James Peebles Interview: Conversations with History; Institute of International Studies, UC Berkeley

A Cosmologist’s Intellectual Journey: Conversations with James E. Peebles, Professor Emeritus of Cosmology, Princeton University; October 12, 2006 by Harry Kreisler

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Research Leading to Current Knowledge

In the program for your lecture, it says, "Peebles laid the foundation for many modern cosmological investigations by predicting the existence of cosmic background radiation, popularizing the notion of dark matter in the universe." What does that mean?

With all due respect, it isn't quite right.

Okay. Let's correct the program right now.

This radiation, of course, was first understood before the Second World War by Richard Tolman at Caltech. After the war, my teacher, Bob Dickie, was the one who said, "What is this radiation? We ought to look for it." At that time, he persuaded two young guys to build the instrument along the lines he had invented during the war, to look for this radiation. We should just remind ourselves that it is radiation that fills space, that pretty unambiguously was produced when the universe was young, has all the properties of thermal radiation, and that it could only have acquired those properties when the universe was young and dense and hot. He said to me, "Go think about the theoretical considerations." That set my career.

Some of the considerations I invented were reinventions, others were new. So, yeah, I guess I can claim I did set the basis for this subject in many ways, but I certainly didn't start from scratch. No one ever does, let's face it. In particular, I was able to do this as a post-doc because the field of study of large scale structure of the universe in the 1960s was so small. There had been great interest in the subject in the thirties, but by the fifties and sixties interest had fallen away to the point that I, as a raw post-doc, had the field much to myself. I could do all of these interesting things.

I wrote the book that he mentioned in the late sixties -- I think it was published in '71. Lots of stuff in there, it was wonderful. I could do it all by myself. No one -- no competition. It's so different now. Of course, I don't regret [losing] the old days because the subject is so much richer, but it was an amazing opportunity for me to do all of this interesting stuff without looking over my shoulder.

But then as was said yesterday, you laid a foundation that even if you didn't get everything right, it became the benchmark for the development of exercises to prove that there was physical evidence for what you were saying.

Yes, that's true.

And these were, in a way -- to make our audience -- I think you used the term "fossils" -- this cosmic background radiation were like fossils for the people in your field.

Yes, that's right. Since the universe is not forever, it was different, it must have left evidence of that, and one fossil is this thermal radiation. I talked about lots of others in the book, and about lots of puzzles. For example, it was clear even then that there's something wrong with our reckoning of mass. I mentioned Zwicky and his mass anomalies. I, in the book, collected many of these. In part, I was simply collecting bits and pieces of evidence that some people knew but weren't realizing they ought to tell other people.

Methods of analysis of large-scale structure -- there were many things to be invented, so, well, what could I do? I invented them. Analysis of the degree to which the clustering exists and is evolving. The growth of mass clustering, of course, is key to our ideas about large-scale structure because we are forced into this notion that the galaxies are not forever, when the universe was young and dense and hot there weren't any [galaxies], and there weren't any stars, they grew through the action mainly of gravity. The analysis of how that would happen was certainly a large part of the book, and of course is now almost an industry.

Tell us a little about your feelings as you came upon these ideas or these discoveries for this particular publication. You've just suggested that a lot of this had come before, you were putting it together. It was an uncrowded field, people didn't see the importance of this, so you didn't have to worry about what the competitors were doing. I want a sense of the factors that made it possible for this to happen, on the one hand (you mentioned some), and what your feelings were as you were doing the work.

It occurs to me that I was a little nervous. You might ask yourself, "Why is no one else working on this subject?" There was a very good reason. Although we had bits and pieces of evidence, they were rather scanty. This was not a subject at the time that was strongly supported by observational evidence.

I do recall the feeling that many of my colleagues and my superiors, the tenured faculty, although they never discouraged me from working on this subject, I got the feeling that they were saying, "Better you than me." How do you know you'll make progress in these great ideas? How do you know you'll be able to explore the universe at such immense distances and make sense of it and be able to piece it together into a well-established theory?

I had no idea how far this subject would go when I was working on it in the sixties. In fact, to begin with, I think I remember correctly, I thought, "Well, I'll stick with this, write a couple of papers and then I'll do something that makes some sense." It really was very speculative. How far could things go? In fact, I know for sure that I shied away from studies of the fossil thermal radiation during the seventies because as it was being measured. The measurements were very difficult and the preliminary indications from those measurements was that this radiation didn't quite have the properties expected of it. So, I went off and studied the distribution of galaxies. It wasn't obvious at all to me that this subject would have grown as rich as it now has. Who could tell? Technology advances.

So, risk taking -- this is something that comes up with a lot of the scientists I interview, that you go out on an intellectual limb, I guess one would have to say.

How else are you going to do something new? And of course, the limb can always break.

With you on it!

I must admit, I don't think I was at all being brave. Maybe I was being oblivious. But also, in those times -- remember, this is not so long after the Second World War -- education was ramping up after the hiatus of the war. The fact that we were being hired -- although it's true, I wasn't offered any other job than at Princeton, somehow there was a feeling I could get a job if I needed it.

That's not so much the case anymore. It is a serious point of concern for a young scientist: "Am I going to be able to continue my career?" That's a real burden added onto all the other things you placed on the limb. "I'm on the limb, I'm doing good work, but the limb breaks because I can't find a job." That is a real concern that didn't occupy me, and although I don't think I ever thought about it, it was for good reason: there were jobs. Yes. But risk taking ...

You mentioned in your lecture a post-doc who committed early in his career to the development of the COBE [Cosmic Background Explorer] satellite. Talk a little about that, because that was crucial for providing the evidence for some of these theories that we've been talking about.

Yes. I mentioned during the seventies, the apparent evidence for anomalies that didn't make sense. It was obvious what could be done: build a satellite devoted to the measurement above the atmosphere where the observing is much clearer. There was a young post-doc, a student of Paul Richards here at Berkeley, a graduate student who learned a lot from Paul, then moved to the east coast -- this is John Mather -- and as a post-doc decided he would love to build the satellite that could do the job of studying this radiation above the atmosphere. As a post-doc he recruited the help of some of the major people in the field, my dear colleague David Wilkinson and a few others. They got together, proposed to NASA to build a satellite, the proposal was accepted, and Mather as a post-doc stepped into the position of lead scientist at NASA to direct the building of this thing.

It's a very difficult job. He has not only to understand the technology and the science but also to hold off all of the bureaucrats who want, for example, to take away engineers working on his project and put them onto some other satellite. He has a marvelous book, The Very First Light, in which he details the agony, as well as the ecstasy, of building such a thing, chapter after chapter of emergencies and who I turned to. Fifteen years of such work -- he is now approaching middle life and he has not a large record of academic accomplishments. All his eggs are in this one basket. He has the deep respect of a handful of people who know what's going on, but if that rocket had exploded on launch -- and it happens -- where's his career? A brave man.

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