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Interview of Dennis Sciama by Alan Lightman on 1989 January 25, Niels Bohr Library & Archives, American Institute of Physics, College Park, MD USA, www.aip.org/history-programs/niels-bohr-library/oral-histories/33994
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Background of father; discouraged by father to go into science; early reading in science; early desire to be a Fellow at Trinity College; early interest in philosophy and influence of lectures by Wittenstein; switch in graduate school from statistical mechanics to cosmology; interest in Mach's principle; desire to understand the "great questions"; desire to impose order on the universe; poor grades as an undergraduate student at Cambridge; job in a government research lab called TRE; re-admittance to Cambridge by Hartree; business agreement with father to withdraw from graduate school if unable to get research fellowship to Trinity; influence of Fred Hoyle, Herman Bondi, and Thomas Gold; rebellious nature of Hoyle, Bondi, and Gold; Dirac as thesis advisor; attraction of the steady state model; reaction to hostile evidence against the steady state theory; predictive power of the steady state theory relative to the big bang model; preference for flat universes (in big bang models) because of Mach's principle; Sciama's influence on Dicke and Wheeler regarding Mach's principle; motivation of interest in Mach's principle and its discussion in the BondiGold paper on the steady state; work with Martin Rees in plotting the spatial distribution of quasars and initial intention of defending the steady state model; personality of Martin Rees; giving up the steady state model after the calculation with Rees; approach to advising students; advice given to students Brandon Carter and Stephen Hawking; general scorn of physicists toward cosmology in the 1950s; recognition of cosmology by physicists after the cosmological prediction of the number of neutrino types; introduction to and attitudes toward the horizon and flatness problems; attitude toward the inflationary universe model; problem in appreciating those problems because so few people in the field; problem with inflationary universe model having so many variations and being oversold; reasons why the inflationary universe model has been so influential; reaction to de Lapparent, Geller, and Huchra's work on large-scale inhomogeneities; problems if inhomogeneity in cosmic background radiation not found with factor of 10 improvement in detection limits; discussion of dark matter and missing mass; current state of mess of inflationary universe model; interplay of theory and observation in cosmology, particularly in the number of types of neutrinos; reasonableness of extrapolating physics back to the very early universe; outstanding problems in cosmology: the cosmological constant, fate of the universe, dark matter, galaxy formation; ideal design of the universe; belief in the strong anthropic principle; belief that Penrose and Hawking are wrong in their proposal of very special initial conditions for the universe; question of whether the universe has a point.
I wanted to start by asking you a few questions about your childhood. Can you tell me a little about what your parents were like, what they did?
My father was a businessman. Actually you have taken me slightly aback because lots of things are rather personal, and I don't know if I would like to talk about them for publication. But certainly he was a businessman in Manchester. I grew up in Manchester. I then went to what we in England call a public school — that means a private school — from which I got a very good mathematical training. Those schools could afford to pay for the better teachers. In fact, my main teacher was a man who these days wouldn't go into school teaching. He got first-class honors in all three parts of the mathematical tripos in Cambridge, and he went into school teaching, and he helped me to get a scholarship to Cambridge.
Were either of your parents interested in science?
No, not at all. The atmosphere was entirely a business one. It rather surprised my father when I had this interest in science, which was outside his orbit. He was a very clever man, but he had left school at the age of 12 because his father had died, and he wasn't therefore used to higher education or anything like that. Although he had a fine brain, it hadn't been trained. He was trained in the world, but not trained in institutions. He therefore didn't particularly know about higher education until I told him. I told him Cambridge was great and Trinity was great, and he accepted that. But it wouldn't have been anything in his world.
When he knew that you had an interest in science, when he became aware of that, did he discourage you or encourage you?
He tried to discourage me because he thought that I ought to go into his business.
What about your mother?
She helped me a little bit, but he was much the stronger personality. It was just that I was so motivated to do science and mathematics. I suppose at that age I didn't even distinguish them. I originally thought of myself as a mathematician, and only later did I move first toward physics and then to cosmology.
Do you remember in your childhood, do you remember any particular books that you read that had a strong influence on you?
Yes, I can't remember how old I was when I read them, but I think it must have been in school. So many people of several generations were around then — Eddington, in particular. Although I did read Jeans a bit, I found Eddington more challenging.
He had several popular books.
He had several popular books. Perhaps now they've faded out a bit. I don't know. At that time they were very well known and considered the leading books of that kind. I don't know if you have read them — they are very imaginative.
I have read one or two of his books, and I think he is a beautiful writer as well as a good scientist.
So that certainly appealed to me, although at that time I wasn't thinking of myself as an astronomer. There were other people, mainly connected with Trinity. G.H. Hardy, the pure mathematician, wrote a lovely little book called A Mathematician's Apology.
That is one of my favorites.
Then you may remember how he says from an early age his one ambition was to become a Fellow of Trinity. Again, this reads a bit old-fashioned now, and some people would even say it is no longer [impressive] and so on, but at the time it thrilled me.
Did you read Hardy's book when you were a youngster?
Yes. I also read some Bertrand Russell, who again was associated with Trinity.
So you were interested in philosophy?
I've always had a mild interest in philosophy. In fact, I'm giving a talk on the philosophical aspects of the anthropic principle in a week or two. So, I have had an interest in philosophy. When I went up to Trinity in 1944, I attended a whole course of lectures by Wittgenstein, who was then still a professor and giving lectures. That was a very good experience. So, while I was basically doing mathematics, I had this interest in philosophical things, and it just so happened that many of the leading people at the time were Fellows of Trinity, or had been. Trinity was the most prominent college. That was all part of the image of what a youngster would be attracted to, to strive, as it were, because there was this goal. So that played an important part.
At this age, before you went up to Cambridge, did you have an intention to go into science or mathematics?
Yes, from about the age of 15 or 16, I suppose. Before that, I was very young, and I naturally said I would go into my father's business because that was the obvious thing to say. I don't remember precisely, but roughly from the age of about 15 or 16, when I was beginning to be coached to take the scholarship to Cambridge, I realized [science and mathematics was] what I wanted to do.
One thing you said in your interview with Spencer Weart in 1978 was that at this age you developed a passion for mathematics and science. Do you have any idea how that passion developed or what caused you to be so taken with this subject?
I think in retrospect I can answer that question perhaps, but it's a bit wisdom after the event. In fact, I came to cosmology and astronomy relatively late. When I was doing my Ph.D., for instance, I started out in statistical mechanics. Only in the middle, partly under the influence of people here like Fred Hoyle and Hermann Bondi, and Tommy Gold, did I start getting interested in cosmology and Mach's principle and so forth. Rather unusually, in the middle of my Ph.D., I switched to relativity and Mach's principle and so on. They had to give me a new supervisor as a result. They gave me no less than [Paul] Dirac, in order to try and cope with this rather alarming change of subject from the point of view of the authorities. So, something inside of me must have burst out at that point. Although the statistical mechanics problem — it was about the Onsager, Ising type of work — is very attractive theoretical physics. But it doesn't, of course, have the connotations of understanding the origin of the universe. Once I started doing things beginning with Mach's principle, I then realized my real passion was for understanding the fundamental nature of the universe. Some people, and perhaps the majority, do that by particle physics, and a few of us do it by cosmology. Of course, as I dare say you will discuss later, now the two things are linked together. So, then I said "ah, hah, it's clear to me what it's all about, and I want to understand the way the world is made, where it comes from, and what it means in the scientific sense." That's my passion. Therefore, always I've tended not so much to work on very technical detailed problems — although some of my students have — but rather on problems that in some way help to understand the great questions. So, that's obviously what my real passion is. But at 15, I didn't say all that. It expressed itself then as an interest in, say, mathematics. I remember enjoying projective geometry at school. I thought it was very beautiful and well ordered, and so on. Cosmology came much later.
Did you like well-ordered things?
Yes. Because, you see, if you do understand the universe... I mean, if Mach's principle had been true and sensible and worked well, or if superstrings or something are right, you are imposing order on the universe. And no doubt a psychoanalyst would have his own views as to why one wants to do that. Again, I think I mentioned this to Spencer. If you impose order on [the universe], then you help to achieve it yourself. Roughly speaking, what I like to say is that the universe is enormous — it is much stronger than you are — and your only way of hitting back at it is to understand it. No doubt, a psychoanalyst would use psychoanalytic jargon to describe [that idea], but that's what it amounts to, I guess.
Do you think that kind of motivation was something you sensed at a young age, or was it something that developed later?
I don't think I sensed it as explicitly as that. When I was enjoying projective geometry, I just said "how beautiful, and what a nice intellectual challenge, and what lovely theorems you get when you use your intellect, and that's great fun." I didn't realize all that I am now saying, probably until I made that switch in the middle of my Ph.D. But no doubt it was underneath.
Can you tell me a little about your undergraduate and graduate work at Cambridge? I don't want you to go into too much length because you said quite a bit to Spencer Weart but just give me some of the high points.
The high point is that I was a disastrously bad student. No, that's putting it too strongly. I did get a minor scholarship in mathematics at Trinity, which was a great achievement. A large part of that was due to very good coaching by the particular school teacher I mentioned earlier.
Did you say his name?
I didn't. His name was R.H. Cobb. Anyway, it's a bit like training for a race or something, learning how to solve these problems. It's all book work. You learn how to prove these things. You've been through this yourself, I'm sure. You remember how to prove book-work theorems, and you do many, many "riders," as we used to call them — examples based on the theorems. And so you trained. I was good enough to be trainable to get even a minor scholarship at Trinity, which was the great place in maths at Cambridge. But then I did extremely badly in exams here, so badly that when I finished I had to go into the army. This was just after the war, but there was still conscription, and I couldn't remain to be a research student. I got a lower second in finals, and two thirds in my earlier exams. So I was in disgrace. However, during the two years that I had to be in the army, for 18 months of it I managed to get sent to a government research lab, which was called TRE in those days. [That lab] originally had done a lot of radar work in the war. One was still concerned with detecting enemy airplanes, detecting infrared radiation. They were studying photoconductors, or semiconductors — they become conducting when the light hits them. And I with a team — of course I was guided by the senior people — worked on the quantum mechanics of the band structure in the lead sulfide group of elements.
So you got to do physics.
Yes, I wrote internal reports. Hartree was one of the professors here at the time. You know his name, I'm sure. He I had seen just as I was leaving as a student, and I told him I wanted to get back into research. He helped me to get transferred to this government lab and then accepted me back as a research student when he had seen these internal reports. It was all about the group theory, and the levels, and so on. So, that is how I got back in to the system.
So they thought you might have been dismissed out of hand from Trinity?
Well, I wouldn't take a student on with my exam records. It's all rather embarrassing when I now have to take students on. If it were a question of a grant, I wouldn't be allowed to give a grant, because you’ve got to get a first or an upper second to get a grant. But he took me back without a grant, and that's where my father being a businessman came in. I was able to live through the help of my father, despite his early discouragement.
How did he feel about supporting you in this intellectual pursuit?
Well, he was still terribly upset that I had rejected business, but he saw that I was so determined that he let me do it. Later, I agreed with him whether I would continue depended on certain things. It was a crazy thing to do, because clearly if I was going to be a tenth-rate researcher, then maybe it's better to earn a lot of money in a good firm. So, I agreed with him that [I would stay in scientific research] only if I got the research fellowship at Trinity — the thing Hardy had written all about. That would be a sign that it was worth the sacrifices, and otherwise not. That was a crazy [agreement], because even if I were very good — which I didn't know really at that time — it's very chancy whether you get a [fellowship]. You're competing with a whole group of people in a whole range of all subjects.
Was this his proposition or your proposition?
I think I said at one point, "well look, the natural thing for me to do is go in for a Fellowship." It's such a prestigious thing to get, which I explained to him, and he accepted that. Because if I did get [the Fellowship], that would be the sign that it would be worth the sacrifices.
Then did you also complete the proposition and say that if you didn't get [the Fellowship]; you would put your [fate] in his hands?
Yes. If I didn't get it, then that would show that it wasn't justified to give up these good prospects in the textile business.
So you made him a business proposition.
I made him a business proposition. Exactly. But a very bad one. [Lightman and Sciama laugh.] Arnold Weinstock would never do that today. Perhaps you don't know him. He is the chap in GEC here, and they've just been trying to take him over with clever tricks. Yes, so by sheer luck I did get the damn thing, so I was able to remain in an academic career.
When you decided to do cosmology, you said that you came under the influence of Hoyle and Bondi.
And Gold. They were all here. They were senior to me, but I got a bit friendly, particularly with Tommy Gold, and to some extent with Hermann Bondi. Hoyle was still older than that. They were all playing a strong part here. You probably know that they were all considered sort of rebels at that time. Hoyle was not Sir Fred Hoyle, Plumian Professor. He probably had a lectureship then, and I think Bondi did. But Bondi wasn't Sir Hermann Bondi, et cetera, et cetera.
This was in the early fifties?
Yes. I got my fellowship in 1952, and I actually got the degree of Ph.D. in 1953. I started being a research student in 1949. The steady-state theory, which was one of the dominating ideas in cosmology at that time, was published in 1948. So at that time it was far too soon for the hostile evidence to arise. [The steady state] was a very attractive idea to some of us. Also, [Hoyle, Bondi, and Gold] were concerned with astronomical questions. But in a lot of their work, they were introducing rather new points of view, which tended to be the kinds of points of view that got resistance from the establishment. They were the young rebels, and they were an exciting influence at the time for a younger person like myself. Even when I was doing the statistical mechanics, I must have gone to their lectures and realized that their personalities were robust and exciting. I suppose that played a part. I don't remember waking up one day and saying "no more Ising [models], I will now do distant galaxies or something." I can't remember the precise details, but it's clear that I started thinking about questions of that kind, and then I proposed a change of subject, and they got very agitated because you don't normally make such a big change. And then there are questions like "have you been working long enough at the new topic?" As I say, they gave me [Dirac], because there weren't many people around at the time. I don't know why they didn't give me Bondi.
Yes, why did they give you Dirac instead of Bondi?
I don't know. It's not that I can't remember. I wasn't privy to the discussion. They may have felt that since it was a slightly delicate matter — this big change — they ought to give me a very senior person. But I'm only guessing.
Dirac didn't really work in general relativity, did he?
Well, he had done things in cosmology, like the large number business. And he had one something in general relativity. He had done this Hamiltonian theory for quantization purposes. It was all part of his theory of constraints in quantum mechanics, when you have theories with invariants. Electrodynamics is the first example, when you have gauge invanance. [It becomes] coordinate invariance in the relativity case. This gives rise to a lot of technical problems when you try and quantize. He had a whole theory of first-class constraints and second-class constraints designed to deal with that. Then he decided to apply that to general relativity. It was quite important work actually, in a way. Nothing like his greatest work, but it's very considerable. He found a Hamiltonian for general relativity, as distinct from the Lagrangian. He tried to quantize it. And he wrote other papers on general relativity. So, while [general relativity] is obviously not the first thing you would think of with Dirac, he had done quite a bit. Maybe the mere fact that he was a major theoretical physicist was taken into consideration. But by the time I got Dirac, as I think I explained before, I had already worked out this Mach's principle thing that I wrote my thesis on. So, he didn't particularly help me — not through any fault of his. But I did have access to him, and that was fascinating.
You mentioned steady state a moment ago. Obviously that was extremely important during this period. Can you tell me a little bit about why you were so attracted to the steady state theory?
I suppose because of its simplicity and predictive power. The big bang — even now, of course, we're struggling to understand the big bang. [I accept the big bang], although Fred Hoyle still doesn't. But I accept now that basically the big bang picture is clearly correct. But, it's a naturally very complicated physics that goes on near the bang. There were even questions like: can you be sure the laws of physics are the same in a changing universe. You see, there might be philosophical reasons for worrying about that. This was all part of the original discussion.
That was in the original papers.
Whereas it's at least reasonable to say that if the universe always has the same large-scale appearance, it's less of an assumption that the laws are unchanged. And there were various arguments of that kind. The whole picture you got of the universe was a rather simple, appealing one. And [the steady state theory] did have predictive power, and therefore that was good. All those things didn't mean I believed it, as it were, but just that it was so attractive that I felt in a small way to try and make it work. When hostile evidence started to appear, you weren't sure what to make of it. I remember writing various papers at the time and having arguments with Martin Ryle about whether the evidence against the steady state was good or not. It was worth trying to save [the steady state theory], but as the evidence mounted, there came a point where one couldn't. But the reason for supporting it was not, as I say, that it had to be right, but just that it was to me very attractive and the penalty of having creation of matter didn't seem to be such a terrific penalty. It was rather an interesting process to study. As they used to say at that time, [continuous creation of matter] is even less of a thing to introduce than the creation of a whole universe at one go.
Was that an argument that you talked about at that time?
I suppose. I recognized that the standard theory didn't in fact have a creation moment. What we later came to call the singularity was not well understood. But, I never felt then and I don't now feel so alarmed about outrageous proposals in physics, unless they're easily disposed of by experimental evidence. I never felt creation of matter was something disturbing. It was a rather interesting phenomenon, and the bang was obviously even more interesting. It was very remarkable. But I wasn't frightened by saying "let's not have a bang, let's have a steady, continuing process which is subject to physical investigation because it's repetitive."
You said that you felt that steady state had predictive power, and that appealed to you. Did you feel that it had more predictive power than the big bang model?
It did in some respects, because by denying the possibility of evolution of the average properties of galaxies, you could make much more specific predictions about, for instance, the number of sources as a function of redshift. Whereas, indeed as we all know now, the [big bang model] requires evolution. You don't just get a distribution of these quantities that is different from steady state because the metric of the universe is different. There is very strong evolution, which, of course, does occur. I accept that. But, from the point of view of making predictions, [in the steady state model] you are denied evolution, which would have many parameters. Then you can be very specific. So, that was certainly appealing in the sense of being useful. Then you decide very quickly, perhaps with luck, whether this proposal was reasonable or not, because you couldn't keep cheating every time there was hostile evidence. At first, you could worry about whether the evidence was accurate or not and so on, but you couldn't say "oh well, we’ll introduce this fudge factor and that fudge factor."
At this time, during the 1950s, when you did think about the big bang model, did you have any preference for a particular model in the big bang, say open versus closed or that kind of thing?
I did, and that was linked to my interest in Mach's principle, although this was never fully worked out. But, as did other people perhaps for similar reasons, I preferred the Einstein-de Sitter model, the one that only just expands forever, the k = 0 model. That's the Machian thing, because k, in the Newtonian analogue of these models, is the energy-kinetic plus gravitational. If the energy is due to gravitation, ala Mach, rather than having a kind of spontaneous existence, then at least it might seem as though it would be rather natural to have one [energy] balance the other. One made the other. Therefore, that would be the attractive model. But that turned out not to work later, because I had a student, Derek Raine, now a lecturer at Leicester University, who worked later on Mach's principle, producing a much better theoretical statement of the principle. The principle is a kind of boundary condition. He produced, as far as I'm concerned, still the best discussion of what boundary condition you're really groping for. But when he did that, he found that because of feedback effects in the different models, all the cosmological models of the Robertson- Walker type, with the exception of Minkowski, are Machian. Essentially, if you were to use technical language, you introduce a Green's function to tell you how much a particular piece of source influences the metric here. In relativity, that's got to be a functional of metric. It can't be a fixed quantity. I wrote a paper, with others, which I was quite pleased with, in which I showed that general relativity could be written as an integral equation to represent the metric here as a sum of contributions from the energy momentum tensor everywhere. [That formulation] used a propagator or Green's function, which itself was a functional of metric but had certain structural properties that made it rather attractive. Derek Raine used that idea to make a Machian boundary condition. He has written an article on this by the way. So, he used those ideas and generalized them a bit to say that if you want a Machian boundary condition in addition to the propagator, which is entirely implied by GR itself, you need some statement about boundary conditions somewhere. When he made the most Machian statement he could — a statement that I approved of — he then found that all the Robertson-Walker models except the empty one would count as Machian. Owing to the fact that the Green's function itself depended on the metric. If you chose a non-Einstein Sitter case, there would be adjustments.
To make itself consistent.
Each one was self-consistent. The sources were doing their job. The way they did their job was different in each case. I had to accept that, but it was disappointing. But, until that was done, I would have preferred the Einstein-de Sitter model.
I think the Brans-Dicke theory, which partially incorporates Mach's principle through the scalar field, much more than general relativity, also allows all Roberton-Walker metrics (flat, open, and closed) for cosmology.
It probably does. I suppose, in a way, the Brans-Dicke theory was at least partly stimulated by my own writings. But I never quite liked that theory. I preferred to [incorporate Mach's principle] within GR [general relativity] if I could, rather than introducing extra fields. Of course, one now introduces extra fields for other purposes. They are very likely. But at that time, I didn't really quite like that. So when [the Brans-Dicke theory] ran into difficulty from observations, I wasn't sorry. I'm sure Bob Dicke was sorry. But I wasn't.
I know that he was certainly influenced by Mach's principle in designing that theory, and probably your work as well.
Well, also John Wheeler had seen my work and had written many things himself on it, and we all influenced each other. I suppose of the three of us, I was slightly the first, but we all had different ways of incorporating the principle. Naturally, I like my way the best. But in the end, that hasn't been terribly successful. It all sort of went into the sand, I believe.
We have been talking about Mach's principle, which has been a theme of a lot of your work starting with your Ph.D. thesis. Do you remember why you got interested in Mach's principle in the first place?
I have a vague memory that I was thinking about other cosmological questions and steady state questions — how one could make a field theory of steady state. I remember one time writing an article or variation of the thesis that actually pointed out that the scheme I was developing was not consistent with Mach's principle. I then started to attack Mach's principle, [because] I wanted my scheme to be a good one. Then, at a certain moment, I got converted and said, "No, I've got it the wrong way around. The nice thing is Mach's principle, and I'm missing the point."
Why were you thinking about Mach's principle at all? I didn't know that that was something on people's minds at the time.
There is a simple answer to that. I probably picked up the idea from Bondi.
Was he discussing Mach's principle?
If you look at the Bondi-Gold paper on steady state and you look at Bondi's very lovely book on cosmology that came out in 1952, there was a lot about Mach's principle in both of them. You see, in the steady state, the idea was whatever makes Mach's principle work in the steady state would be happening all the time. So, the arrangement of the world let Mach's principle apply. Also, I went to a course of lectures Bondi gave on cosmology. In fact, I was telling him the other day — because I'm at the college here where he is master now — that I still have the notes from that course. His book came out a little later, but I would have heard about it from the course. I found the idea extremely attractive, and this has something to do with my psychology. I like simple ideas with very great power in physics — the idea that centrifugal forces and Newton's rotating bucket is mainly due to galaxies. As I have pointed out in my books, the main contribution came from galaxies beyond what you can see with telescopes — suggesting that the whole universe acts one unit in this way. That seemed to me to be a mind-blowing idea, as one might say. I realized quite soon that most physicists thought I was not quite a crank, but at least peculiar. Despite the tradition of Mach and Einstein about Mach's principle, most of my contemporaries would have said it was a will of the wisp, a semi-crank [idea]. Yet, after all, the little calculations I did then would show that if an object accelerates towards you, it produces a 1/r force, just like an accelerating [electrical] charge does.
This is gravitational.
Gravitational. And you know very well that if you have a 1/r force, distant [sources] are more important than near ones. It's worse than Olber's paradox. It's no good saying it's cranky to talk about distant galaxies, they just dominate. You just do a sum of two lines, and they dominate. The other question is: do they dominate so completely that they do the whole job? That's the boundary condition problem. But, to me it was clear that you had to worry about that. It was no good saying this is cranky. If it's a long-range force, then distant [sources] dominate. As I say, it was the power and the sweep of the idea — the idea that the whole universe was acting as a mechanism. Indeed, my first book was called The Unity of the Universe. That was my [belief]. That's why I liked [Mach's principle], once I learned the idea. And I was very disappointed when it all went into the sand.
Let me ask you about another project that you worked on somewhat later. Do you remember what motivated you to work with Martin Rees on plotting the distribution of quasar redshifts versus intensities?
Oh yes! I have probably told Spencer [Weart] this. That was very funny. That was typical of a lot of my work, where the student really does it much better. At that time, the hostile evidence [against the steady state theory] was accumulating, but it was in the early days, and you could still try to save the steady-state theory. So I was tittling around with these various things. The microwave background had just been discovered. But at that stage you couldn't be sure it wasn't due to [things other than the big bang]. In fact, I wrote a paper saying that there might be a type of radio source whose integrated radiation would mimic a black body spectrum over at least a limited range of wavelengths — which was all that could be measured at that time.
So you were defending the steady-state.
The idea was to defend the steady-state, and also I learned astrophysics in the process. It was an interesting thing for various reasons. I knew from the great battle between [Martin] Ryle and Hoyle about the radio source counts that questions of counts would be crucial, or might be crucial. Quasar data was beginning to come in during that period. Of course, quasars were just three years old or something. In fact, in 1965 was the great discovery by Maarten Schmidt of a quasar with a redshift of 2. So, I started plotting out the number of quasars as a function of redshift.
Why did you do that?
To see whether it agreed with the steady state. This relation between number and red shift is a unique prediction of steady state. You [don't have] to worry about whether [the quasars] evolve at different redshifts. So there was a specific formula, which I knew. I think it probably was in the original Bondi-Gold paper. Anyway, it was a known formula, a straight-forward formula. So, the question was: is there enough data accumulated to test this? You see, today there are far more people in the field, and this sort of thing would be done instantly. But at that time there were fewer of us, and therefore it still had to be done. So I plotted out the number-redshift relation. The way I do these things, it was sloppy. And lo-and-behold, it fit the steady state [prediction]. I remember going to Martin and saying "Martin, Martin, look. I have plotted out N [number] as a function of z [redshift] and the steady state is supported." Martin was then a research student of mine, with whom I discussed all the more astrophysical types of questions involving cosmology. He was always a bit skeptical about my enthusiasm for steady state. He is a very well balanced chap. He said, "well, I'll have a look at it," and he went away to have a look at it, and he did it better. Two days later — I forget how long it took him — he came back and said, "I've done it properly, and it's very bad for steady state. The [observed] relation is quite different [from that predicted by steady state.]" It was the same general kind [of relation] as what I was finding for the regular radio sources. I looked at what he'd done, and I agreed that he'd done it properly. That was the thing, as I probably told Spencer, that for me made me give up steady state. I wasn't prepared. You see, there was a conceivable let-out from people like Hoyle and [Geoffrey] Burbidge, who were then saying that quasars are local. I didn't like that — it was piling one thing on top of another. I have a bit of a conscience, somewhere along the lines, and I couldn't play that game. It really wasn't reasonable. So, I said "okay, the quasars are cosmological, and therefore this decides it." At that time, the blackbody thing was still debatable. So, for me at least — though not for most people... it was this study that was decisive, and I had a bad month giving up steady-state. Then, of course, Maarten Schmidt did a much better job, and it's now always attributed to him, and I think quite rightly. He did a much better job of getting this evolution, about a year later - much better data and more details. But we were the first to actually point out that quasars evolve, so I'm quite proud of that. But, it was Martin, not me.
This is what convinced you?
That's what convinced me.
Martin Rees, and some others, brings up an interesting question: You have been the advisor of a number of students who have gone on to brilliant careers. Can you tell me a little bit about your approach to advising students?
Let me first say, as I probably said in my last interview [with Spencer Weart], I always feel that I've been in a false position, particularly by being at Cambridge, and to some extent also in Oxford. We've had the best students in England, because of the structure in England. And so, if you have a very good student, you just sit back and let him go, and he does wonderful things, you see. So, that's what's happened in quite a numb~r of cases. My only role was enabling them to do relativity and cosmology. That required a certain structure and someone who is willing to take them on, but then they did their own thing.
Did you talk to them on a regular basis?
Oh yes. Well, let's say I'm the kind of person who suggests problems to people. A good example, actually, is Brandon Carter, who did some very important work on the uniqueness of the Kerr solution and other such things. I remember saying to him one day early on when he was my student - and he still remembers this and he says he's grateful for it — I said to him, "Brandon, why don't you do axisymmetric collapse. I think there is a lot of richness and interesting [things there]." And he went away and did axisymmetric collapse. [Sciama laughs] So, therefore, I provoked them a little bit in some cases. In Steve Hawking's case — as Steve himself has recorded now I think in his book and elsewhere for the first year or two he was struggling for a good problem. At that time, in the more relativistic side of cosmology, as distinct from astrophysical, there wasn't too much to do that was] high-class. Then in 1965, Roger Penrose produced the singularity paper — a bombshell, but for a star, a collapsing star. I know there are articles which credit me with saying one ought to look at the singularity theorems more generally. I can't honestly remember doing that. My memory is that Steve came to me one day and said "I can adapt Roger's arguments for the whole universe and get the singularity of the big bang." I said "Yes. Good. Do that." The last chapter of his thesis is his first singularity theorem. Although, in fact, in an article by George Ellis, Chris Clark and Frank Tipler, whom you may know, about the singularity theory, there is a footnote or something that says I insisted that people work on singularity theorems. Perhaps I did. I can't remember. But mainly, it's that they [my students] are gifted to that extent, and there are problems lying around worthy of their gifts, but "do-able."
Do you think about whether a problem is "do-able" before you suggest it to one of your students?
Well, I can't necessarily tell. In the case of axisymmetric collapse, it seemed to me that not much had been done on it. I think in the case of the uniqueness of Kerr, I can remember Hawking saying around the department, after [Werner] Israel's proof of the uniqueness of the Schwarzschild [solution], that we should be able to do Kerr. That probably helped Brandon — who was already in that area because of my original suggestion — but I remember Steve saying that. I don't think I would have had the technical understanding to see that it was do-able. So, I regard it as a matter of sheer luck that I've been associated in a minor way with all these students.
Let me go back to the 1950s again, when you were here among the young Turks — Bondi, Gold, and Hoyle and so forth — and the steady state was in the air. Can you tell me a little bit about the general attitude in the larger community towards cosmology — cosmology in general, not steady state in particular. How did people regard cosmology?
Physicists regarded it very badly, I think. Physicists generally, and in particular particle physicists, would have said that [cosmology] is highly speculative — everything is uncertain. They were very scornful. I remember Murray Gellman was once a visitor at Cambridge, and he came to dinner — it must have been in the mid-1960s — and he said to me "there has been no progress in cosmology since Friedmann in 1922." [Sciama laughs.] Generally, I think, it was then [regarded] as just speculation — not because of its intrinsic nature, but because of the lack of good observational evidence. [Cosmology] was not quite respected.
How would a general astronomer have regarded cosmology at that time?
I think an astronomer would not have had those particular feelings that the particle theorists did. Someone like Hubble was regarded as a great man. Astronomers would have been even more aware of the uncertainties of the data, but they would recognize it as a worthy enterprise, I suppose. The intellectual scorn was more characteristic of the particle theory-type of person.
What about an astronomical theorist who was not particularly aware of the observational problems?
An astronomical theorist would have been. Someone like Martin Schwarzschild, say, would have been enough of a general astronomer to know. Well, everybody tried to do things like decide the deceleration parameter, or even the value of the Hubble constant. It was known how uncertain those things were. But I don't think they would have felt, [not quite] the spite and the scorn, but the attitude that this was a low-grade activity that [is undertaken] by people who can't solve problems in particle physics. Astronomers didn't feel that because they were already astronomers. They might have had a few smiles at the passions with which cosmologists argued. But there wouldn't have been the contempt. I don't think contempt is too strong a word in those early days, among physicists. That changed, bit by bit, as the new era came in and particle physics [ideas] became important. Maybe we will talk about that later. [Things changed] particularly when, [for example, the physicists realized] that cosmologists could do much better than the particle physicists at restricting the number of neutrino types. All that came in later. Then they [the physicists] had to admit that maybe the cosmologists have got something.
Do you think that's when physicists began taking cosmology seriously?
I believe so.
Grand unified theories, and so forth?
Well, slightly earlier maybe than that, because the business of the number of neutrinos slightly predates that. That was perhaps the first sign that you could say something that couldn't be said just from particle physics]. A different example comes more from astronomy than cosmology, though it's linked up. Willie Fowler, who of course by now has won the Nobel Prize for nuclear astrophysics, came in to the subject through the influence of Fred Hoyle. It was partly the famous story about the level of carbon twelve. Here was Willie Fowler, a down-to-earth nuclear physicist at Caltech, being told by this madman that this crazy nonsense could tell him a specific level in a particular nucleus, which was only suspected to exist then by laboratory experiment. Then they do a careful experiment and find out it's there, bang on at the [predicted] energy. [Fowler] said, "it's fantastic that astronomy can do that." And it was taken seriously, and that was one of the major factors, plus the personal attitude, that brought Willie into the fold. Although that's astrophysics and not cosmology, there is a relation, because if you believe in the steady-state theory, you have to make heavy elements in stars. And that actually is one of the great selling points of the steady state theory. Now we know it's wrong. [But] it forced people like Fred to make elements in stars. That was very successful. So actually there is a link. The fact that Fred was studying that problem was directly due to the fact that steady state theory required [that elements be made in stars]. Do you know the old joke of Eddington about a hotter place?
In early days, people had vague ideas that the elements had to be made by high-temperature nuclear reactions, and Eddington must have had some kind of primitive theory of this long before the supernova theory of Hoyle. People said to him that the stars he was dealing with weren't hot enough to do this job, and he said "then go and find a hotter place." But, in fact, there is a direct link back with cosmology, so Fred was working on these problems because steady state required some hot place, not the big bang, to make at least the major range of elements like carbon, etc. Supernovae were the obvious choice. And then Willie came into it for the reason I said.
I wanted to switch gears a little bit and ask you about your reactions to some recent theoretical and observational discoveries. As background for that, let me ask you I first, do you remember when you first heard about the horizon problem, the causality problem, or thought about it on your own?
Just about, because the person who wrote the key paper on horizons is a great personal friend of mine, Wolfgang Rindler.
Yes, as I understand it [however], he didn't discuss the puzzle. He didn't raise the issue of why there is a problem with the current universe in that paper.
So, I want to ask you, when did you first hear that there was a problem with the current universe, that there are regions that are causally disconnected according to the big bang theory, and yet have the same temperature and the same properties, and so forth?
I do understand. I think that the answer to that question is that I am vaguely aware that [Robert] Dicke had raised that point, but it was not in the forefront of, certainly, my consciousness until Alan Guth's paper. Although the history of inflation is complicated. There were people before Guth, who now never get mentioned, and that, I think, is not fair. But then we are not discussing that.
We will in a moment.
Okay. I am not very well informed about the fine details, but we can come to that in a moment. As far as I'm concerned, it was, in practice, [Guth's] paper which emphasized that [the horizon problem] had to be taken very seriously. And the business about the flatness. In fact, it was the flatness, perhaps, that Dicke had referred to even more than the communication problem, the horizon problem. Maybe I'm getting them slightly confused. So, perhaps that was what I was referring to a moment ago...
Do you remember when you became aware of Dicke's discussion of that?
Well, I was vaguely aware of it because I knew him personally already by then — if only because of our mutual interest in Mach's [principle]. But it's not something I would have given a talk about or gone shouting about. It was just vaguely in my mind that he had said something at that time.
When you did become vaguely aware of it, did it worry you as a serious problem?
No, I don't think so. This was probably my concern with other matters or my lack of being smart enough to spot that it really was rather important. I would not have been in a position to say this is so important that I've got to tell people about it and worry about it. No. You're asking about me, and I'm not sure that I'm representative or not.
I'm just asking about you.
As far as I'm concerned, it was only very vague. I wouldn't have even known off-hand the formula you would use to show how the density parameter scales with time. I was just vaguely aware that [Dicke] had made some remarks that something was a bit worrisome. That's all that was in my mind.
You mentioned that you became much more aware of these problems [the horizon and flatness problems] after Guth's paper. When you read that paper, did you take these problems seriously in the sense that they were important problems that demanded solutions? How did you feel about them after Guth's work?
I do remember that I was a bit slow to appreciate the significance of what Guth had done — perhaps again because I had other things to attend to. When his paper came out, I glanced at it and I didn't say to myself, "ah, hah, here is a great breakthrough. Whether true or not we must attend to this thing." I didn't quite even know fully what it was all about. It was only a few months later, I suppose, when other people started talking a lot about it, that I said "ah, hah, I'm getting left behind, I better find out what this is all about." Then I either read his paper again or read something by Mike Turner or heard a talk, or something. I learned the stuff. I did my book work. Then, it all fell into place and I saw how potentially important it was. In fact, Guth came to the Royal Society in London for some meeting. He spoke, and at lunch I remember saying to him "do you realize that your inflationary epoch is just the steady state theory?" And he said, "What is the steady state theory?" He hadn't even heard of it. So that is just one of many reminders about culture gaps, or time gaps and culture gaps. So I explained to him the way the steady state theory worked. Even things now like the so-called "no hair" theorem, you see with de Sitter. Many, many of the ideas were just steady state, but only for this shortish [epoch], at this early time. I was very amused that it occurred in that way. Fred has recently tried to make more of it than is justified.
Yes, I saw a recent paper [of Hoyle's to that effect] in Comments on Astrophysics.
Yes. In that sense, I could understand what Guth had done.
Once you understood the horizon and flatness problems, or thought about them more deeply, did they seem to you to be serious, fundamental problems?
Yes. Now we get on to slightly delicate ground because there is still a bit of debate about these things, and I'm one of those who thinks that inflation is getting a bit oversold. I'm sure Roger Penrose talked to you about that.
I want to ask you about inflation separately in a moment, but I just wanted to ask you now about these two particular problems: the flatness problem and the horizon problem — whether or not inflation ever arrived.
Yes, I think they are genuine problems, and the reason we weren't all worrying about [them] is partly because until recently there were so few people in the field. What was worked on or worried about at that time was it very sensitive function of who happened to be in the field and what their interests happened to be. It's the same when you look at the history of cosmology and black holes, where rather strange views were peddled by top people like Eddington. They only got away with that because there weren't an army of technically equipped people to say the correct thing and push him aside. It's interesting when a subject depends for its development on so few people that it depends on their individual attitudes and what interests them. Whereas when hundreds of people do it, you very rapidly get a kind of streamlined view. Now, there is a whole army [of researchers]. For any new idea about particle physics, there are hundreds of people ready to apply it to the early universe. In those days there were only a handful of us, you see, and if this handful hadn't paid attention to these problems, then they weren't in the literature or currently debated. I think that's the reason. I suppose once they are thoroughly pointed out to you and your nose is rubbed into it, then yes, they are very important problems. Whether inflation has solved them or not is a separate, technical question. But clearly they are important problems.
Putting aside inflation, do you have any view as to how the flatness and horizon problems might be solved?
There's a third problem that's also very important — and I agree with Roger Penrose that inflation doesn't solve it — and that's the smoothness. It's related to the horizon problem. One argument is that the early wrinkles get pulled out by inflation. But that is not a correct argument. What inflation does, if it works well, is provides a possibility for a transport process being slower than light to equilibrate different regions and remove temperature gradients. And that was all that was claimed originally. Then there was a kind of shift of view that came in almost surreptitiously, [which said] that, in addition, inflation already does the smoothing out for you automatically, because of pulling out the smaller scales to larger scales. But if the small scales are very rough and they're pulled out to larger scales, the larger scales are rough. Or, to put it more mathematically, given any state now with a regular differential equation, there's some early state that matched it. This point had been made earlier, in fact, by John Stewart, about [Charles] Misner's mixmaster model. The same idea had been attempted: that, independent of the initial conditions, by mixing processes [you arrive at the present universe]. But it's strictly speaking not true. However, that's perhaps not what you wanted me to talk about.
That's certainly relevant. Let me ask you about inflation itself, since we have referred to that. You already mentioned the history. When the paper first came out, you were thinking about other things and it took you a few months to read it. What is your view about the inflationary model now, either in the original form or one of the derivatives of it?
Well, in the end I think it's turned out a bit disappointing. It was a marvelous idea. It had various difficulties, as you know. You referred to the various variants that were produced. It's now in what I call a Baroque state. There are so many variations, and there is no formalism, there is no reasonable grand unified theory and a cosmological formalism that gives a scheme that really does all that is required of it. There are many sub cases. Half a dozen people in the field have produced their own variations. A related question has also ended up rather disappointing, and that's baryosynthesis, which would occur, perhaps, just after inflation. Again, it was a glorious idea, and again it has not worked out in a kind of definitive way. There are many variations of the possibilities. Perhaps this is the nature of scientific research. I'm not saying therefore the idea is wrong, but it's a mess at the moment. I do think that it is oversold by some of the pundits, who no doubt find it an advantage to them, being a highly regarded theory, and it has all these virtues. I do have to say I think it's oversold. But it's still potentially a marvelous idea we just need more particle physics first, to get a grand unified theory that we might have faith in.
Let me ask you a sociological question: Why do you think that the inflationary idea has caught on so widely?
Two reasons, I suppose. One is the very elegant link with the most advanced questions of particle physics. Cosmologists like me are happy that particle physics plays a key role, but also the particle physicists enter the arena. And partly that [inflation] doubly delivered what it advertised. To some extent it does. It solves great problems. Those are two perfectly adequate reasons. Plus, it's not every day that there is a great new idea in cosmology. [There is the] fighting for recognition. So therefore people jump at it. And that's fine. It's only if then it's oversold, it's a shame. One ought to be rational.
Let me ask you about an observational discovery. Do you remember when you first heard about the work of Geller, de Lapparent, and Huchra on the bubble-like structure of the distribution of galaxies? That was a few years ago.
How did you react to that work?
I was very excited. That seems to me extremely important. I’ve talked to Margaret Geller about it. She visited Trieste where I work mainly now, and she spoke to the summer school I was organizing. She was saying quite rightly that the irregularities she's finding. [continue] to the largest length scale that she observes, and therefore why shouldn't it go on forever, and maybe the whole idea of a homogeneous universe is lousy.
How do you feel about that?
I said to her afterwards, over a meal, "look Margaret, there is one constraint that you have got to recognize, and that is the isotropy of the microwave background. If you put too much irregularity on too large a scale you conflict with that, and that's therefore an overall constraint, although it doesn't come in at 100 megaparsecs."
Unless our interpretation of that is wrong.
She said "what would you do if we go on making the studies, and we keep finding this effect, let's just say out to 1,000 megaparsecs?" I said, "Well, that would be the most devastating thing in physics and astrophysics. I don't know what I would do." There is no obvious, easy way out. To say we've totally misinterpreted the microwave background ... We considered that in the early days. There were jokes that if it's so isotropic, that's because your box which is measuring the thing is isotropic. But by now, it would be very, very difficult to reconcile a bumpy universe on a scale of 1,000 megaparsecs with the isotropy of the microwave background.
Does that worry you? Did that worry you?
No. I therefore feel confident that the universe has to smooth itself out on that scale. Obviously you can ask me a hypothetical question: "What would you do if it didn't?" But that would just be a crisis in physics. It's silly to speculate.
No, I don't want to ask you that hypothetical question. I would rather ask you about what your attitude is right now about the thing.
Well, my attitude is that it's an extremely important discovery because, of course, galaxy formation has to be understood. And it's related to the nature of the dark matter that we haven't talked about — how galaxies form and so forth. It was totally unexpected from a theoretical point of view. Therefore, it's a very, very important scientific discovery.
I gather from what you have just said, though, that it doesn't shake your belief in the large-scale homogeneity.
Well, fortunately, up to the scale that's now been found, it wouldn't conflict with the isotropy, although it's interestingly coming close to it.
A factor of five or six or something [in distance].
That's right, and there are plans afoot to improve the measurements of the isotropy another factor of ten. If they don't find anything then, that would also be worrying, even from other points of view. Just structures you can see in the sky would then work at the one in a million level. Therefore, I'm confident they will find something. I think that's reasonable. But if not, then we will have this crisis. So, I just have to suppose that they have almost reached the limit [where the two types of observations are consistent]. It's a numerical matter. Obviously, there is some lumpiness on the scale of 1,000 megaparsecs. It's a matter of the numbers. But I would suppose that you wouldn't find the same effect [inhomogeneities in the distribution of galaxies] at a much larger scale. Perhaps a bit larger, but not ten times larger. So, I'm not worried about this. I'm very much excited because it's got to be understood.
You mentioned the dark matter. I guess there are two kinds of dark matter: there is the dark matter that we know is there, that takes omega from .01 to .1; and then there is the missing matter that would have to be there if inflation is right, that takes omega from 0.1 to 1. What is your belief in that range of possibilities?
Well, as a matter of fact, there is an argument going on at the moment between two of my old students, — George Ellis and Martin Rees — as to whether inflation does require an omega of 1. That's a rather technical matter, and I don't want to go into that. But the statement that [inflation] requires omega close to 1 is at least up for argument.
But let us suppose for the purpose of this discussion that inflation does require that. Then, of course, we have to identify that matter. But we still [also] have to identify the matter in galactic haloes. If you are just asking me about my view of the present position, I don't have a particularly individual view. We all agree that any proposal made never seems to work out quite nicely. In fact, just recently, with some colleagues, I have shown that a particular candidate can probably been ruled out because of the supernova in the Magellanic cloud. This is the case of certain super symmetry particles, like photinos, if they have low mass, like 100 eV or something. They've been very seriously considered as candidates [for the missing mass]. I liked [those particles] for various reasons, such as when they decayed and made photons, these photons might show up in astronomy. I've written a number of papers about that recently. But we've just shown that the neutrino data from the supernova and the energetics involved in that and in the neutron star that formed in the supernova — using the very latest ideas about the coupling between photinos and nucleons — can rule out the existence in nature of these [hypothesized] low-mass photinos. Otherwise, the supernova would radiate more energy than it could tolerate in that form. So that's a particular candidate that's gone. Then, of course, with the recent upper limit on the electron-type neutrino mass, both from the lab and from the supernova, [that neutrino] almost certainly can't be responsible [for the missing mass]. There are still candidates left, but I think perhaps the best candidate is the tau-type neutrino. Or a GeV mass photino.
Something that we have the least data on.
Well, strictly speaking, I believe that neutrino hasn't yet been detected, although there was a claim from CERN some while ago that, at last, it had. But I think that claim is not substantiated. I'm not seriously suggesting that it doesn't exist. Anyway, it's certainly not clear.
I gather that since you're not necessarily a strong proponent of inflation, you are not convinced that this missing matter has to be there.
With an omega of one?
Yes. I don't want to state your position; I'm just trying to understand it.
No, I take inflation very seriously. I was only saying — it's an objective fact, I think — that the theory is in a bit of a mess. That is objective. But some form of inflation may very well be correct. It's a marvelous idea. Whether it requires omega as 1, I'm still trying to join in this argument with my colleagues, and I'm not completely sure. I don't want my view to go on record, with two of my good friends next. No, seriously, if there were a decisive argument I would accept it. And, linking with our earlier discussion, since I can no longer claim that [the universe] has to be Einstein-de Sitter [flat] because of Mach, there is no requirement for omega being one. Therefore, it is an open question. Of course, there might be other reasons we don't yet understand why omega equals one. It's a nice thing from the point of view of theoretical physics. So I would be very happy with an omega of one on these vague grounds of fundamental theoretical-physics. It's great fun looking for a form of the dark matter, although equally you have to worry about galactic haloes anyway.
Yes, we know that's there.
We know that is there even though, in that case too, it's sometimes been slightly exaggerated how much there is. But I think even the skeptics agree that there is some [dark matter] there. We have to make this identification [of the dark matter], and that's still an unsolved problem. It's very embarrassing.
How do you feel that theory and observations have worked together in modern cosmology, let's say in the last 15 or 20 years?
I think extremely well. One example, which I mentioned, is this business about the number of neutrino types. It fits almost too well. If you take the present abundances of the helium-4 and the other light elements and do the theory of it and so on and worry about the neutron half-life, which isn't quite as well in line, you still find that you are only allowed three or four neutrino types. Whether it's 3 or 4 even depends on what you take as the errors of the observation. In particular, a very good friend of mine, Bernard Pagel, who has got the latest measurement of the helium abundance, puts a very low error on his work - and is, perhaps, a little optimistic about that — but he insists that you can't even have 4 neutrino types. Also, you can't have a low mass photino, unless there are tricks for suppressing it. If you don't suppress it, you can't even be allowed that. When this was first realized, the best limit from the lab on the number of neutrino types was several thousand. Now, with the data from CERN on the Z0 particle, it's down to about five. But that, by the way, was one of the things that, I believe, made the particle physicists take cosmology seriously — the fact that we could, ahead of them, make a very stringent constraint on this number. We really stuck our neck out, and then when they do the necessary experiment with their best equipment they get the same result. Now amazingly, as I am sure you know, the supernova, from the same kind of argument about how much energy is emitted, limits the number of neutrino types to perhaps five or six. So all this involves observations of all different kinds — both particle physics and astronomical. It all fits together. I think that's very remarkable. I don't know if that is the kind of thing you had in mind when you asked me. It's not the same as things like great big bubbles and so on, but it's a cosmological thing which involves a variety of arguments — from measuring helium abundances in compact galaxies, to measuring the half-life of a neutron, to measuring things about the Z0 particle, to measuring neutrinos from a supernova. Everything fits together in a consistent way.
Let me ask you this. Some of modern cosmology in recent years has extrapolated backwards in time to very close to the big bang. What is your attitude about those theoretical extrapolations? Do you think that they are justified? Do you think that's a good way we should be working right now in cosmology?
Well, I think asking "is it justified?" is not quite the same question as "is it a good way to proceed?" I think it's a good way to proceed, because we have got to proceed in some ordered way. Justifying it would mean I can try and argue and say you've got to do this. Clearly you can extrapolate back to the [period of] nuclear reactions. I know that you are talking about much earlier.
Much earlier, yes.
And it's clear that if, say, Linde's ideas are right, where you get these different domains and so on, you might not extrapolate the simplest Robertson-Walker system right back to a very early [time]. But that's part of this kind of theory — whether this domain structure occurs or not. You can't say, "Okay, things got hot enough to make helium, but we won't discuss what it was like when it was hotter or denser." You've got to extrapolate back. Something unexpected or something you overlooked may occur, but this is the nature of the business, at least in astrophysics and cosmology. You proceed by making a natural extrapolation unless you have a strong reason for not doing so. Steady state would say I have another reason, which I bring in, which prevents me going to the densest state, but then if you have a good point to make you are allowed to consider that as an alternative. If that is not present, then of course you would say density, temperature, time relations are so and so in the simplest models; they would imply such and such parameters in the early stages, and that's important to the particle physics. So all that must be done. If you can actually find an explanation of why there is more mater than anti-matter in that process, it's fantastic. Clearly one must proceed that way.
You have mentioned some of this already, but let me ask you what you consider to be the major outstanding problems in cosmology right now?
I suppose it depends a bit if you are more interested in astrophysics or fundamental physics. For your fundamental physics — and I'm only saying what everybody says — the essential vanishing of the cosmological constant, because the grand unified theory type of discussion will rather naturally throw out a cosmological constant of 10120 times bigger than any value you have astronomically. With the possible exception of last week's paper on superstrings, which attempts to claim that their particular model gives you a zero cosmological constant, it's completely not understood why that fine tuning occurs. So I think — and I agree with what everybody says — from the point of view of fundamental physical theory, the [problem in] cosmology that is the most glaringly obvious and outstanding is [the question of the vanishing of the cosmological constant]. If you think more astronomically, there is a clutch of problems. Some of them are quite old, like is the universe going to expand forever or collapse or what? That is clearly still not settled. The nature of the dark matter is not settled. The way galaxies form is not settled. We don't even know, observationally, the ultimate scale of [the universe]. I would have said all of those are important problems. Plus the problems that inflation aims to solve. I don't know that there is one outstanding problem. That whole group of problems would be high on everybody's list. In the case of the cosmological constant, one could say that fundamental physicists would feel that is the key. The fact that they can't explain as simple a thing as that means that their grandest theories are still hopelessly missing something, in spite of all the things they might do. But, astronomically speaking, this whole set of problems is about equal in importance. I think most people would say the same.
Let me end with a couple of philosophical questions. Here you might have to put some of your scientific caution aside a little bit. If you could design the universe any way that you wanted to, how would you do it?
Can I first answer evasively? I have a view, which I am giving a talk on here in Cambridge in a couple of weeks, and I talked about at a meeting on the anthropic principle. I have a view which by-passes that question. So let me explain it to you, very briefly. The problem of course, as the phrase anthropic principle indicates, is that the universe has to be very fine-tuned to bring about the possibility of intelligent life and human beings, or if you like, myself. That is probably not controversial at all. The controversy is: what is the significance of that [statement]? Very rapidly, there seem to me three possibilities. The one I favor relates to your question. The first is just chance, which I think is really unpalatable. You can't disprove it. The second is purposiveness, or God or something. God exists and regards us as the highest point of creation. He wants us to come about, so he fine-tuned the universe to make jolly sure that we came about. And I find that unpalatable, although many people accept that. And then there is the third proposal, which I didn't invent, but I favor very much. Incidentally, Brandon Carter, when he was working with me, did one of his early, very influential things on the anthropic principle. [According to this third proposal], there are many disjoint universes, where the laws and constants of nature are different from one to another. In fact, I would put it even stronger: any logically possible universe exists, not just for anthropic reasons. Of course the anthropic theory clearly [leads just to the type of universe] we're in.
Yes, the anthropic principle singles out the universe we're in.
And the whole problem is trivial. But there is another reason why I favor all these universes. People might say to me, "what about Ocam’s razor? You're crazy." But, on the other hand, I believe that [this third proposal] in a sense satisfies Ocam’s razor, because you want to minimize the arbitrary constraints which you place on the universe. Now, if you imagine all these logically possible universes, then you've got to think there is a committee, or maybe just a chairperson, who looks at this list and says "well, we're not going to have that one, and we won't have that one. We'll have that one, only that one." Now, that could have happened, but it seems to me a remarkable thing that that happened. It's much more satisfying to say that there is no constraint on the universe. All logically possible cases are realized, and we're in one of the few that allow us. So, that's not quite answering your question, but I prefer to say it that way.
That is an answer. Let me ask you this question: It could turn out, could it not, that when we find a theory of everything — if such a theory is possible — we will discover that there is only one way that the universe could have been formed, consistent with most general notions of relativity theory and quantum theory. That is a possibility, isn't it?
I would put it slightly differently. In my view, relativity wouldn't hold in some of these universes, or quantum theory wouldn't hold, as long as they're logically possible. Now there is a possibility, which is an extension of what you have asked and which I believe Spinoza advocated, which is that there is only one logically possible universe, period.
If that were the case, then one wouldn't have all these different branches involved with your third possibility.
That's correct. I mentioned that in an article I've written on my talk at Venice, so I recognize that that would be a very attractive [possibility] in a way, and yet it doesn't solve this problem, because it's still puzzling why the one logically possible [world] should be just the one that has the fine-tuning that leads to us. That is still unexplained, although it is possible that there is this unique case, right?
Yes, so that would then go into the same as your first category: that [our universe] is an accident.
Yes, it's still an accident that the one logically possible case has this very remarkable structure — that doesn't seem to be part of what goes into showing that it's logically possible.
So you prefer the third possibility? I asked you which universe would you design. You would prefer the third case, where there are many different logically possible universes and there are no constraints, and we happened to be in one of those that allows life.
Could I add [something], in case you or anyone would think that this is an untestable proposal. It's not like Linde's chaotic inflation. He has something a bit like that, but where [the regions with different physical properties] are all part of this universe. [In the possibility I have mentioned], these would really be disjoint universes. So people might say, "If it's disjoint and there is no way you get a message from it, what are you talking about? It's empty." Now, the whole point is it's not empty, and I make a prediction which is testable. So let me just explain this very rapidly to give some sort of [idea].
Go ahead. I want to check the tape, but I have another, so talk as long as you wish.
Except that we ought to go for coffee at some point or I will fade out. Let's consider all the cases which do lead to me. Now we would not expect that we're in a very special one of those. All I know is that I exist, and I'm happy enough with that. If the universe is unique, however, you might expect a very special initial condition, and Roger Penrose and differently Steven Hawking have both made proposals for the special initial conditions, which I'm sure you know.
Now my view, or my prediction — and I'm very proud of this sentence which more or less ends my talk — my prediction is that Penrose is wrong and Hawking is wrong, because if there are these other universes, and ones very close to ours, equivalent to ours, then we should be in a generic universe of the set that could lead to me. Therefore, I would not expect a beautiful, elegant, mathematical ersatz, like the Penrose one or the Hawking one, to apply to the initial universe. The initial conditions would be messy, but not too messy, or I [life] wouldn't emerge. But a bit messy. Therefore, when you do a measurement, in principle, of the initial conditions — and in Roger's case you can even make it the isotropy of the background because his statement that the Weyl tensor vanishes at the origin of the universe makes the universe isotropic, and in Steve's case it may be a bit more complicated — I would predict them to be messy, and not describable by a simple, mathematical, elegant statement.
You would predict that [the initial conditions] would be as messy as possible and still allow life.
Of course, to make real sense of that you need a measure theory of metrics, and that measure theory is very difficult and hasn't yet been achieved, so I can't do a technical job on this at the moment, but the fact that I make a physical prediction means that there is physics in my proposal. It's not just empty metaphysics.
If you have a measure of what messiness is and uniqueness is and what a generic metric is, and all of that, if you can make some quantitative measure of that.
That's right. So if you measure the early anisotropy and it's so and so — delta T over T is some number — does that favor me or [Penrose].
You would also have to know what range of anisotropy would allow life, to know whether you have the generic amount of anisotropy, which you are sort of in the middle. Let's suppose that at the Planck time, delta T over T has to be less than a certain value to allow life. You have to know what the value is.
So you are saying that in principle, what you are saying is testable.
That's good enough for the moment. My proposal, therefore, is a proposal of physics. That's the idea.
There is a place in Steve Weinberg's book, The First Three Minutes, where he says that the more the universe seems comprehensible, the more it also seems pointless.
Have you ever thought about this question of whether the universe has a point?
I have thought about it, and I can't think of any point it has. It's the old question about why there is something rather than nothing. In fact, Sidney Coleman has written a recent paper called “Why there is Nothing Rather than Something”, referring to the cosmological constant. If you're going to have some logically possible cases, even one, you ought to have the whole lot. But why have any? I find that quite inscrutable. Of course, the very concept of a meaning is perhaps too anthropomorphic. I don't know. But I have nothing to contribute to that. Obviously I have thought about it, but I have nothing to contribute.
Your explanation number two for your anthropic idea was not unrelated to this.
But it doesn't really explain. I'm allowing that when I talked in Venice, I permitted that as a conceivable explanation. In fact, it was a Jesuit astronomer who spoke after me, and he said "I am prepared to have all Sciama's universes. I don't mind that these days. But there is God in all of them." But as far as I'm concerned, I'm afraid — and I'm not a professional here — the word "God" is just a word. When this Jesuit spoke after me, he knew so much about God. It was amazing. God was a person, he said. So we have to say "he," "she" or "it," because those are the only personal pronouns in English — not just that God was some force that made the world, it was a person. How can he possibly know such things? It's ridiculous. As far as I'm concerned, it's just a word, and I sometimes argue with my friends and I jokingly say, "Suppose I asked you does the "spongula" exist?" In other words, using a word doesn't mean that there is something that correlates with it. If you had — and this is a schoolboy argument — if you had a concept of something that made the world, and it was needed in order that the world be made, then who made that person or thing or whatever it was, and so on. These are old, standard arguments, but they still have force as far as I'm concerned. It's true that people have, internally, a religious feeling, which they use the word God to express, but how a feeling inside of you can tell you that a thing made the whole universe? There is no relation between the two matters of concern. Therefore, while I'm prepared for and I can't rule out that there is another order of structure than ordinary matter, I know nothing about that order. There could be many orders, and so on. Therefore, the word God just doesn't denote any structure.
That's a good place to end the interview.
 e.g. A.S. Eddington The Expanding Universe (New York: McMillan, 1933); The Internal Constitution of the Stars (Cambridge, 1926)
 e.g. J. Jeans Astronomy and Cosmogony (Cambridge, 1928); The Universe Around Us (New York: McMillan, 1929)
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 Interview of Dennis Sciama by Spencer Weart, April 14, 1978, Sources for History of Modern Astrophysics, American Institute of Physics, New York
 H. Bondi and T. Gold, Monthly Notices of the Royal Astronomical Society, vol. 108, pg. 252 (1948); F. Hoyle, Monthly Notices of the Royal Astronomical Society, vol. 108, pg. 372 (1948)
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 D.W. Sciama, "On the Origin of Inertia," Monthly Notices of the Royal Astronomical Society, vol. 113, pg. 34 (1953); "Inertia," Scientific American, vol. 196, no. 2, pg. 99 (1957)
 D.W. Sciama, P.C. Waylen, and R.C. Gilman, Physical Review, vol. 187, pg.1762 (1969)
 D.J. Raine, Reports on the Progress of Physics, vol. 44, pg. 1151 (1981)
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 See Ref. 5.
 H. Bondi, Cosmology (Cambridge: Cambridge University Press, 1952)
 D.W. Sciama, The Unity of the Universe (Garden City: Doubleday, 1959); The Physical Foundations of General Relativity (Garden City: Doubleday: 1969)
 See Ref. 15.
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 D.W. Sciama, "On the Origin of the Microwave Background," Nature, vol. 211, pg. 277 (1966)
 M. Schmidt, "Space Distribution and Luminosity Functions of Quasi Stellar Radio Sources," The Astrophysical Journal, vol. 151, pg. 393 (1968)
 See Ref. 4.
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 Editor's Note: Sciama may be confusing his earliest recollections of the horizon and flatness problems here. Dicke did, in fact, discuss the horizon problem in R.H. Dicke, Gravitation and the Univerae, The Jayne Lectures for 1969 (American Philosophical Society, 1969), pg. 62; and in R.H. Dicke and P.J .E. Peebles, "The Big Bang Cosmology — Enigmas and Nostrums," in General Relativity: An Einstein Centenary Survey, ed. S.W. Hawking and W. Israel (Cambridge University Press, 1979)
 A. Guth, "Inflationary Universe: A possible solution to the horizon and flatness problems," Physical Review D, vol. 23, pg. 347 (1981)
 R. Brout, F. Englert, and P. Spindel, "Cosmological Origin of the Grand-Unification Mass Scale," Physical Review Letters, vol. 43, pg. 417 (1979); A. Starobinsky, JETP Letters, vol. 30, pg. 682 (1979); A. Starobinsky, "A New Type of Isotropic Cosmological Models without Singularity," Physical Letters, vol. 91B, pg. 99 (1980); D. Kazanas, "Dynamics of the Universe and Spontaneous Symmetry Breaking," The Astrophysical Journal Letters, vol. 241, pg. L95 (1980); M.B. Einhorn and K. Sato, "Monopole Production in the Very Early Universe in a First-Order Phase Transition," Nuclear Physics B, vol. B180, pg. 385 (1981)
 Dicke referred to the flatness problem, as well as the horizon problem, in the articles in Ref. 32.
 F. Hoyle, "The Steady State Theory Revived," Comments on Astrophysics, vol. 13, pg. 81 (1989)
 C.W. Misner, "Mixmaster Universe," Physical Review Letters, vol. 22, pg. 1071 (1969)
 A.D. Linde, Physics Letters B, vol. 108, pg. 389 (1982); A. Albrecht, and P.I. Steinhardt, Physical Review Letters, vol. 48, pg. 1220 (1982); A.D. Linde, Physics Letters, vol. 129B, pg. 177 (1983)
 V. de Lapparent, M.J. Geller, and J.P. Huchra, "A Slice of the Universe," Astrophysical Journal Letters, vol. 302, pg. L1 (1986)
 J. Ellis, K.A. Olive, S. Barker, and D.W. Sciama, "Low-Mass Photinos and Supernova 1987 A," Physics Letters, vol. 215B, pg. 404 (1988)
 e.g. D. W. Sciama, "Photino Decay and the Ionization of Lyman ex Clouds at Large Redshifts," Monthly Notices of the Royal Astronomical Society, vol. 230, pg. 13p (1988)
 A.D. Linde, Physics Letters, vol. 129B, pg. 177 (1983); see also A.D. Linde "Particle Physics and Inflationary Cosmology," Physics Today, September (1987) and references thererin.
 B. Carter, unpublished Cambridge University preprint (1968); first published in Confrontation of Cosmological Theories with Observational Data, ed. M.S. Longair, IAU Symposium 63, Cracow (Reidel: Dordrecht 1974)
 in The Anthropic Principle, ed. F. Bertola and U. Curi (to appear, Cambridge University Press)
 See. Ref. 42
 R. Penrose, "Conformal Treatments of Infinity," in Relativity, Groups, and Topology, ed. C. DeWitt and B.S. DeWitt (New York: Gordon and Breach, 1964); R. Penrose in General Relativity: An Einstein Centenary Survey, ed. S.W. Hawking and W. Israel (Cambridge University Press, 1979); S.W. Hawking, Pontificae Academiae Scientarium Scripta Varia, vol. 48, pg. 563 (1982); J .B. Hartle and S.W. Hawking, Physical Review D, vol. D28, pg. 2960 (1983); S.W. Hawking, Nuclear Physics, vol. B239, pg. 257 (1984)
 S. Weinberg, The First Three Minutes (Basic Books: New York, 1977), pg. 154
 S. Coleman, "Why there is Nothing Rather than Something: A Theory of the Cosmological Constant," Nuclear Physics B, vol. 310, pg. 643 (1988)