Identifying and Engaging Authentic Problems: Exploring “Good” Research in the 21st Century

By Daniel Clausen - 04 April 2024
Identifying and Engaging Authentic Problems: Exploring “Good” Research in the 21st Century

Daniel Clausen argues for “challenge-based” and “solution-generating” research.

What should we research? How should we spend our time (and institutional money) conducting research? Why should our colleagues spend time reading our research? Will the many hours we spend doing research result in something worthy of our scholarly communities?

Answering these various “So what?” questions will lead to deep soul-searching and maybe even anxiety that hinders the research process (see Gustafsson & Hagström, 2018, 2023). (For that reason, one may ignore all the aspects of this article that cause you anxiety and instead conceptualize research as a useful form of “play.”)

A research project may be justified in terms of “filling gaps” in current knowledge. However, are those gaps in knowledge worth filling? Research projects may be designed to respond to or answer “hot” topics in the field where cutting-edge research is being done. However, designing research in such a way may saturate certain topics while leaving others neglected. It may also lead scholars to chase the latest academic fad, motivated mainly by a desire to “join the conversation” and not be left out. In some cases, researchers may fit their research topics and objects of study to meet their preferred methods instead of the other way around (see Shapiro, 2002, p. 589). Motivations for prioritizing methodological purity over other concerns may include: a wariness to travel outside of methodological comfort zones; a fear of having a less pristine research design rejected by a journal; or even the pull of social conventions within the discipline. 

Each of these dynamics—filling holes, chasing fads, and fitting our research to our methods—has pitfalls. 

Certainly, there is no one right way to formulate a research project. In some cases, “pure research” in the sense of trying to expand the boundaries of the discipline can have value even when the chances of success are rare. Usually, one major breakthrough will lead to a number of fruitful research paths. In addition, sticking with tried-and-true methods of exploration can lead to even finer-tuned methodological instruments that regularly generate valuable research results. 

However, I would like to offer another opinion based on my own experiences and attempts to grapple with the problem of research relevance: research should tackle the most pressing problems, even when researchers cannot tackle these problems in a pure way.

Such an approach is what I call “challenge-based” research. 

The main criticism of this approach is that it simply duplicates what other thinkers (often non-scholars) do outside the university (see Gustafsson & Hagström, 2023, p. 3). Think-tanks, government analysts, consultancies, and practitioners often engage in this kind of research. Perhaps that is not the worst criticism. Perhaps the answer to value-added research is to get scholars closer to practitioners and their daily struggles. One can even think of this as “blue-collar” research.  

When reading research results as well, you may also judge (not too harshly) the article based on this criteria of “authentic problems.” Indeed, an entire edited volume (Alvesson, Gabriel, & Paulsen, 2017), looking specifically at disciplines in the social sciences, has taken seriously the notion that the constant competition to publish has created a noisy landscape, cluttered with research papers that have very little to say. According to the authors, too much research is written in esoteric language, focuses on issues of marginal concern, and fails to take on pressing issues (Alvesson, Gabriel, & Paulsen, 2017). 

One way to ask if a research paper is important and meaningful is to evaluate it based on its ability to address challenges. Is the research tackling an urgent issue or simply fiddling on the margins of a topic (while genuine human suffering is happening in their institution or community)? When sifting through the latest journal articles in your discipline, you may also ask yourself why you are not engaged with articles or why your intellectual curiosity drifts elsewhere. Do you just read the abstract and move on, or does the article grab you and force you to read it? When was the last time you felt that reading a research article was the most valuable part of your day? 

Though space does not allow me to elaborate fully on what “challenge-based” research is, here are a few principles for choosing topics and conducting research. 

  • Start with problems you know locally, either in your institution or in your community, that other institutions and communities are also dealing with. 
  • Prioritize problems that are causing human suffering. 
  • Try to approach various problems that have no immediately identifiable solution with a series of small experiments that do little to no harm but may lead to a revolutionary idea, also known as pilot projects or simply tinkering. (For the value of “tinkering,” see Schomburg, 2019, February 20.) 
  • If you believe a problem is genuinely important, do not feel the need to rationalize researching the problem and looking for a solution.  
  • Ask yourself basic questions to test the value of your research: Would I conduct research on this topic, even if I couldn’t publish it in an academic journal, and just share the results with people struggling with the problem? If I didn’t have the time to do this research myself, how much would I pay someone else to undertake it? 

These principles may set a high bar for research. That is exactly the point. If the research does not demand our time, then there are perhaps better things we could be doing: becoming better teachers, volunteering in our community, or spending more time with loved ones. 

Perhaps the best way to determine whether our research meets the high bar set above is to conduct some pre-research (again, tinkering). Conduct a survey or several interviews to see whether your research is interesting or relevant to the target audience. Not only will this save you the time and frustration of examining an irrelevant topic, but it will also help you recruit research partners, readers, and a “tribe” that is adamantly invested in your success. 

The tentative hypothesis is that “challenge-based” and “solution-generating” research will naturally attract an engaged audience.



Daniel Clausen is a full-time lecturer at Nagasaki University of Foreign Studies. He is a graduate of Florida International University’s Ph.D. program in International Relations. His research interests vary widely from Japanese foreign policy to English language teaching. His research has been published in Asian Politics and Policy, e-International Relations, Electronic Journal of Contemporary Japanese Studies, The Diplomatic Courier, and Culture and Conflict Review, among other publications.

Photo by Pixabay



Works Cited

Alvesson, M., Gabriel, Y., & Paulsen, R. (2017). The Problem: So Much Noise, So Little to Say. In Return to Meaning: A Social Science with Something to Say. Oxford Academic.

Gustafsson, K., & Hagström, L. (2018). What is the point? Teaching graduate students how to construct political science research puzzles. European Political Science, 17(4), 634-648.

Gustafsson, K., & Hagström, L. (2023). The insecurity of doing research and the ‘so what question’ in political science: how to develop more compelling research problems by facing anxiety. European Political Science, 1-15.

Schomburg, A. (2019, February 20). The Value of Tinkering. Scientific American. 

Shapiro, I. (2002). Problems, Methods, and Theories in the Study of Politics, or What’s Wrong with Political Science and What to do About It. Political Theory 30 (4): 596–619.

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