Finding Research Agendas: Getting Started Weick-Like

Craig C. Lundberg
Cornell University

If you want to understand what a science is you should look in the first instance not at its theories or findings and certainly not at what its apologists say about it; you would look at what the practitioners of it do.

—Clifford Geertz (1973)

What are the ways by which scholars initiate significant organizational research? How might an organizational inquirer go about discovering research foci that are likely to result in substantial advances in understanding? These are obviously very important and at the same time very difficult questions. Following the advice in our epigram, this article will suggest some tentative answers by examining the agenda-finding practices of one influential and widely acknowledged creative scholar—Karl E. Weick, the Rensis Likert Professor of Organizational Behavior and Psychology at the University of Michigan.

Selecting a phenomenon, topic, or issue to study is the first step in conceiving/initiating research projects. As crucial as this activity is generally acknowledged to be, it remains relatively underdiscussed and underinvestigated—with two, somewhat dated, notable exceptions, Lundberg (1976) and Campbell, Daft, and Hulin (1982). At the present time, the organizational sciences seem to have entered a period in which research is initiated primarily either for compassion, confirmability, or comformability, in other words, it strives to respond to either what practitioners perceive are problems or extends ascendent theory. While there are no doubt many approaches for generating researchable questions, in fact there is remarkably little attention to this important first step of research.

With the intention of bringing attention to research agenda discovery generally, and the useful if unconventional practices of Weick, this article will proceed in three sections. In the first, we will briefly review the conventional advice for getting started in research and what has been suggested for differentiating significant from not-so-significant research. The second section outlines and examines the several opening tactics and gambits observable in the work of Weick. Finally, we attempt to stand back from Weick's agenda-finding practices and note the themes and beliefs behind them.

On Conventional Advice

The locus problem may be described as that of selecting the ultimate subject-matter for inquiring in behavioral science, the attribute space for its description, and the conceptual structure within which hypotheses about it are to be formulated.

—Abraham Kaplan (1964)

A casual survey of the literature offering advice on initiating research shows either no mention at all of how one goes about finding a focal question, topic, or problem to study, or statements so general as to be essentially useless. In business, for example, Zikmund (1984, p. 33) states "…the research process begins with problem discovery…the word `problem' in general usage, suggests something has gone wrong…Actually, the research task may be to clarify a problem or define an opportunity." Another example, for social science generally, is provided by Phillips (1966, p. 73), "When a scientist speaks of `defining a problem,' he usually means utilizing the best ideas he has in order to decide on the goals of his inquiry." Selltiz, Writhtsman, and Cook (1976) are not much more helpful when they note that the selection of a topic for social research may arise from a "concern with" some social problem, from an "interest in" some general theme or area of behavior, or from some body of theory.

Some organizational researchers, probably the minority, attempt to emulate the physical sciences who "…first ask what is known and from this they formulate their questions about what needs to be known" (Lawrence, 1992, p. 140). This is put somewhat more elegantly by Easterby-Smith, et al. (1991, p. 46), "The conventional view of scientific, and social scientific, method is that one should review the existing literature and research findings, identify some gaps and inconsistencies in the state of the art, and then design experiments or collect data that will enable existing ideas to be tested further, or cover evident gaps in knowledge and theory." Lawrence (1992, p. 140) however, points out a fundamental difference between the physical and the organizational sciences, namely, "Their subjects cannot tell them about their problems, whereas ours most emphatically can.... Our subjects can tell us what needs to be studied—where our theories and knowledge are inadequate." The majority of organizational researchers probably agree with Lawrence who states that "The better work in our field has come from problem-oriented research rather than from theory-oriented research." He goes on to suggest that the research process he recommends: "always starts with the choice of a significant emerging problem. To prepare for this, one needs to broadly observe both current affairs and history. One has to be a good listener, to interact as thoughtfully as possible with managers and employees."

Discovery of a research agenda then tends to be portrayed in two contrasting ways—either when a researcher pays attention to practitioners and what they say are problems; or, when a researcher pays attention to accumulated knowledge/theory and wonders how it can be tractably refined, extended, or applied. While this bifurcation has probably been overstated, many researchers would no doubt argue that significant research both focuses on real problems, and is concerned with theory—a finding reported by Daft (1984).

Research projects are variously evaluated as good, valuable, innovative, and interesting. Good research usually refers to the technical competency with which it was performed. Valuable research refers to the project's contribu tion—furthering understanding, explanation, or action. Innovative research refers to either novelty of ideas or methodology. Interesting research, after Davis (1971), denies commonly held assumptions (otherwise it will be seen as obvious). Impactive and significant research will always be interesting; research that is good, valuable and/or innovative, however, may not be significant research. Both theory-extending and problem-oriented research strives to be good and valuable, and is sometimes innovative. The common criteria for topic or problem choice have been identified by Webb (1961, p. 223): "Curiosity, confirmability, compassion, cost, cupidity, and conformability—or more simply, `Am I interested?' `Can I get answers?' `Will it help?' `How much will it cost?" `What's the payola?' `Is everyone else doing it?'"

By their very nature, however, both the problem-oriented and knowledge-extending approaches to finding research agendas are unlikely to be interesting, and thus usually less significant. It appears that the common advice for discovering research agendas is inherently flawed. If this be so, how might we go about discovering topics, problems, or questions that will be interesting? It is the premise of this article that an answer to this question may be found in the unconventional work of Karl Weick.

Weick's Opening Ploys

Weick (1992, p. 173) notes that what drives his research, "…are such things as incompleteness, novelty, counterintuitive implications, puzzlement, and fascination." To begin working, he says, all he needs is some kind of difference, something that attracts attention. He goes on to state that, "My impetus to begin a study is the question, what do I find interesting?" Put this way, Weick's alternative to theory extending and problem-oriented agenda finding appears to be individualistic. As I will attempt to show below, what may appear as an individualistic, even idiosyncratic practice, actually assembles into several identifiable gambits or opening tactics for initiating intellectual work. The identification of Weick's research agenda finding ploys, it should be noted, utilizes his own dictums for understanding what's going on—you'll know once you act, and, how can I know what I think until I see what I say (Weick, 1979, p. 207). Examination of a large number of his published studies prompted the induction of the following ways in which he discovers interesting research agendas. Weick, however, would modestly disclaim that any of these ploys are unique to him, pointing instead to the work of others such as Kaplan (1964), McGuire (1983), Meehl (1972), Nisbet (1962), and Webb (1961). It is Weick's conscious, consistent use of these ploys that deserves them being called Weickian.

Notice an Anomaly, and Try to Explain it.

Anomalies are unexpected and hence surprising events. That they have occurred at all is puzzling, and by definition they do not led themselves readily to known explanations. Focusing on an anomaly, whether personally observed or described by others, raises the question, how could that happen? If sufficiently bothered by this question, then sense-making efforts follow—garnering additional facts, valuing some facts differently, arranging and rearranging the facts of the situation until new understandings suggest themselves, until there is an explanation of how the event could have happened. One example of a triggering, anomalous event is to notice that in spite of the technically sophisticated systems and the considerable expertise of all the parties involved, two 747 airliners collided on the ground with catastrophic results (Weick, 1990a). Another example occurred in the events surrounding the death of all but three of a 13 man team of professional smoke jumpers in a Montana forest fire (Weick, 1993b). While obviously a situation of considerable risk, what was puzzling was why such an experienced crew disregarded their foreman's order, panicked, and ran.

Notice the Level of Analysis that Dominates the Explanation of Something, and Try an Explanation at Another Level.

The phenomena of interest in the organizational sciences ranges from the intrapsychic to the societal. The theorizing about some particular unit of analysis usually reflects the level at which the phenomena is first conceived. This ploy simply asks if the prevalent level of theorizing might be augmented by explanations at some other level; that is, could useful explanations also be made that are more fine- grained or more inclusive than those that currently exist? For example, while organizational theory at one time was devoted to structural variables about collectivities (e.g., centralization, formalization, and hierarchy), organizations can also be conceived in terms of patterned alliances among members, that is, collectivities as sets of interpersonal relationships (Weick, 1979). Shifting the level of analysis typically provides provocative insights, for example, the environment changes from the structural antecedent to an outcome in the above example. A variant of this ploy takes an idea developed for one unit of analysis and applies it to another unit at a different level, for example, using the mind to explain high reliability organizations by means of collective mental processes (Weick & Roberts, 1993). In a recent example, Weick and Quinn (1999) reframe organizational change as episodic or continuous by viewing it from either a macro or micro level of analysis, respectively.

Notice (or Create) Language that May Enrich Explanation and Explore it.

This ploy is based on the view that research is basically theory work (i.e., theory brackets and frames phenomena, defines what is data, is confirmed or disconfirmed, etc.), and theory work in turn is language work (i.e., language as symbols and rules for symbol arranging and manipulation). Words common to one field or endeavor may be suggestive of new insights when used in a different context. For example, "bricolage," which means making do with whatever resources are at hand, when applied to organizationally relevant learning, sug gests that organizations may already know what they need to know to survive which counteracts the assumptions of accumulation in the organizational learning literature (Weick, 1993c). Another example is "galumphing," a type of play observed among baboons where there is a deliberate complication of process not controlled by goals. When applied to persons, it has implications for dealing with novel problems (Weick, 1979). A variant of this stratagem is to take seriously the ideas in unfamiliar combinations of words. "Loose-coupled systems," once a throwaway phrase in a talk by J. G. March, suggested to Weick (1976) that organizations might usefully be conceived in terms of the degree of their internal coupling—now a standard idea in organizational theory.

Notice Common or Simple Activities or Things and Exploit Them as Metaphors.

This ploy rests upon the notion that metaphors are not only one of the oldest, most deeply imbedded, even indispensable ways of knowing in the history of human consciousness (Nisbet, 1969), but are the basis of some of the most central bodies of theory in the social sciences (Galt & Smith, 1976). Metaphors let us explore analogically from one thing to another. All sorts of things, events, and activities may serve as metaphors. For example, a carpenter's contour gauge is suggestive of the several properties of medium; and when these are used to describe leadership as a medium, many useful implications appear, for example, followers use the leader as a contour gauge, leaders who are good mediums will have shorter time horizons, and so forth. (Weick, 1978). For another example, a laboratory experiment using three-person groups playing the common target game over and over with one member being occasionally replaced is used to show the perpetuation of arbitrary traditions (Weick & Gilfillan, 1971) and later used to tease out properties of organizational learning (Weick, 1993c). We note that science for Weick is metaphorically a mosaic, that is, built piece by piece, rather than accumulating a pile of findings as science is often popularly understood.

Notice the Context of an Explanation, and Apply the Explanation to Another Context.

This ploy works in two ways. One way is to take our understandings from one situation and ask if they help to explain a different situation. For example, the interpersonal dynamics in love relationships have much to say about long-term, self-managing organizational teams (Weick, 1992). Other examples are to see the close parallel between theory building, something we know little about, and evolutionary processes, something we know a lot about (Weick, 1989), or the parallels between technology and sensemaking (Weick, 1990b). The other way this stratagem works is to take understandings of some things or events and then complicate those explanations so that they generalize to other settings. One now- famous example was the creation of a cause map for a jazz orchestra, which prompted a method (an etiograph) for representing complex cause maps with loops, which then enabled a test of the proposition that system fate is not in the content of the variables but in the structure of causality among them—a finding generalizable to all organizations (Bougon, Weick, and Binkhorst, 1977).

Notice Commonly Accepted Knowledge or Practices, and Pursue Possible Counterintuitive Explanations.

This ploy quite clearly is an application of Davis's (1971) proposition of what's "interesting." While many others have seemingly used it, Weick does so often. As before, we will restrict ourselves to just a few examples. Where almost all stress- management advice argues for removing or avoiding stressors, Weick (1975), noting the futility of this, shows that training under very stressful conditions is more effective because then the normal regression toward simplified thinking under the next stress means the person will regress to what in others would be a relatively unstressful cognitive condition. A second example concerns learning. Many organizational learning theorists posit a parallel between individual learning and organizational learning. Weick (1991) however, disconnects this parallel when he points out, appropriately, that individual learning is a different response to the same stimulus, and organizational learning is the same response to different stimulus.

The six question-generating ploys of Weick sketched above, while admittedly attributions and probably not exhaustive of Weick's creative gambits (the late Lou Pondy attributes two others to Weick, that is, take a well accepted aphorism and turn it around; take everyday life and embellish it seriously) seem to be quite different than those conventionally advocated. We now turn to the explication of these differences as well as what seems to be thermal to the Weickian ploys.

Stepping Back

The conventional advice for finding research agendas speaks to the discovery of problems, either by listening closely to what practitioners say are problems or by specifying the intellectual problems of how extant knowledge might be refined or extended. In contrast, Weick believes "problems" of all types are designed, not discovered (Weick, 1995). Each of the ploys noted above begins by "noticing" an intentional behavior guided by the cognitive framing, punctuation, and bracketing of the researcher. This noticing is presumably not emotionally neutral. In contrast to the empathy with practitioners facing pragmatic problems (i.e., compassion) that seemingly motivates problem-oriented researchers or the pragmatic pseudo-neutrality (i.e., curiosity, conformability, conformability) of theory-extending researchers, Weick appears to be bothered by practices and explanations that gloss over factual complexity or gloss over cause and effect, thought and action, structure and process, and the like (Weick, 1979, 1983, 1995).

While Weick has relied on phrases that incorporate the word "problem" for example, "problem finding" (Weick, 1992), "problem statement" (Weick, 1989), it is clear that his ploys do not identify problems per se but surface questions—questions about what is actually going on, how one thing might resemble another, how representations might be enriched or refined, where explanations might apply, what might be alternative explanations, and so forth. Perhaps, however, we should let Weick (1993a, p. 312) express himself:

To know my contexts, therefore is to know my work… I was struck by the frequency with which I seem to study what happens when people don't understand what is going on. My concern is not déjà vu (I've been here before), but rather, vuja de (I have never been here before and have not an idea where I am). Consider the evidence. I study interpretation, sensemaking, equivocality, stress, dissonance, and crises behavior, all of which are associated with the question, what is going on here?

Whereas a "problem" implies discrete solutionability (Lundberg, 1994), questions lead to sensemaking variety. In research agenda finding, the variety of Weick's opening ploys begins to outline the requisite variety in the equivocality of multiple realities. Said differently, to make sense out of the equivocal, the more ways we can come to questions and the more questions we can ask, the more we will eventually understand. For Weick (1995), understanding means sensemaking—how managers and scholars make sense of situations, more or less collectively with more or less coordination, and, how to make sense out of sensemaking. In this way, Weick discredits organizational phenomena as either disordered, indeterminate, or chaotic and thus essentially incomprehensible, or as fully ordered and determinate, merely awaiting discovery with the right approach. Rather, he seems to advocate an image of organizational scienceing that is rich in the multiplicity of meanings that can be imposed on equally complex phenomenological situations—if we are risky and playful enough.

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