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.)
Hi Sean,
I disagree with you on this. I think Simon White made a very important point that, due to the narrow interests those “fundamentalists” have in mind when designing these dark energy experiments, we might eventually get very little astrophysics out of them (unlike the astronomers’ survey such as SDSS) despite huge amount of investment. To me, it is significant for someone with the expertise and insights like Simon White to say:
Simon White accurately described the mentality of the “fundamentalists”: they ignore the complexity of astrophysics and regard it as irrelevant to the “Truth” thus uninteresting. So they won’t care very much to study stuffs like the properties, diversities and environments of low-z supernova. However, it appears very likely to me that the “boring” astrophysics will make the fundamentalist-oriented surveys to be fruitless in the end…
And all this time I thought the way to get funding was to insert “Mars” in the proposal…thank god for search-and-replace keyboard functions.
Here is an idea: instead of disparaging the personality flaws and hypothetical motivations of other scientists, let’s make the positive case for the kind of science that we think is interesting, and why it deserves funding. In the long run that will be much more persuasive.
i’ve personally seen the effects of large collaborations in astronomy. the first round of telescope proposals i submitted as a grad student were all turned down with the comment “wait for [insert large survey] data to be released”. the problem is that survey data takes years to be observed, reduced, sifted through by collaboration members and publicly released… which is/was too long a time scale for me to use in my dissertation. ultimately, i’ve been able to piece together a good dataset by combining many different publicly available datasets with my own spurious observations… but it is a disappointing prospect for my future in astronomy if i can’t continue to do interesting science without becoming a member of a large collaboration…
(i guess its arguable that i just need to be a little more clever with my ideas… 😉
There are recordings available on the KITP website, both audio and video (in Real… format) of a “blackboard lunch” talk at the KITP given by Simon White in July 2006, entitled “Why Dark Energy May Be Bad for Astronomy”. Take this link. Very interesting ideas presented including some about the culture around astronomy – both within the professional community and in wider society.
So let me ask a simple layman’s question. If Dark Energy represents approximately 75% energy in of the universe, doesn’t it almost automatically jump to the top of the list of things that need explaining?
I disagree with the entire premise that things are “good or bad” for astronomy. Nobody asked for Dark Energy to show up, it is an outcome of observations. Whatever ways make it understandable or accessible are fine with me. Be they small or large.
Elliot
Sean: “lay the smack down.” Separate words. As opposed to “Dark Energy Smackdown! All z>2 supernovae, all the time! Call 1800555555 and ask your NSF funding provider for MORE SMACKDOWN!”
Sorry, it’s driving me nutso.
Like many compound words, this usage of “smackdown” began life as two separate words, but is increasingly written as a single word (e.g.). Like we used to say “Inter Net.” I’m just a bit ahead of the curve.
Too far ahead of fashion is out of fashion.
While I agree that we should try to be polite, I have to say: we don’t have *a clue* about what 75% of the universe is made of….and you want to tell me that the other stuff he mentions is “as interesting”? Come on. Being polite doesn’t absolve us of the duty to speak the truth. Dark energy *is* enormously more important than anything else, even if you don’t give a damn about particle physics!
While I agree that White has some valid points about the need for balance and examining whether a particular project gives good scientific value for the dollar, its hard to get past the whining. Not to mention the gratuitous attacks on particle physicists, or that he apparently has no idea how particle physics collaborations actually work. And yet he claims astronomers are good at understanding complex interrelated systems with incomplete data…
This is an important issue, so it’s vital to get good data.
Google shows 1.1 million hits for “smack down”, but 8.8 million for “smackdown”. (In fact, when you search for “smack down”, Googe asks if you don’t actually mean “smackdown”.)
But the phrase “lays the smack down” wins out over “lays the smackdown”, 24,400 to 16,700. This validates the distinction made by loonunit. On the other hand, the top 10 hits for “lays the smackdown” include articles by MSNBC and AP, so this phrasing is being validated by MSM editors. (The top 10 hits for “lays the smack down” include no MSM sources.) I conclude that Sean is just about even with the curve.
I haven’t had time to read the whole article, but while I’m sympathetic to the general argument, I’m suspicious that I’ll disagree with it in detail. For example, as someone who spends a lot of time thinking about ancillary science that you can get from dark-energy-oriented surveys, I’m completely dumbfounded by the statement (see comment #1) that a bigger dataset won’t help us much in understanding galaxy formation. I mean, look how much more we know about the local galaxy population now that we have SDSS! Two square degrees is bupkes by comparison. I work on a three-square-degree survey, and I can’t wait for the next generation of deep surveys.
The point is this. The “culture of astronomy”–the tendency to be interested ina broad array of topics–really arose because, when you look carefully at the sky, you tend to see things that you weren’t necessarily looking for. This will continue to be the case, no matter whether we’re looking for Dark Energy, killer asteroids, or little green men. Heck, even WMAP, that supposedly laserlike “particle physics” experiment has produced science that has nothing at all to do with cosmology. (It’s become clear that we don’t totally understand the microwave emission from our own galaxy, for example.) So I think, as long as we’re doing astronomy, the “culture” of astronomy must remain, even as the budgets and the teams swell with particle types.
Then again, Simon is both older and smarter than I, so what do I know? I’m probably just being a wide-eyed idealist grad student.
While I too agree with some of Simon White’s conclusions (especially that the broader impact on astrophysics should be an important criterion in selecting dark energy projects), I have to take issue with some of his other points. To be specific:
1. There is plenty of interesting astrophysics to be done in large surveys of the type being considered for dark energy projects. The astrophysical figure of merit of an imaging survey is inherently many-dimensional, and includes angular coverage as well as sensitivity, number of filters, and resolution. For example:
a) Most of the Galactic structure science that came out of the Sloan Digital Sky Survey (SDSS) would have been impossible in a survey that covered a few square degrees, even if it went to 30th magnitude.
b) Galaxy clustering and galaxy-galaxy lensing have proven to be invaluable tools in probing the relation of galaxies to their host dark matter haloes. Yet even in the SDSS with 10^6 spectra and several times 10^7 source galaxies for lensing, some investigations (such as lensing by rare classes of objects) are still statistics-limited!
Of course, opportunities like these can be lost if people from the relevant areas of astrophysics are not present (or are ignored) when the surveys are designed. I for one think this would be a shame.
2. I do not think it would be a bad thing if astrophysicists did some “nourishing” of “data-processing/statistics skills.” I have seen more than a few papers on galaxy formation/evolution (no names here — I’m not trying to embarrass anyone) whose conclusions are suspect (or even wrong) because of data processing/statistics issues. I realize that astrophysics is often not a “precision” subject and it is much more than calculating error bars, but this does not obviate the need to get one’s error bars right.
As an example of why astrophysics can benefit from advanced data processing, consider the maps of polarized Galactic emission from WMAP, which are the first all-sky Galactic polarization maps whose interpretation is not clouded by severe Faraday rotation. Nothing of the sort would be remotely possible in a culture where the images are reduced by a lone graduate student spending six months with a canned software package.
To answer the concern about whether data processing is creative: there is a large amount of creativity involved in the process, although as with everything else each new idea takes a substantial amount of hard work (math, coding, etc.) to turn into reality. Also it is often hidden from view because e.g. WMAP talks always show a picture of the satellite and a picture of the CMB sky, but for some reason never show a viewgraph containing the code that estimates the sidelobes.
3. I very much agree with Simon White that astrophysical systematic errors are a serious problem for dark energy investigations, and that proponents of certain projects have likely underestimated them. Right now, this unfortunate human tendency is checked mainly by the desire of each program to uncover everyone else’s warts. The good news is that there are people working on ways of identifying, constraining, and removing these systematics both in current data and working on algorithms for doing this in future data. The bad news is that (A) the ratio of project proponents to people doing hard work on systematics is too high; and (B) project proponents are often fearful of drawing too much attention to the open issues in systematics because they don’t want to look bad. I suspect that both of these problems in dark energy studies are fundamentally cultural. (A) occurs because trying to understand systematics in X cosmological probe is not a good way to get a job when there are people on committees who denigrate the work as “not real physics” or “only math/statistics”. (B) occurs because the standard of proof in astronomy is usually pretty low — I have seen claims of “significant detection” meaning that the *90%* confidence region excludes no effect that have been taken seriously by the community. (This would be laughed at in particle physics.) I suspect that trying to force the “traditional astronomy” culture (which has produced many advances, but also with many false steps that were eventually corrected) onto cosmology will not help these problems, it will only make them worse. I should add that (B) is also encouraged by the far too many people arrogant enough to believe they already “know” the answer to dark energy (w = -1 +/- 0) and accept uncritically any result that agrees with their belief. (I’m glad to report I haven’t seen this attitude on display here.)
Like it or not, low-redshift cosmology needs to develop a culture in which eliminating instrumental and astrophysical systematics is just as valued as other contributions. The consequences if we do not are that we will remain ignorant of the basic phenomenological properties of 70% of the universe.
Mark: interesting results. Will you be extending them to look at other search engines? What effects do you expect from Internet Variance (i.e. there’s only one internet)? 😉
In relation to the article, I would say that being able to do general surveys is great – but they will only get us so far. Dedicated instruments looking for specific, important things are already routine – take the large amount of CMB experiments for example, or the many (radio) telescope receivers built for specific things – and inevitably additional information on the universe comes out of them (look at all of the galactic work that WMAP has done, for example). I really hope that we don’t go to the extrema that particle physics is at, with only a couple of research-class instruments in the world, but I doubt that will happen in the near (
Oops: your blog doesn’t like less-than symbols. :-/ Here’s the rest of my post:
… but I doubt that will happen in the near (less than 50 years) future.
Fundamentally, astronomy is a science where you can go out and build a telescope/receiver relatively cheaply, and get publication-quality results out of it that contain interesting science. Until that changes, which will most likely be never (assuming technology keeps improving and dropping in price), we don’t have to fear becoming “particle-physics Borg”.
I will guess that to understand the aim of Simon White’s essay, one would also have to know more about the poltiical context. I will guess (and I really am guessing) that it is in part a reaction to recent developments like the Dark Energy Task Force and the Quarks to the Cosmos report (http://www.quarkstothecosmos.org/, http://www.sciencemag.org/cgi/content/abstract/315/5808/59). I am sure that the Quarks to the Cosmos authors would disagree, but one interpretation is that it is a mid-decade redirection of priorities which rewrites the previous astronomy & astrophysics Decadal Survey. Specifically, it seems interested in selling astronomical projects as a tool for probing fundamental physics, and perhaps not so much as ends in themselves. (I’m not _yet_ ready to endorse this interpretation.) This predictably will get people’s backs up.
By the way, Sean, if you’re going to call astrophysicists’ mode of operation “small-scale and nimble and charming,” why not go all the way and call us “quaint”? I don’t think you intended it to sound patronizing, but it does. It is Physicist Disease. I have a physics degree, and can recognize it.
Finally, there are multiple cultural differences between large experimental physics collaborations and large astrophysical surveys. Just one example: Nearly all major astronomical surveys have obligations to release data in usable catalog forms (SDSS is one example). So far as I know, few particle experiments do this. They are not under the obligation to take data in such a manner as to enable other projects by other people. This may not be an issue for collider experiments, but it can spell trouble when grafting that model onto astronomy.
“astronomy is one of those nice fields in which it’s hard to learn about one thing without learning about something else”
I agree with you!We must learn the world in many different ways,and understand the world in many different ways,and may be they will all or some of them are proven to be true,and this will give birth to a better way of understanding the world.
I agree with three of Simon’s points:
1. Concentrating on dark energy to the exclusion of everything else in astronomy is a Bad Thing (who is promoting or advocating this??)
2. Dark energy experiments need to provide realistic (not optimistic) estimates of their systematic issues and how they plan to address them, and also be judged on the basis of serendipitous observations that benefit the rest of astronomy.
3. One should not have to slap a “cosmology” label on a project which is of much more “astrophysical” interest than “cosmological”, in order to get it funded.
I disagree with most of the rest of the paper:
1. It seems to me to be very unscientific to “assume” the dark sector (95% of the universe) is extremely simple and there is nothing more to be discovered except errorbars tightening around w=-1. The 4% “we understand” is not “simple”. Many times we think we understand something and then try to go and measure it better, we figure out something amazing and new, and the discovery of dark energy is a case in point. The “physics experiment” WMAP has produced a nice model of the large scale magnetic field of the Galaxy. It also has the best measurements of the temperature of the atmosphere of Jupiter.
2. Data processing and statistics of the sort employed in cosmology and particle physics are not creative…? It takes a lot of innovation, creative thinking, and yes, extremely hard work to learn about the universe with the methods of cosmology. Displaying a sneering attitude towards these skills and saying cosmologists are not generalists is very counterproductive. Most cosmologists I know have a huge dynamic range of research interests (out of necessity). In addition to cosmology talks, I go to almost all the astronomy talks and about half the physics talks, and this is very common of my colleagues. I completely agree with Chris’s point that many astronomy papers could use a good dose of rigorous statistical methods and clear distinction between assumptions, methods, results and interpretation – not all “physicist’s” skills are inapplicable to astronomers.
3. I was very bemused by constant references to the public support astronomy gains from the amateur community, and that fundamental physics has little public support base. This is completely not in accord with my experience (speaking as a former amateur astronomer myself). I have talked at many astronomy clubs (and to members of the public in many other situations) and upon learning that I am cosmologist they often ask detailed and interesting questions, and they are mostly about black holes, the Big Bang, and yes, dark energy. A significant part of public is deeply interested in fundamental questions about the universe, which is something I find extremely gratifying.
4. I am similarly bemused by the implication that a 2 degree survey has given us all the information we will ever need about galaxy formation / evolution, and a big, deep, multicolour imaging and spectroscopic survey can add nothing further.
5. The implication that cosmologists are (or will in the future) become uncreative “drones” in large collaborations seems to me to be a bit alarmist. For example, even now, most CMB experiments are small collaborations in which a group of people design and build an experiment, and take data and analyse it in such a way that this can be a student’s thesis. Also, the idea that the most creative people will be put off by being unable to get credit for first or single author credit in their field and not want to think about “fundamental physics” and go off into condensed matter and biology seems to me to be an over-generalization. There are plenty of the best people around who are not motivated in their research by credit and self-promotion, but by their deep curiosity about the universe.
I’m suppose to take seriously someone who labels me and my colleagues “fundamentalists”?!?
Excuse me while I go kick an astro grad student. Might kill a puppy while I’m at it, too.
-Irate Particle Physicist
It’s not primarily a matter of cultures or sociology; it’s a matter of the science questions we are trying to address.
To be fair, White does address that. It is a difference of culture, but the culture arises from the nature of the questions, and what is needed to address them.
However, the immediate effects are cultural.
I know from first hand experience that using the term “dark energy “doesn’t get you funding. When I was first at Vanderbilt, I was still trying to be a member of the Supernova Cosmology Project. I would write proposals. The reviews would come back saying that they loved the science, but what was *I* going to do? The problem was, I was part of a big group. I could describe my roll in the group, and describe the group’s plans for the next few years, but even though I was on the Executive Committee of the SCP, I was hardly in a position to dictate unilaterally a direction for the group.
Perhaps my problem was honesty; perhaps I should have claimed more ability than I had, and perhaps I should have said “this is me, me, me, all me.”
The fact is that I was coming from a group that was steeped in the culture of particle physics, and trying to convince a panel steeped in the culture of astronomy (where it is the Warrior Hero Professor and his or her Faithful Single Post-Doc and Two Graduate Students) to fund me. They didn’t “get” the group membership thing. And, yes, because people who don’t get funding always grumble, to be fair I have to say that I didn’t do a good enough job describing it. But it was frustrating; I wasn’t sure it could be described. It might be easier now, but I don’t know about it.
Being in the particle physics community can be destructive for an astronomer’s career. Post-docs in the SCP would occasionally whinge that we weren’t getting enough papers out, in particular first-author papers. We were told, “oh, don’t worry, in particle physics people understand who made the contributions.” I’m not sure it’s worked, though. I will say that the letters of recommendation got me a job even though I had zero first-author SCP papers during my five years with the SCP at LBL, but it doesn’t seemed to have worked as well for most others.
I have also talked to astronomers who comment on people applying from a large project like Sloane. “It’s impossible to know what they did,” is what I hear. I object that, well, if you look past the papers and at the recommendations and such, you can figure that out. But, the very reasonable response is: there’s enough of a supply of top-notch Steidel graduate students and the like that there’s no need to go digging into Sloane to figure out which post-docs are really worth it.
It doesn’t make sense to “blame” the culture of particle physics, or the culture of astronomy — but the cultural divide needs to be recognized, and young people who think that they might be able to bridge the culture in one direction or the other need to be strongly cautioned that old attitudes die very, very hard.
-Rob (who wonders why he didn’t just post all of this on his own blog!)
Here is an idea: instead of disparaging the personality flaws and hypothetical motivations of other scientists,
This is a great idea, and there would be a huge side benefit: faculty meetings would be much, much shorter if we stopped doing that!
Rob, it seems to me that if the culture of astronomy is preventing career progress for people who are interested in answering a fundamental physics question which can only be investigated through astronomical observations, the solution is not for young people to be cautioned from doing research in that area, but for the culture of astronomy to change to accommodate them and recognize their importance. It is unlikely that the hero(ine) professor and two grad students are going to solve the dark energy puzzle any time soon.
I confess I haven’t read everything here yet (I had to dash to the airport after Hiranya’s talk yesterday), but here’s a manual trackback anyway.
agree with Hirata’s, Elliot’s, Gerke’s, Hiranya’s comments (and the others in this line of reasoning)…
not to mention that the idea of “small astronomy” was, is, and certainly is becoming _far_ more of a myth than reality — HST, Spitzer, + large ground-based projects like Keck, Gemini, etc easily compete well with, and in the case of HST & JWST, easily beat, accelerator projects in cost. Not that that’s in the slightest bit wasteful, it’s just a fact, and there needs to be a moratorium on whining between fields about who’s taking a bigger (tiny) slice of pie.
I’d posit that Simon’s argument is much more akin to “fundamentalist” religious types than the arguments of people after fundamental properties of nature.