Among the many fascinating blog posts you would get from me if I didn't have a day job is one on "Why Everyone Loves to Hate on Particle Physicists." I would not be in favor of the hating, but I would examine it as a sociological phenomenon. But now we have an explicit example, provided by respected astrophysicist Simon White, who has put a paper on the arXiv (apparently destined to appear in Nature, if it hasn't already) entitled Fundamentalist physics: why Dark Energy is bad for Astronomy. Here's the abstract:
Astronomers carry out observations to explore the diverse processes and objects which populate our Universe. High-energy physicists carry out experiments to approach the Fundamental Theory underlying space, time and matter. Dark Energy is a unique link between them, reflecting deep aspects of the Fundamental Theory, yet apparently accessible only through astronomical observation. Large sections of the two communities have therefore converged in support of astronomical projects to constrain Dark Energy. In this essay I argue that this convergence can be damaging for astronomy. The two communities have different methodologies and different scientific cultures. By uncritically adopting the values of an alien system, astronomers risk undermining the foundations of their own current success and endangering the future vitality of their field. Dark Energy is undeniably an interesting problem to attack through astronomical observation, but it is one of many and not necessarily the one where significant progress is most likely to follow a major investment of resources.
Simon contrasts the way that astronomers like to work -- "observatory"-style instruments, aimed at addressing many problems and used by a large number of small groups -- with the favored mode of particle physicists -- dedicated experiments, controlled by large groups, aimed largely at a single purpose. He holds up the Hubble Space Telescope as a very successful example of the former philosophy, and WMAP as an (also quite successful) example of the latter. HST does all sorts of things, and many of its greatest contributions weren't even imagined when it was first built; WMAP was aimed like a laser beam on a single target (the cosmic microwave background), and when it's done everything it can on that observation it will gracefully expire. His real worry is that the emergence of dark energy as a deep problem introduces the danger that the particle-physics way of doing things will take over astronomy. On the one hand, trying to understand the nature of the dark energy is undoubtedly interesting and important, and might only be addressable via astronomical observations; on the other, there is some danger that we devote too much of our resources to a small number of monstrous collaborations that are all tackling that one problem, to the ultimate detriment of the agile and creative nature of traditional astronomy. I kind of agree, actually. More specifically, this is one of those cases where I disagree with all of the background philosophizing, but am sympathetic to the ultimate conclusions. (In contrast to the framing discussion, where I'm sympathetic to the philosophizing but disagree when it comes down to specific recommendations.) Dark energy is extremely interesting, and any little bit of info we can get about it is useful; on the other hand, there is a fairly narrow set of things that we can do to get info about it, and concentrating on doing those things to the detriment of the rest of astronomy would be a bad thing. Happily, astronomy is one of those nice fields in which it's hard to learn about one thing without learning about something else; in particular, as the dark energy task force has recognized, the actual things that can be usefully observed in an attempt to get at dark energy will inevitably teach us many interesting things about galaxies, clusters, and large-scale structure. Still, it's worthwhile not going overboard. More than one working astronomer has grumbled that the way to get funding these days is to insert "dark energy" randomly into each paragraph of one's proposal. (Not that such grumblings make it true; scientists applying for funding love to grumble.) But the backstory of "particle physics" vs. "astrophysics" (or "every other kind of physics") is a misleading one. It's not primarily a matter of cultures or sociology; it's a matter of the science questions we are trying to address. There is something about particle physics that is different from most other kinds of science -- you need to spend a lot of money on big, expensive, long-term experiments to get detailed information about the questions you are trying to ask. The LHC is an expensive machine. But if you choose to spend half as much money on building an accelerator, you won't get half the results -- you'll get nothing. It might be that the results are not worth the cost; I disagree, but that's a worthwhile debate to have. But if you decide that this kind of science is worth doing for what it costs, then big collaborations and expensive machines are the only way to get it done. (Not, obviously, the only way to get information about particle physics; that can come from all sorts of clever smaller-scale experiments. But if you want the kind of detailed information necessary to figure out the structure of what is really going on at high energies, big accelerators are the way to go.) The issue for astrophysicists is not whether they want to continue to be small-scale and nimble and charming vs. giving into the particle-physics Borg. It's what kind of questions are interesting, and how best to get at them. There is plenty of room out there for world-class astronomy of the quirky small-science type. But there's also an increasing need for big targeted projects to answer otherwise intractable questions. Having a passionate debate about how to balance our portfolio is a good thing; casting aspersions on the sociological tendencies of our colleagues isn't really relevant to the discussion. Update:Rob Knop chimes in. From comments: Here's video/audio for the talk at KITP that Simon White gave last summer, on which this paper is based. (Thanks to John Edge.)
