Honestly, the first good research question that occurred to me arrived during my third year of graduate school. Maybe that is because I’m not that bright. Or, maybe it is because of the way that we develop our understanding of the world. During the first three years of graduate school, we took courses that reflected the breadth of political science, and courses that immersed us deeply in the literature of our subfields (in my case the study of Congress). Without understanding the questions that came before—and the answers that were offered—it is nearly impossible to develop a truly unique research question.
The first step in developing a research question is to have some familiarity with the literature in your discipline.
Chances are, you are an undergraduate student. You have received a broad introduction to political science, sociology, or whatever your field happens to be. Now, you are being asked to write a research paper for a course, a capstone class, or an honors thesis. You’ve read and heard a lot about different topics, but how is one to choose to focus on a single topic?
My first research question was not really mine. The eminent Yale political scientist, David Mayhew, had just published a book titled Divided We Govern. In the book, he examined the question whether fewer important laws were passed when the White House was controlled by one party and Congress. His finding was that important laws were just as likely to pass under divided government as under united government.
Based on what I thought the existing literature had to say, this was an odd finding. It was a finding that puzzled me. The literature told us that divided party government will result in more conflict between Congress and the president, and thus result in fewer “important laws.”
What was going on here? My first impulse was to believe the finding. David Mayhew was the father of congressional studies. His book was published by Yale University Press (a very prestigious university press). Political scientists were hailing the finding.
But the finding just did not ring true to me.
Professor Mayhew included his data in the book, so I pored through it. He used an interesting approach to generate his list of important laws. It proceeded in two steps. First, Professor Mayhew looked at the New York Times and Washington Post to identify important laws as indicated by end of year “wrap up” articles about Congress. Then, he scoured libraries for books about important laws. Presumably, if someone is taking the time to write about a law it is considered important. These two lists were put together to generate a list of important laws.
What occurred to me was that an important law was one that 1) addressed a contemporary “problem” in governance (as indicated by newspaper articles) and, 2) it endured, it lasted, it was judged in retrospect, in books, to be of lasting importance.
When I narrowed his list using these two criteria, I found the opposite of Professor Mayhew’s finding: fewer important laws passed under conditions of divided government. My finding was robust and it was consistent with the existing literature on Congress and the presidency.
How does one find a research question?
The truth is, they are all around you. Listen to what people around you are talking about or news stories you hear in the media. Statements that you find in your textbook or other readings for your classes are especially ripe for research and are often (for a variety of reasons) unsupported by evidence. A curious observer will hear assertions of fact all around and ask herself: “Is that really true? What’s the evidence to support that? Is there any evidence?”
Sometimes research questions are found in the concluding sections of journal articles and book chapters. Researchers will often highlight future directions for research or discussion questions that are unanswered by their work. That can be a good place to get started on your research.
What is a good research question?
A good research question is relatively narrow. Mine was not a “major finding.” It was not going to win me a Nobel Prize. But it was important. It produced an article in a journal and helped me to get my first academic job. It did not answer all the questions about how divided government impacted American national governance, but it took on a small part of the debate, which has raged ever since.
A good research question can be answered, at least tentatively, through the research process. Normative statements or questions are usually not amenable to research. “Capitalism is better than Socialism” or “Donald Trump is a good president,” these statements cannot be resolved through research. Answers to these questions depend on individual values. Your research should focus on a question that can be answered by appealing to empirical data (qualitative or quantitative). Productive research questions might be “Do capitalist countries generate a higher standard of living than do socialist countries.” You will have to define what you mean by “higher standard of living” (e.g., more personal income, higher levels of education, less civil unrest), but your research question will produce a useful basis for your project.
A good research question does not need to be profound. This is particularly the case with undergraduate research. If you are working on a Masters or Doctoral thesis, a unique, and more profound finding is important. But for undergraduates, at least in my opinion, your research project should illustrate your ability to complete a research project, interpret your results, and defend your approach. Hopefully, this is NOT the last time you are engaging in research, and you will get better at it each time you take on a project.
A good research question does not need to have an immediate application. It was not clear at the time, for instance, what the immediate application of John Nash’s discovery of the “Nash Equilibrium,” or Darwin’s Theory of Evolution was. However, these ideas eventually became useful in many fields. Your research does not have to be this important or have any immediate applicability. You should be able to explain why answering the question is “important” may have implications for some larger constellation of questions or problems.
A good research question is one that you have the data to address. This does not mean that your data have to be original. Sometimes, as was the case with my work on Mayhew, you can make use of existing data and look to replicate an existing finding. That is, using the same data and approach as an existing study, can you arrive at the same results? What if you add some new variable, or conceive the “dependent variable” differently—like I did. What happens to the original results? Faculty web pages often contain the data to replicate their studies. The Interuniversity Consortium for Political and Social Research (ICPSR) has thousands of datasets, and bibliographical references, that you might be able to download for your research project.
A good research question is “doable.” No matter what the assignment (course project, capstone, honors thesis, master’s thesis, or doctoral dissertation), your research question should be something that you can complete in the time you have available. Big research questions are good. You might be interested to know whether NAFTA was good or bad for the American economy. But do you have the time available to answer that question? Probably not. That could take years. Maybe an entire academic career.
A good research question is interesting to you. You are going to be working on this project for a few weeks, months…maybe even years. Does the research question get you excited? If it does, you’re on to something. If it doesn’t, you may want to reconsider. It is difficult to become motivated to work on a project that is of no interest to you. You may have to work long nights and weekends. Is this a project that you are willing to make those sacrifices for?
There is nothing easy about conducting research. If research were easy, everyone would be doing it! Doing research is like anything else, you have to do it repeatedly to become really good at it (and even the best researchers experience failure!). But research is exciting. For the curious mind, having the opportunity to address something you find puzzling is can be one of the most rewarding things you can do. Without a doubt, conducting research has provided me with a career full of excitement, along with some disappointments and moments of enormous exhilaration.