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A sequential framework for teaching how to write good research questions

The more theses I supervise, the more essays I read and the more papers I have to peer-review for publication, the more I realize how important it is to teach how to craft good research questions. Many students of mine come with a general idea of what they want to study for their thesis, but then get stuck with how to develop the research project. And for me, the core issue when doing research is asking good, researchable questions. Key to this issue of “researchable” is the practicality and feasibility of undertaking a project that will provide answers to the question.

My campus office when I am working

To develop good research questions you need to READ, absorb and synthesize a lot of literature in order to find a gap to fill.

I use my own work to teach my students how to write good research questions. I show them how I am interested in particular topics, and how my work is driven by having an inquisitive mind and wanting to get answers to complex challenges by asking the right questions (you can read more about my research trajectory here).

I had been pondering for a long while how to teach my students how to write good research questions, and as I was reading Patrick White’s “Developing Research Questions”, I came up with a sequential approach to teaching the craft of writing good, researchable questions. This approach (which is a bit different from White’s funnel (see page 26), but at the same time, uses the same general-to-specific strategy) walks the student (or researcher!) through the different stages of developing a solid research question by going from the more general to the more specific.

In this blog post, I walk the reader through my sequential framework.

  • Research Topic: This refers to the broader topic one is interested in. For example, I am quite interested in theories of the commons as posited by Elinor Ostrom. That’s one of my broad research areas: the governance of resources that can be accessed by many but are also exhaustible. One can have an interest in many research topics, but it is always important to go broad in deciding what kinds of issues one wants to research (for example, health policy in Mexico, homelessness policy in the United States). Then one can go narrower when focusing on a specific area of interest (geographical, scale, sub-sector/population).
  • Research Interests: These refer to more narrowly defined sections or parts of a broader research topic. In my case, my specific research interests lie in the governance of unorthodox commons, such as wastewater, bottled water, and solid waste. Some people may find the notions of “interest” and “topic” interchangeable. I view the Topic as a broader area of work, whereas Interest is specific to the researcher. For example, I work in water governance, but I am interested more specifically in how urban water is managed.
  • Gap in the Literature: The gap in the literature refers to that specific niche where your contribution may lie. The unanswered questions. The broader realm (narrower than the research interest, but broader than a research question) where you have a wide range of questions to ask. I have already written about how we can find the gap: for a dissertation or thesis proposal and for a research paper and/or literature review. As an example, in my case, I contribute to narrow our gap in understanding how commons theories work in the case of unorthodox, “unwanted” resources. These resources are what I, in my research, have called “negative commons”. My work fills the gap on how negative commons are managed and re-valued.
  • Originality: This property of research work refers to the novelty, to how and why is a new analysis worthy of study. Generally, what I ask my students to think about is when trying to understand whether their work is original is: “how is it that nobody or few people had thought about this particular topic and interest and issue before in the way you are approaching it?” When I ask my students this question, their eyes light up. They understand that you can be original by looking at an older dataset with new theories, developing a new theory, or assembling a new dataset (see my discussion and conversation with Dr. Michael Horowitz). In the example I provide, my work is original because wastewater governance researchers hadn’t discussed effluents as “negative commons” (though Dr. Alida Cantor has contributed to this conversation in her own work analyzing wastewater as a commons, we use slightly different conceptual frameworks).
  • Research Question: A good research question can be answered, is researchable, feasible, and contributes to narrow/close athe gap in the literature through an original or novel contribution. Again, it is important to remember that the contribution does not need to be “life-changing” or “earth-shattering”. Most scientific research is incremental and therefore one contributes by adding bits and pieces to a broader, larger global puzzle. See, for example, my earlier post on developing solid research questions. In my case, I have studied and researched some of the key obstacles to robust wastewater management in one specific geographical area of Mexico, the Lerma-Chapala river basin. I have done so by developing and applying my “negative commons governance” framework.

I have crafted a handy Google Sheets spreadsheet that you can use to both teach how to write good research questions with my framework, and for your own research projects. It can be downloaded by clicking on this hyperlink. Hopefully this blog post, framework and spreadsheet will be of use to you all, and if you are an instructor, to your students!

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Posted in academia, research, research methods.

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