Finding a research problem worth studying
Chapter 3: Develop Research Ideas and Questions — Video 2
https://ghrbook.com/videos/finding-a-research-problem/

[Slide 1] Every study begins with a motivating research problem. This video is about how to find one.
[Slide 2] A research problem is your study's ikigai, its reason for being, to borrow a Japanese concept. A research problem should convey a clear reason for being, a clear sense of purpose. Typically, a research problem gets framed as the gap in our knowledge, a gap in the literature.
[Slide 3] A defining characteristic of all research problems is that they are potentially solvable. To qualify as a research problem, we must be able to use systematic, public methods to gather and analyze data on the problem.
[Slide 4] Here's what that looks like. Research has shown that insecticide treated bed nets can prevent malaria infections in kids. But in many places, kids are not sleeping underneath bed nets every night. So a research problem to solve might be that we don't know how to encourage families to adopt and use this effective method of prevention.
[Slide 5] Finding research problems worth studying becomes easier with experience. Once you've studied a field for a few years, you'll have cultivated a list of journals, conferences, funders, and colleagues whom you follow to know the latest developments and priorities. As you read and learn, it'll become easier to spot important gaps that you can help to fill. Likewise, if you're a practitioner or a policy-maker, your accumulated daily observations will generate ideas.
[Slide 6] But let's assume that this does not describe you today. Where do YOU start? Students often come to me with a general awareness about a health challenge, not a specific problem or research idea. I'm interested in mental health, they'll say. For students at this early stage of training, I encourage them to adopt someone else's research problem and jump into an ongoing project to gain experience, rather than develop an independent project.
[Slide 7] Aside from soaking in experience, there are steps you can take to expose yourself to new ideas. Read the health and science sections of major news publications and set alerts for topics you find interesting. Look up the professional associations for your research area and subscribe to their mailing lists, and attend their talks and webinars. And network with local practitioners and policy-makers who have a front row seat to applied challenges and gaps in our knowledge. There are a couple more in the book.
[Slide 8] Above all, start reading the scientific literature. A useful strategy for finding reading material is to visit the websites of the most popular journals in your discipline and browse recent issues.
[Slide 9] Once you find a few articles of interest, try this strategy for expanding your search and identifying gaps worth studying. First, find the keywords. An article's keywords make great search terms, and they sit near the abstract. Second, read the Introduction. A good Introduction will frame gaps in our knowledge of a topic, so pull out a highlighter and get to work. Third, review the Discussion. Authors use it to link their results to the existing literature, and a good Discussion will include the limitations of the current study and might offer ideas for future research. And fourth, take note of the cited authors and journals. The Reference section holds clues to your next great find, and tools like Google Scholar let you search for those references and discover where else they appear.
[Slide 10] Once you start looking, you'll find research problems everywhere. Your next challenge will be deciding where to direct your attention and energy. I encourage you to favor problems that meet four criteria. Important to you. Contributing to your field. Meaningful to society. And potentially solvable using systematic, public methods, which we've already covered. Let me expand on the first three.
[Slide 11] First, the quality of your work will be better if you believe you are working on something interesting and important. Research projects in global health can have a long life-cycle with ups and downs. A genuine interest in solving the problem can help you get through the low points.
[Slide 12] Second, when selecting a research problem for study, you should seek to understand from the outset how the answers will contribute to your field. Will your study provide an initial answer to a known problem? Clarify an issue marked by contradictory findings? Support an evolving consensus, or provide an important counterpoint to a previously held view? Bring attention to an overlooked issue, or apply cross-disciplinary learning to help scholars in your field think differently about a problem? Knowing your study's purpose will help you to frame your contribution.
[Slide 13] Not everyone will agree on the third criterion, importance to society. There are many areas of research, especially in the basic sciences, where you can engage in scientifically important work without knowing if or how that work might benefit society one day. Global health is different. There are almost endless applied problems to solve, and you can't work on them all.
[Slide 14] In asking you to find problems that are meaningful to society, I'm suggesting that you be intentional. You'll make many decisions over your career, about training programs, mentors, grant opportunities, collaborators, and each decision has an opportunity cost. Some research problems won't be a good use of your time and talent, and we need both to solve big problems. So when deciding to pursue new work, stop and ask yourself, how are we better off if we solve this problem? In the next video, we turn from the problem to the goal: are you describing, explaining, or predicting?