After being inspired in Part One and sweating through some calculations in Part Two, we’ve assembled all the ingredients of a good paper. We have an interesting question: “What would happen if there were a preferred spatial direction during inflation?” We have suggested a robust answer — an expression for the generalized power spectrum of density fluctuations — and calculated its observable effects. And then we proposed one specific model, lending credence to the idea that this is a sensible scenario to contemplate. Next it’s time to write the paper up, and then it’s cocoa and schnapps all around.
Which we proceeded to do, of course. Except that, as we were writing, there was something nagging at the back of my brain. We were thinking like field theorists, coming up with an idea (“a preferred direction during inflation”) and exploring how it could be constrained by data. But weren’t there people out there engaged in the converse — looking at the data and asking what it implies? Why, yes, there were. In fact, it gradually occurred to me, there was already a claim on the market that the actual CMB data were indicating a preferred direction in space! This had totally slipped my mind, in the excitement of exploring our little idea. (As the professional cosmologist of the collaboration, remembering such things was implicitly my job.)
The claim that there actually is evidence for a preferred direction in the CMB goes by the clever name of the axis of evil. If one looks closely at the observed anisotropies on the very largest scales, two interesting facts present themselves. First, there is less anisotropy than one would expect, on very large angular scales. Second, and somewhat more controversially, the anisotropy that does exist seems to be oriented along a certain plane in the sky, defining a preferred direction perpendicular to that plane. This preferred direction has been dubbed the “axis of evil.”
Is the axis of evil real? That depends on what one means by “real.” It does seem to be there in the data. On the other hand, maybe it’s just a fluke. Nobody has a theory that predicts CMB anisotropy directly as a function of position on the sky — rather, theories like inflation probabilistically predict the amplitude of anisotropy on each angular scale. But at each scale there are only a fixed number of independent observations one can make, implying an irreducible uncertainty in ones predictions — that was the original definition of cosmic variance, before we re-purposed the phrase. For what it’s worth, the actual plane in the sky defined by the large-scale anisotropy seems to coincide with the ecliptic, the plane in which the various planets orbit the Sun. Many people believe it’s just some local effect, or an artifact of a particular way of reducing data, or just a fluke — to be honest, nobody knows.
What’s relevant to the present discussion is that the very existence of the axis of evil phenomenon meant that other people had already been asking about preferred spatial directions in the CMB, even before our seminal work that didn’t yet quite exist. This fact dawned on me in the middle of our writing, and I started digging through the A of E literature. Lo and behold, I found the work of Gumrukcuoglu, Contaldi, and Peloso. They had, in fact, derived a few of the equations of which we were justifiably proud.
But not all of them! We had, in other words, been partially scooped, although not entirely so. This is a remarkably frequent occurrence — you think you’re working on some project for esoteric reasons that are of importance only to you, only to find that similar tendencies had been floating around in the air, either recently or some number of years prior. Occasionally the scoopage is so dramatic that you really have nothing new to add; in that case the only respectable thing is to suck it up and move on to another project. Very often, the overlap is noticeable but far from complete, and you still have something interesting to contribute; that turned out to be the case this time. So we soldiered on, giving credit in our paper to those who blazed trails before us, and highlighting those roads which we had traversed all by ourselves.
At the end of the process — from meandering speculation, focusing in on an interesting question, gathering the necessary technical tools, performing the relevant calculation, comparing with the existing literature, and finally writing up the useful results — you have a paper. Considering all the work you have put into it, the actual paper is annoyingly slight as a physical artifact, even if it’s one of the longer ones. Unless you are really lucky (and perhaps also good), the amount of work you really do and stuff you figure out is much more than shows up in the distilled and polished final product. Nevertheless, I always finish the paper-writing process with a feeling of accomplishment and a degree of surprise that it seemed to work yet again.
As often as not, however, the nominal capstone of the process — submitting the paper to the arxiv — is not the final step. There is, of course, the matter of submitting it to a journal and going through the refereeing process, but in this gilded electronic age that’s usually somewhat anticlimactic. No, the real action comes in the couple of days after you’ve put the paper online, in which time you collect helpful emails from your colleagues around the world:
Dear Dr. X:
I enjoyed reading your new paper astro-ph/0701357. You might be interested in the related work I did years ago, astro-ph/yymmnnn.
Warmly, Dr. Y.
Translation: “I want a citation, you bastard.” Although it’s often not at all impolite, and can even be quite helpful — there’s a lot of science out there, and no way for any one person to keep track of it all. Perhaps the most useful feature of the electronic age (as far as scientists go) are the citations services like SPIRES, which put at your fingertips a network of related papers, connected through a web of referencing and being-referenced-by. It’s by no means unreasonable, when one has written a potentially relevant paper, to make some token effort to see that it is included in that network; otherwise it could easily be lost forever. It can be annoying to get too many requests for citations, especially irrelevant ones, but I essentially always go ahead and add them into a revised version of the paper; it doesn’t kill any electrons.
In our case, we didn’t get any of the dreaded emails that point out that someone else had done exactly what our paper had done. There were a couple of confused exchanges back and forth with friends who figured that we must have been motivated by the axis-of-evil stuff, and were trying to convince us that our particular model (with an effect that was scale invariant, rather than concentrated on the largest scales) wasn’t the right way to tackle that problem; we had to explain that we really weren’t trying to solve any sort of pre-existing puzzle, we were just trying to probe the fundamental robustness of the usual assumptions about inflation. In fact, we didn’t go so far in our paper as to actually compare to any CMB data sets — we are possessed of sufficient self-knowledge to understand that there are other people out there much better equipped than we are to carry out such a task. Hopefully it will be carried out soon!
But, although we didn’t get any deal-breaking emails from the outside world, we did get a post-submission insight from the inside world, namely me. As we were writing, there was another thing that had been nibbling at the edges of my consciousness — isn’t there some good reason why inflation usually doesn’t pick out a preferred direction, but rather is completely isotropic? And finally I recalled what it was — something called the Cosmic No-Hair Theorem. This is a result, due to Bob Wald, which essentially says that in a universe filled with positive vacuum energy plus some other stuff, the vacuum energy always wins out. The other stuff always dilutes away, leaving you with the usual isotropic expansion.
Which was interesting, since we had just written a paper featuring a model that did have vacuum energy plus some other (vector) fields, in which the other stuff did not dilute away, but rather imprinted a direction-dependent effect at all scales. Did we goof, or take advantage of a loophole? Happily, it was the latter. In general relativity, you can prove almost nothing without assuming something “reasonable” about the energy-momentum sources, in the form of energy conditions that restrict the energy density and pressure of the stuff you are considering. The cosmic no-hair theorem assumed the Dominant Energy Condition, which is perfectly reasonable; without assuming the DEC, you can’t be sure that your theory is stable.
But our vector fields, it turns out, were more clever than we were. Our theory violates the dominant energy condition, so it is consistent with the results of the theorem. But it is not unstable; if we divide the fields into a homogeneous background plus a set of small perturbations, the background (which is effecting inflation) violates the DEC, but the fluctuations (which would possibly lead to instabilities) actually obey the DEC. So we managed to find a theory that was well-behaved, but which sidestepped the crucial assumption of the cosmic no-hair theorem. That’s why it had been a little tricky to find a good model in which inflation was anisotropic for an extended period; there was a theorem that said it couldn’t happen, and we had to find a clever loophole, even though we didn’t know that’s what we were doing. So we updated the paper to include a few sentences about that situation.
And now, I think, we’re truly done. The paper has been accepted and published and all that. But of course, one good project suggests all sorts of others. If we explored whether the cherished assumption of rotational invariance could be violated during inflation, are there other cherished assumptions we could contemplate violating? Answer: sure, there are plenty. But there are also plenty of unconnected science ideas that are worth pursuing. So we have to decide whether we should continue to move forward with this kind of investigation, or switch to something completely different. (I tend to go with the latter, more often than not.) One of the happy things about being a professional scientist is that there’s no worry that one day you will wake up and all of the good questions will be answered. On to whatever comes next.
Mmmmhhh…. and you actually get paid for this?
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Fascinating stuff! I’ll point anyone who wants to know what theorists do in more detail than “sit around and think hard” to these posts.
I am intrigued by your dismissive reference to refereeing and publishing in journals. I’m told such things are less important now that there’s the arxiv, but I don’t know the whys and wherefores. Then there’s the question of how much of science’s legitimacy comes from peer review and if we’re losing any of that. I think it’d be another great topic for a blog post from you! 🙂
Regarding citations. I’m an old amateur, no PhD, no academic job, no published papers, not even an arXiv papers. Last year I wrote up a prediction for the neutrino masses based on Koide’s formula for the charged lepton masses.
You’d think I’d be fairly completely ignored. Instead, I ended up with four journal citations in the past year and a couple of arXiv mentions. All without asking for citations, though I did send a couple emails pointing out that previous claims that “Koide’s formula could not be extended to the neutrinos” were incorrect.
I suspect that the physics community is better at giving credit than a lot of people think. And I don’t think that amateurs get ignored here. It’s just that most of the time their stuff is completely vacuous, and most of the others are playing with ideas that might be correct useful, but that no one else is interested in at this time.
When you get people sending you emails pointing out similar previous work, I think that is a good sign that you’re doing something interesting and useful.
Carl Brannen: Yesss! This is what I’ve been waiting to hear about. Please tell me, how did you publish or present, what format/s, how did you publicize it, etc. I have published a few times, but one of my best ideas reached number one etc. in Google search for “quantum measurement paradox” from a NG discussion thread (sci.physics.research) I started in 2000. It got enough attention from enough pros to link well. I don’t think it received much attention outside that thread, but I hope that will change with the increasing interest in “weak measurements” and their apparent validity to some extent. I described an improved form and justification for the concept in nearby threads.
PS: About emails, some university servers etc. block dotcom etc. emails. Sometimes I can get to .gov or .edu mail and more often not, so have you any advice about that problem? Is it as bad as they say anyway, since no answer could mean a lot of things. I remember sending an email survey about space dimensionality to many top physicists in the late 90s. I got lots of answers, about 40% back, from Andrei Linde, M. Kaku, and such. The emails got burned up in my hard drive later, which was heartbreaking. Today, I find it harder to get responses.
This is not the thread to talk about how amateurs can get noticed, so let’s please don’t.
I’m an undergrad engaging right now in my first physics research experience as part of an REU program.
I’ve been reading through plenty of papers off arXiv and so forth. It’s a theory project and there’s plenty of related work out there.
So here’s my question: at what point is it appropriate for me to use the contact emails in papers to ask questions or make comments? Obviously at this point most of my initial questions are pretty “stupid” and thus best directed to my adviser, but sometimes I’m curious if the author of a paper has considered this or that particular facet that would be relevant to my project. Basically, I’m reading the paper and thinking that the problem I’m working on is an obvious followup to what I’m reading.
I’ve read about scientists collaborating via email or conferences and so forth, and I get the sense that that’s what a lot of PIs spend substantial time doing, but at this point I wouldn’t dare bother some senior researcher. Are there some sort of unwritten rules of engagement that generally limit these discussions to people at a certain level up the academic/career hierarchy? Or is that just all in my head?
Any thoughts on these lines would be appreciated.
Stephan, that’s a very good question — the rules are not only unwritten, but fundamentally vague, and only intermittently followed. But if you’ve made a real attempt to understand a paper and answer the question yourself, and you’ve gone past what your advisor (or other likely suspects nearby) can tell you, then by all means you should email the person who wrote the paper. Given that most working scientists get all sorts of crank email, they would most likely appreciate a thoughtful question from a student.
Stephan,
If there’s no one around to talk with and you haven’t been able to figure out something yourself, email away. People love to talk about their research in general and are flattered to have an interest shown in their papers and presentations. Just be able to explain what it is that you are not understanding (briefly), so that the person, if they take the time to answer, can do so efficiently.
When I started on my current project, it involved adding a new model that had been recently updated by the author, who builds this type of model better than nearly anyone else in the field. I went searching for papers that used this model, leading me to email a colleague of this model’s author about something related. He just forwarded it straight on to the other researcher, and both were happy to help. In fact, things like this have happened multiple times — if I can’t figure something out on my own, I email the relevant people and describe the difficulty I’m having understanding their work. If nothing else, these people have all been happy to know that someone looked at their creations and appreciated them enough to ask about it.
That’s what I’m always worried of – finding yourself repeating someone else’s ideas. I wonder how often does that happen? Original ideas are always the most interesting. I’m glad you managed to accomplish something in this world of billions of people, and did get that letter.
I’m just starting theory research in a physics grad program. The one thing I’ve noticed is that I frequently have ideas that sound feasible, but when I work them out I eventually find some killer flaws (i.e. only valid if we abolish spherical symmetry, or if the electron were the size of Pluto, etc.). I’ve also noticed that some of the faculty members have books of ideas that never quite panned out. My question is this: What is average “good idea” density that you experience? In other words, how many failed concepts do you go through before you hit upon a good one?
Well, dang. If Sean had posted this about 12 years ago, I might have actually stuck with my physics major rather than dropping it for literature – based on the incorrect assumption that all the crap lab work we were given was an accurate picture of day to day theoretical work.
OK, sorry (but the digression seemed to develop naturally from an issue brought up in to the post), so getting back on topic: Simplistically, there isn’t any big deal about there merely being a hot and cold spot in CMB along our motion in the radiation, due to Doppler shift. The real curiosity is about inherent preferred directions/axes/planes in the background, as stated. I found an interesting paper, ‘Is the Cosmic ‘Axis of Evil” due to a Large-Scale Magnetic Field?’ by Michael J. Longo, University of Michigan, Ann Arbor, MI; March 27, 2007 (Link
I let the abstract make the point:
I propose a mechanism that would explain the near alignment of the low order multipoles of the cosmic microwave background (CMB). This mechanism supposes a large-scale cosmic magnetic field that tends to align the cyclotron orbit axes of electrons in hot plasmas along the same direction. Inverse Compton scattering of the CMB photons then imprints this pattern on the CMB, thus causing the low-multipoles to be generally aligned. The spins of the majority of spiral galaxies and that of our own Galaxy appear to be aligned along the cosmic magnetic field.
Well, I figure cosmologists are skeptical about EM approaches to the universe as a whole, maybe because some invoke those considerations to doubt the big bang (or what is it called now?). However, maybe the author is on to something, yet he doesn’t explain why the universe or at least a large region around us would have a large-scale magnetic field in a particular direction. How could it, does this make sense?
JerseyBoy, I think the ratio of ideas that pan out to ideas that end up in the trash bin is likely to vary quite a bit from person to person and field to field, but is typically pretty small. I have lots of ideas, the vast majority of which don’t turn out to be worth anything. But it depends on your type of work, even just within the world of theorists. If you’re mostly interested in using established laws of physics and improving our understanding of certain phenomena, your batting average is likely to be larger than if you’re trying to propose new models from scratch. But in either case it’s not going to be very big. Coming up with good ideas that are truly novel is hard, almost by definition.
Writing up the results can be a lot of work too. At least that’s usually the case for me. You can get stuck on a few sentences and spend a whole day on that. This is the most frustrating thing of the whole process.
Freiddie wrote:
>
> That’s what I’m always worried of – finding yourself repeating
> someone else’s ideas. I wonder how often does that happen?
I’ve heard some horror stories, like the chemistry PhD student who
spent several years studying an obscure organic chemical group and
writing his thesis, only to find that all his work had already been done
years before and published in the Outer Mongolian Chemical Review
or somewhere.
> Original ideas are always the most interesting.
Don’t bet on it. I bought a book called Creativity (P E Vernon ed)
in a charity bookshop the other day. I haven’t got round to reading
it yet; but browsing at random, I noticed the interesting point, amply
demonstrated countless times, that a truly original idea is almost
inevitably disagreeable (especially to experts) and strenuously
resisted or preferably ignored. There’s some website that lists
dozens of examples from science.
Cheers
New template around??
Well, just an extra suggestion: why don’t you write a post about peer-reviewing a paper? Maybe even a worked example ;-). Seriously speaking, that would be a very curious topic, since in general peer-reviewing is learnt by reading the referee reports of your own papers…
John R Ramsden:
You bring up an interesting question, and does anyone know how to efficiently really find out what’s ever been done for sure? Now there’s the Internet, including Google Scholar, but glib references to “literature search” aren’t very helpful. There are attempts to get just about every abstract in the world into some kind of database, but I don’t think it’s fully comprehensive and fully integrated etc. Not only that, but writers can make side comments that establish them as technically having first said or thought about X, without explaining that at first.
Your second point is also mostly true, but to find a pattern I’d like to see comparison of the new ideas that were more accepted versus less accepted. BTW, where’s a good site/blog/resource covering more the “science of science” and history of ideas than physics per se? This blog does sometimes, and is interesting then, but I was looking for more. tx.
Curious, the template has begun to spontaneously change itself on occasion. Not really sure why.
I don’t have that much to say about reviewing papers. In my own field, I trust my personal judgment of how interesting and valid a paper is infinitely more than I would trust that of an anonymous referee, and I suspect that the vast majority of others feel likewise. So refereeing is just kind of a burden, not an interesting intellectual challenge.
Neil B.: You can never be 100% sure that the same idea has not been published elsewhere unless 1) You know that it has been published before or 2) It is a solution to a problem that is famous for being unsolved (i.e. Proof on whether P=NP, proof of the Riemann hypothesis, or up until relatively recently Fermat’s Last Theorem).
The examples in the second case are all from mathematics, and that is hardly suprising, since you know once you have a proof for something, and can verify it. There are similar things in physics, but it can be a bit harder to tell. You can know an open problem and come up with a candidate solution that has already been discovered, but has been already rejected due to some flaw or experiment ruling it out.
In my view the best you can do is to read around the area carefully, and to search arXiv, Web of Science and google scholar for keywords related to the problem. If this turns up nothing, then you’re still not 100% sure, and once your paper is up on a preprint server or undergoing peer review there is a chance that someone will point out a reference to a similar work (as Sean mentions somewhere above). This happens quite frequently.
It is important to do a thorough search, since it’s somewhat embarassing if someone points out that the idea has already been published in a prominant journal.
All that’s good, but don’t forget people!
If you talk to the experts in a subject, and find out what they know, what they know they don’t know, what they’ve read, and so on, you’ll be in a lot better position to take advantage of all the previous work on a subject, and avoid reinventing the wheel.
This is one good thing about conferences. People do it almost unconsciously: trade information, tips, and references about what they’re interested in.
The “lone researcher” is at a great disadvantage. The social network of knowledge is a wonderful thing.
This is why I spend a few hours each day exchanging emails about math and physics.
The “lone researcher” is at a great disadvantage. The social network of knowledge is a wonderful thing.
Then how do you explain the observation, often made, that single-author papers are on average better than the other kind?
John, I totally agree. I certainly should have mentioned that. I suppose what I was trying to say is that you can never be 100% sure that a similar idea wasn’t published in some Russian journal in the 70s (hasn’t everything been?).
I agree with John, let me add also that the wonderful network of knowledge often tells you what ideas have been tried and failed, and why they didn’t work. This is a great time saver, and often is not available in published literature for obvious reasons. I have a feeling this is one of the services the lone researcher can use the most…
Myhatma, the most important physics papers do indeed have one or two authors. Some notable exceptions:
Theory of Superconductivity
Infinite conformal symmetry in two-dimensional quantum field theory
This not so difficult to explain. If you have a briliant idea then you will, of course, write it up yourself. Most of the time you don’t have brilliant ideas and usually that leads to collaborations…