Interview with James Pebbles
How did your journey in physics start?
What motivated me was simply that I enjoyed physics. I went to Princeton University in 1958 as a graduate student and observed the research of Robert Dicke, who had recently turned to the study of gravity physics. I thought that what his work was interesting, so I decided to do my PhD thesis with him in aspects of gravity physics, rather than theoretical particle physics, which was my first interest. Cosmology later became my field. In 1964, he raised the idea that a hot Big Bang might have occurred and that the thermal radiation from this explosion might be detectable. He suggested that two people in his group (David Wilkinson and Peter Roll) should look for this radiation and asked me to consider the physical implications of detecting or not detecting it and cover as many of the different scenarios as possible. That was actually my introduction to cosmology.
I felt very uncomfortable about the modest experimental evidence in support of any cosmology theories. I did not think I would spend much time in this field, but, surprisingly, kept finding things to explore during my entire career.
Do you remember when it was that you got interested in cosmology in particular?
Yes, I guess I can pretty definitely date that. This was the famous idea of Bob Dicke's to look for the microwave radiation left over from a hot big bang. I can't give you a year. I took no notes. He probably could tell you. It would be around 1964. It was in the summer, I do remember — a very hot day. We met in his usual evening group, but with a small number of people. I don't remember why, perhaps because it was the summer. For some reason, we met in the attic [in Palmer lab]. It was really ridiculously hot, I remember. He explained to us first why one might want to think that the universe was hot in its early phases. I don't know how widely this is described, [but] his thought at that time - and one that he does keep returning to — is that the universe might oscillate.
What was the general environment in which these ideas and theories emerged? Was it easy to adopt the idea of a hot Big Bang?
At that time, general relativity and cosmology were not widely studied, though research was increasing, largely as result of Dicke’s efforts. Let’s say cosmology was the field of only a small group of people and I was not really aware of their work, partly because I studied cosmology from Landau and Lifshitz’s Classical theory of fields, in which empirical evidence is not discussed.
So were General Relativity and cosmology dominated by theory at that time?
Yes, most of the research in the field was theoretical. There was the work by Alan Sandage. and others in Astronomy, mapping galaxies, measuring redshift distance and the Hubble constant, but very little work on what I would call physical cosmology, which was the title of my first book.
The circumstances seemed ideal for junior researchers like me, as there were few international conferences and we were the primary actors in cosmology. I did not have competition or criticism by many of them, because we all worked on different topics.
Did you also feel some loneliness in the field because of the small number of researchers?
I didn’t feel lonely but rather uneasy due to the very modest level of evidence. Around that time, I started wondering why is it that other people don’t work in the field. For me, the situation was simple and straightforward: I could think of interesting ideas and I pursued them. This was a unique freedom that we could enjoy as early researchers in the field.
What do you think was a critical moment when the situation changed?
I don’t believe that there was only a single step — a critical discovery that suddenly made cosmology relevant. I can think of many steps and clearly one of the most important during my career was the detection of the cosmic microwave background (CMB) radiation that immediately attracted attention. At this point, I must say that I am not sure why a previous discovery, the detection of a significant helium abundance in our Milky Way galaxy that could be a remnant of the Big Bang, didn’t get this amount of attention.
In any case, it was the detection of CMB that shed light on the field; it attracted experimentalists, who were interested in measuring the properties of this radiation, and theorists, who joined me in analysing the implications. However, cosmology remained a small field.
The next big step was complicated. By the 1970s we knew that the spectrum of this radiation is very close to the theoretical thermal spectrum at long wavelengths — the so-called Rayleigh Jeans part of the spectrum. But in the 1960s and for the next 20 years there was evidence of an excess of radiation beyond thermal radiation at shorter wavelengths. For this effect to be real, one would have to admit that there was violent activity in the early Universe that added radiation at short wavelengths.
This violent activity would have quite disturbed the spatial distribution of the radiation and, therefore, the present angular distribution of the radiation could not be easily interpreted. This situation discouraged me from working on many aspects of cosmology through the 1970s. Instead, I turned to another field, the characterisation of the spatial distribution of galaxies and their motions, as it allows us to explore and make inferences about the how structure grew in the Universe, and how much mass was involved.
Indeed by the 1980s. I was convinced by the evidence that we don’t live in an Einstein–de Sitter Universe, as was previously the “prejudice” of most people, including me. The next big event in cosmology was the demonstration that the spectrum is in fact very close to thermal. That happened near the 1990s thanks to the hard work of two groups: the US NASA COBE mission, a brilliant result for which a Nobel prise was given, and a group from the University of British Columbia in Western Canada led by Herb Gush, an equally brilliant result that did not receive as much attention. Both experiments took 15 years of work for completion and yet they got similar results within months. It is also important to notice that once you are confident that the spectrum is thermal, you can infer that the radiation has not been very disturbed since the early Universe. In this case it is interesting to analyse the processes in the early Universe that were the seeds of cosmic structure formation might have affected the angular distribution of the radiation. We had fierce debates over how the departures from the an exactly smooth distribution of this thermal radiation might have occurred In the 1980s and 1990s, there were heated discussions over what were the initial conditions in the Universe that lead to the formation of galaxies. The answer would depend on more precise measurements of the CMB radiation distribution.
By 2000 we had several experiments, including the WMAP (Wilkinson Microwave Anisotropy Probe) measurements, that convinced everyone that a particular type of special initial conditions existed. Still, there was a lot of resistance to the idea that the Universe was not Einstein–de Sitter, but we finally ended up with dark matter, not Einstein–de Sitter.
Why was the idea of an Einstein–de Sitter Universe so persistent?
First of all because an Einstein–de Sitter Universe is the simplest of all: it has only matter and radiation, no space curvature, no cosmological constant. Its evolution is very simply an expansion that is a power of time depending on the amount of matter and radiation. Many people believed that the cosmological constant is quite ugly and wondered why we should involve hypothetical dark matter.
The prevalent opinion in the 1980s through the 1990s was that the solution to Einstein’s equation describing the Universe must be Einstein–de Sitter and people went to great lengths to reconcile it with the growing evidence to the contrary.
For a few years, I enjoyed pointing out to my friends and colleagues the weakness of their case for the Einstein-de Sitter cosmology, based on my measurements of the motion and distribution of the galaxies.
The transition from from general acceptance of Einstein–de Sitter to the Standard Model (Λ-CDM) followed two steps. First, there was the acceptance that we need non-baryonic matter (gas or other material with negligible pressure and negligible interaction with other matter). This was introduced in the early 1980s and was welcomed by many, as it resolved the great puzzle of how the Universe can such a strongly clumpy matter distribution, but such a smooth radiation distribution. I pointed to the idea of non-baryonic, non-interacting dark matter that could reconcile the two observations.
Second, the acceptance of Lambda, which in GR allows the low mass density the observations were indicating with a cosmologically flat universe that the inflation concept favors. The SNeIa redshift-magnitude relation pointed to Lambda., and not long after so did CMB anisotropy measurements with the astronomers’ distance scale.
Once of course you introduce the notion of colliso-nless initially cold non-baryonic matter, then you may ask how the galaxies were formed. There were at the time other ideas to explain that, but dark matter had a great attraction, as it was conceptually simple to set up numerical simulations to follow its distribution and create models for the formation of structures or galaxies.
I must say that I felt uneasy with this popular line of approach, because I considered dark matter as just one way to reconcile the clumpy distribution of matter with the smooth distribution of radiation. I could think of other ways to do it; perhaps less elegant, but still conceivable, such as cosmic strings, isothermal initial conditions, rather than adiabatic or even interactions involving self-interactions in the dark matter sector.
In the late 1980s, several models were considered . Consider that there is only baryonic matter but with an initial power spectrum that is very different from Chandra. I started working on models that could explain this observation. I gave up in 2000, when good measurements of CMB from WMAP supported the cold dark matter model. The community soon agreed that we need dark matter.
However, the cosmological constant debate continued: the options of the early 2000s were either that space sections are curved or that there is a cosmological constant. Both possibilities were not welcome.
The way around that, for which I had argued a lot earlier, was to learn to live with Λ (that was the title of many colloquia I gave around that time). It wasn’t appreciated, but eventually the community did learn to live with the cosmological constant in the late 2000s, especially following the observation and supernova redshift magnitude and the power spectrum of galaxy distribution that didn’t fit at all well with an Einstein–de Sitter Universe.
The idea of inflation also had a significant influence in the debate. A Universe with curved space sections seemed so ugly that the opinion shifted in favour of the cosmological constant. The later observations of anisotropies in the CMB spectrum in the recent mission show that the Λ-CDM model is a remarkably good approximation to the real world.
You mentioned that the cosmological constant, dark matter, and inflation were conceived as ugly. What do you mean by that? What is the place of ugliness in a physical theory?
I think the reason I suggested the existence of cold dark matter, although I was uneasy with this concept, was that I always paid more attention to observations than most of my colleagues.
For example, in the early 1980s, I showed accumulating evidence that the mass density is less that the Einstein–de Sitter prediction. One had the choice of arguing that the evidence we had was insufficient or stick to them and try to understand their implications for our description of the Universe. The community by large decided to ignore it; a decision that was understandable at that time. I decided to overcome the criteria of ugliness and, despite what would seem as the natural intuition, to continue my theoretical work to see what the evidence suggested.
Why space curvature is considered ugly? I think largely because it’s not indicated by the inflation scenario
Why is Lambda ugly? In the 1950s because it seemed to be an unnecessary appendage to an elegant theory, and through the 1990s because natural estimates of the quantum physics indicate ridiculously large values of Lambda, and the reasonable-looking hypothesis was that some symmetry to be discovered forces Lambda = 0..
Do you accept this whole idea of extrapolating our theories back to the first few seconds or so of the universe?
It's awfully brave, isn't it? On the other hand, it worked so wonderfully well with nucleosynthesis — unless, of course, it didn't. Perhaps it was an unfortunate accident that the naive calculation worked so well. Perhaps these ideas we heard today at lunch are right, and indeed the heavy elements were made by conventional physics, only slightly modified when the universe was only a few minutes old. In that case, the present observations are to be reproduced not in the naive way, by ignoring any new processes operating back then, but through a combination of different parameters and a little new physics –- such as decaying inos or inhomogeneities in the neutron distribution — that led by another route from the standard nucleosynthesis calculation to the observed abundances.
I could imagine that happening. And, of course, if you can imagine that happening, I guess you can imagine that physics back then was wildly different from what we suppose, and by some other accidental route we ended up with the observed abundances. I guess I'm loath to think that the universe would have been so unkind as to give that a possible chance. I guess I feel fairly comfortable with the notion that the physics of the universe when it was one second old can be traced back from the physics of the present epoch. It seems at least a reasonable possibility. If we go back another factor of 1010 in expansion to approach the epoch of inflation, then I feel very skeptical that we can know enough physics to be very confident in predicting what can have gone on.
I have no idea how that situation can be improved, because now we're talking about energies that are reached only in the most energetic cosmic ray events, 1020 volts. So it's going to be very difficult to have an experimental check of physics of those energies. Actually one nightmare I can imagine is that as particle theory advances, particle theorists will hit upon a convincing story - convincing to them — of high-energy physics from which they derive a cosmology of the early universe, of which there are no observational tests, aside from the standard ones that, say, the universe is homogeneous. We knew that already, so it's not really a prediction. Or that space curvature is negligibly small. Well, we didn't know that already, but a lot of us were hoping it would be true. So, if out of this complete theory of particle physics and complete theory of the early universe, we get no predictions other than things we already knew or were hoping for, will we be entitled to think that we have a physical theory here? How will we know it's right? It would be very frustrating.
The observations point to a physical reality or to a description of a reality?
We all work on the assumption that there is an objective reality, which we can discover in successful approximations. No one has issued a guarantee that it exists, but this implicit assumption has prevailed for centuries.
I think that on occasion we should remind ourselves that we assume there is a reality to be discovered, without brooding over it, as it is a wonderful and very productive assumption.
During all these steps that we reviewed, what was the role of developing new instruments?
The role of technology in the natural sciences, or curiosity-driven science if you like, is very important. Astrophysics and HEP experiments that take place today thanks to the latest exciting advancements wouldn’t be possible few years ago. Our understanding of nature has advanced in step with technological developments.
It is also the case that some of these advancements may be used for other purposes, so funding for research should concern society as a whole.
Instruments such as the arrays of technologies in BICEP or LIGO, or the high-tech detectors used in the LHC experiments and its upgrade phases are essential to scientific progress. This expensive technology requires support from the governments. There is always intense competition for funding but work is continuing quickly, I think because the funding agencies realise that the scientific community is remarkably productive. And many non-scientists are fascinated by the results of cusiosity-driven research.
Let me however clarify that progress is not only a matter of new technology. Sometimes technology might not be the entire answer. Discoveries are also driven by new ideas that can be tested either by developing new technologies or by finding new uses for old technologies. I think we are at a stage that fundamental science requires considerable investment in new technology, specifically built for answering some of our deepest questions. This includes telescopes, research infrastructures, and new accelerators. As a side note, it is rare these days to hear of an experiment not motivated by a specific theoretical issue. This was not the case when I entered the field: our research was driven by our curiosity to find out what else existed. We explored ideas not predicted by any theory, but by speculation. Nowadays, it would be difficult to do an experiment that lacks specific motivation. That is to be regretted, because the Universe has the proven capability to surprise us and there should be resources aside for speculative, curiosity-driven experiments, measurements, and observations.
From where do you think this new stance is coming? Why do we lose this exploratory potential, if you wish?
Now that we have a well-tested theory, many lose motivation for looking beyond it. That is to be regretted but a facet of human nature. By focusing on the current theory, examining and testing it in the highest precision, we might be surprised to find elements that don’t fit quite right. Then, we could discover new things – perhaps what would have been found by following the speculative approach.
You know that the nature of dark matter is highly uncertain; there are many possible candidates and some of them are being pursued by large experiments. The problem, however, is that these experiments can only explore a limited number of ideas and there is no guarantee that they are moving in the right direction. I definitely do not want to discourage the current experiments, as they are indeed valuable; they may detect some components of dark matter or provide clear answers about this line of research. However, dark matter is one of the fields in which speculative research certainly can be justified.
Do you think we may need a more radical understanding of gravity?
Bear in mind that the theory of general relativity that Einstein developed 100 years ago was based on very little evidence. The first successful test he performed was the orbit of Mercury, where he was able to explain the orbit parameters by applying general relativity corrections. Basically, the orbit's eccentricity would precess around the Sun, a phenomenon that classical stellar mechanics (or Newtonian gravity) could not explain.
In cosmology, there is the characteristic concept of the Hubble length that is 10^27cm, while the orbit of Mercury is 10^13cm, which means that this is an extrapolation of 14 times of magnitude in Einstein’s theories. It is remarkable that general relativity remains a solid theory and a close approximation to reality. However, there are no complete theories in the physical sciences. They all have unanswered questions; quantum field theory is no exception. In any case, any new ideas or adjustments to current theories will have to respect the many successes of general relativity.
Whether progress in this field will be made by building a theory on totally new foundations or not is hard to predict. My feeling is that refinements will come as perturbations or certain adjustments to Einstein’s general relativity. We do not know whether and how quantum mechanics and general relativity can co-exist. I suspect that there will be a unified theory of the two; I do not know what it will look like, but one thing is certain; you will recognize Einstein’s theory in it. The situation is surprisingly different in the case of dark matter. I am open to finding out that dark matter might have properties not anticipated by any of the ideas currently on the table.
Do you think they might also open a new window in our understanding of the dark sector?
I hope so. You may consider the visible sector spectacularly complicated, but we have an elegant theory with a lot of parameters and a complex world. The dark sector seems quite simple as a gas of non-interacting particles. My emotional guess is that the dark sector is also complicated; perhaps not so much as to allow us to hypothesise about stars made of dark matter, but I believe it is far more interesting than our current ideas suggest.
Do you think that recent developments in the Standard Model of particle physics and cosmology point to the lack of a deeper understanding of nature?
It is certainly an interesting time for particle physics. The inflation theory explains what happened before the classical theory becomes a good approximation of reality and many people feel comfortable with this approach. Some, however, argue that our theory about the Universe remains incomplete, even by inserting inflation. I think that both sides are right. Inflation is indeed incomplete, but then all of physics is incomplete, so I do not judge inflation on that grounds. What makes me uneasy is that it has very little empirical support. On the other hand, when I started working in cosmology, there was little empirical support for the Hot Big Bang Model.
Moreover, the properties of dark matter, the need for Einstein’s cosmological constant, and the existence of dark energy still pose considerable empirical problems. I think that the new generation of experiments will drive us to a deeper understanding and a reconsideration of our previous ideas about these topics and I am looking forward to that.
What would be your advice to young scientists now entering the field?
During one’s career, one may decide to follow a course that is already well-established, as there are always new questions to explore or discrepancies and inconsistencies that can lead to further progress. The alternative is to follow a much more speculative line of research. This is more dangerous, as the odds are that speculation will fail, but there is the possibility of a new discovery, which will have big payoffs. In my career I followed both directions. I find it rewarding and interesting to explore marginal ideas and I think that trying to combine the two paths might be good advice. You should ask yourself which of the two directions makes you feel more fulfilled; if speculative science feels too uncertain, you may turn to a well-established field and vice versa. Finally, you may also consider to move to an entirely new field that is not deeply explored; there is immense demand for new researchers in fields like biophysics or computational physics. We still understand so little about chemistry, or open cells, or even what it means to “think”. In a nutshell, don’t be afraid to get surprised and ask yourself what you are interested in doing in your life.