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.)
I agree with Simon’s views on the likely limitations of what we are likely to learn about dark energy and the importance of many areas of “non-fundamental” astronomy, I must say that I think his views on astronomy vs. physics culture are almost completely wrong. Astronomy gains much more than it loses by importing parts of the “physics culture”.
Simon presents a caricature of physics culture as the culture of giant particle accelerator experiments, so I’ll retaliate by starting with a simplistic and somewhat unfair caricature of “astronomy culture”: astronomy is done on general purpose telescopes using general purpose instruments and general purpose data reduction software provided by NOAO or ESO. No “creativity” is involved in building the telescope, instrument, or writing the data reduction software, so sole credit for the science goes to the users of these tools. This traditional astronomy mode allows astronomers to address a very wide range of problems, but it often seems that astronomers rely upon this mode of research too much. As a result, a large fraction of the breakthroughs in astronomy come from physicists who cross over into astronomy. Examples include the expansion of astronomy into radio, x-ray and gamma ray wavelengths and the introduction of CCD detectors. Other examples include gravitational microlensing surveys and the type 1a supernovae surveys that produced the first convincing evidence for dark energy in the first place. As a founding member of the MACHO Project, I can say that something like 90% of astronomers thought that we would fail to get any useful results – largely because most astronomers couldn’t seem to imagine how a project requiring more than 10 people could succeed. The Supernova Cosmology Project also faced similar skepticism.
The abhorrence for large projects by astronomers also seems to cause significant problems for astronomy when large projects are undertaken. The Sloan Digital Sky Survey (SDSS) is a good example of this. For many years it was considered a prime example of large project mismanagement, and it was only after a group of particle physicists was brought in that it succeeded (at something like 5 times the original projected cost). Similarly, part of the blame for the HST spherical aberration can be attributed to the distaste of astronomers for getting involved in such a large project (as is made clear in a famous “letter to the community” from Jim Gunn).
Finally, Simon’s attempt to support his claims with publication statistics seem particularly silly. The threshold to get a paper accepted for publication is so low that it is absurd to imply, as Simon does, that productivity is somehow related to some count of papers published. By Simon’s reasoning, the 70’s and 80’s would have been a much more productive period for CMBR spectrum measurements than the early 90’s when COBE/FIRAS provided the data set that settled all questions in the field. The 70’s and 80’s were full of measurements of different points on the spectrum with periodic blizzards of theory papers explaining each exciting (but ultimately wrong) data point that seemed to differ from the standard Big Bang.
I think that the publication trends that Simon has identified are actually signs that the field is growing more healthy by abandoning some of the traditional astronomy culture of very small research projects in favor of larger groups when there is a clear scientific benefit. Our research would progress much more slowly without the help of the “physics culture”.
Ben (17) — I, on the other hand, do not have a physics degree; both my undergraduate and graduate degrees are in astronomy. So I can’t agree with your diagnosis.
Does nobody get that when I contrast “nimble and charming” with “joining the Borg” I am exaggerating each position for rhetorical effect?
“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
With respect, I think that you’re taking this entirely the wrong way. That a leading astrophysicist like Simon White would single out the “culture” of particle physics as being such a threat because “The pursuit of a deeper truth, of a fundamental theory which underlies all the others is a powerful motivator in physics” actually sounds rather complimentary to me. I mean, who wouldn’t want to “abstract from the complexity of the world a truth which embodies the ultimate foundation of the physics of particles and fields, thus by extension, of all physics, chemistry, and biology”? What an endorsement! Can we put this guy on retainer?
All along I have been puttering along in my reasearch, looking at the data here, “constucting many Dark Energy Models consistent with the observed expansion and structure growth histories” there, … an innocuous activity, I assumed, but at least I got to work on something that interested me. So it was intensely gratifying to me to be informed that my dabblings represented the embodiment of an “alien” value system so irresistably seductive that astromomers would be temped to adopt it even though it would “risk undermining the foundations of their own current success and endangering the future vitality of the field”. I had no idea that I was having so much delightfully nefarious fun!
I must have been reading a different paper, or perhaps just putting it through an astronomer filter, but I don’t see this as an attack on the culture of particle physicists. What I read Simon’s main point to be is:
If we have a limited pot of money to fund observatories and astronomy in general, astronomers have traditionally done better by spending this money on infrastructure which is designed to be as general as possible so as to allow the brilliance of individual investigators on relatively small projects to drive the scientific discoveries instead of building a super-instrument to go after one tiny corner of astronomical data-space, and then another super-instrument to go after a different corner once we’re done with that. So perhaps we should think twice before devoting a significant chunk of the resources we’ll have for the next decade to projects which are all geared to obtain good data on one small corner of astronomy.
In this I think Simon is absolutely correct – as he points out, while WMAP is a success, if you were to create a figure of merit to judge scientific discoveries (even per dollar spent or per year), HST would beat WMAP hands down because it has been able to make discoveries in so many different parts of astronomy.
That said, I am a member of two different groups proposing to do dark energy surveys, and I think most of the members of the groups are already in agreement with one of Simon’s main points, although from a slightly different point of view – if we’re going to spend all this money to build observatories with the primary goal of measuring dark energy, we’re going to build these to also bring back the best, most widely-varied data sets possible in the course of doing this.
I actually have some interesting things to say about this, but I believe my comment will be eaten up by the InterNet again, and I am too lazy to write to the editors so I will simply go back to computing some 3 points.
Wow, my comment survived, so I am going to post after all!
(a) Hiranya and Chris made the best points about how “big time particle physics” have taught the astronomy community how to do statistics. And handle large amounts of data too, for that matter.
(b) It is not fair to compare HST with WMAP, since these two projects are orders of magnitude different in terms of money needed to run them, and isn’t White talking about money at the end? One project is Battlestar Galactica, and the other is small one man fighter sent to take out the Death Star. Being focused is not a bad thing.
(c) The next big NASA project is the Jim Webb telescope, for all I know, a Battlestar Galactica class project.
(d) There is nothing wrong with trying to pin down what Dark Energy is, we have to temper our enthusiasm about *what* actually we can do at the moment. No names here, but I think the current slate of experiments proposed to pin down w(z) is overly hopeful about what they can do. And I don’t mean in the systematics sense, but in the theoretical sense. I mean : how many of you actually believe that w(z) is going to vary sufficiently around the limited z-range we can probe? We built the LHC because years of research tell us that we *gotta* see the Higgs (and if not, we will be even be happier in some sense). But where is the similar amount of theoretical research behind the dynamics of w(z)?
That should be “Imperial Battle Cruiser,” not “Battlestar Galactica.” You don’t want to be mixing metaphors, do you?
I know, but I am very partial to Battlestar Galactica, which I think is the greatest TV show on Earth, and I don’t even own a TV.
The HST total life-cycle cost was recently estimated at $14 billion, and I think that WMAP was something like 100 times less. So, it is pretty doubtful that HST really beats WMAP in science results per dollar.
From Hiranya in #19…
See, the way I see this is how, when it comes down to it, an amateur astronomer can go out into their backyard and do real science using what are essentially smaller versions of what the pros use. This is different from fundamental physics because, well, it’s not like you can get your own private particle accelerator and set it up in your backyard when you have a moment.
Here’s the ultimate test in my mind- go to any major newsstand, and see what science magazines are sold beyond the general stuff like Discover. You will not see a physics magazine (or a chemistry or a biology one, at that), but you will see at least one or as many as five astronomy ones. This happens for a reason!
Yes, there is a huge interest in funamental questions, of course, but I think the tendency amongst amateurs from my experience is to bunch that all under astronomy rather than to think of it as physics (because why would you be looking up without wondering about those questions in the first place?). It can be disguised very well actually- I didn’t realize until I encountered physics in uni that what I was in love with was the physics behind all the stuff I was observing. It was an interesting realization to make.
Anyways, tirade over now…
So I read it over, and my entire conclusion from the paper was basically “don’t be stupid and compromise good science in the name of science.” Makes sense. Didn’t we already know that though?
Yvette: I completely agree with you – I was an amateur astronomer as a kid too, and realized in high school it was the physics and maths I was in love with. I think its stupid to drive a wedge between physics and astronomy just because you don’t like a “culture”, and say if you are an astronomer, you can’t do research on certain questions. Cultures can change, but the entire universe is the cosmologists’ playground.
Skeptic: I doubt very much Simon intended to compare HST and WMAP in the way you are doing and state that “HST wins hands down”. HST is $14 billion dollar mission with its own Institute of hundreds of scientists to support it, and the whole NASA publicity bandwagon to promote it. WMAP is a Midex mission of 150 million (I believe 120 million of that was for the launch) and the data was processed and analyzed by a couple of dozen scientists and then made public for anyone to use. In case you don’t know, despite its relative economy, WMAP was responsible for 1% of world science in 2004, and has over 9000 citations in the SPIRES-HEP database. HST’s impact on world science is comparable. HST and WMAP are *both* spectacularly successful by any metric, and if you are arguing one over the other you gotta have *some* filter on…. I think (hope) Simon’s point is that you have to have some observatories and some focused missions (a diverse portfolio).
Eugene: go BSG!
As a lay person Elliot’s point in relation to what constitues most of the make up of the universe would seem extremely important to me as well.
So in the earlys days of the “disaster scenarios” at the collider, strangelets were suppose to be a consequence of this collsion process. Clarifciations were done to answer this?
Now to me this sets up what comes after, and “what if” any can contribute to the dark energy. As well, what and how it contributes to the geometrical propensity of this universe.
While highly astronomical energy events in terms of the galaxies, what stage can these reach to contribute? You needed a reductionistic view in which to see how such contributions would fuel the dark energy/matter aspect?
Particle showers from cosmic particle collisions? So while you have an experimental situation set up with the LHC, there was a natural process being spoken to as well.
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As a particle physicist who crossed over into cosmology, I am surprised by the apparent misunderstanding on both sides of the aisle about the other. First on particle physics…
1. It doesn’t consist only of huge collaborations, unless you consider 40-50 huge. One recent example is Kamland where a relatively small team of particle and nuclear physicists put together an experiment quickly and (again relatively) inexpensively to study neutrinos from Japanese reactors. Not only did they make an important measurement of the fundamental properties of neutrinos (oscillations) but they even found weak evidence for geo-neutrinos from the center of the earth.
I could give other examples if people are interested.
2. Even the huge collaborations are not monolithic. Collaborations like CDF or D0 (about 500 each) are actually federations of smaller teams studying a very wide range of phenomena in a focused way. Sure the discovery of the top quark involved hundreds but most of the publications are really the work of 3-4 people backed by cooperative working groups of 10-20. Is this unattractive to new students? It shouldn’t be. If you are a student with a good idea, you have a powerful detector at your disposal and an experienced team to help you acquire and process the data.
3. Particle physicists don’t work in big collaborations just because they like to publish with 500 of their closest friends. Rather it is a “what the science requires ” attitude. We went through the evolution of studying diverse limited topics with small teams until it reached the point of diminishing returns on most fronts. Astronomy and astrophysics are beginning to confront similar issues in some (but not all as Simon White correcty points out) areas. Science advances by developing the necessary and appropriate tools.
And on the astronomy and astrophysics side:
1. I have a very healthy respect for the subtleties of astrophysical systematics. As a newcomer, many of the techniques and procedures did seem “quaint” to me at first but the more I learn the more I understand that there are good reasons for most of ways things are done. Even if I still don’t understand all the systematics I do know very well that they are there and that they will have to be understood. Any new dark energy project will have a well-thought out program for addressing them.
2. While I freely admit that I am personally motivated by the fundamental aspect s of dark energy, I agree that an investment of the magnitude required should also address the needs of the broader astronomical community operating within their own culture. Look at all the astronomy that has come out of the SDSS and HDF. Now image 10 square degrees to 30th AB magnitude in nine well-calibrated
bands from optical through near infrared and 4000 square degrees to 28th magnitude in the same bands, both with exquisite PSF. Studying dark energy an d traditional astronomy can co-exist in the same project. Looking at the total science per dollar is a reasonable thing to do.
what about a distributed system to allocate our interest using value trust metrics?
seriously it is against the grain of your represented interests to attempt convincing others toward your perspective
no conflict – collaboration is favored in surplus economies, supporting interdisciplinary engagement, so competition takes a back seat. slight indirect correlation between dollars & scientific value. 🙂
in my opinion “dark energy” may attract our memetic focus unduly by misinterpretation as potential source of energy flow… seems more like inverted potential energy of finite quanta pattern
every “point” in the dimensionally resonant universe is equally accessible to the source of infinite energy – unordered chaos – patterns osmos characteristic energies to fill sinks in harmonious balance with flow toward desired outcomes of patterned attachment
feels like limitlessness in magnitude is assured via 2 parts unstructured energy into pattern accompanied by 1 part dissolving decay outward. energy flows in *balance* across duality into interwoven dimensions, providing less/more equivalence between contextual components/states.
allowing the unknown/known aspects of 2 parts inward to settle toward intended results without judging fulfillment intermittently offers suspension of disbelief & necessary shifts discerned by pattern… meta-level removed from centric conscious notice
I would like to ask a very naive question (I am a grad student in astrophysics): how much attention do particle physicists pay to data analysis? Mind you, I do not doubt their results/abilities, just curious how different astrophysicists and particle physicists are when it comes to data analysis. Could someone explain in detail?
I’m not the one to give you details, but the short answer is: particle physicists pay an enormous amount of attention to data analysis. They’re the world’s experts, to a good approximation. The data rate is huge (the LHC will be recording less than a millionth of its data), and you have to be able to sift through it carefully.
Hmmm. This is fascinating, hearing different “tribes” and “alien cultures” within physics talking it out and wondering where resources should be allocated. Asad Raza over at 3 quarks daily analyzed the Dawkins-Eagleton animosity as two academic cultures — empiricim and culture studies — duking it out over “cultural capital and resources.” But you-all are so much more civilized about it!
So here’s my question (which I’m pursuing over at my weblog, http://www.deepgraceoftheory.com). If we stepped back and returned to Plato and Aristotle for a fresh look at the various legitimate and genuine ways of knowing, could scientists seeking knowledge of various complex facets of the natural world and theists seeking knowledge in various religious traditions and areas of theology of the practice of their relationship with God ever respect one another and “affirm one another’s full humanity”?
It’s tragic that hardheaded scientistic religious people are wrongheadedly attempting to foist their “creation science” onto science classrooms. They do so because they too have been indoctrinated by this reductive late-modern outlook that scientific “fact” is the only kind of truth that matters, that is “really” true. That is how I would define “fundamentalism,” as the belief that only one’s OWN way of knowing gets at “fundamental reality.”
But isn’t it equally tragic for equally hardheaded scientistic scientists to use science to attack people’s most treasured experiences and practices, by claiming that science can somehow know these are illusory, when science isn’t addressed to exploring such questions or areas of human experience at all. Will the fundamental GUT when it arrives and if it arrives show that our well-nigh religious devotion to music or sports or other things we humans hold sacred are unreasonable because they do not explain the workings of the physical world?
Religion has many many aspects and is a complex social phenomenon, but in my own fields of epistemology and literary theory, it has always been deeply respected in various manifestations as carrying our exploration of realities we formalize further. Religious thinkers, who include Plato and Aristotle, have thought within their disciplined interpretive communities with great precision and rigor, and history has not undone the value of their contributions any more than science has left behind Newton’s contributions while recasting or re-orienting them.
I understand the rancor that arises when one tradition threatens another in its very identity, as religious fundamentalists threaten the science classroom and scientific methodology.
But wouldn’t greater clarity about where our ways of knowing LEAVE OFF contribute to more honesty and intellectual clarity in the future? I suspect the polls showing support for IT or creation science to be taught along with evolution reflect a deep sense of unfairness and disesteem that people feel over the way that evolution has been taught and represented as demolishing faith in God.
Human beings whose religious practice is central to their identity know they are being patronized and discounted in a way that is not fair or intellectually honest. (Personally, I don’t think we would have the red-state phenomenon in such an extreme form if university intellectuals hadn’t been so consistently arrogant towards less “educated” people, another thing the Greek vision of the ways of knowing tends to alleviate.)
One has only to look at the quality and numbers of scientists who are devout Christians, or Jews, or Muslims (and so on) to see this unfairness. These human beings belong to both cultures and include great scientists like Polkinghorne or Polanyi.
P.S. I ask a question about Copenhagen interpretations of quantum mechanics vis-a-vis “physical reality” over in my Pages, under “The Fundamental Paradox of Late Twentieth-Century Thought.” Could anyone help me out with that? http://www.deepgraceoftheory.com
I’m not sure why Sean says this paper is supposed to appear in Nature. The arxiv page says, “Essay commissioned for publication in Reports on Progress in Physics.”
Oops, that was a mistake; it just seemed to be formatted in Nature’s style.
Sean, re (27), sorry, I should have been more clear that I didn’t think you were patronizing, but that the language is charged enough to be playing with fire. I appreciate that you were trying to exaggerate two opposing positions, but it is an asymmetric situation. Some (not all) people near the top of the funding pyramid may not mind the comparison to the Borg. They want to run a big enterprise. The rest of us are a little defensive about realignments of funding priorities.
I don’t think the comparison of HST and WMAP was well-chosen. There are plenty of relatively directed astrophysical or astronomical projects like WMAP, nor should any rational person say WMAP was imposed on the astrophysics world by physics outsiders. A better comparison of the two cultures might be HST to LIGO or (God help us every one, in terms of schedule at least) Gravity Probe B.
Although JWST is a very large project, it is a general purpose observatory with a GO (Guest Observer) program, like HST and like most major observatories. By comparison, you can’t even get access to LIGO data without joining the consortium. Now, there are reasons for this, and if I had access to LIGO data I wouldn’t know what to do with it. But running the next big project like a Dark Energy Telescope/Satellite (whatever it happens to be) in this way could be a real problem.
not to mention that the idea of “small astronomy” was, is, and certainly is becoming _far_ more of a myth than reality
This is wrong, by the way.
There still are a vast number of astronomers who live primarily using small telescopes.
Some of them also use national facilities– but nowadays, a 4m telescope is considered small.
All of the observing I’ve done since leaving the Supernova Cosmology project has been done on 1m, 1.5m, and 3.5m telescopes. I have put in an HST proposal or two, but they’ve been turned down. I’ve got a Chandra proposal waiting.
But, there’s another way in which it’s wrong.
JWST and HST, while being as costly as a particle physics project, are not monolithic projects the way particle physics detectors are. The typical accelerator will have a collaboration of no more than a handful of mammoth groups each building a big detector complex.
In contrast, in astronomy, the expensive “general use” facilities get used by a wide range of observers, from groups large and small. This is another way in which “small” astronomy very much does exist. Not necessarily in cost, but certainly in the organization of the research teams.
The HST total life-cycle cost was recently estimated at $14 billion, and I think that WMAP was something like 100 times less. So, it is pretty doubtful that HST really beats WMAP in science results per dollar.
I’d take that bet in a second.
100x more science from HST than WMAP? Easily!
100x as much “high profile” science? No. More like 10x as much.
But as for science itself, I’d guess that HST has generated many more than 100x as much science as WMAP.
-Rob
It doesn’t consist only of huge collaborations, unless you consider 40-50 huge.
To an astronomer, that is huge.
The mere fact that various cosmology groups– supernova groups and the like– came in with author lists this size and required the AAS to re-think the way they handled author lists for papers submitted to their conferences indicates that 40-50 is a regime of author number that had not been much explored by astronomy before the late 1990’s.
-Rob
Rob, re (48) – by science results per dollar, I really meant to refer to the total scientific value of the science results – not the number of results. The folks that foot the bill for WMAP and HST (i.e. taxpayers) do not care about the number of papers published – they expect major scientific advances from these expensive instruments. So, your numbers seem to imply that WMAP should beat HST by a large margin in “high profile” science per dolar. I suppose that HST also provides some value beyond the pure science results, however, since it provides a lot more support to the astronomy community and does much better at communicating with the public than any other astronomical facility.