Tutorial 12: How to find problems to work on February 3, 2011

Millions long for immortality who don’t know what to do with themselves on a rainy Sunday afternoon. –Susan Ertz, Anger in the Sky

If you’ve been following the past few tutorials, you now know how to get copies of academic papers (learn Google fu and ask politely) and how to become a paleontologist (write and publish papers). But what are you going to write and publish papers about?

My own experience, and my impression from talking with many others, is that when you move into a new field for the first time, it often seems like all of the good projects are taken. Or you’ll have what feels like a great idea for a project and then find out that Romer already solved that problem back in the middle of the 20th century. My advice is going to seem trite, but it’s worked for me several times and it seems to be what most other people do as well. Are you ready?

Step 1: Work on something



Seems obvious, right? Of course you have to work on something. You can’t just be a generic scientist (the idea is attractive, but that occupation closed about four centuries ago), and you can’t accumulate papers on everything. You need a focus. But if you’re just starting out, how do you know what to work on while you decide what to work on? It’s a Catch-22.

There are basically two solutions: work on something that appeals to you, or let someone else pick something for you.

Don’t discount the second path. It’s a big benefit of having an advisor who can provide you with a starter project. I didn’t have any particular fascination for sauropods before Rich Cifelli put me to work on what would become Sauroposeidon; I fell in love with them along the way (Buddhists would call this my awakening). As far as I can tell, Mike took the first path, and started working on sauropods because they seemed cool, and fell more deeply in love with them along the way.

I don’t describe this as “falling in love” lightly. That’s what it feels like: a positive feedback loop wherein the more you engage with a subject, the more you enjoy engaging with it, and so on. A few rounds of that and you may find yourself in a committed relationship, also known as a “research program”, because that’s how you maximize your time with the object of your affection.

You may not fall in love with your first project. It might crash and burn. You might not even finish it. It’s really just there to be your runway, to get you up in the air and flying under your own power. One way or another, you’re going on to something else. If you get a paper or two out of it along the way, that’s gravy.

Some people may find all this talk about falling in love overwrought or goofy, and some people may not feel that way about what they work on. If that’s you, you have my full sympathy, and my advice is to keep trying new things until you find something that you really do fall in love with. It’s worth it. Also note that I am using the word “love” to mean something involving commitment, investment, and self-sacrifice, as opposed to infatuation; find something that gives you satisfaction, not merely pleasure.

The point of working on something, as opposed to taking a more general approach, is not just to cut the problem of becoming a scientist down to a manageable size. It’s also to give you some traction with real data and real arguments. If you tried to become a generic paleontologist, you’d have to fly at such a high level that you couldn’t afford to get engaged with the details of any one particular problem. If you go that route you will never “drill down” enough to make a useful contribution; you may become a very well-informed enthusiast, but you won’t be a very productive researcher.

Step 2: Learn lots of stuff

“Data! Data! Data! I cannot make bricks without clay!” — Sherlock Holmes, “The Adventure of the Copper Beeches”, by Sir Arthur Conan Doyle

Once you have a direction, even a vague and temporary one, you have to accumulate clay. The clay comes in the form of facts, hypotheses (tested and otherwise), ideas, suggestions, and so on, and you get it mostly from reading papers.

You need clay for two reasons. First, you simply have to have a foundation of knowledge before you’re going to be able to contribute anything. Furthermore–and this is the step that seems to trip up many who aspire to contribute–you really need to have a handle on where the field is right now, and how it got there.

It’s pretty common for internet cranks in general, and absolutely pandemic for dinosaur cranks in particular, to argue that Ivory Tower so-called experts are all blinkered by orthodoxy and that outsiders with no technical training are better suited to having the big ideas because they are unshackled by the weight of knowing all that has gone before. These people are almost always wrong, because they keep reinventing the wheel, and the wheels they reinvent are often square. Either they’re solutions to problems that have already been solved (behind the state of the art), or solutions to problems that don’t exist (they misunderstand the state of the art), or, more rarely, solutions no one could implement because the methods or evidence just aren’t good enough yet (too far ahead of the state of the art). A good idea for a project has to be testable, but so far untested. Which means that if you want to make a useful contribution, you have to catch up with the cutting edge, and then stay caught up.

If you trust yourself and believe in your dreams and follow your star, you’ll still get beaten by people who spent their time working hard and learning things and weren’t so lazy. –Terry Pratchett, The Wee Free Men

It’s not a trivial amount of work, and it requires some humility. Rich Cifelli put me to work on what would become Sauroposeidon in the late spring of 1996, and we had a paper ready to submit in the late spring of 1999. Thanks to Brooks Britt and Kent Sanders, I started CT scanning and really thinking seriously about sauropod pneumaticity in 1998, and the major papers that came out of that were written in 2001 and published in 2003. So both of those major steps required about three years of work from inception to submission (and an additional year or two until publication). Not all of my papers have three years of work behind them, because as you progress you learn stuff that applies to more than one project and you get better at figuring out what you need to know to complete a project; the earlier ones involve more faffing about. But if you’ve never published, it wouldn’t be a bad idea to mentally prepare to spend a few years getting up to speed.

That’s another benefit of doing a formal degree program that Mike didn’t mention in Tutorial 10: it gives you some protected time in which to get up to speed. You can do it without doing a formal degree program. It will require more effort on your part, since you won’t have an advisor to guide you or fellow students to challenge you (although you may be able to find substitutes). But there’s no reason why it can’t be done.

Step 3: Think about things

When Newton was asked years later how he had discovered his laws of celestial dyamics, he replied, “By thinking of them without ceasing.” — Timothy Ferris, Coming of Age in the Milky Way

This seems like the easy step, when you’re considering it at one remove, either because you haven’t plunged in or because you’ve already learned to swim. After all, what could be more fun than thinking about dinosaurs (to pick an example completely at random)? But when you first start pulling the clay together, it seems like all the good ideas have been taken, like everyone else in the world is working on something 100 times cooler than anything you could ever think of, and that you will surely be doomed to work only on the most trivial problems because you’ll never have any really good ideas.

(Aside: if you have loads of what seem like really good ideas, then either you have already grown through this stage, in which case get back to work, or you skipped Step 2, in which case I’ll be happy to talk with you–in about three years.)

Fear not, because as long as you keep at it, you are going to have good ideas. In fact, pretty soon you’ll be drowning in them, and it will happen a lot sooner than you think. And I’ll tell you exactly how that’s going to happen.

At first, you don’t know anything, and it seems like all the good ideas are taken, but that’s because you don’t know anything. But as you catch up with the cutting edge, you will start to notice holes in the fabric of science: things that no one has done before, ideas that haven’t been tested, established “facts” that seem a little wonky or that have been upset by new discoveries. Now you’re getting traction. Not all of these holes are going to be worth patching. As you learn more (Step 2 again, forever and ever, world without end), you may find that some things haven’t been tried because they’re just intractable, and that some established facts only seemed wonky because you didn’t fully understand them (beware–this happens a lot). So stay humble, and keep learning, and keep thinking.

By “thinking” here I don’t mean simply staring off into space (although that is sometimes a symptom of deep thought), or sitting down with a notebook and pencil and deciding to think, although that can be a useful exercise now and then. It’s more along the lines of living and breathing your work. You have to engage with your subject material on a deep level. It will become what you think about in the shower. It may even invade your dreams. This is what I meant up above when I described it as “falling in love”. When you fall in love with someone, it’s almost impossible to think about anything else. With any luck, you’ll find a problem that occupies your mind similarly, at least for part of the day. I wrote the GDI tutorial when I was doing a lot of mass estimation for a couple of upcoming projects, and I found that I was mentally rotating volumetric models of Plateosaurus in my head on the drive home from work. Often I went to sleep with visions of translucent 3D sauropodomorphs dancing in my head.

At some point you are going to go through what I call the Big Flip, where the exponentially rising curve of your knowledge passes the exponentially falling curve of your perception of how much science has actually been done. As you attain some level of mastery of the field, you won’t see just a few holes in the fabric of science, you’ll see that science is mostly holes, and that what we know is tiny compared to what we don’t know, about just about everything. At that point, you’ll see potential projects everywhere you look. The problem then becomes not thinking of a project to work on, but deciding what to pursue from among the almost limitless array of things that you could work on, and that’s a problem for another tutorial.

Maybe. Neither Mike nor I have been active long enough to tell if we’re any good at sorting projects, and Darren is no help because his “solution” is simply to work on everything. About the only thing I know for sure is that sometimes you have to start a project to find out that it’s not worth finishing. Don’t feel bad about hopping off a project like that onto another, more promising one (to a point; you’re going to have to settle down and work sometime). Some projects actually get to the moon, and others burn up in the atmosphere, go into dead-end orbits, or blow up on the pad. Sometimes the only way to find out which is which is to strap yourself in and light the engines.

Surely, you think, I’m exaggerating about the “almost limitless” array of things to work on. But I’m not. Just as big-S Science is dwarfed by big-I Ignorance, pretty soon your own completed science will fall far behind your own potential science, and it will never catch up. Right now I have about a dozen published papers, and 35 folders on my hard drive for projects I have taken seriously enough to start working on. A handful of those will be published in the not-too-distant future, a few more are things I might work on after that, and the vast majority are things I’ll never get around to. Everyone I know who is active in science feels exactly like this (Darren Tanke has “about 55 writing projects on the go”, by his own count). In fact, one sign that you’ve had your Big Flip is when you look around at all of the stuff you have going on and realize that you are going to die with a lot of work left to do, whether that’s tomorrow or a century from now. When that realization hits, don’t despair. It means you’ve arrived. Dive into whatever looks the most promising at the moment, and vamp till fade.

Step 4. Be open

If we knew what it was we were doing, it would not be called research, would it? –Albert Einstein

I can tell you from experience that parents with infants are hyper-alert, because they don’t want to drop their babies. For the first few hours and days, this alertness is almost exhausting. It’s like when you first learn to drive and you’re constantly twitching the steering wheel. Eventually you learn how to be hyper-alert and still do other things. The “don’t trip on that rug/avoid sharp corners/be prepared to fall on your back” program is still running, but you can have other windows open on your mental desktop. Evaluating the potential hazards in whatever space you’re in becomes reflexive.

When I say, “be open”, I’m talking about cultivating an alertness of that kind. Your research program will be running most of the time, even it it’s minimized or in the tray while you do other stuff, and it will constantly evaluate the facts and ideas you encounter and see if they fit. The other part of being open is feeding your brain a cosmopolitan diet. Inspiration comes from the most unpredictable sources. There’s no way to force inspiration to happen, but you can improve the odds by deliberately seeking out the unfamiliar.

There is a great bit in one of David Quammen’s essays in which Quammen is roaming the Montana State University library and he comes across Jack Horner sitting on the floor between two rows of shelves with journals spread out all around him. Quammen says, “Hey, Jack, what are you doing here?” Horner looks up and says, “Having ideas.” The best part is that the journals weren’t even paleo journals, they were ornithology journals. (Note to DMLers: including a positive anecdote about Jack Horner is an intelligence test. Try not to fail.)

The downside of deliberately seeking out new stuff instead of staying with the bounds of your research program (the Sofa of Science!) is that it will make you feel stupid. It doesn’t matter what line of work you’re in, whether it’s paleontology or programming or construction, there is something that you are an expert on now that you weren’t when you started, whether it is taphonomy or recursive subroutines or pouring concrete. But you weren’t an expert when you started, and when you started you probably spent a lot of time feeling stupid. But you learned quickly, partly because you were anxious to get past feeling stupid, and partly because trying dumb stuff is a good way to learn what works and what doesn’t. If you’re not feeling stupid, you’re too comfortable, and it might be time to do an audit and see if you’re actually contributing to science at all. Science requires a certain kind of stupidity (Schwarz 2008).

And once you’ve got a research program, it’s all potential grist for the mill. Throw facts and ideas in the air and see where they land (the whole idea is that you can’t predict that in advance). Some will land behind the cutting edge, some too far out in front, and some entirely off the map. But one or two might land on the cutting edge, or ideally just ahead, and then you can push the whole field forward, just a little bit.

Conferences are valuable because they give your mental program a huge slug of input. You don’t get sprinkled with new facts and ideas, you get carpet-bombed, and as the volume of fire increases, so do the chances for a successful hit. I got an idea for a sauropod neck paper from a talk on the foot morphology of perching birds at ICVM last summer. Another long-delayed project was inspired by a talk on the development of snail shells by a fellow grad student back at Berkeley. That’s one reason I like smaller conferences like SVPCA, with no concurrent sessions. If everyone is in one room, you’re bound to sit through talks you wouldn’t see otherwise, and those are where you’re most likely to get fresh ideas. At SVP I always opt for the dinosaur talks over the mammal talks, and that’s good for Step 2, but bad for Step 4, because I already know what most of the dinosaur talks are about. I’m adding a little clay, but possibly losing out on a lot of inspiration. If I was really taking my own advice, I’d go see the fish talks.

So, conferences are good, but really they’re just an intense version of something you can do all the time, which is choose to feed yourself new things.

Coda: Publish

“I was on an [email] list with Tom Clancy once. Mr. Clancy’s

contribution to the list was, ‘Write the damn book’.” –Greg Gunther.

I know Mike used that quote before, but it bears repeating.

This tutorial is not aimed at everyone. It’s aimed specifically at people who were inspired by Tutorial 10 but don’t know where to start. Well, now you know. Step 1 is a choice. Steps 2, 3, and 4 are habits to be cultivated, for the rest of your life. But you can pick a project, read all the papers you want, think about your topic constantly, and drench yourself in the rainstorm of new ideas, and none of it counts until you publish. It may be a great way to pass the time, it may be tremendously rewarding, and you may develop as a person, but it won’t be science until you communicate it in a form that other people can use (i.e., papers, not mailing list posts–you dino folks know who I’m secretly addressing).

Write the damn paper.

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Disclosure: a couple of passages in this post are cribbed from the never-completed series, “Blundering toward productivity”, on my old blog. That series was a straight up pastiche of Paul Graham, but it includes a few more relevant ideas and might be of interest. Part 1, Part 2, Part 3, Part 4.

Finally: I can only link to things, I can’t put a gun to your head and force you to read them. But if I could, I’d make you read Schwarz (2008) first–it’s one page, and it’s important. After that, I’d make you read all the linked Paul Graham essays. If you have time to slog through my blatherations, you have time to read the better stuff that inspired me.

Update 2014-03-16: This post inspired a follow-up, and this much later post touches on some of the same issues.

Reference

Schwartz, M.A. 2008. The importance of stupidity in scientific research. Journal of Cell Science 121:1771.