RESEARCH ISSUES

SHAWNEE VICKERY, Feature Editor, Eli Broad Graduate School of Management, Michigan State University

Toward Scientific Progress of DSS Research

by Sean B. Eom, Southeast Missouri State University

Last year's professional development workshops at the Decision Sciences Institute's annual meeting entitled "End-of-the Century Vision of Decision-Making Research" provided an especially useful overview of research in the area of decision sciences and decision support systems (DSS). Professor Goul's research issues article, in the September/October 1992 issue of titled "A Dyed-in- the Wool... New Romance with `O`DSS'", focused on new research opportunities with organizational DSS. I would like to continue the dialogue about the major established and emerging research areas in DSS.

More than ten years ago, Peter Keen (1980) stated that management information systems (MIS) research lacked a cumulative tradition in a paper presented at the First International Conference on Information Systems. In his view, there was virtually no cumulative research tradition in the MIS area without "continued follow-up on interesting lines of inquiry." He defined a cumulative research tradition (Keen, 1980, p. 13) as one where:

1. Researchers build on each other's and their own previous work;
2. Definitions, topics and concepts are shared;
3. Senior researchers view their main role as shaping the field;
4. Each journal in the field has a clear focus;
5. There is some definition of orthodoxy, while unorthodoxy is not discouraged.

Since then, a number of studies have been conducted to assess the extent of progress in the MIS area. To investigate the first and second parts of Keen's above definition, Culnan (1986, 1987) conducted examinations of the intellectual evolution and development of the MIS area. These studies concluded that significant progress had been made toward a cumulative research tradition in MIS and identified several groups of MIS research subfields. On the other hand, others perceived that MIS researchers felt that there was an overemphasis on transient topics and that there was continuing evidence of fragmentation and lack of both a cumulative research tradition and articulated MIS theories (Teng and Galletta, 1990; Farhoomand, 1987).

According to Price (1963), researchers in any academic discipline have a tendency to cluster into informal networks, or "invisible colleges," focusing on common problems in common ways. Within these networks, concepts and findings by a researcher are soon picked up by another to be extended and refined. The intellectual history of the field is a systematic account of how various paradigms have emerged in a field through analyzing and correlating the work of the members of this network. Culnan (1986, p. 156) also discusses the importance of studying the intellectual development of a field in this way. "Researchers can benefit by understanding this process and its outcomes because it reveals the vitality and the evolution of thought in a discipline and because it gives a sense of its future. In a relatively new field such as MIS, this understanding is even more beneficial because it identifies the basic commitments that will serve as the foundations of the field as it matures." Nonetheless, little research has been conducted to identify the intellectual structure, cumulative tradition, and reference disciplines of DSS.

Several of our previous research projects applied bibliometrics methodology to a huge database file of DSS references to better understand how DSS had evolved to its present state and examined the existence of a cumulative research tradition (identifying various DSS research subspecialties) over the past two decades. The major conclusion of these studies (Eom et al. 1993, Eom and Min, 1992) was that DSS are weakly grounded in such contributing disciplines as:

1. organizational science;
2. multiple criteria decision making;
3. artificial intelligence; and
4. management science/operations research;

In addition, these studies provided a piece of empirical evidence to support the notions that progress is being made toward the development of DSS as a field of scientific research, and the DSS area is in the early stage of building its own articulated theories in the subareas of:

5. foundations;
6. group decision support systems;
7. model/data management;
8. cognitive styles and human-computer interfaces;
9. multiple criteria decision support systems; and
10. decision support systems implementation.

For DSS to become a coherent area, a continuing line of research must be built on previous work. Without it, there may be good individual fragments rather than a cumulative tradition (Keen, 1980). Keen further emphasized the importance of thinking about research that has already been done: "It atrophies if it cuts itself off from curiosity, diversity, and reflection" and "Let us make sure we keep a few philosophers, historians, general systems theorists and social activists within our network; even if only to write useful survey papers."

In the professional development workshops of the 1992 Decision Sciences Institute San Francisco meeting, panelists, consisting of editors of Decision Sciences, and attendees exchanged their opinions as to the research tracts that must be stopped and emerging research fields that need more attention. Further, many of us agreed that there are some research areas which are not recommended for non-tenured faculty due to the high risks associated with it. In the long run, initiating a new line of research may give higher return, along with higher level of risks. Primarily because of its newness, there may be a higher rate of rejection as well as longer lead time. Therefore, our research described here can be a valuable guideline for new faculty members who are interested in doing DSS research (DSS application development, DSS theory research, and DSS contributing disciplines). Some friendly advice from the panelists to new untenured faculty members was to research and publish in the well established research field such as subareas (5) through (10).

A final comment on Professor Goul's excitement about a new romance with organizational DSS (ODSS). At this moment, it may be too early to conclude whether ODSS can itself be established as a distinctive DSS research subspecialty, as our studies indicated. Our studies clearly suggest that the DSS area is struggling to demarcate itself from reference disciplines and solidify its domain. Nevertheless, our research supports the notion that DSS research lacks its own articulated theories. Then the important question is what obstacles have inhibited the accumulation of scientific knowledge of DSS and how to overcome them. This issue is not trivial. Answers to this issue are also not simple. Kuhn (1970) defines science as þthe constellation of facts, theories, and methods collectedþ through the piece-meal process to the ever growing stockpile that constitute scientific techniques and knowledge. Articulation of theories comes after the following three prior stages--(1) consensus building among DSS researchers about the concepts, definitions, and the nature of legitimate scientific problems and methods, (2) empirical study of the phenomena to establish a particular fact, (3) generalization of empirical facts to provide a unified explanation. Most of DSS research areas are making great efforts to conduct empirical studies to establish facts, but failed to generalize the results. No GDSS empirical research, for example, claims that their results are generalizable yet. Simply they can not build on each other's results which are not generalizable. For example, based on the review of the GDSS literature on group process and outcome, Dennis et al. (1988, p. 602) state:

It is important to observe, however, that the 10 studies that compared Decision Rooms to no computer support were conducted using seven different GDSSs. Each GDSS facility was designed based on a different philosophy, and the software used in each facility also varied widely. Different tasks, as well as different measures of dependent variables, were used in the studies. There is so much variation across these studies that generalizations become problematic. A coherent body of knowledge concerning GDSS can be accumulated if researchers share software designs, experimental tasks, and variable measures in the future.

The essence of the issue I would like to emphasize here is that in order for Group DSS, ODSS, strategic DSS, and other DSS research subspecialties to be "established" research areas, they should be grounded firmly in diverse contributing disciplines, and should be able to develop their own theories distinguishable from one other. According to Dubin (1969), essential part of theory building is measuring accuracy of empirical indicators to test the reliability of the model (theory) so that we can build viable models of empirical world that can be comprehended by the human mind. Our DSS empirical research will not gain credibility if its results can not be reproducible. We believe the most critical obstacle that has inhibited the accumulation of scientific knowledge of DSS is the lack of what Dubin called "observer reliability" and "instrument reliability."

Furthermore, there was absolute agreement among the panelists in the 1992 DSI workshops as to the importance of a cross-functional approach in decision-making research. Whatever we may name this DSS research subspecialty (ODSS or strategic DSS), this cross-functional approach may be the core of several research issues. In addition, we must face the urgent need for cross-national boundary decision making to develop global DSS (International or multinational DSS). Undoubtedly, the international dimension of DSS research will be an emerging area in DSS research. As of this writing, we do not have even a clear definition of international DSS. Expanding DSS research into multinational environments will be exciting as well as challenging for DSS researchers. How can multinational decision variables be systematically integrated in the design of international DSS? How can data bases/model bases and data base management systems/model base management systems be optimally designed for multinational corporations? How can interface systems be effectively designed to deal with the international communications between users of DSS in many different languages and cultures? These are just several issues we need to address as we enter the 21st century.

References

Culnan, M.J. "The Intellectual Development of Management Information Systems, 1972-1982: A Co-citation Analysis," Management Science, (32:2), February 1986, pp. 156-172.

Culnan, M.J. Mapping the Intellectual Structure of MIS, 1980-1985: A Co-citation Analysis," MIS Quarterly, (11:3), September 1987, pp. 341-353.

Dennis, A.R., George, J.F., Jessup, L.M., Nunamaker, J.F. Jr. and Vogel, D.R. "Information Technology to Support Electronic Meetings," MIS Quarterly, (12:4), December 1988, pp. 591-624.

Dubin, R., Theory Building, The Free Press, New York, 1969.

Eom, S.B., Lee, S.M., and Kim, J. (1993). "Intellectual Structure of Decision Support Systems (1971-1989)," Decision Support Systems, (10:1), July 1993, pp. 19-35.

Eom, S.B. and Min, H. (1992). "The Changing Role of Multiple Criteria in Decision Support Systems," Human Systems Management, (11:3), 1992, pp. 137-144.

Farhoomand, A.F. "Scientific Progress of Management Information Systems," Data Base, (18:4), Summer 1987, pp. 48-56.

Goul, M. "A Dyed-in-the-Wool Tool Builder Sings the Blues for DSS and Becomes Somewhat Excited about a New Romance with `O'DSS,'' Decision Line, (23:5), September/October 1992, pp. 14-16.

Keen, P.G.W. "MIS Research: Reference Disciplines and a Cumulative Tradition," Proceedings of the First International Conference on Information Systems, Philadelphia, PA, December 8-10 1980, pp. 9-18.

Kuhn T. S. The Structure of Scientific Revolutions, 2nd ed., The University of Chicago Press, Chicago, IL, 1970.

Price D. Little Science, Big Science, Columbia University Press, New York, NY, 1963.

Teng, J.T.C. and Galletta, D.F. "MIS Research Directions: A Survey of Researchers's Views,'' Data Base, (21:3-4), Fall 1990, pp. 1-10.

SEAN B. EOM is a Professor of MIS in the Department of Management at Southeast Missouri State University. He is responsible for designing and implementing management information systems courses in the College of Business at the University. He received a Ph.D. in management science from the University of Nebraska-Lincoln in 1985. His current research interests include the application of decision support and expert systems for multinational corporate planning and serves on the editorial review board of Journal of Global Information Management and Journal of Financial and Strategic Decisions.