FORUM: A future for operations

Getting serious about the context of big problems.

By Stelios Kavadias, Christoph Loch and Stefan Scholtes

A plethora of big, important problems cry out for innovative research in operations.

A plethora of big, important problems cry out for innovative research in operations.

We were rather taken aback when we read an interview with Professor Gerard Cachon in the December 2015 issue of OR/MS Today (“What’s Your Story?” page 11). When asked, “What is the best advice you can give to students in your field?” he replied: “Pick another field. One with big, important problems, like economics, or computer science or climate science.”

At first glance, if this is our current reality, then we are on the verge of bankruptcy in our field. Have we suddenly resolved all challenges related to the design and management of efficient and effective processes and projects? Is it really time to move on into other scientific fields? A statement from a former editor in chief of M&SOM and Management Science cannot be taken lightly; Professor Cachon is one of the leaders of the operations field, so his opinion probably reflects a wider perception about our field.

But we think this worrying perception can be positively addressed by focusing on some of the world’s major unmet needs and our field’s crucial role in meeting them. In so doing, we can show a new generation of OR/MS specialists that they can make a demonstrable contribution to society by tackling a big, specific problem in a practical, down-to-earth way that complements their scholarly pursuits, as we outline below.

On a purely academic surface, citation evidence supports Professor Cachon’s gloomy advice. Citation rates, even of the leading operations journals, are depressingly low – as is probably the active readership of our papers. We are not producing research that people wait to read, not even academics in our own field, let alone senior decision-makers in the proverbial real world. Ask a senior operations manager whether they know about management science, and if they would entertain sitting through an academic operations conference?

A few celebrated examples of real impact cannot hide the fact that the academic field that is concerned at its heart with productivity is not very productive at creating high-impact solutions to big problems. This state of affairs is disheartening, and if we don’t change it, students will increasingly follow Professor Cachon’s advice, and the field, as we know it, will disappear – with the management challenges it sets out to address being subsumed into other management disciplines.

Such a downward spiral will most probably first affect newcomers to the field – our Ph.D. students. In fact, assessing the attractiveness of an academic field from the perspective of prospective Ph.D. students is a very sensible health check. Most prospective Ph.D. students across management disciplines share three characteristics: They are very smart, very naïve and very passionate about doing something meaningful through their research. They don’t know what it is, nor how to do it – but they long to be part of a big story. Professor Cachon is right in that if we don’t offer them the opportunity to participate in the solution of “big, important problems” we’ll lose them to other fields. However, while his diagnosis is spot on, we would argue that sending the students to other fields is the wrong treatment.

If we look at our field narrowly and assess additional opportunities for the derivation of closed-form mathematical solutions that have impactful implications, then Professor Cachon is right – it’s a serious challenge.  But this reaction reflects a narrow view of our field, one that is oriented toward generic formal methods and one that defines the field from the supply side. The picture completely changes if we look at our field from the demand-side and consider the huge problems that need solving, problems that need operations expertise and an operations mindset.  

Fortunately for the field, there is a plethora of big, important problems that cry out for innovative research in operations. Whether developing new antibiotics or a cure for Alzheimer’s, keeping a lid on healthcare costs, preventing terror attacks, managing refugee crises, securing energy supply, saving the climate, or helping African countries assimilate funds and catch up with the rest of the world, there is not a single really big problem in the world that does not pose the same immense operational challenge: how to achieve a desirable goal with limited resources? Our understanding and the evidence-based advice that we, as an academic community, can give to leaders in business and society who wrestle with these big problems is rather limited, and the more limited it is, the bigger the problem. Big problems are complex, so generic solutions based on convenient assumptions are simply not valid. Any good operational solution to such a problem has to be context-specific, and its development requires deep knowledge of this context.

Over the past decades, our field has largely focused on the development of generic insights that apply across contexts. We have shed light on isolated phenomena, but the importance of these insights in a specific context can be quite limited and the underlying assumptions that allow the isolated study of a phenomenon are typically not satisfied. Big problems require novel solutions. To contribute to the immense operational challenges posed by these problems, we can draw on the existing insights, but they need to be adapted, often substantially, and they need to be integrated into the specific context of the real problem. What works for banks doesn’t necessarily work for hospitals, and what works in the United States doesn’t necessarily work in Africa. The context matters.

If we look at the opportunities for our field with such an attitude, we should be thriving. It is up to us to grab these opportunities, and to involve our Ph.D. students in ways that make them not only technical method specialists but also knowledgeable experts in big domains where they can make big contributions to business and society.

So we may offer an alternative advice (a plea): operations academics, and in particular the leaders in our field, should encourage their Ph.D. students to engage at least as much with the context of one “big problem” as they do with methods. Both are important: Engagement with big problems without rigorous methodology leads to pseudo-academic advocacy, while rigorous methodology without engagement with big problems adds little value and is unsustainable, particularly in business schools. A symptom of the latter is a junior faculty job market that is populated by an amorphous mass of “suits” who have lost the spark of passion and are only differentiated by their varying chance of success at publishing technical papers with their supervisors in leading journals that are neither widely read nor cited. We can rekindle the passion in our Ph.D.s if the field begins to complement its exceptional methodological expertise with serious engagement with the context of big practical problems. This takes a lot of time and effort and, in the absence of market incentives, requires real leadership.

Christoph Loch is dean of the Judge Business School, University of Cambridge (U.K.), Stelios Kavadias is the director of research at the school, and Stefan Scholtes is director of the school’s Ph.D. program. Along with their positions as senior members of the operations group at the Judge Business School, all three hold or have held associate editor positions on such INFORMS journals as Management Science, M&SOM, Operations Research and Mathematics of Operations Research.