Want Your Research To Have Impact? Consider These Three Questions

by Olav Sorenson

Most academics I know want their research to have an impact, to influence the way people think and behave. But few of us succeed. Who’s to blame? Usually, the blame gets placed on practitioners, for failing either to read the research or to understand how to put it into practice. Efforts to improve impact therefore often focus on translating research into a format and language open to a broader audience.

However, no matter how well written and how widely disseminated research findings might be they will do little to influence people if the problems studied and the solutions provided do not seem relevant to those people. Researchers wanting to have impact therefore have a responsibility to study problems and phenomena that actually matter to others.

What is the best way to choose such problems? People generally agree on the importance of some problems, such as cancer, world peace, and global warming. Why? Because these problems affect almost everyone, including future generations, in ways that can profoundly shorten the length, and diminish the quality, of their lives. 

But absent such near-universal agreement, how should we decide what other problems merit attention, what research has a potential for impact? We can apply the same principles.

Start with these two questions: How many people does this problem touch? And, how large of an effect does it have on their health, their wealth, or their well-being?

Having impact, however, also implies that there will be a change in behavior or policy. Increasing awareness of, or understanding an important problem better, does not necessarily provide any solutions to it. So, ask yourself also this third question: who, if anyone, would change his or her behaviors after learning the results of this research?

That question has several implications, not just for the choice of problems, but also for research design. Being able to answer with something other than “no one” generally requires that research has three features: 

  1. It must examine the consequences of variation in some factor that an individual, an executive, or a bureaucrat could change. Many things matter yet change remains outside of one’s control.
  2. It needs to identify a causal relationship between a change in this factor, a potential intervention, and the desired outcomes. Without that, we have little basis on which to believe that a change in policy or behavior would have the intended consequences.
  3. It should generally test a theory for why the intervention matters, including a mechanism or set of mechanisms. Without a theory and a mechanism, even a causal test, such as an A/B-style experiment, does not allow for extrapolation beyond the narrow test and the subpopulation within which that research occurred. 

Most likely having impact will still require increased effort in disseminating results more broadly. It will still mean translating the research into something amenable to a more general audience. But it has to start with choosing research projects that have the potential to influence behavior and policies in ways that improve lives. That’s impact.

2 comments on “Want Your Research To Have Impact? Consider These Three Questions

  1. Thanks Olav for this comment. These 3 principles are useful but, perhaps unsurprisingly, I find that they omit other kinds of important research that might still have a major impact.

    One missed opportunity is that these principles would not include many forms of qualitative research that still have an important role to play in creating high impact research. Some of the most impactful research in management is qualitative. As I’ve argued elsewhere (with Richard Whittington and Mike Pratt, ASQ 2019), “if we assume the world comprises open systems, subject to continuous change and characterized by complex contingencies,…a horizontal notion of knowledge accumulation may be more effective as it furnishes a stock of broad principles generated across many past situations, each of them unique. In a changing, complex world, where every circumstance is different, safety lies in doubting previous experience and having available wide repertoires of tentative theories and concepts with which to address always-novel conditions.” And, qualitative research is equally well-suited to those kinds of insights.

    A second missed opportunity in your recommendations is that it might lead students to focus on finding the perfect natural experiment or instrument while neglecting the fact that some of the most interesting questions cannot be answered as cleanly as your principles might imply. I’ve seen so many students going down pathways that lead to boring yet cleanly identified studies. So, while I’m sure you didn’t mean that in your comment, I worry that some students might take the wrong message away.

  2. Research is an expensive investment for business schools, and its value should be justifiable relative to other investments, such as financial aid for students (especially salient today, with interest rates on student loans rising). There may certainly be value in individual research projects that do not offer clear answers to all of Olav’s questions, as Sarah’s response suggests, but I think that any research portfolio should be able to address all of them. These questions offer a useful template for faculty writing research statements who should be able to look across their work and offer answers to what could change based on their research, how that change would matter, and why it would have its effect. Likewise, our evaluation procedures would be more appropriate and fair if evaluators used these questions to structure their evaluation of the scholarly portfolios they are asked to review when writing letters for tenure or promotion cases, or writing subcommittees reports on promotion candidates at our own institutions. Responsible business research, and responsible business education based on that research, will be enabled by holding ourselves to the standards that these questions set.

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