How I Choose Problems

By

Alok Gupta

Associate Professor of Information Systems

Carlson School of Management

University of Minnesota

(Created: 4/16/03)

Reading Ron Weber’s editorial in the March 2003 issue of MISQ got me thinking for the first time how I choose my research problems. Until now, having been often caste as the MS type as defined by many published opinions, I thought mostly about justifying my research as IS research because of my belief that whatever I have done would be either irrelevant, trivial, or non-existent without IT/IS artifacts. It was a struggle! Often editors returned manuscript without reading them … apparent from their comments on the contribution of research and why it wasn’t appropriate for the journal in question.

However, I never even thought about how and why I choose to do what I do. Since it is kind of soul searching activity, I didn’t know how to systematically examine this issue. Therefore, I first decided to evaluate my motivations against some of the motivations Ron mentioned in his editorial to see whether I can fit in a mould. The analysis yielded interesting insights.

First, I realized I am a poor methodologist – and I apologize to my coauthors for not telling them this, however, I just realized it myself. I haven’t used standard, well accepted, methodology in most of the papers I have been involved in. Without getting into details of each paper, I think what happened was that other researchers were simply not interested in finding answers to the questions that my co-authors and I were seeking answers to. Sometimes, I confess, it may have been because the problem was perceived as solution oriented and, as mentioned by Ron, perhaps just “normal science.” However, I could not, literally, sleep until I had the answers or at least a hint or till I encountered a positively negative outcome, i.e., a dead end. So, I invented methods to suite my questions – always based on my formal training in engineering, statistics, OR, economics, decision sciences, information systems, and logic – usually an amalgamation of approaches that collectively answer the question at hand. This discussion is probably incomplete without some comment on my “perception” of reaction from evaluators of my research in formal and non-formal settings. As expected, it has been mixed. Some people find these approaches annoying and have indeed questioned methodological base. Fortunately, many have found them innovative. Initially, when I encountered a methodological challenge, my first reaction was that of “not again!” And, the response originally used to be: “Please tell us how that approach addresses this problem.” Now, though, I simply demonstrate why “it” wasn’t appropriate or is in fact inferior to the presented methodology. I must confess that the response didn’t and haven’t always succeeded in convincing the referees. Upon reflection, I still haven’t figured out how I managed to convince my co-authors of some of the crazy ideas at their inception and/or why I subscribed to theirs. Nonetheless, it has always been fun.

Second, I think my strategy (if one could call it that) was suicidal. How on earth could I think, I would be able to sell my research to major journals in IS that are, as Ron mentioned, so methodologically oriented. As it turns out, the strategy didn’t result in my suicide and I must thank all those anonymous AEs and referees that weren’t so methodology oriented – I mean that in most respectful and awe-inspiring way. Still, the high quality publication couldn’t have been my primary motivation.

Next, I decided to look at simply the way I first encountered the various research problems that I have or have been looking at. The first thing that struck me was none of those were chosen by me. Instead, they chose me. Let me explain. The first major project I worked on was my dissertation research on Internet Traffic Pricing. Well, I was looking at many ideas related to internal transfer pricing with my advisors (Andy Whinston and Dale Stahl) when Internet happened. All of us were very intrigued that while there was so much potential for network services (it was 1992 and yes it was still only potential then) there were really no economic incentives to develop and sustain high-speed networks and services. While there were many interesting problems in that domain, we got fixated on the issue of computing real-time economic resource allocation schemes. It was never done before, there was literally no literature on how one could go about calculating “optimal prices” based on information that was “transient” almost all the time. I eventually developed a tool that could just do that; it required synthesis of material from queuing theory, time series analysis, comparative statics, simulation techniques, economic analytical modeling, algorithm design, and purely logical constructs. Sometimes, my advisors weren’t convinced that I could do it and other times they certainly questioned how I was doing things. The problem haunted me for a whole year and some of the trickiest “solutions” came to me in my dreams. Nonetheless, why did I choose the problem? The answer is clear, simply because I didn’t know the answer, I couldn’t find one, and there were at least two more individuals who were interested in what I was doing.

Similarly, other problems I have worked on fit in the following categories:

· Accidental exposure to interesting problems that I didn’t know the answer to and couldn’t find an answer to. Since I think I am a person who always looks for the path of least resistance (and perhaps a bit lazy too), I tend to search for an answer for long times before I actually try to address the problem myself. However, when I can’t find an answer, it annoys me and I want to get at least some insight into the answer or solution. This process gives rise to huge amount of inactivity or wasted activity. However, it also gives rise to huge numbers of interesting problems and when I find that there is at least one more person interested in a similar problem, it gives rise to a research problem.

· Observations from daily activity – usually web surfing. Often, the questions/solutions posed in a different context makes me think of “what if…” scenarios. Many times these “what ifs” are generated from the exposure to or efforts in different research contexts. However, the application of these “what ifs” have resulted in interesting insights and alternative approaches that yielded surprising results for even my collaborators and I.

· Generating practical solutions with cutting edge technology. I have been lucky to be involved with some large companies in trying to find appropriate technology oriented redesigns of their existing business processes. This kind of work (I’m not sure whether it is research since one of the editors in a major journal called one such effort as an application – I disagree, but…) has been surprisingly invigorating. My colleagues and I have identified and developed fundamental ideas and modifications to cutting edge technology to be applicable to the business processes at hand -- at least to be an acceptable solutions.

The key realization, for me, was that in none of these cases I was consciously trying to develop a research problem, at least not the one that I eventually dealt with. Also, I seem to have always started with a small problem and have ended with a big one. I just hope this keeps on happening.

Finally, a thought on IS as a research domain. I think the centrality of IS/IT construct is perhaps not the only important factor; vitality of IS/IT construct for the problem domain is an equally important factor. I think good examples of such vitality are the Internet based multi-unit auctions. Such auctions were virtually ignored in economic literature because it wasn’t feasible to have a competitive auction environment and certainly the scope of the auctions was infeasible before the Internet. Here, technology fundamentally changed the problem characteristics, application environment and domain, incentives of participants, and above all technology provided new ways to measure and manipulate participants’ incentive. While the central questions here are still efficacy of the mechanism and its outcomes, IT is vital here both from implementation and design perspective. In general, I don’t think I would have been able to solve any problems, convince anyone of its value, or retain my own interest in the problem if I didn’t have my IS/IT training. While I won’t even pretend to have an answer to the problem of problems, I have an opinion on what at least one of the values MIS provides as a research domain. It is to pose new questions about old beliefs due to technological advances in IS/IT. We do that because MIS researchers are the first one to embrace technology as vital business component. That’s why MIS researchers were first to examine Electronic Commerce as a research domain when many thought (as they probably do now) it is a fad. I can never forget one of the question during one of my job interviews (by a non MIS faculty) in 1996 when I replied that my research interests are in electronic commerce: “Couldn’t you choose a more rigorous area of research?” In case you’re wondering, I didn’t get that job.

Thanks Ron, for making me think about this. As always, I didn’t choose to think about it.