PRODUCTION/OPERATIONS MANAGEMENTKEONG LEONG, Feature Editor, Fisher
College of Business, Towards Greater Relevance in Production and Operations Managementby Manoj K. Malhotra, College of Business Administration, University of South Carolina What should we research and teach in production and operations /management (POM)? This question is indeed a difficult, onerous, and a controversial one to answer. There would be a plethora of opinions that would exist among the large constituency of scholars who conduct research in a variety of operations management related topics, and convey the results of such research to students of the field. Some would even ponder whether such a question should be raised at all, since it is well nigh impossible for a single individual or a group of scholars to establish an agenda for the field that would represent some sort of a consensus opinion. Nevertheless, this issue is of such importance that several prominent POM scholars have joined this debate in one form or the other since the early 1980's (e.g., Buffa, 1980; Chase, 1980; Meredith et al., 1989). In these changing times when almost every process in the business world is being reengineered, it may be worthwhile to revisit this question. Extending the debate may be valuable since our field is still attempting to clearly define its identity. While I do not profess to have all the requisite answers, it is hoped that this article will help define the challenges that must be tackled by leading-edge thinkers in the field. I will also outline some of the barriers that have impeded the growth of the field, along with my own thoughts regarding where we need to go forward from here. Much of the ensuing discussion amalgamates and interchangeably talks about teaching- and research-related ideas, since I believe that the two are inextricably linked with one another. A partial evidence of this belief lies in the fact that a perusal of a typical introductory-level textbook in POM shows that most topical chapters are based on existing research in the field. In addition, a substantially large portion of the reference material is from academic sources. In other words, we tend to teach what we research. In order to better understand where we currently stand, it might be helpful to first briefly trace the origins of our field and discuss some of the trends that have occurred over time. The discipline of POM evolved primarily from operations research as increasingly new and sophisticated techniques were applied to solve problems that had a potential application in the manufacturing or service sector firms. The advent of computers and the simplex technique helped solve large-scale linear programming problems as they began to be applied to decision areas like aggregate production planning, machine scheduling, location analysis, project planning, etc. Thus the availability of techniques fueled the growth of the field. Consequently, Buffa in 1980 called for an evolution of the field from beyond this phase to the next level, in which actual problems encountered in different manufacturing and service operations would become the basis of future research and teaching. Instead, by and large we stayed with the methodology-driven research and teaching agenda that had provided the initial impetus for the growth of the field. This issue was also noted by Meredith et al. (1989), almost a decade after the call to arms was issued by Buffa for establishing in our research and teaching a "strong element of relationship to the practicing world." It is interesting to note that during a similar time frame, other fields of study in business were evolving in different directions. The disciplines of marketing, organizational behavior, strategic management, and later, information systems, were patterned more after the tradition of research and learning in social sciences. Knowledge was being built on the basis of empirical evidence that was collected from the field. Their methodologies were centered on case studies, executive surveys, and experimental analysis. Despite several problems that are inherently present in these methodologies, they were intrinsically closer to the source of the real world problems than the discipline of operations management. As an applied science, we as POM researchers and teachers need to focus our efforts on real-world problems to a greater extent than what we have done in the past. This does not imply that our endeavors should take on the flavor of consulting projects that only look at narrow firm-specific problems with no generalizable content. Instead, our research and teaching must focus on creating and disseminating knowledge that has greater relevance. While there is a considerable degree of agreement within the field regarding this assertion, it is easier said than done. What are some of the obstacles to achieving greater relevance in POM with respect to the efforts of the academic community? An obvious impediment, and perhaps the greatest one, is our inability to go beyond the confines of what we can do with the limited set of methodologies in which we have been trained. We find it almost impossible to model and neatly structure complex cross-functional problems that invariably occur at higher levels of the organization. Yet solving such problems are at the very core of what executives believe are the most critical and important issues currently facing US manufacturing (Malhotra et al., 1994). It is unfortunate that our functional-area-based view of the business world is different from the cross-functional processes based view that is being adopted by actual firms. We must be cognizant of this reality when attempting to define the direction in which we must progress. It is obvious that a considerable investment of resources would be needed to shift or re-orient the direction in which we have travelled so far. We would have to re-examine our methodologies, borrow some from related disciplines, and even create new ones in order to re-tool ourselves for a considerably different research and teaching agenda. In addition, we would have to interact more with actual firms to ensure that our problems are well-anchored in the real world. More uncertainty would be faced by researchers in such a scenario. Payoffs would be less clear, and gestational periods for research projects would be much longer. In addition, pedagogical materials would need to be revised and updated at a considerable cost to ensure that we actually teach our students the skills that are needed by the industry. Such large-scale changes will not take place miraculously, at least not without an appropriately revised set of incentive systems being put into place. Based on these observations, I have outlined five major teaching and research related initiatives that we collectively need to take as a community of POM scholars. While the ensuing discussion provides my own perspectives, much more debate needs to take place in further defining and resolving the issues and challenges facing us as we collectively journey towards greater relevance. The development of empirical field data based research needs to accelerate, with a particular focus on higher level strategic decision making. This is needed to not only increase the relevance of our research, but also to ensure that it informs business practice even as we learn from it. It can take the form of survey research or well done case studies. Such case studies would be useful for teaching purposes, along with providing initial evidence from which theory building can occur. However, we definitely need to move away from the anecdotal evidence gathering stage and progress rapidly down the learning curve that has already been established by other social science disciplines. It goes without saying that such studies should be done more rigorously, because the methodology-related knowledge that provides the guidelines for conducting such research is already available. Related to the above issue is what must be done with traditional modeling methodologies. We could be in the danger of throwing out the baby with the bath water if a bias towards more field-based empirical research tends to discourage the efforts of those researchers who focus on traditional methods like simulation and mathematical modeling. After all, a significant proportion of our active scholars are still steeped in that tradition. What should be discouraged is a "technique in search of a problem" orientation. Building analytical or simulation models for the purpose of solving actual problems that have generalizability can be invaluable. But the modeling efforts need to be better meshed in with practice than what has traditionally been done. Doing so could provide the POM discipline with a distinct identity of its own, and clearly delineate it from operations research and other related disciplines from which it evolved in the first place. Internationalization of research agenda and teaching curriculum is in sore need of greater attention. We all understand the importance of global operations and formulation of strategies that transcend national boundaries. But what exactly is international POM? We currently do not have the appropriate frameworks or paradigms in the field around which the conventional knowledge and study of POM can be organized. Some work has been done in this direction for both teaching (e.g., Lawrence and Rosenblatt, 1992; Schmenner, 1995) and research (e.g., Klassen and Whybark, 1994). But obviously much more needs to be done. A comprehensive textbook that focuses on international POM issues and contrasts them with traditional POM issues would be a much welcome addition to the existing pedagogical material in the field. Integrated teaching curriculums that provide a cross-functional perspective must be developed. The linkage of POM with other functional areas of a firm should be the cornerstone of any redesign that takes place. As an example, a study of many facets of POM such as inventory management, production planning and control, and logistics planning cannot be accomplished without understanding the role played by information systems and newly developed communication technologies. Similarly, organizational behavior knowledge must be integrated into work design issues. Several other examples of a similar nature abound. Such a redesign should incorporate feedback from potential employers of our graduates. Moving in the direction of integrated curriculum would hopefully make it easier to communicate the results of our own evolving research work to students in the classroom, and perhaps in many cases also influence the related research agenda in turn. Appropriate reward systems must be established for published research. Risky projects should have higher proportionate returns. Journal editors, reviewers, and senior scholars in the field may have the most influence on what kind of research they would like to see published in the field. A shift towards greater relevance in published research is already taking place. This trend needs to be further encouraged and accelerated. We must train our doctoral students to do more relevant research projects (whether field-based or modeling-based), examine alternate methodologies that can facilitate such enquiries, and finally reorient the publication acceptance criteria in this direction. A careful balancing act will have to be performed between relevance and rigor of published research for the time being; hopefully, the field will evolve to the point where both can be achieved simultaneously to a large extent. The pedagogical material will also evolve accordingly, though with some time lag. The preceding discussion has only looked at a microcosm of initiatives that must be taken to move the field forward. In this context, we must recognize that the overall structure within which universities operate largely dictates how rapidly these changes can take place. Unlike the corporate world, we are more lethargic in our response to changing trends. It will be impossible to convince scholars to move in a particular direction if the incentive systems encourage them to do otherwise. The fallacy of expecting behavior A while rewarding behavior B has been well-established (Kerr, 1975). We must avoid such a trap, since ignoring the need for change and not moving towards greater relevance in our academic efforts will inevitably lead to failure in the long run. The promise of what can be achieved by reexamining our research and teaching priorities and agendas is great, but so are the challenges that lie in-between.
References Buffa, E.S., 1980, "Research in Operations Management," Journal of Operations Management, Vol. 1, No. 1, pp. 1-8. Chase, R.B., 1980, "A Classification and Evaluation of Research in Operations Management," Journal of Operations Management, Vol. 1, No. 1, pp. 9-14. Kerr, S., 1975, "On the Folly of Rewarding A, While Hoping For B," Academy of Management Journal, Vol. 18, pp. 769-783. Klassen, R.D., and Whybark, D.C., 1994, "Barriers to the Management of International Operations," Journal of Operations Management, Vol. 11, pp. 385-396. Lawrence, S.R., and Rosenblatt, M.J., 1992, "Introducing International Issues Into Operations Management Curricula," Production and Operations Management, Vol. 1, No. 1, pp. 103-117. Malhotra, M.K., Steele, D.C., and Grover V., 1994, "Important Strategic and Tactical Manufacturing Issues in the 1990's," Decision Sciences, Vol. 25, No. 2, pp. 189-214. Meredith, J.R., Raturi, A., Amoako-Gyampah, K., and Kaplan, B., 1989, "Alternative Research Paradigms in Operations," Journal of Operations Management, Vol. 8, No. 4, pp. 297-326. Schmenner, R.W., 1995, "International Pedagogy," Decision Line, May, pp. 5-6. Manoj K. Malhotra is Associate Professor of Management Science at the University of South Carolina, Columbia. He holds an engineering undergraduate degree from The Indian Institute of Technology (IIT) Kanpur, India, and a Ph.D. in operations management from The Ohio State University. His teaching and research interests include production planning and control in multistage production systems, shop floor control, flexible manufacturing systems, group technology, service sector scheduling, business process reengineering, and manufacturing strategy. He has published several papers on these and related issues in Decision Sciences, European Journal of Operational Research, IIE Transactions, International Journal of Production Research, Journal of Operations Management, OMEGA, and Production and Operations Management. Dr. Malhotra is a recipient of the Decision Sciences Institute's Outstanding Achievement Award for the Best Application Paper in 1990, and Alfred G. Smith Jr. Teaching Excellence Award in 1995 from the College of Business Administration at the University of South Carolina. He serves on the editorial review board of two journals, and is an active referee for several others. He is a member of the Decision Sciences Institute, INFORMS, Production and Operations Management Society, and the American Production and Inventory Control Society.
Dr. G. Keong Leong |