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Interview of Jim Peebles by Alan Lightman on 1988 January 19, Niels Bohr Library & Archives, American Institute of Physics, College Park, MD USA, www.aip.org/history-programs/niels-bohr-library/oral-histories/33957
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The interview focuses primarily on Peebles' many contributions to physical cosmology: research on nucleosynthesis in the early universe in 1965, the theoretical and observational study of large scale structure formation in the 70s, and the development of the cold dark matter model and numerical simulations of structure formation, to mention the most prominent topics. Peebles describes his interactions with colleagues and other influences that shaped his research, as well as describing his own research style and the style of physicists he admires (notably that of his mentor, Bob Dicke). He discusses in detail his response to and assessment of various other topics in cosmology: the anthropic principle, different types of dark matter, dark energy, inflationary cosmology, MOND, various structure formation scenarios, and quantum gravity. We briefly discuss the institutional support and funding for cosmology and how that has changed over the course of Peebles' career. Peebles also describes several of the changes that have taken place in the practice of cosmology, from describing the introduction of numerical techniques and increased interaction in particle physics, to the increasing pace of research.
I wanted to start with your childhood and find out a little bit how you got interested in science, particularly, if you read anything or talked to any people who had a particular influence on you early on.
I've always been interested in mechanical things. I think I must have been heavily influenced by my father, who is also very good with his hands. He liked to build things. I always loved to watch him do it, and I loved to build things on my own. I was never exposed as a kid to any real science. I read the occasional popular science book, and I loved Mechanics Illustrated, which had a lot of pseudo-science in it: It wasn't until I got to college that I began to appreciate what physics is all about, and that was really an accident also. I started in engineering, where I think I could have happily remained and, who knows, made a bundle as a civil engineer or mechanical engineer. But more of my friends happened to be majoring in physics than engineering, so I switched over. No more compelling reason than that. But I then decided, once I was in physics, that it was great stuff and stuck there ever since.
When you were younger, before college, do you remember any particular books or authors that you read that had an impression on you?
No, not a one. As I say, I did read the occasional book on popular science, but they were never of any great depth. So, I can't say that I had any idea what science was all about before I got to college. In fact, I didn't know what engineering was all about before I went to college. I just wandered in. I came from a very small high school in which there was no guidance and not any appreciable amount of physics taught, nor much mathematics. So I didn't know what academia was all about until I got to college.
Did you build things when you were young?
I built things, yes, mechanical things. I built slingshots, electric motors, long yo-yo strings, that sort of thing.
Did you enter science fair projects?
Oh no, there was no such concept where I was situated.
You probably weren't thinking about cosmology at all, or even the universe at all, at that age then?
I had no idea what cosmology was.
Let me talk a little about your undergraduate education, when you did begin finding out what physics was. Can you tell me about that?
At that time, the University of Manitoba was quite strong in classical physics, but pretty weak in modern theory. So I came away from the University of Manitoba with a pretty good grounding [in what] I would need in astrophysics, in the sense that it was broad and strong on the classical parts, but weak on modern physics. I didn't know any relativistic quantum mechanics although I did know a fair amount of non-relativistic quantum [mechanics].
I don't think many undergraduates learn relativistic quantum mechanics.
I think they do these days. We hit them with a little of the Dirac equation and we certainly go further into non-relativistic quantum mechanics than I did. It was, as you can imagine, quite a shock to come from the University of Manitoba, as it was in the 1950s, to Princeton University — to come from being top dog in my class [and] getting all the honors to being totally bewildered and totally surrounded by all these people who knew so much more than I [did]. So that was a shock that lasted for maybe a year, until I managed to catch up and to find out what was going on in physics. Again, because Manitoba was not strong in modern physics, I didn't have a very clear idea what modern physics was all about or what the research possibilities were. That was something I had to learn when I came to Princeton. As is inevitable, my first interest was particle theory. It was the glamorous subject then as it is now, and I started working in that direction. Particularly, I was very inspired by some of the people here at the time. Murph Goldberger was doing his dispersion theory game at the time. He gave a brilliant series of lectures that I was totally overwhelmed by and totally grabbed by. So for some time I was dreaming of being a particle theorist. Many of us must go through that phase — it's so glamorous. But then I ran into Bob Dicke, who had a weekly evening meeting on his research on gravity physics. I dropped in on it mainly because I knew some of the people in the group — fellow graduate students — but I soon came to attend because of the subject, which is fascinating. In gravity physics then, as now, one had to look at many different subjects, from the structure of the planets to the structure of the galaxy to cosmology. That's where I first began to see a little of what cosmology is and to become very fascinated by it and also to become fascinated in general with gravity physics and all of the physics it brought in to research projects. So I deflected my interest [and] wrote a thesis with Bob Dicke on the possibility of variability in the fine structure constant, a topic that has come and gone so many times during the years. I placed empirical limits on how much alpha [the fine structure constant] could have varied through radioactive decay [and the ages] of meteorites. Then it was [when I was] a post-doc that he and I moved in the direction of cosmology as a way to do gravity physics.
Let's see, the Brans-Dicke theory I was around at this time.
The Brans-Dicke theory was around at that time, right. That's not something I ever worked on very much, although there was then, as you know, great interest in the possibility that the precession of the perihelion of Mercury might have been wrongly interpreted.
Part of the contribution to the precession [might] come from an oblate [flattened] sun. So I did spend a long time looking at solar physics and the constraints one might have in a differentially rotating sun. I guess you could say that was an introduction to cosmology, although it was all strictly local solar system physics that we were dealing with at that time. Bob Dicke had found cosmological solutions for his theory. I don't know how much attention he paid to them. I didn't think they were very exciting at the time because I didn't appreciate really the excitement of cosmology. It seemed to me, at the time, to be rather a limited subject — a subject, as it used to be advertised, with two or three numbers. A science with two or three numbers always seemed to me to be pretty dismal. [It was] a science with Hubble's constant, the deceleration parameter, and the density parameter. If that's all there were to cosmology, I wouldn't have found it very interesting.
And that's all that people were talking about at that time?
At the time, much of the subject was concentrating on that. Of course, there was the other great topic, which was the debate between the steady state theory and conventional big bang cosmology.
Can you tell me a little about your thoughts on that debate.
Well, mainly I was scandalized that there should be such intense debate over what seemed to me to be such a vacuous question. At the time, I found that, if anything, cosmology was not appealing because it based so much on an assumption that the universe is homogeneous, which seemed to me to be highly questionable. Of course, I hadn't looked into the observational basis for why one believed in homogeneity, which even then was not by any means insignificant. It seemed to me just unrealistic on the-face of it to think that you could make a theory of the universe. It seems to me still to be a reasonable first guess — how can you make a theory for the universe? I guess I remember first thinking that the assumption of homogeneity was unrealistic when I was preparing for general exams as a graduate student here — you know about the general exams that replaced course requirements. Among other things, you could anticipate that there might be a question in the relativity part on cosmology, and all sensible graduate students knew this and prepared themselves by learning about the standard solutions to Einstein's field equations for a homogeneous expanding universe. So I dutifully learned them, but I remember thinking to myself, "Boy, this is silly. Who could imagine the universe would be so simple?"
That's what you mean when you say that you can't imagine anybody making a theory of the universe?
Right. The universe surely is — I guess I would have said at the time if I had thought it through — a hierarchy of complexity. One could imagine making a theory of galaxies, a theory of clusters of galaxies, and so on, but to have a theory of the universe as a whole sounds to me more like a meta theory rather than physics as I know it.
And yet that's what Einstein himself did in 1917.
Yes, yes. In fact, I've often wondered how he could ever bring himself to make such a simple assumption, and I've wondered also why people like de Sitter let him get away with it. De Sitter was pretty cautious, in fact...
De Sitter argued a lot with him.
Right, on that point. Other sensible astronomers and many physicists quickly accepted his idea as the way it has to be. The universe has to be so simple that we can analyze it in a one-dimensional differential equation - everything a function of time alone. Of course, Einstein had brilliant intuition and he surely was awfully close to the truth — that's the way the universe looks.
So have you changed your view about whether it's silly to make theories of the universe?
I think it's amazing still, but I have to agree that it does make sense to make theories of the universe. They work so very well First, I think the observations pretty clearly show us that in the large-scale average — on scales comparable to the Hubble distance now — the universe is remarkably isotropic. And more indirectly, but I think; still pretty convincingly, the universe is remarkably close to homogeneous. So, if one should believe general relativity theory, you have it. The universe is simple. It's expanding in a computable way — which is an amazing thing. I never would have anticipated it could have worked out so easily, but there it is.
Do you think the observations between then and now have made you stop thinking that it's a silly idea to make these theories?
Yes. Remember at the time I wasn't aware of the observations. I could have known then that the faint radio sources are quite isotropically distributed — that was known. I guess that was the main observational datum that showed homogeneity in the large scale. There were the galaxy counts but they were always very questionable — still are –- because it's so hard to make the k-correction and to correct for local mass concentrations, the local galaxy concentrations. As you know, in the simplest model, you would expect the galaxy counts to vary as flux density to the -2/3 [power], apparent magnitude to the 0.6, isn't it? The [actual] plot of [the] logarithm [of the] galaxy counts against apparent magnitude is remarkably close to a straight line, but with the wrong slope, going all the way from the bright end to the faintest end, which one thinks is a conspiracy of two corrections: the k-correction of the faint end and the local concentration of galaxies in the local super cluster on the bright end. Given that fact, it's hard to argue that we have much evidence of homogeneity there. Isotropy, of course, is wildly improved in the last twenty to thirty years. But, as I say, even in the late 1950s I could have looked at the radio source counts and I could have been impressed at how isotropic they are, but I didn't know about them.
You mentioned that going to Dicke's evening meetings got you very interested in relativity theory. Do you remember when it was that you got interested in cosmology in particular?
Yes, I guess I can pretty definitely date that. This was the famous idea of Bob Dicke's to look for the microwave radiation left over from a hot big bang. I can't give you a year. I took no notes. He probably could tell you. It would be around 1964. It was in the summer, I do remember — a very hot day. We met in his usual evening group, but with a small number of people. I don't remember why, perhaps because it was the summer. For some reason, we met in the attic [in Palmer lab]. It was really ridiculously hot, I remember. He explained to us first why one might want to think that the universe was hot in its early phases. I don't know how widely this is described, [but] his thought at that time - and one that he does keep returning to — is that the universe might oscillate.
Yes, that's certainly described in the beginning of your paper in 1965. And an oscillating universe does require something to destroy heavy elements so one could start again with hydrogen. The way you destroy heavy elements is to thermally decompose them in blackbody radiation. So he explained to us then why you would like a universe that's filled with blackbody radiation. He explained to us how this blackbody radiation would remember its thermal spectrum as the universe expanded [and] would cool off. He explained to us that a good window for looking at this was around 3 centimeters wavelength, and in pretty short order, he had Dave Wilkinson and Peter Roll looking into the design of a radiometer to look for this radiation. I remember his off-handed but very inspiring remark to me, "Why don't you go think about the theoretical consequences?" — which is a sign, I guess, of a great physicist. You can throw off these remarks that can move mountains. And it certainly gave me an awful lot to think about.
That turned you on?
That turned me on. He and I wrote a paper, I think before the discovery of the microwave background, in which we expressed many of the theoretical ideas that had come up as a consequence of thinking about the microwave background. I guess that was my first paper in cosmology, and it was really a lot of fun to write it. We could see so many things to be done.
Was that 1964?
That would be about 1964.
Do you remember at that time, when you were just beginning to think about cosmology — and obviously you had taken relativity by then and you knew the relativistic background — having a preference for any particular cosmological model, say, open versus closed or homogeneous versus inhomogeneous?
I guess my reaction there was consistent with my initial reaction to cosmology as a subject. Again, I said, suppose someone told me whether the universe was open or closed. I think it would be a great let-down because what would I do with that knowledge? I've always assumed that we won't know whether the universe is closed or open until the information becomes, so to speak, irrelevant because it will have been enmeshed in a much larger picture in which it's obvious that the universe has to be the way it is on other, deeper grounds. So, I could never bring myself to get very excited about the question of open versus closed. It always seemed to me to be really a side issue. You'll find that in the book I wrote a few years afterwards, Physical Cosmology, I was very cautious about this question and didn't address it in any detail because it didn't seem to me to be very interesting. In fact, I think that's still the case. Now, with inflation, we have a reason, of course, to look for open versus closed, and within inflation suddenly this question becomes very dramatic and very compelling. So now, we can see that if we knew that the universe was not cosmologically flat, it would be of overwhelming interest because it would knock down a beautiful idea of inflation.
And bring back all the problems that it answered.
And bring back all the problems that inflation promised to answer. Which would also be fun, of course. It's always fun to have problems.
Did you give much credibility to the steady state universe at this time, in the mid-1960's?
No. I must confess I hadn't looked at it closely. I had heard a talk on the subject. In fact, I heard the talk while I was still an undergraduate. I remember being amazed that grown people could get excited about such speculative ideas. By the time the blackbody radiation came along, it became clear that if this radiation was found, then, of course, it had to be an expanding universe. Shortly thereafter, the radiation did seem to have been found so the steady state theory very quickly drifted away before I had a chance really to think about it long enough to decide whether or not it would have been a theory I would have fought for.
Let me ask you about the work on the microwave background which you had mentioned a minute ago. You mentioned that Dicke had talked about this problem in an evening seminar. Do you remember what your motivation was in thinking about this?
Well, as I say, it was very direct motivation from Bob Dicke — "You go think about this." [In response to] whether I found that an exciting challenge, yes, I certainly did. I could think of lots of physics to be done here. If you have radiation, you have radiation drag; you have thermal history so you can think about reaction rates; you can think of turning a plasma into atomic hydrogen, into molecular hydrogen; you can think of turning a gas of protons and neutrons into helium and so on. So that was fun because it was cross-sections, it was thermodynamics, it was something you could compute and .relate to observations. So I got very excited about it very quickly.
Did you buy [Dicke's] theoretical motivation for the whole thing, that is, the oscillating universe idea?
No. That was fine. I was willing to go along with it, but I couldn't get excited about the idea. I think it seemed to me then, as it does now, [to be] a possibility that we'd better pay attention to because it is an alternative to the standard lore now of inflation. And since inflation isn't all that firmly established, we'd better consider the alternatives, and that certainly is one of them that I would want to think about. But, in fact, I have never gone beyond that view — that it is an alternative and we better bear it in mind. I don't think I've ever written a paper exploring the possibilities of an oscillating universe. I have no idea how you invent physics that will make a universe oscillate and maintain its homogeneity — that's a real trick. It's an attractive idea, I must say. It's not as elegant as the inflationary picture, but I think it could be borne in mind.
One of the things I was curious about and the reason I was asking about this is because in your 1965 paper, you have the statement that if the universe is oscillating, then one does not have to worry about the initial determination of the matter to antimatter ratio at any finite time in the past. That's part of your reason for believing in the oscillating universe, which then leads to the prediction of the microwave background or the black body radiation.
I see. I wonder how clearly I was thinking when I wrote that. Of course, I don't remember all of my opinions from that long back. I think I'd recognized pretty quickly that one could not have a universe that oscillates indefinitely into the past because one would have an entropy catastrophe. You would imagine that you will make entropy on each phase of the oscillation, but [since] the universe now has a finite amount of entropy, then one knows that it could have had only a finite number of previous oscillations. I think I remember computing fairly early — but perhaps after the paper you've mentioned — that the universe could have oscillated 100 times up to the present, starting from dead cold and with the present content of baryons. That's the number of oscillations that would be required to turn the radiation from stars into the energy density of the radiation from the microwave background. Of course, one recognizes that if you have only 100 oscillations, that makes the universe exceedingly old indeed, but none the less a finite age.
You still have to worry about this initial...
You still have the initial condition problem, that's for sure. Light man: But maybe that kind of thinking about the entropy problem was after your thinking in 1964.
That could well be. Remember my thinking in 1964 was heavily conditioned on the thinking of the guy next door, Robert Henry Dicke. I think it is true to say that he was motivated by this thought that a universe that's oscillating at least pushes back the crisis of initial conditions from the standard big bang case — which is perhaps a step in the right direction.
I guess I'll have to ask him about that.
Yes, it will be fascinating to see what he says.
Let me ask you a little about the flatness problem that you posed with Dicke in 1979 in the Einstein Centenary volume, although I understand it had a history before that. That is a particularly interesting issue to me because Alan Guth claims that that was a key motivating factor in his development of the inflationary universe model. So, historically, the clarification of that problem, the articulation of it by you and Dicke had a very big effect. Can you tell me when it was that [the flatness] puzzle first occurred to you?
Again, to be honest, it didn't occur to me. It occurred to Bob Dicke. You know it's hard to remember when you learned to tie your shoes, and it's hard for me to remember when I didn't know and believe that as a good argument. I think Bob Dicke must have been presenting it to us back in the days when we were in Palmer Lab and when we met in the evenings in these gravity research group meetings. It always seemed to me to be a very obvious argument, and I was amazed when it suddenly became canonical conventional wisdom because the argument hadn't changed any from one that Bob had been giving for years and I had been giving in colloquia for years. It was an argument, an argument of reasonableness and of coincidence, but it was never a geometrical demonstration and, of course, still isn't.
No, but it seems to me that for the argument to be compelling, to sort of sweep you away, you have to imagine that the universe could have been made in many different kinds of ways, with lots of different initial conditions.
Yes, and of course that recalls to us another of Bob Dicke's ideas — the anthropomorphic universe idea [the weak anthropic principle].
Yes, but he seemed to explain that in a much more natural way. I mean [his idea] wasn't intended as a puzzle that needed an explanation. He gave the explanation. Whereas [the flatness problem] is something that poses a puzzle which is very compelling if you can believe that our initial conditions are a set of measure zero [highly unlikely] out of a very large number of possible initial conditions. If you think of it that way, then you realize that you require a physical explanation.
Let me see if I understand what you're getting at. There are two parts to this.
Yes, I don't want to phrase it incorrectly.
One part is the coincidence argument that if the universe has an appreciable cosmological constant or if it has space curvature that's appreciably contributing to the expansion rate, then. There was a special epoch at which this contribution to the expansion rate by the lambda term [the cosmological constant] or by space curvature became comparable to the contribution by the mass density, [leading to an omega of about one]. That special epoch then exists and there are two problems with that. First, initial conditions in the very early universe, whenever classical physics became applicable, had to have set an enormous time scale, which seems a little difficult to arrange. Second, we have to have come on the scene just as the epoch reached that preferred time. Then you have to ask, could the second be only a coincidence or could it be such an unlikely event that this characteristic time, if it exists, in fact, is in the indefinite future — very far off in the future. [In that case], the space curvature cannot have been important, and lambda cannot have been important, and we arrived on the scene at some randomly chosen time so far as the evolution of the universe is considered. So, if space curvature is negligibly small and lambda is negligibly small, then we have a problem indeed. How did the universe arrange these initial conditions?
That's the version of the problem that I've been discussing.
Right, and of course we have a problem no matter what the space curvature is, since the universe is so dramatically homogeneous and we know that it began as separate pieces.
Yes, that's another problem.
Right. So, all along there was a deep problem — how did the universe get to be so homogeneous? And that certainly is something that worried me a lot through the years. I've written papers on that, and I must say that the inflationary idea certainly is a brilliant way to solve the problem. A separate problem is what is the space curvature value now and could it be appreciable in its contribution to the expansion rate compared to the mass density's contribution. Another aspect of the Dicke argument is that you would be surprised to find that space curvature is appreciable now since· that would require, as I say, that we came on the scene just as space curvature was becoming important, which is a coincidence argument. It seems to me that the second argument that space curvature has to be negligibly small is a weaker one because, of course, we had to come on the scene at some time or another and that meant that there had to be some sort of configuration of events and any specific configuration of events always is wildly improbable. How do you judge which is more improbable — that we should have come on the scene now or at some other time?
That anthropic element was not a part of the way that you stated [the flatness problem] in the Einstein Centenary volume.
Right. I don't remember in fact what we put in the Einstein Centenary volume. I presume we emphasized both sides of this question - how did the universe get to be homogeneous, which is very deep, and second, could we imagine that space curvature is appreciable now?
Yes. The reason why I would like to separate the anthropic part is because Alan Guth tells me — and I've interviewed him — that he is completely turned off by all anthropic arguments. But he was still overwhelmingly influenced by the flatness puzzle as stated by you and Bob Dicke.
Now, by flatness puzzle you are not referring to the homogeneity puzzle. That's a separate puzzle.
No, not the homogeneity puzzle — [Guth] distinguishes the flatness problem from the horizon problem, which goes back to Rindler or somebody like that. But he's speaking of the fact that for omega to be so close to one now, it had to be incredibly close to unity at either a Planck time or, as you put it in your article, one second. So that argument by itself, without the anthropic principle, apparently has a lot of power to some people — Guth in particular.
Yes. We know it has a lot of power because very quickly the argument that space curvature must be negligibly small now was taken up by the community, and I think in many circles [it] is now considered to be gospel — a geometrical demonstration of the way things must be — which I think is over-stating the case. As I say, it really does boil down to a coincidence argument, isn't that right?
Yes, whether you're willing to accept the coincidence or not accept it.
That's right. That we came on the scene as omega started to drop away [from] unity. Actually, one can approach this from another direction and ask what the observations say. As you know, there is still the terrible problem that it's awfully hard to find this extra mass that's required to make omega equal to unity — which [is something] I tend to pay more attention to than these philosophical arguments.
For some reason, these puzzles stated in your article in 1979, although they had been around for a long time, ignited the community at that time. I don't know exactly why. Do you have any opinion as to why those arguments suddenly took hold at that particular time and how people responded to them?
I've often wondered why the arguments took hold so rapidly from that one article since, as you observed; these arguments all were known — at least to many professional cosmologists — well before the article. I have the feeling that the ground had become fertile for these arguments, that particle physics was coming with the ingredients needed for the inflationary concept, and I suppose you could argue that the particle theorists needed some philosophical motivation for their ideas on inflation and here they were, ready-made, at just the right time. I could imagine it's as simple as that.
You call them philosophical.
Well, philosophical in the sense that one is arguing that a reasonable universe ought to have zero space curvature — I call that philosophy. It's not quite philosophy, perhaps, but you know what I mean. In other words, I'm wondering if perhaps our article wasn't window-dressing for ideas that the particle theorists would have put forward anyway. In fact, wasn't Alan Guth mainly, and in the first instance, motivated by the need to get rid of monopoles?
That was something that he'd thought about, and [the inflationary universe model] solves that problem, too. But after talking to him, that doesn't seem to have been the thing that stimulated him most.
The other thing I've often wondered is whether he used the name inflation because at the time he invented this idea, we were just going into the hyper-inflation, or stag-flation, era. I was wondering if he was being led, at least in inventing the name, by the economic situation of our country.
I don't know. I haven't asked him about that. Do you remember any of the initial reactions of people to the flatness problem after your article in 1979 came out? I know that some astronomers and some people that I've talked to dismissed the argument on the grounds that the universe is as we observe it, and it makes no sense to talk about an ensemble of universes. There is only one universe. They dismiss [the flatness problem] as being not a serious argument or not something that required us to go out and look for physical processes. So it definitely polarized the community.
I don't know that it polarized the community at that [time]. Perhaps it did, because the arguments were made visible. Certainly responses of the sort you mentioned were familiar to me. I'd heard them earlier many times from sensible people. So I can't say that I noticed any difference in response to these arguments before and after the publication of the paper. The only thing I can recall noticing is a gradual drift toward acceptance of the arguments. One that, as I say, became very surprising to me, as it became such a strong current opinion — these arguments had to be the way it is. It would be fun to ask Bob Dicke how seriously he took these arguments when we presented them in the 1979 paper. I thought they were good arguments, but I never felt that we were laying down the law the way the world has to be.
Well, you weren't giving a physical explanation.
No, we weren't.
You were presenting an argument that there needed to be some physical explanation.
Right. And, of course, at the time I was pretty convinced by the argument, say, that omega really ought to be unity if the universe is at all rationally constructed. It still seems to me to be a good argument for omega to be equal to one, but I don't think I thought then, and I don't know, that it was a demonstration that omega has to be unity. What I found a little surprising was the fact that many people took these arguments to be demonstrations for the way the universe had to be — that omega had to be unity.
Let me ask you a little bit about your reactions to some of the new discoveries, both theoretical and observational, in the last ten years. We've talked a little bit about this already. Do you remember your initial reaction to the inflationary universe model when you heard it?
Yes, I remember great skepticism because of a simple point. In the original inflationary picture, one goes through a phase in which the universe is almost Einstein-de Sitter. One knows that an Einstein-de Sitter universe is invariant not only under translation in space and time but also under change of velocity. It seemed to me to be an amazing thing that the universe could have made the phase transition back to a Friedmann-Lemaitre phase in such a way that all the parts were moving in the same direction. How did part "A and part B know to be moving relative to each other such as to have the general expansion we observe if locally they have no signal from the geometry as to how they should move? It took me a long time to appreciate that there is that scalar field phi floating around, and it does have a gradient that does define a preferred direction, that does define hypersurfaces. So I remember for a long time screaming at people, "This just doesn't make sense." I remember some of the responses. I remember Ed Witten saying, "Well, perhaps Lorentz invariance is violated in the early universe. It's a possibility." I remember asking Alan Guth about this in some detail. He didn't think it was a problem. I guess I now understand why I was misled. As I say, one does have this scalar field. It does have a gradient always, even in the almost Einstein-de Sitler phase.
I thought the gradient was randomly distributed outside of the horizon?
That's the gradient in the fluctuating part. So one has an inflation field that has an almost classical part and a small fluctuating part on top of that. So I'm talking about the gradient of the classical part which I think does rationally define hyper-surfaces on which you can have re-heating such as to make the universe almost exactly homogeneous. I'm only giving you my uninformed opinion. At the time, I was stuck on that point. I gradually came to see that it is not a problem and at the same time I could see how beautifully [the inflation model] so lved what seemed to me to be the essential puzzle, how did the universe get to be homogeneous. On the basis of those two realizations, I was glad to adopt the inflationary picture as a good possibility. I was not — and still am not — convinced that it has to be the way the universe started, but I certainly had to agree that it was a wonderfully elegant idea and so certainly should be pushed harder.
I'm personally amazed at how rapidly and how widely it caught on.
Yes, but that's the way physics operates, isn't it? In the absence of any other idea, a good idea will capture the field. And before inflation, we really had a blank. One could extrapolate the conventional models back in time to a singularity, which is a very ugly thing. So we all knew that we had this horrible problem, and I think it's no surprise that the first idea that seemed to make some sense that came along would capture the field and become the canonical, standard model. Of course, it doesn't mean that the idea is right. It means that we didn't have any options. So, as I say, I'm not surprised. I think we should be careful. I think there's a reasonable chance we've been led down the wrong path. It certainly has happened before. I've heard comparisons of the steady state idea with the inflationary idea, and indeed they have some similarities. In both cases, we had problems — in fact, the same problem. What do you do about initial conditions? In the absence of any very hard evidence — in fact in the absence of any great movement in the canonical model — a new idea came along and because it was new and provocative and accounted for some of the known problems, it captured a lot of attention. Certainly the steady state theory did in the 1950s. It soon became at least a co-equal in credibility with the expanding universe model, and that wasn't because of any observational evidence as far as I know. There were a few bits and pieces of evidence that the steady state theory might do better. One had a time scale problem [with the big bang model]. But I think sensible people didn't think the time scale problem was really serious. I think it was more a question that it was a new idea, not manifestly wrong, and worth exploring. And I think we saw much the same thing happen with inflation. A new idea came along, solved some known problems, so people jumped at it and started exploring it.
You mentioned that both models had in common some kind of a treatment of the initial conditions. Do you think physicists like to avoid specifying initial conditions?
I remember a remark of Eugene P. Wigner many years ago, [commenting on astronomy], in which he said, "We used to think that the interest was in the physics, the laws of physics, and that initial conditions could be left to engineers." I think that is an attitude that pervades much of physics. I don't find the same attitude nearly as strongly in astronomy, interestingly. I don't find there the nervousness with initial conditions that I do notice among many physicists.
Why do you think that is?
Well, as Eugene P. Wigner remarked, one thinks of the interesting part of physics as being the laws of physics, and the initial conditions as being the province of engineers who set things up.
Then why have we gone to so much effort in both the steady state and the inflationary models to get around having to specify the initial conditions?
I guess we didn't trust the engineers.
I guess not. [Laughter]
I would draw another analogy to steady state, and that is that the invention was not motivated, in the first instance, by observation. Instead, it was a beautiful idea that solved some problems possibly, but not something that was guided [by observations]. For example, when Lemaitre was re-introducing the expanding universe idea, I think he was strongly driven by the observations — by the red shift, the receding nebulae. That was sharply in focus. So I would say that here is an example where someone was led to a revolutionary picture by fairly direct observations that prodded him in that direction. I don't think there are any observations that prodded people into inventing the steady state theory. That was just a beautiful idea. I think it's true to say that there were no very close observations that led to the inflationary concept. That was theory, a heavy dose of it. Well-motivated theory, to be sure, and I think it could very well be right. In fact, we have another example of that in Einstein's introduction of the homogeneity assumption in cosmology. He certainly wasn't motivated by any observations — quite the opposite. He deliberately ignored them. So that path can work. Of course, it's not guaranteed to.
This is getting to some more recent discoveries, but do you remember your initial reactions to the work of de Lapparent and Huchra and Geller on large-scale structure?
Yes, that was a case of the curtain opening. We had before then hints that galaxies tended to be in sheet-like distributions, but I was very nervous about believing those hints because I was so aware of the tendency of the eye to pick patterns out of noise. In fact, I wrote some pretty vitriolic papers with examples in the past of how astronomers had been misled by just this tendency. When I saw the Geller et ale map, I was just flabbergasted. Here it is. The window had been cleared and one could see the three-dimensional distribution, and there it was -linear. So I accepted it, I think without regrets. It certainly helped that at just about the same time, we saw the red shift maps of Martha Haynes and Riccardo Giovanelli, which looked awfully similar. So there it is — reproducibility. What more could you want?
Did this change your thinking about the large-scale structure?
It certainly did. Previously, I had in mind the notion of a rather chaotic process that would lead to large-scale structure without much pattern formation. With these linear structures, it was clear you need a pattern-forming mechanism, which is not an element I'd ever given much attention to before. So, yes, I was quite strongly deflected in the way I thought of theories of origin of large-scale structure.
You were already accepting the possibility of large-scale structure to begin with.
Oh sure. Large-scale structure but not with a pattern in it.
No, not with a pattern.
For example, Ray Soneira and I had made models for realizations of the large-scale structure that reproduced the low-order galaxy correlation functions. In these models, we had no patterns on large scales. It was a hierarchy of clusters within clusters within clusters. When we made maps analogous to the Lick map from these models for space distribution of galaxies, we were delighted to be able to point to regions where we saw little lines of galaxies — again just statistical accidents that the eye is very efficient at picking out. But I tended to think of such lines of galaxies as just that — accidents and not something to which we should pay dynamic attention. Then with the Geller et. ale map, it became clear you need a way to form not only large-scale structure but also patterns in that large-scale structure-linear patterns — which seems quite a trick of nature to me. I'm still not confident we know how those patterns [were produced or] the origin of large-scale structure. I'm not so confident I know what the clue is yet.
Can you think of any other example that has' really altered your thinking in the last ten years? Have I missed something that was a big watershed for you personally?
No, I think not. Of course, the dramatic watershed was the discovery of the microwave background and then very slowly the evidence accumulating that it does have the spectrum you would want for blackbody radiation. I couldn't give you a date at which I had decided that the spectrum had to be blackbody and, therefore, that this radiation had to have come from the early universe. Certainly that didn't happen very quickly because, although the long wavelength part of the spectrum was shown to be pretty close to Rayleigh-Jeans in a couple of years — or perhaps more than a couple years, but surely within five years we knew that — it was considerably longer before we knew that the spectrum turned over, broke away from the Rayleigh-Jeans power law at short wavelengths as it ought to. In fact, for quite a while there were contrary indications, weren't there? Well-conceived rocket and balloon flights that gave excess signal [which] we now know — or think we know — [is] because of earth leak. But it wasn't obvious that these early experiments were contaminated by systematic errors and so there was a considerable period, I would say close [to] ten years, when there was a real possibility that this radiation wasn't blackbody. I guess that it became clear around about 1975 that the stuff was really pretty close to thermal black body. That would fall just outside your ten-year interval. In the last ten years, the two big steps forward have surely been the inflationary concept and linearity ... And I don't know how much the former has altered my thinking. I've been very excited with this concept. I'm willing to pay attention to its predictions, but I don't feel bound to those predictions. And I certainly am a little skeptical that those predictions are even right. As for the linearity, the redshift maps in general have been very important as revealing in more detail what the large-scale structure is. And certainly among the results of the redshift mapping, the one dramatic thing has been the revelation that linear structures are so common.
One of the things that I'm interested in is how scientists use metaphors and visual images in their work — if at all. Apparently some do and some don't. I guess one of the most successful metaphors or images in cosmology has been the expanding balloon model that [Arthur] Eddington first introduced. Do you remember when you were first introduced to that image or metaphor of the expansion of the universe?
No, I don't. I suppose it's like many things — I must have heard it as a graduate student and slowly become aware that it is a very useful picture, not only for me but also as a means of communicating to others what one has in mind. I suppose it might have first become apparent to me that this is a very powerful metaphor with the discovery of the microwave background because a lot of people were puzzled. If there was a big bang, and it did produce radiation, why don't we see this radiation streaming away from the site of the big bang? [This was] always a great puzzle. I remember Arno Penzias was very puzzled about this, and I remember telling him about the balloon picture. So I guess I was very familiar with it then and certainly I found it awfully helpful.
And when you told him, did it begin to make sense to him?
He said, "Oh, all right. Sure, I understand now."
And he's the guy who discovered microwave radiation. That's amazing. Do you use visual images much in your own work?
Yes I do. I tend to think visually, I believe, rather than, say, in equations. I don't know — how else do you think, besides in images? Perhaps some people think in words. I can't imagine thinking in words. For example, when I got into the game of studying large-scale structure, I pictured the distribution of galaxies on large scales as much like the distribution of surface height in water in a choppy pond. I was very interested to know what would be the characteristics of these waves on large scales. In the case of the choppy pond, one has a physical interpretation. This is a result of a competition between wind and dissipation. I wondered if there might not be some similar case for the large-scale fluctuations on the distribution of galaxies. It was strictly a metaphor that drove me to think about galaxy space distributions.
That's an interesting metaphor. Have you ever tried to picture the very, very early universe?
Yes. All I get is a very hot, hot region. [Laughs] Of course, we think of these density fluctuations that must have been present at fantastically low levels, so I try to think about that, but it doesn't really grab me too much.
You can't get a fix on anything?
I can't get a fix. I suppose we don't need to have much of a picture of the early universe if we can believe the conventional ideas. All of the length scales we're interested in were enormous compared to the horizon in the early universe. So apparently we have a very simple situation. Take what you see now, extrapolate back [with] linear perturbation theory, and you've got it. Until you get into quantum fluctuations. I don't know how I think about quantum fluctuations. In fact, I think I have sneaking ideas of waves coming in and out of many regions of space which I know I shouldn't do but I...
Waves — you mean probability waves?
Probability. For example, in inflation we think of the energy density in any large region of space as it leaves the horizon having a fluctuating component. Those fluctuations we compute in quantum field theory. We ask why does the energy in this region fluctuate? Well, I have to think of waves of phi — of the inflation — running in and out of that region. I guess that's legitimate.
And then maybe root N statistics.
And maybe root N statistics, right. And then I write down the equations and compute.
How do you think that theory and observations have worked together in the last fifteen years in cosmology? How well or how poorly?
And to what extent have they gone their separate ways?
And to what extent have they gone their separate ways.
I think we're at a very interesting time. I think that theory has not been very strongly constrained by observation or guided by observation. That's because, at least in large part, the observational situation has been pretty shaky, pretty confusing. But I think that situation is dramatically changing for two reasons. People are getting very detailed models of galaxy formation now. For example, the canonical cold dark matter, scale-invariant model makes a large number of predictions that I think are starting to become firmed up and testable. At the same time, people are starting to observe galaxies at high redshifts. It's impressive that galaxies at a redshift of 1 are now observed and [their] spectrums are measured. That's a galaxy at an appreciably younger age than you see now, and so you can infer quite a bit about how galaxies have been evolving and how galaxies must have formed. So I see a crisis coming up in which surely a lot of our popular theories of how galaxies formed are going to be shown to be wrong. I say surely because we have at least four lively models and at most one can be shown to be right. As I say, I don't think that any of these models were invented on particularly phenomenological grounds, and of course, that's the way it has to be in any particularly rich science. You don't invent theories on phenomenological ground often. But, in cosmology, I think it's been the case that these theories have had a pretty free run, unconstrained by observations — in part, because the observations have been both and I think, in part, because people tend not to be as interested in the observations as they might be. But I think also that we're going to see an interesting clearance of theories in the next five years. I certainly hope we will because the present situation is really wildly confused — both in the sense that we have so many options to consider and that we have so many confident statements of theoretical, successes, all of which can't be right.
Do you accept this whole idea of extrapolating our theories back to the first few seconds or so of the universe?
It's awfully brave, isn't it? On the other hand, it worked so wonderfully well with nucleosynthesis — unless, of course, it didn't. Perhaps it was an unfortunate accident that the naive calculation worked so well. Perhaps these ideas we heard today at lunch are right, and indeed the heavy elements were made by conventional physics, only slightly modified when the universe was only a few minutes old. In that case, the present observations are to be reproduced not in the naive way, by ignoring any new processes operating back then, but through a combination of different parameters and a little new physics –- such as decaying inos or inhomogeneities in the neutron distribution — that led by another route from the standard nucleosynthesis calculation to the observed abundances. I could imagine that happening. And, of course, if you can imagine that happening, I guess you can imagine that physics back then was wildly different from what we suppose, and by some other accidental route we ended up with the observed abundances. I guess I'm loath to think that the universe would have been so unkind as to give that a possible chance. I guess I feel fairly comfortable with the notion that the physics of the universe when it was one second old can be traced back from the physics of the present epoch. It seems at least a reasonable possibility. If we go back another factor of 1010 in expansion to approach the epoch of inflation, then I feel very skeptical that we can know enough physics to be very confident in predicting what can have gone on. I have no idea how that situation can be improved, because now we're talking about energies that are reached only in the most energetic cosmic ray events, 1020 volts. So it's going to be very difficult to have an experimental check of physics of those energies. Actually one nightmare I can imagine is that as particle theory advances, particle theorists [will] hit upon a convincing story - convincing to them — of high-energy physics from which they derive a cosmology of the early universe, of which there are no observational tests, aside from the standard ones that, say, the universe is homogeneous. We knew that already, so it's not really a prediction. Or that space curvature is negligibly small. Well, we didn't know that already, but a lot of us were hoping it would be true. So, if out of this complete theory of particle physics and complete theory of the early universe, we get no predictions other than things we already knew or were hoping for, will we be entitled to think that we have a physical theory here? How will we know it's right? It would be very frustrating. Light man: Yes, it would be.
Of course, nature could have presented us with this frustration many times previously in the history of physics. It hasn't. Always it seems that as physics has advanced, we've been able to test.
We've able to make experimental contact.
And the contact has always seemed to be rather convincing. Such a spectacular thing as the discovery of the Wand Z [particles]. It's just a remarkable thing. So I have hopes that it will continue that way and that, as our ideas mature and develop, we will be led to predictions that are sufficiently startling and different from what people had expected when they invented the theory that the predictions will be testable and will be considered convincing if they work. And so the subject will develop.
Let me end with a couple of questions even more speculative than the ones I've asked you so far. Let me ask you to take a big step backwards, maybe putting some of your natural scientific caution aside. If you could design the universe any way that you wanted to, how would you do it?
I would make space curvature negligibly small, and I would make the cosmological constant...
So you mean you'd make omega very close to the critical value?
Right. I would make omega close to unity, zero space curvature, and zero cosmological constant. I would make the universe out of particles we can see, that is, baryons, but then I would be a little embarrassed because I'm not so sure that my universe is going to agree with the real one. So just how do you mean this question? Are you asking how am I betting the real universe is constructed?
No, it has nothing to do with the real universe. You can design the universe any way that you want to, and it doesn't have to look at all like our universe does.
Okay. I have to admit that whoever designed the universe did a good job in making the universe homogeneous, because it gave us a kindergarten problem to work — everyone can analyze the evolution of the homogeneous expanding universe. Also, an expanding universe has a lot of attractions in the sense that we can start from something compact, where it's easy to imagine that the material is forced to be almost pure hydrogen, which is very useful for making stars. As the universe expands, it's easy to imagine how this material got collected up into galaxies, which are very useful for making stars and collecting the debris from stellar explosions to make planets to make people to look at the universe. So I approve of an expanding universe.
You like the idea of having people.
I like the idea of having people around, yes. I hope there are even a few tribes in the universe — in case we happen to knock ourselves off. I dislike the idea of making the dominant component of the universe some material that is undetectable. So I would make the universe out of baryons, of course, with radiation. It's awfully useful to have that radiation not only to control galaxy formation but also to give us — the inhabitants of this universe — some evidence that the universe really is there and expanding. As I say, I wouldn't put in a cosmological constant because it's ugly, and I wouldn't put in any space curvature because it's ugly. I'd have an Einstein-de Sitter universe. I think it would be Einstein-de Sitter, and I don't really care whether it recollapses at some distant time in the future or keeps expanding forever. One shot is good enough for me.
Let me ask you another question. Somewhere in Steven Weinberg's gravitation and cosmology book he has this interesting statement that the more that we learn about the universe, the less it seems that the universe has a purpose.
Oh. That's seems an awfully egotistical remark.
Have you have ever thought about this question?
Yes, in fact, I remember that comment, and I remember puzzling as to why he made it.
Yes, it sort of stands out, doesn't it?
I think he must have been feeling a little down that day, perhaps a little tired, a little discouraged, a fight with his wife.
I can't remember what part of the section on cosmology it is. It might be towards the end, I think.
Yes, we could look it up. But I remember reading it, and I remember being a little surprised to see it. I have never demanded that the universe explain to me why it's doing what it's doing.
Have you ever worried about or wondered whether it has any kind of purpose?
That's such an anthropomorphic remark, and not in the sense of the anthropomorphism of Bob Dicke, but I think in a much more naive sense. I'm willing to believe that we are flotsam or jetsam — I'm not sure which is the appropriate term — in a much larger scene. And I'm willing to believe that in the lifetime of the human race, we won't discover the full meaning of this larger scene.
 C. Brans and R.H. Dicke, Physical Review, vol. 124, pg. 925 (1961).
 A. Einstein "Cosmological Considerations on the General Theory of Relativity," S.-B. Press. Akad. Wi88., pg. 142 (1917); trans. in The Principle of Relativity (New York: Dover, 1952).
 De Sitter's concern about extrapolating from our local observations is evident in, for example, the first paragraphs of W. De Sitter "On Einstein's Theory of Gravitation and its Astronomical Consequences," Monthly Notice8 of the Royal Astronomical Society, vol. 78, pg. 3 (1917).
 R.H. Dicke, P.J.E. Peebles, P.G. Roll, and D.T. Wilkinson, "Cosmic Blackbody Radiation,"Astrophysical Journal, vol. 142, pg. 414 (1965).
 R.H. Dicke and P.J .E. Peebles, Space Science Reviews, vol. 4, pg. 119 (1965).
 P.J .E. Peebles, Physicai Cosmology (Princeton, 1971).
 R.H. Dicke and P.J.E. Peebles, "The Big Bang Cosmology - Enigmas and Nostrums," in General Relativity: An Ein8tein Centenary Survey, ed. S.W. Hawking and W. Israel (Cambridge University Press, 1979); the flatness problem was actually stated earlier in R.H. Dicke, Gravitation and the Universe, The Jayne Lectures for 1969 (American Philosophical Society, 1969), pg. 62.
 R.H. Dicke "Dirac's Cosmology and Mach's Principle," Nature, vol. 192, pg. 440 (1961).
 Editor's Note: W. Rindler indeed wrote a paper on the cosmological horizon, Monthly Notices of the Royal Astronomical Society, vol. 116, pg. 668 (1956), but this paper did not make reference to the observed uniformity of the universe or state the "horizon problem." The horizon problem was probably first stated after the discovery of the cosmic background radiation, possibly first by C.W. Misner "The Isotropy of the Universe," Astrophysical Journal, vol. 151, pg. 431 (1968).
A. Guth, "Inflationary Universe: A possible solution to the horizon and flatness problems," Physical Review D, vol. 23, pg. 347 (1981).
 H. Bondi and T. Gold, Monthly Notice8 of the Royal A8tronomical Society, vol. 108,pg. 252 (1948); F. Hoyle Monthly Notices of the Royal Astronomical Society, vol. 108, pg.372 (1948).
 G. Lemaitre, "A Homogeneous Universe of Constant Mass and Increasing Radius Accounting for the Radial Velocity of Extra-Galactic Nebulae," Annal3 of the Scientific Society of Bru33e13, vol. 47 A, pg. 49 (1927); trans. in Monthly Notice3, vol. 91, pg. 4~3 (1931).
 V. de Lapparent, M.J. Geller, and J.P. Huchra, "A Slice of the Universe," Astrophysical Journal Letter3, vol. 302, pg. L1 (1986).
 H.P. Haynes and R. Giovanelli, "A 21 Centimeter Survey of the Perseus-Pisces Supercluster. I. The Declination Zone +27.5 to 33.5 degrees," Astronomical Journal, vol. 90,pg. 2445 (1985)
 R.M. Soneira and P.J.E., Peebles, Astrophysical Journal, vol. 211, pg. 1 (1977).
 Editor's note: This statement actually occurs in S. Weinberg, The First Three Minutes (Basic Books: New York, 1977), pg. 154.