Dear Simon (White), recently you presented an interesting comparison between the astronomical and particle physics approaches to cosmology. You suggested that the concentration of theoretical and experimental efforts on the problem of DE, and more generally on themes strongly related to fundamental physics, may be a danger for the astronomical community. Would you like to summarize here your point of view?
Particle physicists and astrophysicists have long interacted productively on topics of mutual interest. Important examples include the discovery of helium in the Sun at the end of the nineteenth century, the elucidation of nucleosynthesis in stars and in the Big Bang, the use of neutron stars to explore the equation of state of ultra dense matter, the solar neutrino problem and its relation to the discovery of neutrino masses, astrophysical constraints on the nature and mass of axions, limits on the parameters of the Minimal Supersymmetric Model from searches for annihilation radiation from clumps of DM, and the use of statistical and data-processing techniques from particle physics to analyze the very large datasets produced by searches for gravitational microlensing. This cross-fertilization has been very fruitful and has stimulated new research directions in both fields. It will undoubtedly continue.
The DE problem fascinates both cosmologists and high energy physicists, but it does not fit the pattern of previous cross-disciplinary collaborations. In my view, a failure to appreciate and take proper account of the differences will seriously weaken astrophysics, reducing its extraordinary current vitality, breadth and versatility, as well as its appeal both to the general public and to the next generation of bright and ambitious young scientists.
It is over 90 years since Einstein introduced the cosmological constant in order to construct a static Universe. Over this period, it has been revived repeatedly as a possible explanation for various cosmological puzzles. The recent demonstration of accelerated expansion was, nevertheless, a great surprise. Suggested explanations include a modification of Einsteinian gravity, an unexpected effect of nonlinearities within it, and an effective scalar field which may reflect the unification of gravity and quantum mechanics in a higher dimensional string theory. These all require new physics which is manifest only in the global evolution of the Universe.
Current observations are consistent with a cosmological constant to within about 10% in the equation of state parameter w, that is, they suggest w = —1 ± 0.05 (1CT). There are plenty of ad hoc theories for DE in which w differs measurably from —1 , but none has strong independent theoretical underpinning. Many high-energy theorists argue that additional fine-tuning, independent of that already needed to explain the unnaturally small value of the current density of DE, is required for w C 1 to be measurably different from zero. Attempting to constrain DE by precise measurements of the cosmic expansion and linear growth histories is thus analogous to searching for lost keys under a street light. Just as the drunk searches in the only place where he could find his keys, rather than in the place where he believes he lost them, so planned DE experiments probe possibilities we can constrain, rather than possibilities which are generally agreed to be plausible.
The precision of current measurements of cosmological parameters is such that uncertainties in the evolution of the cosmic scale factor and the amplitude of linear fluctuations no longer limit our understanding of how galaxies and galaxy clusters form. The complexities of strongly nonlinear processes such as star formation, BH formation and feedback are much more important. Achieving the primary measurement goals of planned DE surveys is thus unlikely to shed light on structure formation issues.
The danger here is clear. Optimizing a survey to obtain, for example, precise measurements of the baryon oscillation signal may require lowering the signal-to-noise of individual spectra in order to maximize the number of redshifts obtained. A successful result would be a more precise measure of the expansion history, but there is a substantial a priori probability that this would simply be a narrowing of the error bound around w = —1. This will not help significantly in understanding the nature of the DE, nor will it help us to understand galaxy formation since the quality of the spectra will be too low to provide much useful information about individual objects. In my view, this would be a meagre return for the effort and money invested.
My conclusion is that we must design observatories to explore DE as one of many issues, rather than experiments tuned specifically for optimal constraints on w and its derivatives. We must ensure that the data returned by our instruments are of the quality and type needed to address a broad range of astronomical issues, not just the expansion and linear growth histories of the Universe.
On the contrary, it is also possible that exactly the need of an extremely precise knowledge of astrophysical phenomena, required to disentangle fundamental physics signatures, further stimulate astrophysical studies, and viceversa. For example, this happened to some extent in the context of the Planck mission project, the logical step forward after WMAP. Do you believe that such a strong interaction between these two different approaches to the Universe science might have also positive consequences for both?
The Planck mission has not yet flown (at the time of writing). My group has been heavily involved in trying to provide computing infrastructure for joint analysis of the data from the two instruments. Our experience over the last decade has not been positive and has reinforced my view that large and diverse collaborations of this kind are an inefficient way to do science. We all hope, of course, that the mission will be successful and will produce great results, but its organization is in dramatic contrast to that of WMAP which involved a small and tightly knit team. While the different national and scientific communities involved in Planck (space experimentalists and instrument-builders, cosmologists from astronomical and high-energy backgrounds, microwave astronomers...) certainly bring differing expertise to the table, they also bring different working habits and expectations. Time will tell whether all this can be brought together to a productive conclusion.
In the DE context, I think the dramatic success story of microwave background experiments over the last decade is a significant factor leading many cosmologists to the unrealistic expectation that surveys to measure the cosmic expansion and structure growth histories will be limited by statistics rather than by systematic uncertainties. The CMB is unique in astrophysics, in that all the information is contained in linear perturbations of an extremely simple system. In addition, confusion from contaminating foregrounds has turned out, fortuitously, to be negligible, at least for the temperature fluctuations. We are unlikely to be this lucky when we use SNe, galaxies or galaxy clusters as cosmic tracers. High-energy physicists are, of course, trained to search large amounts of accelerator data for small signals hidden among a haystack of confusing effects. This expertise will undoubtedly be very helpful when analyzing DE survey data.
To your opinion, comes the major problem you underlined from the necessity of an appropriate balance of available funding resources or is it intrinsic to the two different methodological approaches?
The issue which most concerns me is intrinsic to the two different approaches. For some years the experimental focus of high-energy physics has narrowed to concentrate on fewer and fewer issues. For example, even the internal structure of the proton is now considered by many as "nuclear physics". The community has organized itself into ever larger teams to build ever bigger instruments for an ever smaller number of accelerators. Programmes are organized around a small number of "Big Questions". It is unclear whether the world will be able to afford a successor to the LHC, and each team working on an LHC instrument already involves more than 1,000 physicists. Organization at this level requires an industrial approach, and it is unclear how the field can continue in the future. Concern about such trends is in part responsible for the increasing number of physicists switching to "astroparticle" topics like DM searches.
In contrast, astrophysics has always been opportunistic, making progress simultaneously on many fronts. Its division of labor differs from that of high energy physics, separating those who build observatories and instruments from those who use them, thereby allowing much smaller teams to address problems of forefront interest. Even under today's imperative of single page executive summaries, astronomy has a very diverse set of primary objectives: DM and DE; the origin and evolution of galaxies, stars and planetary systems; the nature of BHs; physics under extreme conditions; the very early Universe; gravitational wave and neutrino astronomy; the origin of life... This diversity has allowed ambitious young scientists to find individual niches and to establish themselves as independent, internationally recognized researchers while still graduate students or postdocs. It is also partially responsible for the popularity of astronomy with the general public - compare the number of popular or amateur astronomy journals with the number of similar journals in high-energy physics, or the number of newspaper articles addressing the two areas.
The rise of "survey astronomy" has resulted in a dramatic expansion in the number of large teams active in our field. Although typically more loosely structured than in high-energy physics, these teams share the general ethos of accelerator instrument teams. The large scale of DE surveys and the active participation of high-energy physicists in them has emphasized and accelerated this trend. Its effects are very clear, for example, in current citation statistics, where many highly cited scientists acquired their status through citations to papers with long author lists where their individual role is invisible. Such teams emphasize hierarchy. Senior scientists determine the careers of their juniors by writing references which provide the sole means for outsiders to judge quality, and in addition they take credit for "team science" where their role is often managerial rather than creative. This is far less egalitarian and transparent than the traditional astronomy system where authorship lists show who is primarily responsible for the content of a research article.
In my view, such "large team science" is less attractive for the best young scientists than traditional astronomical research, where small teams propose science programmes for forefront instrumentation at national or international observatories. Some projects, DE surveys perhaps, do require the large team approach, but astronomy will be impoverished if such projects come to dominate our field. Astronomical advances have typically come from inspired and creative individuals, rather than from planned programmes by large teams. I believe that our understanding of DE, like that of the perihelion advance of Mercury 100 years ago, is more likely to be advanced by a new and revolutionary insight than by an industrial-strength campaign of "precision" measurements.
Thank you Simon.
In: Questions of Modern Cosmology: Galileo's Legacy Edited by Mauro D`Onofrio and Carlo Burigana. Berlin, Springer, 2008, pp. 409-413.
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