Picking a Question

Perhaps the most critical step in doing field biology is picking a question. Tragically, it's the thing that you are expected to do first, when you have the least experience. For example, it helps to get into grad school if you appear to be focused on a particular set of questions that matches a professor's interests. However, at this stage in most students' careers, many topics sound equally interesting, so this forced focus is difficult or even painful.

The question that you pick should reflect your goals as a biologist. If you are a new grad student, your short-term goal might be nothing more than to succeed in grad school. However, it's important to look farther down the road even as you're beginning. A common mid-term goal is getting your first job. For most jobs—those at research universities, small liberal arts colleges, federal agencies, nonprofit organizations—search committees will want to see a strong record of research and publication even if you won't be expected to conduct research or publish a lot on the job. Box 1 presents a justification for this bias. Search committees want to know that you are capable of advancing the field and communicating effectively. (They may also want to see other qualifications and experiences, such as teaching.) We consider strategies for getting different kinds of jobs in ecology in chapter 7. Achieving a goal like getting a first job also demands that you build a mid-term plan for your research. For example, your plan might include solving a problem in restoration, such as how to return a particular piece of real estate to some level of ecological functioning. A more conceptual mid-term goal might involve making people rethink the interactions that are important determinants of the abundance or distribution of species.

Long-term goals are harder to formulate but are at least as important. (If you don't believe this, talk to some burnt-out researchers late in their careers. Some people never bothered to stop and figure out what they really valued and wanted to accomplish for themselves. Thinking through your big-picture, long-term goals makes doing the work more enjoyable.) Some long-term goals that you might want to try out include attempting to influence how you and others think about or practice a certain subdiscipline of biology, or how we manage a habitat or species. Such long-term goals can provide a yardstick with which to evaluate your choice of project. Your long-term goals should suit you and not necessarily your major advisor (who may consider a nonacademic career a waste of time) and not necessarily your parents (who may try to convince you that a conceptual thesis will leave you unemployable). Refer to the "How to Get a Job" section of chapter 7 to begin the difficult work of untangling your goals from theirs.

From the beginning, consider your short-, mid-, and long-term goals as you pick your research question. Push yourself to pose a question that both satisfies your goals and will be of broad interest to others. At the same time, don't let the quest for the perfect question keep you from making tangible research progress. Figure out how narrow or broad you want your research question to be. You should recognize that if you answer a very specific question, your results may be considered important by only a very small community. Academics are more likely to get enthused about a more general question. On the other hand, it is also possible to ask a question that is too general (theoretical), so you should ask yourself if your answer will reflect reality for at least one actual species. Having a model organism in mind will keep you more grounded in reality and increase the size of your audience.

If your question is very specific, ask whether you can generalize from your results. You may find yourself answering a specific, non-conceptual question about fisheries biology, restoration, and so on if you receive funding from an applied source. It may not be possible to couch your question in more conceptual terms. If so, you may be able to ask a complementary, more general question as well. For example, your specific question might be which animals visit a particular night-blooming flower. More general (and interesting) questions might be which visitors succeed at pollinating the flower and what qualities of the flower and visitor make pollination more likely. The answer to these latter questions will be compelling to a wider audience.

Not only should your question be of broad conceptual interest, but it should also be as novel as possible. All projects have to be original to some extent. We all like to hear new stories and new ideas, and ecologists place a large premium on novelty. if you are asking the same question that has been answered in other study systems (that is, with similar organisms in analogous environments), it behooves you to think about what you can do to set your study apart from the others. that said, if you are trying to start a project and haven't yet thought of a novel question, one useful way to begin is to repeat an experiment or a study that captured your attention and imagination. Sometimes repeating a published study as a jumping off place will keep you from getting stuck and will inspire you to move in an exciting new direction.

Policy makers are much less concerned with novelty than academics are. If you are funded by an agency to answer a specific policy question, you will need to balance your academic colleagues' expectation of novelty and your funding source's demands to answer the specific question for which they are giving you money. Your first priority should be to generate relevant data for your funders; however, if possible, ask additional, complementary questions in your study system that can lead to publishable research.

So you're looking for questions that are specific yet general and novel yet relevant to your goals. You could fret about this for years. Don't obsess about thinking up the perfect study before you are willing to begin (see box 2). One of the most unsuccessful personality traits in this business is perfectionism. Field studies are never going to be perfect. For example, don't get stuck thinking that you need to read more before you can do anything else. Reading broadly is great, but you will learn more by watching, tweaking, and thinking about your system. In addition, it is not realistic to expect yourself to sit at your desk and conjure up the perfect study that will revolutionize the field. Revolutionary questions don't get asked in a vacuum; they evolve. You start asking one question, hit a few brick walls, get exposed to some ideas or observations that you hadn't...