Finding problems to solve
Unlike Lizard Guy, who started out with a deep curiosity for lizards, I did not start out with a deep curiosity for my research subject. That would have been quite impossible, since I had never heard of it before starting graduate school. How then, did I get into my subject and start finding problems to solve? As I commented in an earlier post, beginning grad students in my field only rarely identify their own research problems; generally they are suggested by the PhD advisor. Skookumchick asked me to elaborate on this idea:
I’m interested in this “problem-defining” thing you wrote about. How do the professors learn to define problems that are original? Is it just through experience with the field? Or do they just know what the field considers an appropriate PhD-level “problem?”
Generally, each professor or lab has its own expertise– experimental techniques, equipment, theoretical tools, etc. Once you have worked in an area for a while, you generally know what the "big limitations" and challenges of your research area are. Suppose you drill ice core samples in Antarctica, and use them to read out a record of the ambient gasses. You know that the deeper into the ice you are, the farther back you are in time, but that your dates are only accurate plus or minus one hundred years. And suppose EVERYONE you know working on ice core samples has the same problem, and that the ice-core methodology is actually a major method of tracing climate change. And then, one day you have an idea of how to reduce this error to twenty years. Immediately, you start thinking of all sorts of implications of this reduced error for models of global climate. And so even if your idea only has a small chance or working, you see it is a big pay-off problem, and you are motivated to work harder on it.
This is what you gain through experience– an appreciation for which problems (if solved) could have long-range implications. Of course, you are not always correct. Sometimes very obscure problems turn out to be important later on, and seemingly important problems turn out to be relatively useless. Nevertheless, you gain a sense of conviction about what areas are promising, and potentially "worth" working on. (Not to mention: which problems you can get funding for and publications on! Here, the long-range implications are the selling point.)
While an individual grad student might be able to go choose an area of science, start reading relevant papers, and eventually find some problem to solve (whether experimentally, theoretically, or computationally), there is a high chance of either unknowingly duplicating previous work or solving something that no one else seems interested in. This seems to be the case in most areas of physical sciences (chemistry, physics, geology, materials science), chemical, mechanical, and electrical engineering, and applied math. It is particularly the case for highly theoretical fields that require years of training just to approach the subject, like theoretical particle physics. I have known a very few scientists or engineers in these fields who were able to completely define their own problems, starting in grad school, but only a VERY few. It helps to be quite independent and also insensitive to criticism. I also know a few others who found there "was nothing interesting to study" in their grad departments and stayed home all day "working on their own things," e.g. programming increasingly complex computer games, or writing their own economics textbook despite no formal background in the subject. In other words… they followed their own ideas, but never made it to the PhD.
Is it just me, or do advisor types tend to save the highest-risk projects for PhD students. To use your example,
“Ahh, the ice core conundrum. McEnnis’s group spent thirty years before giving up on that one. Mind you, there’s a remote chance that this new thorium disequilibria technique might be applicable; lets get a grad student to work on it.”
Comment by Lab Lemming — August 11, 2006 @ 10:39 am
I did something that I devised on my own after my first high-risk, advisor-suggested project ended in a morass of non-communication (I learned that the other graduate student had moved on to something else secondhand, and not from my advisor). I suppose I can be proud of the fact that I did a project largely on my own, but the constant uncertainty about whether I was even remotely on the right track after the trauma of my first project essentially killed my enthusiasm for staying in physics. Meanwhile, my advisor had his bread and butter research that he was building his name with. I took on just about all of the burden of risk.
Comment by Kristin — August 13, 2006 @ 3:54 pm
Then again… Ashkin and Chu never patented optical tweezers, because they didn’t think they would be “useful for anything.” So much for being able to see (or being motivated by) the long-term implications of a piece of research– they just thought it was a cool effect! Now optical tweezers are a staple experimental technique in molecular biophysics and other fields and are produced commercially.
Comment by drshellie — August 14, 2006 @ 1:23 am
Dr. Shellie,
If you don’t mind my askin’, how did you choose which school to go to grad school at, if you didn’t know anything about your advisor’s research. Just about everyone I know of in geo grad school goes about it in the following way:
1a. Read a paper and decide that the subject interests them, or
1b. Ask their honors/masters supervisor who is working in a field that interests them.
2. contact the paper’s author/ person suggested by their advisor.
3. Decide, based on that contact, that they want to work with that person on their subject matter, apply, and start working.
But both options for 1 involve knowing what your future advosor does before approaching him/her for consideration.
Comment by Lab Lemming — August 14, 2006 @ 1:35 pm
Hi LL, I am a wee big cagey about what subject, exactly, my PhD is in, since knowing that (plus some Googling) is pretty much sufficient info to blow my “anonymity” cover. But suffice it to say that most of the undergrads I knew who were applying to grad school apply in order of school ranking. Top 5, top 10 US schools, etc. depending on how good their records are and how assured they are of getting in to those schools. I did have a very specific idea of what area I wanted to study in grad school based on my undergrad research, but changed directions in grad school based on the working conditions in the different groups– I was looking for a group with a reasonable number of grad students and good funding, for example.
Comment by drshellie — August 14, 2006 @ 3:50 pm
Let me add– in the US, you usually have at least 1 year at the beginning of a PhD program where you are taking classes and not necessarily doing serious research yet. This is because the US undergrad training in science involves fewer science classes than, say, England and many other countries– so we are still taking classes as PhD students. Some fields/departments have research rotations where you work a few months in several different groups. So many people just apply to a department (knowing there are several people there they may want to work with) and pick an advisor later. Often, the advisor will generally NOT commit to accepting you in his/her group before you show up, with certain exceptions. By the time you join a group, you usually do know something about the group’s research area.
Comment by drshellie — August 14, 2006 @ 3:56 pm
LL: I should also mention– typically undergrads I knew applied to five or more universities for grad school at the same time, then chose from among the ones they got in to.
Comment by drshellie — August 15, 2006 @ 5:53 am
I think I am doing my PhD all upside-down and backwards. I thought I was interested in engineering education, and chose my advisor because he had graduated some other PhD students in an engineering education-y area. My difficulty has been that I haven’t been interested in any of the “problems” my advisor has thought interesting (then again, he’s not paying me, so I haven’t had to do them anyway) and I don’t think they are worth the time it would take to understand them. There is no real “field” of engr ed - Purdue is the first university to have a department of it, opened in the last couple of years, followed by Virginia Tech, I think - and I know I’ve read more widely than he in it. I guess one shouldn’t choose a PhD advisor who isn’t really an expert in whatever area you’re interested in; however, that’s no way to trailblaze…
In my current research, I ask people how they determine what problems are worth solving, and, with only one exception, they’ve been ones driven by engineering’s relationship with industry, and not ones that really *need* solving, like global warming or getting the world enough water to drink. What do you do when your area defines problems in ways you think misses the mark? I guess you’re supposed to keep your head low until you get into a steady job, and then start your subversive campaign. Too bad we have to wait that long.
Thanks for this post, and sorry it’s taken me so long to comment…
Comment by skookumchick — August 18, 2006 @ 6:42 pm
Skookumchick– a lot of engineering research seems to be driven by the funding agencies (such as DARPA) and grants from industry. I suspect it is not entirely the attitudes of the resesarchers themselves who are responsible for this focus. To do experiments, you need equipment and salaries for grad students and postdocs and technicians, and certain areas have MUCH more funding that others. Are you looking at these issues in your research? I bet if you look at the few people who are doing sustainable development work in engineering you will find their funding sources are quite different and provide less money overall.
Comment by drshellie — August 19, 2006 @ 8:45 pm
Yes, indeedy, I have come across this in my work. Funding agencies seem to have a tremendous amount of power in controlling the direction of academic research. (I’m trying to find someone who was an NSF program director at my school to interview to try and get a handle on this.) So where do the *funders* get their priorities from? Sometimes directly from the government (like when DOE doles out money) but sometimes there are several layers of bureaucracy - sometimes in the form of academics working as administrators for a few years - that make it more difficult to see who decides. Sometimes, as you say, it’s industry who funds research, but even then it’s not strictly the market which decides which projects are worth funding. More and more, there are non-profits who fund research, but then you get into the thorny issue of which funding is “good” funding for getting tenure? Anyway. I hope to get into this a bit more. Thanks for the thoughts.
Comment by skookumchick — August 21, 2006 @ 10:14 pm
I have some experience with DARPA; the funding priorities get set by a combination of bottom-up and top-down methods. Professors try to sell ideas to DARPA program managers for possible funding. DARPA program managers collect these ideas; meanwhile, they draw on their experience and directives from their bosses to develop “programs.” They then try to sell these programs for funding to their bosses. If they get money, they dole it out to various professors– maybe as many as 30 or 40. Meanwhile, from the top down, Congress allocates funding for different departments and sets the budget for DARPA and other agencies (DOE, NSF, NIH, etc). The heads of various agencies will be partially responsible for deciding how that money gets divided among different fields. And then the people below them divide that money, and so on, until you reach the program manager level.
In NSF, I believe it is less “program” based– there is funding allocated for different types of science, and proposals are solicited for each. The proposals do not have to meet any particular predefined goal.
Some agencies do peer review of proposals– this varies by agency– so in the case of NSF, all proposals get rated by other scientists in the field. The amount of “say” given to the opinion of the reviewers vs. the program managers can vary a lot depending on the program.
Comment by drshellie — August 22, 2006 @ 3:45 am
PS– Skookumchick: if you want a good description of how this all works, find an engineering professor with a big group (20-30 students) and get him/her to describe how they are funded!
Comment by drshellie — August 22, 2006 @ 3:47 am