting. Yes, I was impressed by Veneziano and Schwarz. But by the time that became popular, it was also pretty far removed from my work in cosmology. So, I admired it from a distance. Of course, there was the group of four here at Princeton who did good work, now dispersed.
On the social side of things at this time, in what ways did the campus unrest of the late 1960s and early 1970s affect you?
Well, it was distressing, I must say. An odd- an uncomfortable situation. Classes disrupted by students marching in with demands. At that time my research was supported in part by the US Office of Naval Research. And I remember pamphlets, “What is Peebles doing with the Navy? Is he conspiring to build “weapons of mass destruction?” (laughter) You know, those military grants were really remarkably informal. They requested that you tell them what you’re doing with the money. You didn’t enter a proposal. You just asked for money, you did something, and you told them about it. I remember one reviewer visiting Princeton, saying, “A lot of these people don’t bother telling us what they’re doing with the money.” I sympathized, and we tried to be careful to tell them what we were doing. But, well, you remember the Mansfield Amendment?
It was well-meaning but, boy, it really- the military support of pure research was so smooth and simple, and, of course, its effect on the military budget runs off the decimal places on your calculator, it’s so miniscule. I regret that change in style. But, of course, the style in physics has evolved to the point where bigger money is needed for many purposes.
Jim, with the backdrop of the civil rights movement, the women’s liberation movement, what is your earliest memory in faculty meetings at Princeton that it was important for the department as a whole- students, faculty- to diversify? Famously- of course, Princeton famously didn’t have a women’s bathroom for a very long time. When were the earliest discussions?
(Laughter) Yeah, so, when I arrived in ’58, there were no women on the faculty. There were no women students.
But awareness of that problem grew. At first, women were admitted to graduate study, and then to the undergraduate program- a great improvement. The students in the days when we were all male were a pretty restless group, and there were pretty ugly scenes on weekends. So, the faculty- we went coed when? I can’t remember the time. I don’t remember any faculty discussion of it. Was that because I was still a postdoc? I can’t tell you. I do remember though lots of later anxiety in the faculty about the absence of women on the faculty, and students, or later the scarcity of them, and of course the absence of Blacks, Latinos. There was a time, I think it was in the 1970s, when I kept a list of women who we might be able to persuade to joint our faculty. A woman with a reputation for good work in physics was highly sought after. Glennys Farrar was one of our first graduate students. She, as you know, is by no means a backward person. She knows her rights, and she’ll establish them, and don’t get on my toes. It took that sort of personality to survive here as a woman. People of color, it’s an embarrassment, we don’t have them. But Princeton has made progress. Going coed was such a no-brainer.
Yeah, yeah, meaning that it wasn’t just good politically, it was good for the science?
Well, it was certainly good for the students. Going coed made mixing of the two sexes so much more regular instead of this discontinuous jump on the weekends when, you know, women were bussed into party- an ugly scene. As for the science, well, I don’t know how the science would’ve gone if we’d had more women. I think the education, the teaching, would’ve been a little more gentle with more women. But would the research have profited? I don’t know.
Yeah. Back to the science, Jim, what were some of the major advances in cosmic structure formation that allowed the theory to really advance in the 1970s?
Well, in the 1970s, we had at most crude ideas about how galaxies formed. We had ideas about how we could learn more, for example, by observing galaxies at great distance when they would’ve been younger. So, that was a topic we talked a lot about. I remember a paper with Bruce Partridge, Are young galaxies visible? early on.
We proposed that you might be able to find young galaxies by looking for a strong emission line, the Lyman-alpha line of hydrogen. Galaxies at high redshift, if they’re full of plasma, would be making that recombination line. And the Lyman-alpha line is in the ultraviolet, but at a redshift of three it would be observed in the optical, so go find it. And, in fact, people at Princeton did try. Detection of this emission line is now routine, but it was one of the things we fussed about a lot in the ’70s. I mentioned the integrated light from the galaxies. We tried to find that. Well, things opened up with the introduction of cold dark matter because, suddenly, numerical simulations became feasible. If most of the mass is in cold dark matter, then a simulation could make pretty good steps forward by ignoring the baryons. We recall that a galaxy mass of baryons is a complex situation. It’s going to dissipate strongly, and collapse to stars. The stars are going to explode, and dump energy into the plasma—a real tangled mess. But if most of the mass of the galaxy is not baryonic, but this cold dark matter, then the evolution of the mass distribution is a lot simpler to model. You just follow numerically the paths of individual little particles and move them only under gravity.
I worked a lot on these simulations in the very early days, and Ed Groth and I made pretty good progress, but because I tend not to be a collaborator, I- have no regrets- I never got into big-time computation. That began in Harvard with Mark Davis, who had been a graduate student here at Princeton, and I had worked with him then. He saw the science that could be done by numerical simulations of the cold dark matter alone into making a first approximation to galaxies. That has become big science, and rightly so.
You first follow the dark matter. Then you put in the baryons. You have models for star formation, and the effects stellar formation, winds, explosions on the rest of the baryons. Very complicated, but you can model it in approximations. Very educational. So, yeah, early days, I was interested in numerical simulations, but I started losing interest as it became obvious that this is a lot harder than I’d anticipated.
Jim, would you say that your work with Jerry Ostriker was an exception to the rule of your normal preference to work alone?
Well, that was just two of us. I could handle that.
What did you initially work on with Jerry?
Oh, well, Jerry had worked on stars. He had examined the stability of a rotating star, and he had noticed that if the star rotates too rapidly, it’s going to fragment, won’t hold together. And he asked me whether that is be true of a galaxy. They rotate pretty fast. Why don’t they fall apart?
As it happened, I had been on sabbatical leave at Berkeley. On the way back home, we stopped at Los Alamos National Laboratory for a couple of months. It was kind of weird. I was in those days an immigrant alien, yet they let me into that laboratory. Would that happen today?
Probably not (laughter).
Probably not. They had computers, the best available. I was asked, “What would you like to do while you’re here?” “Well,” I thought, “I’ve been hearing about this missing mass problem in the Coma Cluster. Why don’t I model the motion of the galaxies as they form a cluster like the Coma Cluster?” So, I did some numerical simulations while I was there.
This was in the flavor of modern simulations of galaxy formation, except far more modest. I remember returning and giving a colloquium on that work. And Jerry Ostriker, whether he was in the audience or just heard about it, approached me, saying, “Could you do such simulations on a rotating galaxy to check the idea I have that rotating galaxies should be unstable?” We found it to be so. And to remedy the situation we postulated that most of the mass of a disk galaxy is in what is now termed a dark matter halo. This often is the way research developed in my career. Jerry heard about what I was doing. He saw an application. He approached me. We talked a bit, and we did it.
Jim, what did it feel like when you were named a fellow of the Royal Society in 1982?
Oh, it was fun. You know, that society is quite a few years old. When I signed the register, I was shown the first page, and there was Isaac Newton, Samuel Pepys and many other famous figures. It’s rather a rigid organization. I was firmly instructed that a failure to pay dues could result in having my name scratched off the register.
I signed it. It was vellum, signed with Indian ink, and you could scratch a name off. And [laugh] that would be my punishment if I didn’t pay dues. So different from the Philosophical Society of the United States. That’s an old organization too, but far more informal.
Jim, what were some of the-
-key advances in the seventies and eighties in observation? What telescopes were most interesting to you, for example, land-based and space-based?
Well, of course, IRAS was very important- the Infrared Astronomical Satellite. I even remember Mike Hauser was one of the pioneers in that satellite. He had worked with me on statistical analysis of the distributions of galaxies. In the seventies, one of my biggest research interests was simply measuring statistics of the distribution of galaxies, distributions and motions. I think I mentioned earlier it’s work that Euclid is going to do with exquisite precision. In those days, it was a small operation. But Mike- he was an excellent person, and certainly- now, where were we? What did you ask me? My mind has wandered off.
About telescopes, observational advances with telescopes, seventies and eighties.
Oh, yes. Okay. So, I loved to do statistical analyses. And I loved to know about the infrared luminosities of galaxies, so I was fascinated by the IRAS satellite. It turned out to be wonderfully productive because it detected lots of galaxies that had made lots of stars recently, and a lot of stars make a lot of dust, and that dust made these galaxies bright in the far infrared-I think they used twenty to sixty microns.
Wonderfully productive to have that data on large sections of the sky- in fact, the whole sky, apart from the Zone of Avoidance. That was a beautiful experiment. It’s the kind I like too because it was not a general purpose instrument. There was one experiment to be done: make a catalog of infrared sources. One project, one purpose, so do it, and now you have a treasure-trove of data you can analyze. I loved that.
Well, the Hubble Space Telescope, I remember the furor when it was discovered that the focus was set wrong (laughter). You know, my inclination to work alone certainly was influenced by Bob Dicke, who used to lecture us about the hazards of working in a large group, where necessarily no one person knows everything about the project. It’s a dangerous situation. I remember my good friend and colleague, Ed Groth, decided to join the Hubble Space Telescope collaboration, and I remember Bob shaking his finger at him and saying, “You better be careful. That group will be fragmented, and you’ll not know what all the pieces are doing.” It worked out well in the end, of course.
What other telescopes? Well, you know, radio galaxies, we mentioned earlier, many radio galaxies are at great distance, and their structures give you some indication about how galaxies formed. I was very interested in following early detections of distant radio sources also detected, optical or near infrared. In those days, the hints were that galaxies at high redshift were highly irregular fragments, blobs. That indication has largely gone away, because when you marginally detect a galaxy in optical or infrared the first thing you pick up is a few high spots, brighter spots. And it gave you the notion of great chaos in the structure of the galaxy. It was misleading. But, never mind, that’s part of the game. I certainly was fascinated by those blobs.
I never did any explicit research on it. I followed it with interest and wonder. What is this going to tell us? But, certainly, I was very interested in how galaxies formed, and I thought that was carrying good hints to the way they did form.
Through the seventies, as I said, my main interest on which I spent a lot of time was the statistical analyses of catalogs of extragalactic objects. It was the sort of situation I enjoy. No one else was doing it. That’s an exaggeration. A few people were, but essentially no one. So, I just plugged away.
Jim, how closely were you involved or paying attention to the rapid developments in inflation in the early 1980s-
-and all of the disagreements, the back and forth within the inflation community?
A beautiful idea. Everyone agreed with that from the start. I asked myself, “Should I be involved?” I came with the answer, “No, I shouldn’t.”
Was your first exposure reading Alan Guth’s paper?
It was a colloquium he gave at Princeton early on. I remember Ed Witten being very impressed, so I should be impressed. It was neat, exciting. But, no, from the first, I thought, “What are the predictions that would tell us that this is the way things really happened?” It was emphasized that inflation would explain the large-scale homogeneity of the universe. Maybe, but that idea’s no longer so strongly defended. It would explain why the universe has no space curvature. Well, okay, but we didn’t know that the universe had no space curvature in those days. So, it was, to me, interesting research that I didn’t hunger to get into- so, I didn’t.
To go back to your earlier interactions with Rai Weiss when he was at Princeton, when-
-did you first get the sense at MIT that he was really on to something special, that he wasn’t just tinkering by himself up there, and that exciting things were really happening?
Do you know there was a New Yorker magazine article on an academic with a sweater with leather patches and holes? Gave a talk to some group about how you could maybe detect gravitational waves. That was Rai Weiss early on. That may be the first that I became aware- oh, no, I must’ve known earlier. It was clear from the time he was at Princeton that this is a very capable person, and you paid attention to what he was doing. He also was doing early work on microwave radiation, and in fact he produced Lyman Page, who’s now here and a leading figure. But I think I was somehow aware all along that he was interested in detection of gravitational waves.
I remember spending a few months at Caltech, early eighties. There was on the Caltech campus a prototype gravitational wave detector- much smaller than the big ones of course but operating. And I remember standing near it and jumping down so that I hit the floor on the ground outside. And the detector responded. I did that because I remembered so well Bob Dicke’s caution about how important it would be to isolate the detector from ground noise. That had been sort of conditioned in me, and it was so fascinating to see the reality of that effect. So, I knew that things were getting serious. I was not following closely the progress the LIGO gravity wave detection program. I do remember the strong reaction from the astronomical community that I consider an aspect of sociology, the reaction to the name of the project, LIGO, because the O is for Observatory.
Right, that’s the controversy.
Oh, yes. I mean, what a thing to say to an astronomer. “I’m building an observatory for gravitational waves” (laughter). What? For that kind of money, well, you could have a spectacular optical observatory.
Jim, to go back to how you took cues from Ed Witten, were you paying at all attention to his excitement over the so-called superstring revolution in the mid-eighties?
Well, of course, I was very aware of it and- of the excitement. Many of the important actors besides Witten were in the neighborhood. So, yeah, I certainly knew about it. I never considered getting into that research. It’s just not my style.
And what about AdS/CFT? Did you pay attention to that, what Juan Maldacena was doing?
No. Again, I heard a lot about it. I remember elegant colloquia. But I didn’t hunger to get into it.
You know, there are many directions to go in science.
Of course, of course.
And I felt I had found my niche.
Which was not overly mathematical. You were always rooted in observation?
That’s right, not overly mathematical; just mathematical enough to get on with the job.
What were some-
And, of course, always phenomenology.
What were some of the developments that allowed you to propose the primordial isocurvature baryon model in the mid/late eighties?
The motivation strictly was to show people that they shouldn’t be so strongly committed to dark matter. I just put PIB together as a counterexample to the need for the dark matter hypothesis.
Does it remain a competing theory to dark matter?
Oh, no. It was definitely killed when the CMB anisotropy spectrum was established.
It would be about 1998 or 1999. I remember I was making my latest version of an elegant viable theory without dark matter. I showed Lyman Page my predicted CMB anisotropy spectrum. I remember him smiling, saying nothing. Shortly after that I had the first news of detection of that peak in the anisotropy spectrum. It was a European experiment. And, wow, it looks like there’s a bump where I’d expect a dip. My elaborate theory was dead.
I didn’t regret it. I mean, it’s all part of the game. Yeah, that was an exciting moment, though, because the detection of that bump gave me reason to think that there might be something in my old dark matter postulate.
Is it possible that any of this could get resurrected once we understand what dark matter is?
It’s really dead? (laughter)
Well, I should be more careful. You know, the community opinion these days is that LambdaCDM is it. I’ve heard people- serious people, say that we know the physics, and we know the initial conditions for cosmology. That would mean that the challenge now is to compute the consequences for such things as galaxy formation. That’s good science, but not perfect science, because we don’t really know the initial conditions, and we really don’t know the physics all that well. We know good approximations to both. But these days, I can think of quite a few odd hints in the phenomenology that seem to call for a better theory than LambdaCDM. I’m hoping these hints will suggest something new. I’m hoping the world is more interesting than largely cold dark matter and a cosmological constant with a really weird value. Surely, the universe is more interesting than this.
Jim, when did you first become aware of COBE, and when did you realize that it would be such a foundational project?
Well, of course, COBE was largely built at Princeton down in the machine shop, so I saw that activity. I was aware of it from the early days. Debates on how best to build it, I remember, “Do you have one antenna that swings around or do you have two?” Such discussions. When did I know that it was going to be a revolutionary advance? Well, that was when David Wilkinson showed me the first CMB intensity spectrum, showing that this radiation is very close to thermal.
What did you see in it?
Wow, tangible evidence that this is radiation from the early universe.
Which tells you what?
That the universe did evolve. It’s a simple enough thing to say that the universe evolved from a very different state- hot dense and uniform. To say that is easy. But to demonstrate it, well, that’s really something. That the universe is not forever, I think that was wonderful- I still do.
Yeah, that’s right.
So, that was a memorable moment. You understand that an experiment must not release preliminary data. You can’t even tell your best friend; leaks just release confusion. The COBE project was very good about ensuring that that rule was obeyed.
I remember the day David took me aside, pulled out a sheet of paper as if he was showing me [laugh] a dirty photograph, but showed me the intensity spectrum they hadn’t yet released. It was a moving moment, I remember.
There were other great advances from COBE. I was excited about the infrared measurements by the experiment DIRBE led by Mike Hauser and others, because as I mentioned, in the early days I was very interested in the infrared background as a measure of what galaxies had been doing.
The detection of the anisotropy of the CMB by the DMR experiment on COBE, by George Smoot and colleagues, was exciting, though I didn’t know how much to make of it. It was fine that it was at the level I had predicted a decade earlier when I introduced cold dark matter. Whether these measurements really had the slope of the spectrum right, I couldn’t judge. So, I thought, well, that’s interesting. But I didn’t have quite the same leap of faith that I did with the intensity spectrum.
My leap of faith for the CMB anisotropy measurements came with the detection of that bump in the anisotropy measurement in the late 1990s. Let’s see. The Smoot et al detection was ’92, I believe. And by 1998 the measurements had improved a lot, and were starting to look, wow, like CDM. That was the big moment for me.
Did you see WMAP as a perfect ongoing project to COBE, or where there things that were unique about it that would’ve been there absent COBE?
Well, we should be careful. Absent COBE, and then WMAP, there were lots of ground-based and balloon measurements that were mapping out the anisotropy spectrum. COBE made the measurements more precise, and WMAP still better. But without WMAP we still would have a pretty good anisotropy spectrum, and so we’d be in pretty good shape for the cosmological tests.
But, of course, WMAP made the measurement so much more precise, which made the constraints on cosmological parameters so tight that there was a really good case not only that the universe evolves but that the evolution is pretty well approximated by Einstein’s general theory of relativity. That was a deeply impressive result in the years around 2000. And, of course, the case has only grown more convincing as the precision has increased since then.
We touched on this earlier, but specifically what around this time compelled you to go emeritus?
Well, I think I mentioned, number one, I detest committees. Number two, I looked at all the courses I’d taught and profited from so much. But did I want to teach them again? Number three, well, we had pretty good savings. We could afford it. And number four, I was pretty sure I could keep my office, and keep doing what I love doing.
Jim, I can’t help but think of the metaphor to go back to an earlier comment you made about how advanced cosmology is, and how, at this point in the field, it’s really worth going back and making sure that no stone is left unturned. Right?
Yes, oh, yes.
How have you defined those unturned stones? How have you looked back over this massive body of research that you’ve been a part of to really decide this is something that we should look at further?
Yes. You know, there are different aspects to this wish to leave no stone unturned. There are old lines of thought that have not been followed up, and there are lines of thought that had never been considered. We agree that I’m a very empirical type person. I like something tangible. And I am most interested not in old ideas but in old observations.
You can find lots of them. They’re hazardous, because you can never tell whether an odd-looking observation is odd just because, well, the chips must fall in some way by accident, and that’s the way they fell, and the way they fell may have no significance. I think I mentioned I’m writing an article now about odd phenomenology that might be worth following up, at the hazard of considering odd situations that are just the accidents of how the chips fell.
I’ll mention an example that continues to fascinate me. In our neighborhood, the galaxy distribution is very clumpy, but most of the galaxies are in a sheet, a fat, irregular sheet, known as the local supercluster. Right above the local supercluster is an empty region with just one exception, just one dwarf galaxy. It’s very striking. How did this region, the Local Void, remain so free of objects?
There’s a theory- there’s always a theory that accounts for it, but it’s not a theory I trust. And the numerical simulations of how cosmic structure formed don’t show such empty voids. So, why aren’t we looking more carefully to see what else might be in this Local Void? There is, as I say, one dwarf galaxy. It’s surrounded by a cloud of atomic hydrogen that is detected by the 21-cm emission line. The stars are observable in the old southern sky survey photographic plates. But have people looked hard enough for other little things in this Local Void, smaller clumps of hydrogen that could be detected if you look more carefully?
I might mention that the 21-cm line this one dwarf galaxy in the Local Void was detected by the H I Parkes All Sky Survey, HIPASS. This survey spent seven or eight minutes on each picture element. What if you spent an hour on each picture element? What would you find? I really am captivated by that question. And if instead of using photographic plates you surveyed the sky with high-efficiency detectors, and you looked for a long time, what would you see?
We’ll find out what MeerKAT detects. That’s one of these square-kilometer array projects in Western Australia. I gather there will be an array of 21-centimeter detectors that will be surveying this area. I would love to know what they find.
If you had to guess, what might it be?
Little clouds of hydrogen. Now, you know, it’s fun. If this one dwarf in the Local Void really lived an isolated life, why does it have a peculiar property, that the elongation of the hydrogen is tilted from the elongated distribution of the stars? It doesn’t look like an equilibrium situation, as if it had been disturbed by something. But what disturbed it? Who knows? So, find other objects in there, and see whether they also are odd looking, maybe a consequent of their environment. Which would be curious: so isolated but yet odd? Wouldn’t it be fun to know? It’s the sort of thing I love because it’s accessible to an observation—a hard one, but feasible.
Jim, tell me about John Kormendy at the University of Texas, his work, and why it’s so interesting to you.
You have in mind the pure-disk galaxies.
He instructed me on them. I have become enamored of the phenomenon, that many of the nearby large galaxies, including the Milky Way, are almost pure disks of stars, like a pancake or discus. That’s in contrast to numerical simulations that almost inevitably contain a bulge of stars in the center. These bulges are present in some nearby spirals, but far from all. It’s fascinating to see a difference between the best simulations that can be done at the present state of the art, and what’s observed. Again, I see a sociological phenomenon, that the people who do these simulations are not overly concerned about pure disk galaxies. This is in part because they’re able to point to large surveys of galaxies that turn up lots of bulges. But as Kormendy sensibly explains to me, “You don’t trust those surveys because they scan each galaxy briefly.” They produce precise statistical measures of schematic observations. Tin short, the galaxy bulges that they see are not necessarily real. The presence of pure-disk galaxies is well established only for relatively nearby galaxies where there is lots of spatial resolution to observe the phenomenon. So, you might imagine, right, that we live in a weird neighborhood. But that’s kind of a dangerous thought.
The computations of galaxy formation are improving, and with that the unwanted bulges in simulations may go away. But they haven’t so far. And so, I think Kormendy has pointed to something interesting. A difference between theory and observation is, to me, always exciting because it means we might learn something. Maybe what we learn is that a systematic error has crept into the theory or the observations. But maybe what you learn is that we get to add new physics to the Standard Model.
Jim, to what extent are your more recent interests in isolated galaxies and nearby galaxies intertwined, and to what extent are they separate projects?
Well, they’re both part of the same curiosity of what’s out there. I don’t know that there’s any unity beyond that; it’s to be seen. I would add that isolated dwarfs are fascinating too, particularly those that are in close to empty regions but close enough for detection of their individual stars. And I wonder, “Did they ever interact with another galaxy, or have they been isolated since formation at high redshift?” If they’ve been isolated, then a few things follow. First, they had to have grown the way they are by themselves, rather than through interactions with other galaxies. That’s interesting, and fascinating to me is the fact that if they haven’t interacted strongly with massive galaxies, then their past histories of motion are simple.
They’re moving through the gravitational field of massive objects that are pretty far away. So, the gravitational field through which they’re moving has to be reasonably simple. And if so, can you compute the paths that these guys followed through spacetime from the early universe?
You can’t just integrate the path back in time from measured present positions and motions, because the numerical integration is unstable. You’ll almost certainly find that the solution to the equation of motion has the galaxy moving at ridiculously high speed at high redshift. You have to solve the equation of motion with mixed boundary conditions. I developed a method for doing this; it’s come to be known as the numerical action method, NAM. It works pretty well, and it offers an immediate check. If you start with a measured present position the mixed boundary condition returns the present redshift, which you can compare to the measured value. It works out pretty well.
I must admit that I like the fact that no one apart from a few colleagues is using this approach, so I can work on it at leisure (laughter).
And, yeah, I’m impressed by how good the results look. I’d love to redo that analysis with better data. There are projects going forward to discover more of these isolated dwarf galaxies, and to improve measurements of their distances- that’s the hard part- and apply this technique to still bigger samples. When you consider the progress from discoveries on the Sky Survey photographic plates to ongoing surveys with modern detectors, what will be found?
What will MeerKAT turn up? Lots of stuff, I hope. And I hope to see enough of it that I can try again to analyze that data.
Jim, what were your emotions when LIGO announced the detection?
Oh, joy, wow, a wonderful check of general relativity. You have seen that I’m a rather conservative and cautious person. I used to feel very uneasy about the extrapolation of general relativity theory to the scales of cosmology. I’m just still so amazed that you can extrapolate a gravity theory that passes pretty demanding tests on a scale of the solar system to the vast scales of cosmology.
Consider the numbers: solar system, ten to the power thirteen centimeters; cosmology, ten to the power twenty-eight centimeters. Fifteen orders of magnitude in length extrapolation, and it works? Yes, pretty well. That’s astounding. It’s really just so impressive.
You know, although I respect the research into alternative gravity theories, it’s not something I’m going to get into because general relativity has survived enormous extrapolation pretty well, and is it likely to fail just as you get to cosmology? Well, maybe.
But to return to your question: here is general relativity applied to the detection of those gravitational waves, a very new situation, and again giving sensible results. You understand that much of the application of general relativity on the scales of cosmology involves, first, a solution to Einstein’s general theory- field equation for a homogeneous universe, and then, second, perturbative adjustments from homogeneity. We rely a lot on those perturbative computations. It’s great to have them because perturbation theory works very well here. But you’re not demanding a lot out of general relativity. The merging of massive systems-be it black holes or neutron stars—and the production of gravitational waves, is asking a lot more of general relativity. The fact that the application works so well is impressive, it reinforces the feeling that general relativity is a remarkably durable theory. The other thing to celebrate of course was that an old friend did so very well, and that science marches on.
It’s always joyful to see.
That’s right. Jim is your approach to the, you know, leaving no stone unturned, these are smaller- it’s small-scale work. But do you remain hopeful that it’s possible that one of these advances might yield something really big, really fundamental, the kinds of things that have been out of reach for as long as you’ve been involved in your career, just for one of many examples, you know, merging quantum mechanics and general relativity?
Right. Right. You never know, do you? An example is an odd pattern in the distribution nearby of ordinary galaxies, of clusters of galaxies and of quasars. I mentioned early on that we live on the local flat sheet of galaxies. Peter Shaver and Brent Tully pointed out quite a long time ago that if you extend that plane that we see nearby, relatively speaking, by a factor of 10, most of the bright radio sources are close to that plane, whereas most of the galaxies are not. I checked it. Where are the nearest rich clusters of galaxies? Out to eight-five megaparsecs, the sixteen rich clusters are all pretty close to this same plane, while the massive star-forming galaxies detected by the IRAS survey in the infrared are not concentrated toward the plane. Their distribution is close to isotropic at this distance.
Why are the clusters concentrated toward the plane and star-forming galaxies not? A horrible accident? Maybe. But then the radio sources, quasars, also are concentrated toward the plane, and they’re not in the clusters. Well, some are, but many are not. Another horrible accident? Maybe, or maybe, you know, if you think of time in logarithmic scales, then there is a large span of time between the end of inflation, or whatever happened back then, and synthesis of the light isotopes; a lot of time in which, in our present theory, nothing happened.
Oh, well, there were the particle physics phase transitions, but nothing big. But could there have been something big? You mentioned earlier ideas that have been put aside. One of them is cosmic strings and cosmic walls, domain walls. There’s no evidence of them. But what if domain walls or cosmic strings were running around back then in the early universe where there’s a lot of logarithmic time? And what if they made wrinkles in spacetime- not uniformly random wrinkles but, here and there, a track cut by a wandering cosmic string? I am thinking of the pioneers who left wagon trails across the west, leaving the rest of the land undisturbed. What if the early universe was more or less undisturbed, except for here and there where there’s a rut? And what would those ruts do? Would they encourage the growth of concentrations of galaxies in certain directions, as in clusters of galaxies? Or the formation of quasars? I don’t know. But, well, it could be. That cosmic string would be a quantum particle physics phenomenon. It would be a wonderful connection. How are we ever going to make such a connection real? I have no idea. But here’s a charming phenomenon that is not in our philosophy, so as to speak, but could be added, and wouldn’t that be wonderful?
Jim, after having spent so much time on the origins of the universe, have you ever found it fruitful to consider what’s known as cosmic eschatology, how the universe ends, when it ends, or even with if it ends?
No. In fact, I- well, you know, the simple point is that studying the future is a lot harder than studying the past. Yogi Berra, right?
“Predictions are difficult, particularly about the future.”
That’s right (laughter).
That’s a wise remark. What I love about studying the past is that the past left fossils. The future doesn’t [laugh], unless we have some breakdown of causality, and if the future doesn’t leave fossils then so I find it much less interesting.
And does that suggest a sort an- a sort of philosophy toward the ability to extrapolate scientifically?
Yes, extrapolations are wonderful, but I’m always nervous about them.
So, to extrapolate our present situation into the future is always- well, you’ve got to be cautious. Whereas extrapolating back, well, you have to be cautious, but you can explore implications of what could have happened, and you can test that extrapolation. So, indeed, lots of people love to speculate on how the world will end. And God bless them go speculate. But I just- it leaves me cold.
Jim, I’ve been very privileged to have interviewed most if not nearly most of the living Nobel Prize winners in physics. And there’s a constant theme that crops up in these discussions, and that is the sense of a buzz; that there is a buzz surrounding- that this is going to be the year when this person gets awarded the Nobel Prize.
What’s common with all of them, and which is perhaps unique for you, is that all of the other Nobel Prizewinners- correct me if I’m wrong but their citation, the prize motivation is rather specific: asymptotic freedom, for example, LIGO, right?
Whereas yours, if you just look at the wording of the prize motivation for theoretical discoveries in physical cosmology, do you tend to think of it more as a—as the ultimate lifetime achievement award?
We shouldn’t use those words. The Nobel Committee does not give lifetime achievement awards. But consider Hans Bethe. I guess you might not have been around long enough to interview him.
But that was a lifetime achievement award. No, but we don’t use those words. We never say the Nobel Prize is a lifetime achievement award. But I would remark on your word “buzz”.
I mean, the question is, did you feel buzz, given the fact that the citation apparently was not connected to any particular project you worked on?
Yes, I did feel a buzz, and part of it was curious. Are you aware that the university has publicists who attempt to keep track of what’s interesting that might concern the university, and appropriately deal with it? Also, are you aware that there are betting sites on the web where you can place a bet- a monetary bet, on almost anything happening? In particular, you can bet on who will be awarded the Nobel Prize in physics. My wife has tried to get to that site and failed. I think you have to know someone.
Anyway, the publicity department at Princeton University follows that site because, you know, the payoff depends on the amount of money placed on a bet. And so, if the payoff drops on the speculation about the Nobel Prizewinner, you know that a lot of people are betting that that will be the award. In the years previous to the award, I on two years got an enigmatic message from the publicity department, at about the time of the Nobel announcement: “if you need help with publicity, we are always willing to come to your aid.”
That’s all that was said. And, somehow, there was another buzz, I felt prepared for this. Somehow, I thought, well, alright, this seemed like the right time. It was a feeling in the air. So, when I received the announcement, I was not startled. It seemed right. Let’s face it, I think they made a good choice.
(Laughter) Where were you when you got the call?
Oh, well, I don’t know if this is a standard practice, but the phone call came at 5 o’clock in the morning, a convenient time in Stockholm. Anyway, an aspect of that call strikes me. At five o’clock, I stumble over to the phone. “Are you Professor Phillip James Edwin Peebles?” And I said, “Yes” (laughter). “We have voted to award you the Nobel Prize in physics. Do you accept?” Was this the result of the Bob Dylan fiasco? I don’t know. But, once I said, “Yes, I accept,” the conversation grew more relaxed. I’ve received a lot of other major prizes. Only one other major award was nearly as formal. “Do you accept?”
Which one was that?
The Canada Prize. I’m Canadian, as well as naturalized American, and that was gratifying. They also wanted a fast and explicit acceptance. No offense taken, of course. But other prizes could be as casual as a- in one case, a telegram; in others, a friendly phone call. Very different levels of formality in these different prizes.
If the nomenclature “lifetime achievement award” is not appropriate, what meaning do you make? Do—how do you understand what exactly it is that you’re being recognized for?
We will not use the words “lifetime achievement” but I’ve achieved quite a bit (laughter).
You certainly have. You certainly have.
And, so, it seems appropriate.
Jim, of course, you know the Nobel Prize offers winners a platform, a voice, to talk about all kinds of things well beyond their area of expertise. How-
-if at all, have you chosen to use that platform?
I appreciate the presumption that I know something about, oh, COVID-19. But I don’t. So, I don’t like to sign petitions urging the government to do this or that about COVID. I have opinions, but they’re not anything special. Some Nobel Prizes in physics have gone to people who have decided that, well, I must be an expert in everything. I really am uneasy about that, and I don’t feel any such symptoms. I was told by one of the committee members, “Your life will be different now.” And, indeed, it’s true. Suddenly- suddenly, I’m a godlike figure. I hope you get that aura. No, I’m not a godlike figure. And I am deluged by requests for all kinds of things, most of which I politely refuse. So, yeah, my life has been somewhat disturbed.
And as a hardnosed scientist, I bet to some extent this is bothersome to you because it gets in the way of the science.
Yes, it does, and, also, it’s just wrong. I’m not a godlike figure (laughter) and, well, I love physics but there are lots of parts of it that I don’t understand, and it frustrates me. I wish people wouldn’t assume I know everything.
To talk about a platform that is one that’s specifically scientific that’s unrivaled, that is the opportunity to give a Nobel lecture. What were your motivations? What did you want to do in this address, given the fact that it’s going out to a much wider audience-
-than people who are normally aware of your work?
I didn’t want to do it. I knew I had to. My motivation was, well, they probably wouldn’t give me the prize if I didn’t do it (laughter), so I did it. I give lots of lectures, and, through my career, I’ve lectured to universities, to private audiences, to amateur astronomy clubs, to the general public, time and time again. I think I do it reasonably well. But I don’t really enjoy it totally. Maybe this is a slight hint of autism, that I like to just sit and think and write. So, giving the Nobel lecture, well, I’ve given lectures of that sort time and time and time again. I’ll do it. I didn’t give thought, as I probably should, to the message I am sending out to the world at large.
I remember an illustration of this during the Nobel Week, a week filled with activities. We were treated like royalty: autograph lines, police-escorted caravans of cars roaring through Stockholm, my wife and I in our own vehicle with our own driver and guide. And during the Nobel Week we Nobel Laureates were gathered to have a videotaped discussion. And in that discussion, we got to talking about global warming.
I deeply admire Will Happer but disagree with his reading of the anthropogenic effects on the climate. But what got my goat in this videotaped conference was the confident assertion by others of what is going to happen to the climate. The situation is so complicated. In particular, you know, the major greenhouse gas is water vapor. Without the presence of water vapor, Earth would be frozen. Now, we’re disturbing that major greenhouse gas- which is scary, not only by the addition of methane and carbon dioxide, but by the dust we raise affects where the clouds are. And the clouds have a big effect on climate because they reflect heat coming in from above and they reflect heat coming up from below. And we don’t even understand how clouds form. We don’t know the effect on the clouds of the dust that we kick up in vast quantities by our transportation.
In short, we can’t predict with any confidence what we’re doing to the climate. We’re making a really dangerous experiment, but I wish people didn’t feel so sure that we knew what the outcome will be. I mention this because in this discussion people who were not experts on climate were asserting what’s going to happen. I tried very politely to draw attention to the fact that this is really a very uncertain situation. Well, I was uneasy enough that I resisted joining in on the statement that we know what’s going to happen. I think it’s a scary situation, but, well, predicting the future is difficult.
As you say, as you say. Jim, just to bring our narrative up to the present, what are you working on right now? What issues are most interesting to you?
Well, I’ve just finished a book on sociology and science, the title, On Reality: Lessons from Philosophy, Sociology, and Cosmology. So, cosmology is a rather special branch of science because it’s simple compared to, say, particle physics or condensed matter physics. The tests are simple. The results are pretty convincing. So, we have a good and pretty clear example of how a physical science grew and became convincingly established. And we can ask about the sociology of that growth.
I was, am, fascinated by a familiar effect in physical science. When a new idea arises, the odds are pretty good that someone else has already thought of it, independently. Sociologists term this the phenomenon of multiple discoveries in science. In 1922 the sociologists William Ogburn and Dorothy Thomas published a list of 148 “duplicate independent inventions… collected from histories of astronomy, mathematics, chemistry, physics, electricity, physiology, biology, psychology and practical mechanical inventions.” I looked that up. And I am fascinated by the many examples of multiple independent ideas and discoveries to be seen in cosmology.
Though this a common phenomenon that sociologists know well I think physicists very seldom, if ever, pause to consider that this multiplicity, these independent discoveries, are telling us something about the way science is done. We can think of the obvious reasons for multiple discoveries. Technology makes some ideas timely. And when an idea is timely, it’s not surprising that more than one group will think of what to do with the technology. But also, we talk to each other. We communicate in many ways. I think maybe the feeling that I was going to get the Nobel Prize was communicated to me non-verbally—just a feeling in the air. And I think we do a lot of that indirect communication- hints, nudges, behavior, that conveys thoughts that pass from person to person until they reach someone who is prepared for whatever thought comes through.
So, my book has examples of multiples in the story of how cosmology grew. And then there is the notion of reality. You know, philosophers spend a lot of time wondering, “What is reality?” Interestingly enough, one hundred years ago, physicists were wondering about reality. Some were arguing that, well, reality surely is a social construction. Others felt it obvious that reality is reality. It’s realm there. But others asked themselves, “Why do we think there is an objective reality?” A remarkable person, Charles Peirce, a century ago, made important contributions to philosophy. And Peirce argued that reality is demonstrated by the ability of theories to predict phenomena outside the range of evidence that was used to construct the theory. This predictability is something we celebrate, but I think not as much as we should. It is what you would expect if our theories were reasonable approximations to the way reality operates. And if it’s a good enough good approximation, then you can extrapolate the theory to different circumstances and there’s a good chance you’ll successfully predict the way the situation is.
There were lots of such examples back a century ago, back when Einstein was thinking about such things. There are lots of examples today. And, again, I think the demonstration of reality by the power of predictions is not widely appreciated in the physical science community.
I argue that predictability means there is an objective reality, and that it operates by rules we can hope to discover. That idea was around one hundred years ago. I seldom encounter it expressed, and I think it’s something that should be more broadly appreciated. So, my book has just gone off to the press, and, now, as I said, I’m writing a paper on odd ideas and odd phenomenon that aren’t getting the attention maybe they deserve in cosmology.
Jim, for the last part of our talk, I’d like to ask a few broadly retrospective questions about your career and observations, and then we’ll end-
-we’ll end unfortunately. I can’t help but ask you to extrapolate to the best that you can about the future. So, the first is institutional. Your tenure at Princeton is, perhaps as a matter of chronology, it’s unrivaled, right? I mean, how many people at Princeton have been there as long as you?
Don’t know (laughter).
Yeah, it’s probably not many (laughter).
Probably not many. And, of course, I’ve been lucky enough to remain healthy for a long time.
So, although I am now emeritus, I still have an office, a connection to the department and university.
So, it’s a simple question, but perhaps it’ll be a complicated answer. For better and worse, how has the department of physics changed over the years?
For better: it hasn’t changed much. We still have the gravity research group. The department has been very generous in supporting this particular branch of physics. You understand that there are lots of active ines of research in our department, and each branch is eager to have more faculty hired in their specialty. So, how is it that we continue to prosper in gravity physics? Well, the department has decided that this is a pretty good field, so it’s worth the deep expenditure of faculty positions. It’s been great. I’m very grateful to the rest of our faculty for being generous enough to allow us to continue to prosper.
And this must really be a long-term legacy about Dicke in many ways?
It is, indeed. It is, indeed. You know, his ideas about the evolving strength of the gravitational interaction were much less welcomed then by the particle theorists than they have been now we have superstring theory, where evolution of that sort seems natural. In the late 1950s the department had Bob Dicke in gravity physics phenomenology, and John Wheeler in gravity physics theory. The faculty were a little doubtful about both. Isn’t gravity physics too hard to be done? And so why are we supporting Bob Dicke and John Wheeler?
Bob Dicke had the great advantage of being an experimentalist, and producing things that are useful, like precision gravimeters. He had broad enough impact that he had to be respected. And so, the department implicitly decided that, alright, we’ll go along with the physics, even though it doesn’t seem all that likely to be fruitful. Then it turned out to be very fruitful. John Wheeler’s experience was not so good. He was unable to get anyone tenured in his field of science, theoretical gravity. That was shortsighted. We now have someone, Frans Pretorius, in John Wheeler’s field, but it took a long time. That was not a good decision.
But, you know, the department had to decide whether to hire a brilliant young particle theorist, or a brilliant young general relativity theorist. And for much of the time until recently, too much of the faculty, particle physics looked more promising. That was not a mistake, but of course it was a sacrifice. The department has grown a little larger, but not much, we get along well, we support each other.
We’ve lost the graduate student general examinations. When I was a graduate student, and for many years after, graduate students in physics had to pass pretty demanding exams on basic physics and elements of the main branches of modern physics. You had to know a little nuclear physics, a little condensed matter physics, a little relativity physics, a little optics. I thought it was wonderful, and for many years I served often as chair of the committee setting the exam. I found it rewarding.
There was the growing problem with that exam that as biophysics became more and more important, we had students who really didn’t need to know all that basic physics to do biophysics. I bite my tongue when I say that, but I guess it’s true. Anyway, it’s notable that when I retired, the general exam was retired. We have now a qualifying exam that covers all the basic physics, the stuff that you better understand, mechanics, electromagnetism and so on. But I regret the loss of a broader examination, though I understand the need for it. How else has the department changed? Not much.
Jim, a hallmark of your career, and perhaps this goes back to the formative influence of Wheeler and Dicke, is your ease in moving in between both the theoretical and the experimental worlds, and-
-perhaps that’s the achievement that the Nobel Prize is thinking of, the body of work that’s so unique for you.
I haven’t asked the question yet. The question is this-
Oh, I’m agreeing anyway (laughter).
-when over your long career has the theory driven the experimentation, and when has the experimentation driven the theory, and what might we learn about this fascinating interrelationship that-
-tells us when the field grows in fits and starts, when it hits a wall, and when there are these fundamental advances?
You put it well. Research advances, ideas advance, in fits and starts, sometimes driven by a nice idea, sometimes driven by a new technology, sometimes driven by an unexpected discovery. In my career there’s been a lot of all three, in various combinations. Consider the presence of a near uniform sea of thermal radiation, and the unexpectedly large abundances of the lightest elements. Gamow predicted this a decade and more before these fossils from the early universe were recognized. Consider that when the variation of the temperature of the microwave radiation across the sky was measured with great precision it was seen to have the distinctive features produced by decoupling of the plasma-radiation fluid. That had been worked out a decade earlier. It was another prediction, in a sense, but not wholly a prediction because there were other ideas on the table. The observations singled out one of a set of ideas. But these are examples of progress by fits and starts.
I am impressed to consider that in the 1930 distant galaxies were seen to be moving away from us, that the universe expanding. The more distant the galaxy, the more rapidly the motion away. When I was 1 year old, Edwin Hubble and Milton Humason had detected galaxies so far away that they’re moving away from us at a tenth the speed of light. My goodness.
And getting from a tenth of the speed of light to the speed of light took some sixty-five years to get that last factor of ten. Fits and starts indeed.
Jim, last question, looking to the future, I know- I won’t ask you to extrapolate the science. But I wonder if you can extrapolate your feelings, right? With time as a precious resource, what’s mysterious to the universe that would give you the most intellectual, scientific, and even emotional satisfaction, that you could understand something that you don’t currently understand?
Well, you know, I might put it another way. What are the prospects that we’ll find something we don’t understand?
But that’s extrapolation.
I know (laughter). That’s what I’m hoping for.
There’s so much though. If you had to narrow it down?
Well, if I had to narrow it down to one discovery or one big issue, I would have to say that my favorite thought at the moment, and it could be different tomorrow, is the discovery of something that happened in that long interval of logarithmic time from the end of inflation, if that’s what happened, to the epoch light element production; some remnant of something interesting that happened and left a fossil clue to it. Interesting things are happening now. Why not then? It’s kind of circular to think that interesting things are happening only when they’re close enough that we can see them happening.
Of course, that’s where you’d look first (laughter).
But, surely, things are happening where you can’t see them happening.
Like dark matter, for example.
For example, and what about the very early universe? Was it really as tranquil as we say? It can’t be too different from tranquil or we’d have seen symptoms already. But maybe there were smaller disruptions from tranquility, oh, for example, that made the distribution of the baryons different from the dark matter. We have constraints on this, but they’re constraints based on simple models.
Let’s talk about another wonderful discovery. Maybe some of those distant galaxies are antimatter, not matter. Now, there are hazards in that because a good way to separate matter from antimatter is with a domain wall, and domain walls do serious gravitational things. But I’m sure a theorist could get around that. And if there were domain walls, they would be cutting ruts in spacetime, and I see hints of ruts. I mentioned it, the Tully-Shaver effect, the local supercluster and its extension. Wouldn’t a distant galaxy made of antimatter shake things up?
And why not? Well, the theory’s a little complicated. But, you know, we don’t understand why we have more baryons than antibaryons anyway, so a nice possibility.
Plenty to work on in the future.
We will carve this on my tombstone.
Not for a very long time, I hope (laughter). Jim, it’s been-
-it’s been an absolute pleasure spending this time with you. Thank you for allowing me to convince you to do this, and for the tremendous addition to the historical record, so thank you so much.
Well, thank you for being so persistent. I’ve been putting you off for months.