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Interview of Steven Weinberg by Alan Lightman on 1988 May 5,
Niels Bohr Library & Archives, American Institute of Physics,
College Park, MD USA,
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Awareness in high school of the Sandage Program to observe the rate of expansion of the universe and awareness of the impending operation of the Mt. Palomar telescope; early reading in cosmology; prejudice toward the steady state model in graduate school because of its definite predictions; the reality of cosmology as a legitimate science; Weinberg's early interest in cosmology: influence of Herman Bondi's book; concern in the early 1960s over limited contact between theory and observations; early work in the 1960s on the neutrino version of Olber's Paradox and the possibility of a degenerate sea of neutrinos; preference for an oscillating universe as the next best thing after a steady state universe because you don't have to specify initial conditions; design of an experiment to search for degenerate neutrinos; Weinberg didn't take seriously his own work in cosmology in the 1960s; the importance of the discovery of the cosmic background radiation for making cosmology a legitimate science; the origin of Weinberg's book Gravitation and Cosmology; Weinberg's regret that he spent 1969-1971 working on a textbook when he should have been working on gauge theories in particle physics; history of the application of particle physics to cosmology.
Can you tell me when you first heard or read something about cosmology, in high school or whenever it was?
In high school, I was very much aware that there was a program underway, called the Sandage Program, to observe the large scale expansion of the universe and determine whether the expansion was slowing down and how fast it was slowing down and all that. I didn't understand it in detail, but I also knew at the time I was in high school that the big telescope at Mt. Palomar was going to start operating soon. IT I remember correctly, it started operating in 1952, which is two years after I left high school. We all knew that that was coming, and I thought [that] "as soon as they go from a 100 inch to 200 inch [telescope], then suddenly all the problems are going to be solved, and that's going to be really exciting. We're going to know whether the universe expands forever or collapses. Of course, it didn't work out that way. We're still wondering about those things. But that was exciting.
So you already then knew about the different possible fates for the universe?
I guess so. I had read popular books by George Gamow. I certainly hadn't studied it in a serious way, but it was generally known.
Do you remember whether you had any personal preferences or expectations for what type of universe we might live in at that time?
Yes, yes. I don't remember when I first heard about it, but I do remember quite early, certainly by the time I was in graduate school, I felt that the steady state model of [Herman] Bondi and [Thomas] Gold, and also [Fred] Hoyle, — although [these were] somewhat different versions of the model — was the most attractive. There were many things about it that were attractive. I guess I didn't formulate for myself then what I liked about it, but now looking back, I think I can say what I liked about it, and that is that it offered the biggest possibility of making definite predictions. In any other cosmological model, there's a question about the initial conditions. If you believe in the currently popular big bang models, there are all kinds of questions about why the entropy of the universe is what it is and so on. Some questions, there have been efforts to explain, but they generally just push the question back to some earlier time, whereas in the steady state model, there's a self-consistency condition. If you imagine that there is some mechanism for producing matter in intergalactic space, then that would naturally produce matter at a certain rate. Then you could imagine the universe settling down to an equilibrium situation where it was expanding just fast enough so that the matter was being created at a rate which would just fill up the gaps in the expanding system of galaxies. That seemed very attractive to me: a system where there was no gap at all between the things which are physics and the things which are history, where history is determined just as an equilibrium solution of the equations of physics. I thought that would be really beautiful, and, of course, from a practical point of view, it makes by far the most precise predictions, the most definite predictions of any cosmological theory. The modern Friedmann-Robertson-Walker big bang models leave some parameters undetermined, whereas the steady state model determines everything. The deceleration parameter is -1, and you don't have to worry about evolution when you compare theory with observation, because there's no evolution on the average. Although individual systems evolve, the whole system statistically doesn't evolve.
So even at that age you were vaguely aware...
I really wouldn't say that this was true in high school. I really don't know. It's hard to pin it down. I would say by the time I was in graduate school, I was already strongly prejudiced in favor of the steady state model. And as it happens, it did have the merits that I expected because it was not only falsifiable, it was falsified! It was the first — although it took a while to convince everyone — it was one of the first things that came out of the Hubble Program or the Sandage Program, whatever you want to call it, of measuring redshift as a function of distance. [This work] made it very hard to believe in the steady state model because the deceleration parameter did not look like it was -1. Now, of course, it might be -1, and the effects of evolution may be obscuring that fact, but in the steady state model you're committed not to believe in evolution [of the luminosity distribution]. I don't think that was the thing that actually convinced most people. There were number counts of radio sources that were very important, and probably more important than the Bubble Program. And, of course, the discovery of the microwave radiation background — although, as I pointed out in my book, if you're going to believe in baryon production as the universe expands, you could also believe in the production of low-energy photons. In fact, I worked out in my book what the production rate as a function of frequency would have to be in order to reproduce the steady state — in order to reproduce a thermal black body spectrum in the microwave background. But that is very artificial. In fact, doing that exercise showed how artificial it was, and with the correlation between the microwave temperature and the helium abundance, there's no...
Well, it's comforting to know that you can't propose any cosmological model and have it be consistent with the observations. What you were saying was that the steady state was the first theory that was seriously ruled out.
Yes, it shows that we're really doing something serious. In fact, I've quoted it occasionally as an example — I don't remember where I did, but in some article I wrote — I quoted it as an example of something to be proud of in [making] cosmology a respectable science — that we're not just all making up our favorite cosmological models and then hanging on to them. Some people outside of the field may feel it is that way, but, in fact, it is real science, and observation can kill off [even those] theories that are favorite models.
Let me ask you a little bit about this question of respectability, which you just raised. It's something I wanted to talk about [later], but maybe now is a good time. A lot of people I've walked to, who have been around longer than I, have said that in the 1950s and 1960s cosmology was not taken seriously, with the same legitimacy as other areas of physics. You said some similar things in The First Three Minutes.
Indeed I did, in the preface of The First Three Minutes.
Right. Alan Guth has told me that a big factor in his deciding to come into cosmology was the fact that you had already started working in cosmology.
That's very flattering.
I was wondering if you could talk a little bit about why it is that you started working in cosmology, around 1970.
It really started before that. I think I can be fairly definite. I certainly had some interest in cosmology, as I guess [does] any citizen [who] wonders where the universe came from and all that, but I think it [my serious interest] started with reading Bondi's book. There's an old book by Herman Bondi, which I think is just called Cosmology, but maybe that's not the title, maybe Modern Cosmology. It's short and very readable. It's the sort of book you can-read in the bathtub.
Do you remember when you read it?
Yes. I remember pretty well because I know I read it when I was living in San Francisco, and I lived in San Francisco from 1959 to 1961. Today we would say Bondi's book is terribly out-of-date. As far I recall, it has nothing in it about nucleosynthesis, and certainly the microwave radiation background wasn't known about when he wrote it. It didn't have any review of the work of Gamow and his collaborators on the early universe. But his book showed me for the first time that cosmology was not merely a subject for the observers, but that there was enough mathematical depth to it so that there was something the theorists could learn and do. I hadn't known about the Robertson-Walker metric...
Until then. And the fact that there was a theorem that said that all homogeneous, isotropic universes have this particular metric, irrespective of the dynamics, I thought was great. I didn't know how to — Bondi did not explain how that theorem was proved. I've never been able to understand the articles by Robertson and Walker, and I finally worked out a proof for myself, which is published in my textbook. But I thought that that was really neat, that you could make such a definite conclusion from something as plausible as homogeneity and isotropy. And then at applying the Einstein equations to that, you could then go farther and get a definite equation of motion for the scale factor. It made it as worth learning as any of the other things that I had learned as a student, in quantum mechanics and atomic physics and so on. It was an interesting body of mathematical formalism that said something useful about the universe. And I hadn't realized that that existed before I read Bondi's book.
Can I interrupt just one second? Everything you just mentioned was known well before then [about 1960]...
Okay, why do you suppose it was that the subject was not taken seriously at that point by more people?
Why wasn't it taken seriously by more people? Well, there was that early work [of] Robertson, Walker, Friedmann, Lemaitre, de Sitter, and Einstein. It posed the problem of measuring the scale factor. It wasn't clear there was anything else that you could do. It didn't occur to me that if the scale factor was increasing, it was once much smaller and there must have been a time when physics was very different and it would be interesting to study that physics. I mean it's obvious that that would be a physical problem, but it was very far from my mind that there was any useful confrontation [between] theory and experiments. I guess it was just the limitations of observation that, as far as I knew, the only thing you could do astronomically that would be relevant to cosmological questions was measure distances and redshifts of a lot of things. So the only part of cosmology that seemed worthwhile was that little bit that I'd read about in Bondi's book. I thought that was great, though. I really was enthusiastic about that. I decided I wanted to... I remember very clearly back in that period 1959 to 1961, after reading Bondi's book. I said, "I really want to learn more about cosmology and be a little bit more at home in the field - not just to have read a book." So I gave myself a homework problem. Bondi's book makes a big deal out of the Olber's paradox, which — well, I don't have to explain that.
And it occurred to me that the way Bondi described the solution of the Olber's paradox in terms of the redshift might not apply to neutrinos because neutrinos carry a quantum number, a lepton number, [so] the number of them is significant quite apart from their energy. So I set myself the problem of learning where do neutrinos go? At first, I was just thinking of the neutrinos that are produced in stars. I thought that would be a good problem to work on, because I'd also have to learn something about stellar nucleosynthesis, which I knew almost nothing about. I had read shortly before that a book by Schwarzschild, Structure and Evolution of the Stars, a beautiful book. That was all I knew about stellar nucleosynthesis, and I thought it would be a good way of learning more about that and also learning more about cosmology to answer this question, do stars produce neutrinos? ...
And why aren't there an infinite number [of neutrinos]?
Why aren't there an infinite number, where do they go, and in different cosmological models. And I wrote a couple of papers about them.
That was in the early 1960s?
Yes. In fact, at about that time I went on an around-the-world trip, and I lectured about [the neutrino problem]. At the University of Hong Kong I lectured about it, and in Japan and India, and I had a lot of fun. I wrote two papers, and I think the most interesting thing I did in those papers was to raise the possibility that there was a sea of essentially degenerate neutrinos up to some definite Fermi level, and that this sea had gotten filled over many cycles of an oscillating universe. The oscillating universe is, of course, in a way like the steady state but with...
You don't have to specify initial conditions.
Yes, that's right. It goes on forever. Although it isn't steady, it oscillates, but it's the next best thing to the steady state.
Did it appeal to you for some of the same reasons?
Yes, yes. It still does, in fact, for that reason. I thought in an oscillating universe, the neutrinos that are produced by the stars would gradually fill up the Fermi sea, up to the point where as many were being absorbed in each oscillation as would be emitted in that cycle. Since neutrinos are fairly readily emitted by stars, which have to emit them in order to go through nucleosynthesis, but are very difficult to absorb, that means that there's a very large number of those low-energy neutrinos, and I thought of their filling the Fermi sea up to — well, I didn't know up to what energy, but I knew that limits on the mass density of the universe put a limit of something like, what is it, 20 [electron] volts...
For the rest mass?
No, for the Fermi level.
For the Fermi level.
It's the same as [for] the rest mass. I tried to think of what you could do experimentally to measure that, and actually I thought of an experiment which doesn't succeed [in finding or ruling out a 20 e V Fermi level], but isn't many orders of magnitude off. That is looking for a glitch of the spectrum of a very low-energy beta decay, like tritium. That was fun, because I learned about those tritium beta decay experiments, which are still even to this day the experiments that are used to look for neutrino mass. Occasionally I remind people that when they look for neutrino mass, at the same time they're putting an upper limit on the Fermi energy level. But all my work was based on the assumption that somehow or another, even when the universe collapses, at the end of each cycle, you essentially have a cold universe. And that's silly. I mean today, of course, we're used to thinking of a very hot early universe. I didn't think that through at all. Nobody knew about the microwave background. But there was a sense of unreality about it [cosmology]. I didn't take that work [of mine] very seriously. Of course, if a Fermi energy level, if the degenerate sea of low-energy neutrinos was discovered, I would have been in seventh heaven. But I didn't really take it seriously. I didn't expect it to be discovered because, as I have written in The First Three Minutes, there was a sense of unreality about any speculations about the universe. The wonderful thing about the microwave background is it was the kind of thing that I was only dreaming of with the neutrinos. It was really direct observation of something from the very early universe.
Going forward in time a little bit from the early 1960s, was the textbook that you wrote, Gravitation and Cosmology, in 1972, part of your same program of further educating yourself about cosmology? Why did you write that text book?
I would say the program really took shape in teaching the course. I don't remember the details, but once or twice at Berkeley, and I think twice at MIT, I taught the graduate course in general relativity. I volunteered to do it because I wanted to learn general relativity and I wanted to learn cosmology. Actually, cosmology got to be more and more of the course. In teaching the course, I didn't like existing text books. I wrote about this in the preface of my textbook, Gravitation and Cosmology. I didn't like their attitude of taking Riemannian geometry as something given and then trying to fit a theory of gravity onto that skeleton. I liked taking physical assumptions about gravity, in particular, the principle of equivalence, and then deducing the connection with Riemannian geometry. Especially because there's so little experimental evidence about general relativity, I only wanted to develop formalism that I thought was inescapable. Anything that was not inescapable, I wanted to leave as highly questionable. What I found when I taught the course is that one can make a fairly clear logical dividing line between, on one hand, those parts of general relativity which strictly follow from the principle of equivalence, and that really means the effects of gravity on systems like light rays or rulers or whatever it is. And that includes some tests of general relativity like the redshift of spectral lines on the surface of the sun or in the Jefferson Physical Laboratory. Those can be understood without going beyond that part of general relativity. You build up the whole formalism of general covariance and tensor analysis and so on at that level. Then a further step comes when you assume Einstein's equations, where there are assumptions of simplicity that enter — that there are second order differential equations. Why should they be second order? I don't know. I was willing to keep an open mind about that, and I thought it was worth making a very careful distinction between the two halves of the subject. I didn't like the fact that in most textbooks the two were totally muddled. You know, it's all general relativity and you learn about the Einstein field equations at the same time as you learn what an affine connection is. I didn't like that at all. So, every time I taught it I gave out lecture notes, and the lecture notes got more and more...
Shifted towards cosmology?
I was going to say they got more and more substantial. They got more and more looking like a book, so eventually it just turned into a book. In a way, I'm sorry I wrote the damn thing because the actual work of writing it after all this effort of teaching... it many times at Berkeley and MIT — the actual writing of it was in 1969, '70, '71, and those are the years when I should have dropped everything I was doing and worked on proving that the spontaneously broken gauge theories were renormalizable. I had made that suggestion in 1967 as [Abdus] Salam did in 1968, and I had worked on it in a desultory way, and this book took me away from that problem. I really shouldn't have gone away from that. I should have just worked on that problem, looking back on it. But what can you do?
For your own career?
No, I think for... Well, you know, that's the most exciting thing. It's not a question of career. I mean it's wonderful to write a book that has some impact, but it's even more wonderful to make discoveries that have an impact, and between the two of them I'd rather make discoveries than write books. I'm very proud of that book, but I would have been even prouder of proving myself that these theories were renormalizable rather than just conjecturing it.
Let me go back a little bit to your undergraduate and graduate education. Were there any particular experiences that you had there that you think were very influential to your deciding to include cosmology as well as particle physics in your interests?
No, I didn't have any courses in general relativity. I may have audited one, but it didn't have much of an impact on me, and I don't remember who gave it. And I didn't take any course on cosmology. No, for complicated reasons I was only a graduate student, in a sense, for two years. I was at Copenhagen for my first year and there were essentially no courses there, and then I was a graduate student at Princeton for two years, and then I got my Ph.D. So I didn't take that many courses of any kind.
So most of your exposure was outside of courses.
Yes. I read textbooks, but I didn't like the textbooks I read. I don't mean that they weren't good books, but they didn't suit my taste in the way that the course should be taught.
Let me ask you about the injection of particle physics into cosmology in the 1970s. I think this has been a major revolution in the field and very good for astronomers and cosmologists. In the late 1970s, it seems that a number of independent groups started doing calculations involving particle physics — in explaining such things as the photon to baryon ratio, which you did yourself. Why do you think that all of this activity happened at approximately the same time?
I don't really know. It's a good question. I'm not sure. One thing you can say is that, of course, the mid-1970s was the time when the theoretical work in constructing our standard view of elementary particle physics was essentially completed. The discovery of the [consequences of] instantons by [Gerard] 't Hooft really solved the last outstanding theoretical puzzle. Then, by 1978, the experiments had all fallen in line. So we had a theory of elementary particles that was worth applying and that you could have some confidence in. Although I must say that the kind of elementary particle physics — I guess the first thing I got interested in was the cosmological phase transition, the phase transition in which SU(2) x U(1) is broken.
 G. Gamow, Birth and Death of the Sun (Viking: New York, 1940); One, two, three infinity (Viking: New York, 1947); The Creation of the Universe (Viking: New York, 1952)
 H. Bondi and T. Gold, Monthly Notice$ of the Royal Astronomical Society, vol. 108, pg. 252 (1948); F. Hoyle Monthly Notice$ of the Royal Astronomical Society, vol. 108, pg. 372 (1948)
 S. Weinberg, Gravitation and Cosmology (John Wiley: New York, 1972)
 S. Weinberg, The First Three Minutes (Basic Books: New York, 1977)
 H. Bondi, Cosmology (Cambridge: Cambridge University Press, 1960)
 M. Schwarzschild, The Structure and Evolution of the Star, (Princeton: Princeton University Press, 1958)
 S. Weinberg, "The Neutrino Problem in Cosmology," Nuovo Cimento, Series X, vol. 25, pg. 15 (1962); "Universal Neutrino Degeneracy," Physical Review, vol. 128, pg. 1457 (1962)
 S. Weinberg, "A Model of Leptons," Physical Review Letters, vol. 19, pg. 1264 (1967)
 A. Salam in Elementary Particles, ed. N. Svartholm (Stockholm: Almquist and Wiksels, 1968)
S. Weinberg, Physical Review Letters, vol.42, pg. 850 (1979)