Monday, January 17, 2022

Identifying the Problem (Step 1.1): An Impactful Interdisciplinary Research Project Is One that Fulfills You

By Kai Chan

This is part of a series, How to Write a Winning Proposal—in 10 Hard Steps

The true first step in writing a winning proposal is to identify the (research) problem. Lots has been written about how to identify a good problem, e.g., as a puzzle. For our purposes, though, that step is WAY down the road.

Or rather, identifying a good problem is a crucial and complex process that we’re going to unpack into several steps over the coming posts. But in order to engage in those steps, you need an anchor—a tentative topic or problem—that you can use to ground you through the coming exploration.

But how do you decide on that tentative topic/problem? It’s a chicken-and-egg dilemma: to identify a good topic/problem you need a tentative topic/problem.

Choosing a topic/problem is a chicken-and-egg dilemma (you need
a tentative one to investigate possibilities), but there is a place to
start (read on). ruben alexander, Flikr
My route through this apparent paradox is highly unusual. The vast majority of writing about how to find a good research problem says something like this: “look for under-explored aspects and areas of concern, conflict or controversy.” Or, this: “Ideas for research problems tend to come from two sources: real life and the scholarly arena.

They’re not wrong. They’ve just skipped a key step—in my opinion. And they’re misleading.

They are misleading because there is no such thing as a “under-explored aspect … or area”. Every research area is simultaneously over-explored if it isn’t interesting or important to you, and under-explored for those who find it interesting and important.

There’s only one way to identify a good tentative topic/problem. It’s not to survey the literature or the world around you—it’s to look within. That is, start from your critical ingredients. A good tentative topic is one that would be meaningful to you.

The other authors above would likely agree that looking within—at what you find meaningful—is a good place to start. They likely just think it goes without saying. Having supervised dozens of students and taught twenty in two iterations of this course (RES 602), I know that it still needs to be said.

These other authors are probably fixated on what I’ll call the opportunity theory—that we should choose projects among the low-hanging fruit. I see several problems with this theory.
Low-hanging cashew fruit. (Did you know
that cashews had delicious fruit? They do,
and this is thanks to gomphotheres and 
other prehistoric megavertebrates, which
relates to rewilding.) 
Photo by 
form PxHere

  1. You can’t spot great, easy opportunities (the low-hanging fruit) without really getting to know a field. Those externally-obvious low-hanging fruit have mostly been picked.

  2. There’s no research area that is truly saturated—that doesn’t have a genuine research opportunity. There are areas that are very competitive, there are ones whose methods won’t appeal (e.g., because they are too theoretical, too dependent on fieldwork, or too deeply statistical). But this is all a function of fit with what ‘turns your crank’.

  3. Following apparent low-hanging fruit is unlikely to allow you to develop the methods that are most important to your future, or to enable you to develop connections with your key communities of research and practice, or to jibe with a theory of change that resonates with you. That is, they are unlikely to deliver your critical ingredients.

So start with your critical ingredients, and fine-tune your good tentative problem into a good problem (see steps 2-6 in this series).

But how exactly do a handful of critical ingredients deliver a research problem? At the nexus of each critical ingredient, there is a quadrant in n-dimensional space that represents the set of your most meaningful problems.

For me, this is a project involving the conservation and/or restoration of nature alongside its sustainable use (fields) with a combination of ecological and social dynamics (disciplines), using quantitative and qualitative methods (tools) in southwest British Columbia (geographical study areas). It will engage with values and rewilding in the context of transformative change (theories of change, questions).

So, once you’ve completed the critical ingredients document, the task is to simply layer the various dimensions as I’ve done just above: the promising "problem" is the intersection of your critical ingredient fields, disciplines, tools, study areas, theories of change, and questions.

Next we’ll discuss how to use this starting point to explore the beautiful landscape of research opportunities and approaches.

Next up: What Is a Horizon Scan? (Step 2) + Why You Need To Do One Now

Previous: Why You Need a Theory of Change

The Intro to this series (with links to the full set): How to Write a Winning Proposal—in 10 Hard Steps

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  1. I only realized after leaving the relative privilege of IRES at UBC that most graduate students are substantially constrained within the parameters of grants that their adviser obtains to fund the students' graduate research. The self-reflection described here remains crucial for identifying a personally meaningful project, but there are more boundaries around selecting research questions for most students than this post implies. Depending on the student, these constraints can help projects progress more rapidly and/or can chafe!

    1. Yes, that's entirely true. I haven't discussed the many real-world constraints on students' research. The dynamics around supervisors prescribing or circumscribing projects (often out of need) is a key topic for exploration in another post!