I greatly enjoyed Stephen Zhang and Jiyao Chen’s (Reference Zhang and Chen2024) ‘Responsible Research: Reflections of Two Business Scholars Doing Mental Health Research During COVID-19’. Part of my reaction was admiration. Zhang and Chen had the guts to jump outside their established research programs to conduct studies of the mental health impacts of COVID-19. These studies were urgently needed, within the authors’ competencies, especially in survey research and meta-analysis, and widely published in health science journals. And part of my reaction was that Zhang and Chen are on to something, that something is awry with management research. For Zhang and Chen, management research is at once excessively theoretical and obsessively rigorous. The surfeit of theory may be a matter of collective verbosity where antecedent work is reviewed ad nauseum. Or, more troubling, the surfeit may reflect the absence of an agreed-upon management theory requiring that all theories be given equal credence. Where there is consensus on theory, theorizing can be succinct. Where theory is mathematical, as in economics, it is relegated to an appendix.

The obsession with rigor may reflect a lack of specificity of our theories. If existing theory predicts a particular result, e.g., that the speed of light depends on the velocity of its source, and that result does not obtain as in the famous Michelson–Morley experiment, then the theory is the problem rather than the econometrics. Management theories are generally of the form A varies with B and even when A and B covary we’re not confident whether A causes B, B causes A, or if both are due to C. And hence our preoccupation with model specification and identification. Take something as foundational as goal-setting theory where performance is said to improve with goal difficulty, specificity, and measurability (Locke, Shaw, Sarri, & Latham, Reference Locke, Shaw, Saari and Latham1981). Though generally true, the opposite may obtain whenever targets once met are ratcheted upward and people withhold performance to stop the ratchet. Weitzman (Reference Weitzman1980) argued that the nemesis of planned economies is the combination of target-setting and ratcheting.

I have some quibbles. I think that Zhang and Chen may be overgeneralizing about the health sciences, whose range and complexity is immense. The health sciences encompass basic science (e.g., biology and neuroscience), fundamental medical research, clinical research, and epidemiological research. The skill sets and expectations and, often, the category of faculty appointment for each differ. Zhang and Chen’s work on mental health during COVID-19 appears to fall in the last category, epidemiological research, where social science skills are invaluable. To be sure, publications in the health sciences have in common the following: articles are short, editorial decisions are made quickly with a high proportion of desk rejections, the focus is on results and results are cumulative as in meta-analyses, and co-authorship is extended to all members of the research team. These occur, as Zhang and Chen point out, because there are established research protocols and rules of evidence. This isn’t the case in management because the field is ill-defined and the phenomena are complex, often moving targets. Articles can be long, revisions and final editorial decisions can take forever, results can be equivocal even after robustness checks, and cumulation is not the norm. Most importantly, the significance of a particular result in management research is rarely self-evident even in articles intended to be practical and useful. There are few if any management counterparts to Michelson–Morley.

Should management research attempt to be practical and useful? I’m not sure. Unlike in the health sciences, few of us are practitioners. We don’t have patients, our consulting activities are limited in scope and constrained by confidentiality agreements, and our employers, mostly business schools, are gift rather than grant economies and averse to corporate-sponsored research for fear that it will be perceived as serving commercial interests. Further, the teaching cases we write are ultimately controlled by the firms that are our subjects (imagine medical research controlled by patients). The day-to-day practitioners of management are managers themselves and professional consultants. They together with business journalists have more first-hand knowledge of the issues facing firms than most management professors. And they write best-selling management books. Management professors typically don’t. And if they do it is sometimes held against them.

If not practical and useful, then what should management research be? The core competence of management researchers, in my judgment, is in neither the realm of the natural sciences nor in practical and useful research. Rather it is in the realm of ideas that diffuse through the scholarly community and may or may not filter down to managers and ultimately influence their thinking and actions. These ideas, of course, are informed by data, whether quantitative or qualitative. But they’re more often the result of a synthesis of huge literatures than of hypothesis testing or meta-analysis. Think of Simon’s (Reference Simon1947) concepts of bounded rationality and satisficing. Or Barney’s (Reference Barney1991) resource-based view of the firm. The larger question, then, is whether management research should be a little more like the humanities and a little less like the natural science model many have sought to emulate or the practical-and-useful model Zhang and Chen advocate. The humanities are discursive, rarely constrained by rigorous rules of evidence, and often disorganized. This leaves humanists free to explore nascent ideas, many of which fail the test of time but some of which survive and thrive. My concern is that if we try to be excessively scientific or exclusively practical and useful in the management disciplines, it will be at the expense of mental playfulness and experimentation needed to cultivate new ideas. And the latter may be our main mission.

The above notwithstanding, I think all management scholars should experience practical and useful research, especially when it is urgent to find answers as it was for Zhang and Chen. Each of us needs to learn, usually post-tenure, that our work can have real-world impact. I’ve had two such experiences. The first occurred 46 years ago when, tragically, two Los Angeles police officers shot and killed a deranged Black woman named Eulia Love in a dispute over an unpaid utility bill. The Los Angeles Police Department’s internal investigation of the shooting exonerated the officers even though they could easily have stepped out of range of the butcher knife Eulia Love held in throwing position. Mayor Tom Bradley called on the Los Angeles Police Commission to conduct an independent investigation of the shooting, and the Commission turned to me for an analysis of whether Blacks and Hispanics were disproportionately victims of LAPD shootings. The findings should surprise no one: Blacks were disproportionally involved in LAPD shootings, especially shootings precipitated by ‘furtive movements’, e.g., appearing to reach for a weapon, or disobeying a command to halt, and shootings involving Blacks were disproportionally ruled in policy (Los Angeles Board of Police Commissioners, 1980; Meyer, Reference Meyer1980). The greatest challenge was not the research. It was, rather, persuading the Commission and the command staff of the LAPD to accept these findings and act on them, which they ultimately did. Here I was helped inadvertently by an investigative reporter writing a story alleging the Commission’s ‘cover-up’ of my work. Needless to say, the story was killed and my report released. The lesson is that research intended to be practical and useful may sit on the shelf unless it serves the interests of its sponsors. The publication gauntlet notwithstanding, it can be safer to do academic research.

My other foray into the realm of the practical and useful was, like Zhang and Chen, during COVID-19. In July 2020, my wife and I were returning from a visit with grandchildren in the Washington DC area. While stopped for two accidents ahead on I-95 and in direct sight of two Maryland state troopers, we were rear-ended by a trucker who had driven all night from the Carolinas. Once I dealt with the damage, I asked what was happening on the highways. And what I found was stunning: motor vehicle fatality rates (the number of motor vehicle deaths per million miles of travel) shot up dramatically during the early months of COVID-19 (Meyer, Reference Meyer2020). Moreover, I found no historical precedent for the spike in fatality rates during periods when traffic volumes decreased sharply – motor vehicle fatality rates had always decreased during recessions and when gasoline was rationed during World War II. The impact of the article, titled ‘COVID Lockdowns, Social Distancing, and Fatal Car Crashes’, has been interesting. The number of citations, 33 so far, remains modest. But the Altmetric score gauging buzz on social media has remained fairly high, around 50. I’ve had several requests to follow up on this research but will wait until the end of this year when I can do a five-year retrospective on fatal car crashes since COVID-19.

If this seems like a mixed message, it is intentionally so. Again, I admire what Zhang and Chen did amidst COVID-19. But I believe that the inherent complexity of the subject matter will and perhaps should render management research a little less practical and useful than research in the health sciences and perhaps in other business disciplines. This said, I think management scholars should have the experience of doing research with impact beyond the scholarly community. Often this research is adventitious and outside their long-term research programs. But the opportunity should be seized when it comes along.