I’ve recently submitted a proposal to the National Science Foundation, and it’s got me thinking about how I find ideas for research. The proposal was for an instrument to enable research*, and that meant that, for the first time in years**, I had to write something that could convince other people that my research is interesting, important, and worth doing. Out of all the things I do in my job, that’s the thing that I find the most difficult. I love teaching – teaching is fun, and makes everything worthwhile. (Even grading isn’t so bad all the time.) And doing the research itself is fine, too. But coming up with an idea, and convincing other people that my ideas are worth exploring? That’s the hardest part about science to me, and it’s the part that has brought me closest to quitting many times.
Sciencewoman has a fantastic post on the process of writing a grant proposal, and her commenters have a lot of interesting things to say about how they go about finding ideas. Here’s SW’s initial suggestion for where to get started on the part that’s most difficult for me:
2. Brainstorm some general research topics that build on what you already know. (Read some recent reviews or research papers to help you identify open questions in the field.) Gradually narrow your focus to a few related possible research questions.
I have a confession to make. I am not inspired by research papers. It’s taken me decades to get to the point where I can really read them critically, rather than smiling and nodding and saying “yes! that’s it!” (And that would be the best case – in the worst case, I fall asleep trying to read them, or am completely confused about the argument.) Even now, I need to do something beyond merely reading to try to find the places where there are open questions. In a lot of cases, that means piecing together ideas from a number of different papers, maybe from different sub-fields, and figuring out where they disagree. And yes, I can do that now, and it’s important for me to do that in order to put my research into a context. But it’s not inspiring, if you know what I mean. I need something else to keep me going.
Inspiration, for me, comes from the rocks. Sometimes in the field, sometimes at microscopic levels, but always from the rocks. My favorite moments doing research have been times when I’ve run across things that I didn’t expect – things that shouldn’t have been there if the existing explanations were correct. It’s the unexpected observations that push me to be creative, to think of something new.
As an example: when I moved to Vermont, I decided that I wanted to start doing research there. There were a lot of metamorphic rocks, they were easy for undergrads to get to, and the odds of getting mauled by a grizzly or stranded without enough food while waiting for a helicopter were low. (My Ph.D. field area, in Alaska, involved grizzlies and helicopters.) I chose a possible field area by 1) looking at the metamorphic zones on the Vermont geologic map and picking out an area where the rocks had gotten hot enough to have interesting minerals, 2) skimming the old geologic reports to make sure the rocks would be likely to tell me something, and 3) finally choosing a place that looked like it might have some previously unrecognized complexities. (In this case, the area contained three minerals with the same composition but different crystal structures, representing three different metamorphic depths and/or temperatures. There had to be a story there.) I drove to the area, checked out outcrops near roads, and found a place where I could see some of the interesting minerals in the rocks. And then I went out there with a student.
We didn’t have much of a question other than “what’s really going on here?” until he looked at his samples in detail. We expected to see rocks that had been heated up by contact with a granitic magma after they deformed, and hoped we would find remnants of the previous metamorphism that had accompanied the older deformation. We found something different: rocks that had been deformed after (or during) the contact metamorphism. And my research for the next several years tried to figure out why.
In the end, the research tied into questions other people were asking about how magmas move through the crust. (There’s a session at GSA in Portland dealing with related questions: T73. “Melt Microstructures: Evidence for the Presence of Melt and Consequences for Deforming Continental Crust.” I’m not presenting in it, but I’m planning to go to it.) The structures that I found shouldn’t have been compatible with simultaneous magma intrusion, but they’re there. And that means there’s something going on that we don’t fully understand. And that means there’s room for new research.
So field work feels productive to me, in terms of sparking ideas. But there’s more to it than that. I’m fascinated by places and their histories. I like imagining the changes: here in Durango, a volcanic arc, a sedimentary basin in an unknown tectonic setting, mountains of unknown size, the inland extension of a continental shelf, the edge of the Ancestral Rockies, a delta at the edge of an interior seaway, the shadows of incredibly explosive volcanoes, and finally today, the edge of the Rockies. In New England, I liked to imagine what the continental collision that created the Appalachians was like. In Alaska, I liked imagining subduction, collision, and collapse of the mountain belt that was replaced by the Bering Strait. I guess what I like is a type of historical geology, except that traditionally historical geologists have told their stories with fossils and stratigraphy, and I prefer to read the stories half-recorded by ductile rocks from halfway down in the crust.
I’ve just finished reading The Rejection of Continental Drift*** by Naomi Oreskes, and it’s made me realize that I’m some kind of weird methodological throwback. Back in the day, geologists (especially American geologists) valued knowledge from the field above everything, and pushed their theoretical musings into the final sections of monographs. (Oreskes gives the examples of Clarence Dutton’s Geology of the High Plains of Utah and G.K. Gilbert’s Lake Bonneville – brilliant works, as important for the interpretations in them as for the descriptions that dominate them, but you wouldn’t know it from the titles.) Oreskes argues that American geologists were hostile to Alfred Wegener’s ideas, in part, because Wegener started with his conclusion, and then used field evidence to support his argument – that he constructed his argument in a way that went against American geologists’ ideas of how the science should be done. But by the 1960′s, fieldwork had come to be seen as less scientific than work rooted in fundamental ideas of physics and chemistry, and when plate tectonics was finally accepted, it was based on geophysics, especially seafloor magnetism and seismology (even though field-based evidence, including a lot of work by South African geologist Alexander du Toit, also supported the idea of moving continents). Science that starts in the field has come to be seen as merely descriptive, natural history rather than science, and fundamentally unproductive as a way to understand the world.
Things may be changing since the 1980′s, when solid-earth geoscience was dominated by the people who developed and first applied plate tectonics. Fieldwork may be regaining respect****. As an example, I just received this announcement of a session at AGU (which has risen in prestige, I suspect, because of its traditional roots in experimental and theoretical geoscience): “Continental Deformation and Rheological Complexity”(T07)”…will be accepting contributions from experimentalists, numerical modelers and field geologists across all fields…” And the biggest metamorphic sessions at AGU in recent years have been about ultra-high pressure metamorphic rocks, which have gone deep into the mantle and somehow been exhumed. If it hadn’t been for observations of very high pressure minerals (such as coesite, the high-pressure form of quartz, and diamond), nobody would have suspected that rocks subducted to such depths could return to the surface. And you can’t find rocks with unexpected minerals without doing field work.
But how does a geologist justify doing the field work that could lead to new ideas? I’ve tried to avoid it – I did field work in my own backyard, unfunded except for little grants to support undergrads. These days, I’m doing unfunded field reconnaissance while hiking with my kid. (Unfortunately, the rocks I want to see are at least four miles into the wilderness, and that’s too far to drag a six-year-old. But in a few years…) I’ve also gone for long runs into the wilderness to see the rocks, tagged along with other people’s grad students, or gotten descriptions of rocks from other field geologists. It’s not very efficient. Fortunately, I’m not at a major research university, and my professional survival doesn’t depend on whether I do transformative research or not. But I don’t know how to advise students, because the right way to do science in part depends on what reviewers think is right.
Which is a long way of saying that I have no good suggestions for Sciencewoman.
What about you? Are you inspired by the things you think are supposed to spark your ideas? Do you build ideas from existing theory, or do you stumble across problems in the field, or is your process of science something totally different?
* I submitted it to the NSF-MRI program. If it had been a proposal for an instrument to use in teaching, I would have written it for the NSF-CCLI program, but although I would use this instrument with students, I really want it for my research (and for the research of a whole bunch of colleagues).
** One advantage of being at a teaching-intensive institution: I don’t have graduate students who need to be supported by grants. I’ve gotten grants, but they’ve supported innovative teaching.
*** American geologists didn’t buy Alfred Wegener’s model of continental drift in the 1920′s, but they ended up embracing the concept of moving continents as part of plate tectonics in the 1960′s. Oreskes’ thesis is that the reason that’s frequently given – that Wegener’s model lacked a believable mechanism – is wrong, and that the reasons were far more complicated and interesting. Oreskes’ book is fascinating – thanks, Ron, for recommending it.
**** Other ways of doing geology are also becoming more respected by people who do fieldwork. Modelers, experimentalists, and field geologists use each others’ work all the time. But deriving stuff from physics and chemistry has still been more productive in terms of Big Ideas than field work has: I would argue that the most important work in the geosciences in the past few decades has happened in climate studies, especially in understanding the role of carbon dioxide in shaping climate change. It’s not just important work because of its role in political debates; it inspires the thinking of people working on ancient climates. And it was driven, first, by understanding of physical and chemical processes in the atmosphere.