11

Studying Groups at Work: Ten Critical Needs for Theory and Practice

Joseph E. McGrath

This book deals with the task performance of work groups in organizations. One central premise of this book seems to be that task performance of work groups in organizations ought to be a major field of inquiry. Many of the chapters imply such an idea and further imply that such a topic would be a feasible and valuable focus for systematic research. Only in a few spots have questions been raised about the proper scope or definition of the topic: Should things other than task performance be included? How should the contributions of members of those work groups be dealt with? Should any group phenomena that take place outside work organizations be given consideration? But nowhere does the book question the value or feasibility of building a field of study that concentrates on task performance of work groups in organizations.

Such questions would seem worth asking, I think, because of the history of research in related areas. There is a long history of study of task performance in groups, as well as productivity and task proficiency in work organizations. There is ample reason to question whether research in either of those two areas has been as successful as we would wish. Why, then, should we expect that a concentrated effort in what appears to be the intersection of those two areas of study will somehow be more successful?

That question can be asked in another, more optimistic form, namely, what could we do differently, in our study of work groups in organizations, to increase the chances that such work will be more successful than past work in related areas? This chapter addresses the latter, optimistic form of the question—what are the requirements for successful study in this area?

If we are to build a full-fledged field devoted to the study of task performance of work groups in organizations, we will need to handle certain methodological, conceptual, and substantive issues better than they have been handled in past work in related fields. Specifically, we need:

1. To use better methodological tools, primarily data collection tools
2. To use broadband strategies that are multivariate, multimethod, and multioccasion
3. To put more emphasis on theory
4. To study groups as intact social systems and to do so at a group level of analysis
5. To build a conception of how groups vary in type
6. To build a conception of how group tasks vary in type
7. To use a broader conception of the range of content to be included in our study
8. To study groups in context
9. To take seriously the idea of temporal patterns in groups
10. To take seriously the idea of group process

Some of these critical needs are surely old hat. I call them the “of course” requirements of our field. In much of our literature, they are recognized as needs, and simultaneously dismissed, by prefacing statements about them with “of course….” To wit: “Of course, we need new and better data collection tools and a broadband methodology.” “Of course, we need to give more attention to theory.” “Of course, we need to worry about the context within which these behaviors take place.” But those “of course” needs are far more often honored in the breach than in the observance.

Others of these critical needs are less often talked about, and perhaps they are therefore more important to dwell upon. These include, especially, the need to study groups as intact social systems, in a context that involves time as well as place and situation, and to focus on process. Therefore, this chapter gives more emphasis to these less familiar needs than to the more familiar “of course” requirements.

I will argue that these ten critical needs are important considerations in any systematic attempt to build a field of study that deals with groups at work. I will argue further that, if we give only lip service to them in our study of task performance of work groups in organizations (as we have done for many of them in other related areas of study), we may once again find that we have spent a lot of time and effort to build a “pile of data” that we then cannot translate into a “body of knowledge”—knowledge about task performance of work groups in organizations.

The remainder of this chapter will present brief discussions of these ten critical needs and reflect on parts of the conference in relation to those requirements. The critical needs will be dealt with in three clusters. The first three are methodological, the middle four are conceptual, and the last three are substantive. They are, I think, in order of increasing importance.

Some Methodological Requirements: To Use Better Tools, Broader Strategies and More Theory

The main methodological requirements for successful systematic study of work groups in organizations, I believe, are for a more balanced array of data collection tools, a broader array of strategic approaches, and, especially, a stronger emphasis on theory.

Data Collection Tools. We need improved methodological tools, especially better data-generating tools. We have a powerful array of sophisticated tools for data processing and analysis. They are, if anything, too strong for the data we usually feed them. We need better data to put into them.

We particularly need a better balance of data collection methods that do not rely entirely on self-reports of workers or of managers. It may seem unnecessary to bring up this matter in the present context. Everyone knows it! I would agree that this is surely one of the major “of courses” in our field. Everyone agrees that we need to use measures of different kinds that compensate for each other's strengths and weaknesses. But it is still the case that a very large majority of all empirical evidence in research on work organizations is based on such self-reports.

This is not to downgrade the value of such self-report data. I would join Webb and colleagues (Webb and others, 1981), and many others, in praising the substantial strengths of questionnaires and other self-reports, while at the same time warning of their serious limitations if used exclusively. Research on work organizations, as well as behavioral science research in general, has too often relied totally on such self-reports. Direct observations, with or without mechanical aids, also have serious weaknesses and limitations, but they constitute a powerful complement to self-report measures. Similarly, trace measures, so eloquently urged by Webb and colleagues, have serious limitations. But their very strengths (nonreactivity) are the major weaknesses of self-reports; hence, they are valuable in combination with self-reports and methods of other types. Many behavioral scientists seem to shun the use of archival information, or at least to be uncomfortable with it. But such evidence often could serve valuable purposes, especially in research on continuing work groups within organizations.

This is not an argument for any one method; rather it is an argument for no one method. The need for a better balance of data collection methods is certainly one of those “of course” requirements that we too often accept in principle and ignore in practice.

Diverse Research Strategies. Not only do we need to employ a variety of measurement methods, we also need to bring a broader band of methodological strategies (for example, field studies, experiments, computer simulations, sample surveys, and so on) to our study of work groups in organizations. Furthermore, within each of the strategies that we might employ, we need a broadband approach to data collection. We need sets of data that are multivariate and that involve multiple types of measures from multiple sources for each of those variables. Such bodies of data also need to reflect evidence from multiple occasions and a dynamic view of the systems under study.

At least two chapters in this book give special emphasis to this critical need for a wider array of research strategies than are generally employed in research on work groups in organizations. Davis and Kerr (Chapter Nine) argue eloquently for the value of using a class of research strategies that they term thought experiments and that I call formal theories. These thought experiments are a means to extend and multiply our intellectual muscle, so to speak. Indeed, thought experiments offer us a means to pose, systematically, some questions that we cannot ask at all in a direct empirical fashion. Davis and Kerr do not propose thought experiments as a substitute for experimentation and careful observation. On the contrary, they argue for the use of formal models that are built on the best evidence we have from empirical and theoretical work of the past and that can be used to assess the complex consequences of the most promising hypotheses currently considered of interest in a given topical area.

Schwartzman (Chapter Seven), in contrast, calls for broadening the array of empirical strategies that are used in research on task performance of groups in organizations to take the perspective of the individual into account. She argues that virtually all work in these areas is done from the point of view of the “system,” of the work organization, rather than from the perspective of its members. She suggests that we could learn a lot by asking about the system and its operation from the perspectives of the “natives” who inhabit it and whose behavior is the putative topic of interest. Schwartzman's prescription is quite in keeping with the critical need to use a wider array of research strategies, whose strengths and limitations can complement and offset one another.

More Focus on Theory. We must stop acting as if theory were either a naughty word to be shunned or a public relations consideration to be tacked onto our work later, when it needs to be packaged and sold. We must stop acting as if it were possible (let alone desirable) to have evidence without interpretation.

Since I consider formal theory to be one class of research strategy (Runkel and McGrath, 1972; McGrath, Martin, and Kulka, 1982; Brinberg and McGrath, 1985), the need for more focus on theory is, in my view, really just a special case of the need for a broader array of research strategies. But it is a very special case that deserves special pleading.

Behavioral scientists who have a strong preference for an empirical approach to research often talk about “grounded theory.” That phrase sometimes turns out to mean “theory” that starts at—and largely remains at—the raw empirical level. It is one thing to “ground” theory in empirical evidence, as in Davis and Kerr's use of extant evidence as the base for their thought experiments. It is quite another matter to keep our research information permanently “grounded” because we are unwilling to go beyond empirical description to bring useful theoretical concepts into our interpretations. The latter seems to be, too often, the implicit posture of the behavioral science work on groups in organizations.

Substantive theory has many functions, among them a screening or filtering function and a focusing function. Furthermore, as I have argued elsewhere (for example, Brinberg and McGrath, 1985; McGrath and Brinberg, 1984), an emphasis on substantive theory early in the research process is one route by which the basic researcher and applied researcher can approach the same problems from a common ground, rather than in seeming conflict with each other. Such a rapprochement of applied and basic research is badly needed in research on organizations.

Conceptual Requirements

The central conceptual issues revolve around our need to deal with our units of study with more conceptual clarity. In the present context, that means that we must study work groups in organizations as intact social systems, and do so at a group level of analysis. This need, in turn, implies that we have some means for conceptualizing different classes of groups and different types of tasks in which those groups may be engaged. It also implies that we need to deal with the behavior of those groups with respect to a much broader array of content than just simple task performance outcomes. Rather than identifying our focus as the study of work groups, perhaps we should identify it as the study of groups at work.

Studying Groups at a Group Level of Analysis. We need to study work groups as if they were semiautonomous, intact social systems that are partially independent of, though also interdependent with, other parts of the work organization. We need to approach the group as a unit, not as a collection of members or even a collection of dyadic relations. We need to study groups as concrete systems and to recognize that groups are full-fledged social systems, not just vehicles for task performance.

Closely related to the need to deal with groups as intact social systems is the need to do our group research at a group level of analysis. We need to get beyond the idea that a group is a forum for shaping members. It is that, but it is also much more than that. We also need to get beyond the idea that the group is to be construed as the simple sum of its members, and the group's behavior as the simple sum of its members' behaviors. We need to ask, “What goes on at the group level?”

A group level of analysis is especially important, I think, for those interested in organizations. When researchers try to work without some level of analysis between the organization as a whole and the individuals who are its members, they burden themselves with an incredibly complex set of interconnections. Much of this complexity can be organized, so to speak, by attending to patterns of interrelation among individuals at intermediate levels and construing those patterns as systems in themselves. It is perhaps analogous to the biologist trying to work only with the level of cells and the level of organisms, refusing to take seriously such intermediate levels as organs and functional subsystems (cardiovascular, neural, and so on). It might be possible to do so, but it certainly would be more complex. So it is with organization research that ignores intermediate levels—such as the level of work groups as intact systems.

These themes arose at several points in the conference on which this book is built. Several of the contributors, most notably Hackman and Walton, emphasized the importance of regarding the units of study as intact and complex social systems—not just as a set of people with a common task and a common supervisor, not just as a set of dyads who work together, not just as a task performance vehicle within a subsystem of an organization, but as an intact social system, a concrete social unit, worthy of study in and of itself.

Goodman's approach (Chapter Four) carries this theme to its most extreme form. His is a modified form of a sociotechnical approach, as I understand it; and in any such approach the focus needs to be on the intact social system. But in such a sociotechnical view, the focal system includes the hardware, the location, the work procedures, and the situational factors, as well as the people and their relationships. I am urging just such a sociotechnical view of work groups—namely, a view that focuses on the operating system itself.

Goodman uses this approach to argue for a much more idiographic approach to the study of work groups in organizations than has been the habit of behavioral scientists working on these problems. He believes that we have tried to generalize too much, too far, and too soon. In Goodman's view, I infer, we have tried to generalize across groups and types of groups far too broadly and have done so far too early in our knowledge accrual process. He seems to argue that we should immerse ourselves thoroughly in the particularities of content and process of the specific groups we are studying (in his case, specific mine sites of particular coal-mining companies); we should understand those processes in relatively complete detail before we attempt to generalize that understanding to a broader array of groups—even to other operations of that same mining company or to other similar mining companies, much less to other work organizations that assemble cars or sell insurance or ship cargo overseas. Furthermore, from his work on such groups, he reaches conclusions that suggest that a major part of the variance in work group productivity is associated with “individual differences,” not among the members of such work groups as individual human beings but rather among the specific work groups (the “system” composed of workers, their supervisors, their machinery, their work site, and combinations of all of those contributing sources) as unique, concrete systems that operate as intact social units.

I do not agree with Goodman's idiographic prescription.¹ I do not think it a necessary consequence of an attempt to study work groups as intact social systems at a group level of analysis. If he were right, then we should each set about developing a “science of mine shaft 32,” or mine shaft 46, or assembly plant G, or whatever our personal piece of the grand pie is to be. Further, we would hope that meanwhile someone else is developing an equivalent intimate knowledge of all the other specific instances of mine shafts and offices and field stations and warehouses to which we might ultimately want to generalize our understandings.

I hope Goodman is not right on this issue, for two reasons. One is a matter of personal preference; I really don't want to get to know most “intact social systems” at the level of intimacy that would be necessary to carry off that totally particularistic approach. I just don't want to be the world's leading student of mine shaft 32! To paraphrase Will Rogers, I have never met a group I liked that much!

The other reason, a much more important one, is a matter of the logic of our enterprise. If Goodman were right, then we would be out of the science business altogether and in the history business—as some social psychologists (for example, Gergen, 1973) have argued that we are. By the time we could study each specific system in its full particularity and digest and communicate what we had learned, that concrete system would be a thing of the past. This statement is more than just a version of the Heraclitean saying that we cannot step in the same river twice. The kind of particularistic and idiographic immersion in the focal system reflected in Goodman's work involves not just a stepping into the river, so to speak, but a concentrated splashing around in it. Two consequences of that intense immersion are pertinent here: First, the very thrashing around—the research process itself—changes the river, often in dramatic ways. In the behavioral sciences, research activities themselves disturb the phenomena being studied. Second, surely even the most nondynamic views of such systems would expect substantial changes to occur during the considerable period of time it would take to carry out such a total immersion strategy. So the system we are studying will change while we are studying it and because we are studying it. If we followed this prescription, we would each mount an enormous research effort to learn about one particular concrete system in all its particularistic and idiosyncratic glory, only to find at the end of that effort that the system we presumably know all about no longer exists. And, by this rationale, our information is not to be generalized, even to another copy of that same kind of system, much less to systems of other kinds. Such a resource-consuming enterprise could serve no purpose other than satisfying the curiosity and fattening the vita of the individual researcher! If Goodman is right, in the extreme form of his antigeneralization argument, we are out of the knowledge accrual business and in the business of being social system raconteurs (and raconteuses)!

Nevertheless, I think we must take seriously Goodman's evidence that a very large part of the variance in work group productivity is “between specific groups” variance. Evidence on the same point exists elsewhere. For example, Kent and McGrath (1969) studied groups of various gender compositions working on tasks of three types and found “among groups” variance to be a major component of the variation on task product characteristics, along with task type, whereas very little of the variation was associated with gender composition or with the higher-order interactions of those factors. Furthermore, in their integration of small group research information, McGrath and Altman (1966) found that one of the most consistently significant relations in the small group research literature was for (unspecified) between group differences on a variety of dependent variables.

Such evidence, along with Goodman's, means at least that the groups we study (in both field and lab) differ from one another in a variety of important ways that are not taken into account in our experimental designs. I find this less an argument against generalization than a challenge to do it better—and another strong indication of our fundamental need for more and better theory. I agree with Goodman that we need to study work groups in more detail. But I think we need to do so, not as an alternative to generalization across groups, but as an aid to it.

Classifying Variations in the Groups We Study. One reason for this discrepancy in views, perhaps, is that the matter has been posed in dichotomous terms. Thus far, the discussion has seemed to pose the choice between believing that every group is unique and not comparable to others or that all groups are alike and information about any one of them applies to all others. Actually, of course, neither of those two positions is even sensible, let done likely to be true. Instead, groups come (or are constructed) in a variety of shapes and sizes, colors and kinds. One of the ways in which we can resolve some of the issues already discussed is to try to specify, much more carefully than is often done, just what kinds of groups are to be the subject of any given inquiry.

In short, we need some form of classification of types of groups if we are to clarify how the behavior of different types of groups may vary. In fact, an effective classification of groups, into subclasses that are homogeneous in regard to key system features (including technology), would provide a resolution of the dilemma of generalization versus specificity that was discussed in the preceding section and thereby dissolve the disagreement between Goodman's idiographic view and my own.

It is remarkable how little effort has been given, in the group research field, to what would seem to be a fundamental definitional task for any field of study: the development of a meaningful classification of major varieties of its units of study. I have reviewed some of those efforts elsewhere (McGrath, 1984). The tendency to ignore what types of groups were involved in a given study, when we try to generalize over studies, does not seem to be any less prevalent in studies of work groups in organizations than it has been in the past in group research in general.

Elsewhere (McGrath, 1984), I have presented a classification of types of social units that have been, or could be, the focus of study in work regarded as group research. Some features of that classification are relevant to the present context. In that classification system, the entities that researchers have used as their focal units for study, in work that gets regarded as research on groups, are divided into three main categories, each with a number of subdivisions. Some studies of groups (many would say too few) deal with entities that could reasonably be called natural groups. I regard as natural groups those social units whose existence and behavior is independent of any ongoing research project to which they might (knowingly or unwittingly) be contributing evidence. Such groups are not created by the investigator. Their composition, structure, and process is not determined by the investigator. The tasks on which they work are not chosen by the investigator. They are not behaving so as to attain goals set by that investigator.

Other studies of groups—a far larger set than the first—deal with entities that I call concocted groups. I consider concocted groups to be social units that exist, or have the particular form they do, because they are part of some ongoing research activity. Such units are created, or modified in their composition, structure, task, goals, or process, by researchers and for research purposes.

The distinction between natural and concocted groups is not a distinction between groups that are “real” and “not real.” Concocted groups are real, in the sense that individual behavior and group processes operate in context. But they are not natural groups, in that such behavior and processes are not an integral part of the lives of the group and its members. Concocted groups are doing what they are doing because they are part of a research endeavor. Natural groups are doing what they are doing because they are living their lives.

Still other studies of groups—by far the most numerous category—involve entities that I call quasi-groups. These studies use social units whose social and/or task processes are so highly constrained that we would not be likely to consider them as real, let alone natural. (These quasi-groups, however numerous in the small group research literature, are less pertinent to this chapter and will be given very little further consideration here.) These three categories of units of study for research on groups are not totally distinct. The units of study used in certain kinds of group studies really fit into two of the categories, and thereby the three categories are tied to one another. (See McGrath, 1984, chapter 4, for a more complete presentation of this classification system.)

Furthermore, social units included in the category of natural groups are not all alike. There are at least four main forms, each occuring in “nature” at relatively high base rates but each quite different from one another in terms of their relation to group research. One form of natural group functions more or less as total embedding systems for the individuals who are members of the group. In these groups, the individual carries out a very broad band of his or her activities as part of that group and remains a member of that group for a relatively long time. An example is the family, especially for young children.

Another form of natural group is what I call the expedition. These function as embedding systems for a broad band of the individual's activities, but only for a delimited period of time that is more or less predictable. Exemplars of this form of group would be such social units as an arctic wintering-over party, the crew of a spaceship or a submarine on a very extended mission, and a child's living group in summer camp.

Still another form of natural group is the standing crew. Such groups engage only in certain types of activities—often a certain set of tasks in a work setting. But such groups often persist for (or recur repeatedly during) a relatively long period of time, with more or less the same membership, tasks, and goals. A standing crew would be any case in which the same set of members do the same set of activities for the same organizational goals in a recurring pattern. Exemplars of this form of group would include athletic teams, work crews, and standing committees of a legislature or a college.

The fourth form of natural group in my classification system is the task force. Task forces are groups that are created by natural circumstances (as opposed to experimental purposes) for a one-time performance of a delimited task. Such groups exist for and deal with only a sharply delimited band of activities—a specific task or mission—and they exist only for the period of time needed to carry out that mission. Any ad hoc committee is an example. So is a jury.

In practice, the distinctions between these four forms of natural groups are often far less clear-cut than this classification schema implies. The differentiation between embedding systems and expeditions is a matter of how soon, and how predictably, the group will end. The distinction between embedding systems and standing crews is a matter of how broadband the set of activities are that define the group's purposes and behaviors. The distinction between task forces and the other three forms depend both on the anticipated duration of the group as a major locus of action for its members and on the bandwidth of member activities that are encompassed within the group's purview.

Frequently, natural groups that would seem to fit one of these forms actually end up fitting another. Some athletic teams, for example, deliberately try to become more like a family, broadening the scope of activities that members do together. Conversely, some families seem to migrate toward becoming more like standing crews, sharply delimiting the bandwidth of (recurrent) activities that members carry out with one another. One could postulate, too, that the developing adolescent comes to view his or her family of orientation as an expedition, with its totally embedding nature soon to end as the child gains maturity and independence and develops other relationships that compete for his or her time. But at any given time, natural groups can be characterized, more or less, as being one of these four forms; and that characterization is indicative of the centrality, extensiveness, and intensity of the group's role in its members' lives.

In principle, work groups in organizations include social units that fit all four of these types of natural groups: the embedding system that functions like a family; the expedition that serves as total context but for a predetermined period of time; the standing crew that does its tasks recurrently; and the ad hoc task force that does a job just once. In practice, though, the first type—embedding systems—probably have a low base rate as naturally occurring work groups in organizations. Yet, in a sense, this form is the most natural type of group, and it is such groups that we often have in mind when we talk about how important it is to study “real” or “natural” groups rather than artificial ones. When we set out to study natural groups in work settings, we intend to study social units that encompass a broad band of member activities over a relatively long period of time. But we seldom end up studying work groups that are as broadband and time enduring as families.

Hence, much of the actual interest in natural work groups in organizations focuses on groups of the other three types. Expeditions are a form of work group of relatively high frequency and importance in certain kinds of organizations such as military forces. Task forces (such as ad hoc committees) are even more frequent in many kinds of organizations and often carry out very important functions. Standing crews are the core of the work force in most work contexts.

These four types of natural groups are all quite different from one another, and we have no reason to suppose that the pattern of relations among their structures, processes, tasks, goals, members' abilities and attitudes, and so forth are similar from one type to another. The matter is more complex still if we consider a variety of types of social units called concocted groups in my group classification schema (McGrath, 1984). Concocted groups depart from “naturalness” in group composition, in group task, or in both. The task forces discussed under natural groups, although limited in bandwidth of group activities and in expected duration of the group's existence, are nevertheless “natural” in composition and are engaged in tasks endogenous to the organizational settings in which they exist. That is, the people who are members of such task forces are drawn from the organization within which those task forces are to operate, and their composition occurs by the operation of processes natural to that setting. Furthermore, those task forces are created to do tasks that are a part of the work of the embedding organization.

There is overlap between natural groups of the fourth type, task forces, and certain kinds of concocted groups—ad hoc groups created for the purpose of a research study. By definition, task forces as natural groups are created in forms and for purposes that are natural or endogenous to the context in which they occur. In contrast, similar but concocted groups are often created in forms and for purposes related to some research activity.

The overlap can be shown by a hypothetical example. Suppose a department of an organization decided to form a set of committees to do certain important tasks. They would choose members from the pool of eligible members and assign them to specific committees by the “natural” processes routinely used by that part of the organization. In contrast, suppose that for some reason a research activity intervened just when the committees were to be established. Hence, a set of committees designed to do the same set of tasks would be assigned, from the same pool of eligibles, by the “unnatural” process of having researchers allocate members to committees using a randomizing procedure. The tasks of the two committees would be the same under the two sets of conditions. The actual composition of any one committee might in fact be the same under the two conditions. The composition of all committees would be, in a sense, the same. The distinction between natural and concocted forms of these social units is, at this limit, quite arbitrary; it inheres mainly in what the members know about the assignment process.

But sometimes it is useful to study social units for which one or the other of those two major facets of “naturalness”—composition procedures and tasks—are constrained. There are many cases in which groups doing tasks natural to (endogenous to) the organization are composed in much more “unnatural” ways than just a randomization of the allocation procedure. For example, I have discussed (McGrath, 1984) a category of studies called system tests, involving a completely arbitrary set of participants but an actual set of system tasks. Conversely, there are many cases in which actual group members may be studied while doing relatively “unnatural” tasks—either tasks that are simulations or representations of actual group tasks or tasks that are purely artificial. There is a category of such tasks that I refer to as training tasks; it would include both military training exercises and practice games or scrimmages of athletic teams. Here, the group's composition is natural, and the group's task is a simulation of its endogenous tasks.

When we modify both task naturalness as in the training tasks category and the naturalness of the group's composition as in the system test category, we have a type of study that I call mock studies. I chose the term to suggest one major example of that type of study, the so-called mock jury study. But many simulations (for example, aircraft flight simulations, automobile driving simulations, games simulating international conflict, “in-basket tests,” and the like), when used with groups that are not composed naturally from the organization's own membership and processes, would fit this category.

If we restrict still further the naturalness of task—giving up any attempt to simulate tasks endogenous to the organizational setting and using, instead, “artificial” tasks designed to maximize the precision of certain kinds of performance information—we have a category of studies that I refer to as crew tests. Suppose, for example, that a basketball coach conducts sprinting drills or dribbling and rebounding drills, or that a play director holds dance drills, with members of his or her team or chorus line. The composition of such groups is as natural as it can be. The tasks, however, are not natural, nor are they attempts to simulate the group's natural tasks. Rather, they reflect abilities and skills contained in and/or underlying performance of the endogenous tasks. Why would these not generate data of interest to the researcher who cares about task performance of work groups in organizations?

When we combine the use of artificial tasks with the use of artificial composition procedures, we have the final type of concocted group. I call this type, quite unelegantly, ad hoc laboratory groups with artificial tasks. These are the prototypical “artificial laboratory groups” that so often serve as the whipping boys for critics of experimental approaches: groups composed of an arbitrary combination of individuals, previously unacquainted, who interact with one another only while working on tasks arbitrarily assigned by the experimenter. They are the most restricted of the types of concocted groups. On the other hand, they also can be viewed as the most unconstrained of the types of quasi-groups that have been used in group research. (See McGrath, 1984, chapter 4, for further discussion of quasi-groups.) Such groups are, far and away, the most frequently used type of unit of study for the group research field.

Why study unnatural groups? Among the conference participants and among researchers in general, the people who seem most committed to the development of a field of study focusing on task performance of work groups in organizations are also the people who seem to have the strongest preference for studying natural groups—and studying only natural groups. However, there are many powerful reasons why group researchers often choose to study social units that do not fit my category of natural groups but rather are what I have termed concocted groups. I have presented some of those reasons elsewhere (for example, McGrath, 1984; Runkel and McGrath, 1972) and will deal with them here only briefly to make my central point.

Take, for example, the case of jury studies. It is, in fact, illegal to study juries in their ongoing natural state. Some researchers interested in the problem have chosen to study jurors, retroactively—attending to the naturalness of membership but at the same time accepting artificiality in many other features of the “natural” jury situation. Other researchers have chosen to study what I would call mock juries—simulations of the presentation of evidence from a given case or cases. These mock jury studies are of two kinds: studies that use individuals drawn from jury rolls and studies that use jurors drawn from an arbitrary but accessible population (such as college students). Both of these are “artificial” in composition, but in different ways; and both are “artificial” in the tasks being done, but with the degree of that artificiality being a function of how thoroughly they attempt to simulate the endogenous tasks of actual juries. But we really cannot consider any of these kinds of jury research as dealing with natural groups as here defined. Should we therefore gainsay all opportunity to acquire empirical evidence about juries and their operations?

Furthermore, if it were not illegal or otherwise impractical to study actual juries as naturally occurring groups and if that were the only kind of study we did on the topic, those studies would not be very informative. After all, each jury is unique—it deals only with one case, under one judge in one particular legal jurisdiction, and with one set of attorneys, witnesses, and surrounding conditions. A study of the specific jury that heard case 632 in courtroom B of the Muskogee county courthouse on June 17th, 1956, would be even more particularistic, more idiographic, than the studies of the hypothetical “mine shaft 32” that I conjured up earlier in the chapter.

Generally, we do not want to get into the courtroom equivalent of the “mine shaft 32” bind but rather want to learn about a more general topic than that. To do so, we must somehow get information on lots of cases that are somehow “the same” (that is, comparable) and combine that information over cases. In that intellectual enterprise we call science, we have no way to use single-case information to gain “intellectual leverage” on a topic that is not totally particularized to that case.

If we worked solely with “naturally occurring” juries, even if we got evidence from a lot of cases, we would have no logical basis on which to combine that information over cases. Each case is a specific jury hearing a specific legal case under a specific judge in a specific jurisdiction, and so forth. We cannot combine information from their results unless we are willing to assume that all juries (and all jurors) are alike, that all types of cases (murder, fraud, rape, and so on) are alike, that all judges are alike, and/or that all jurisdictions are alike. Those assumptions are highly dubious (if not downright silly) to anyone who is a substantive system expert in the legal system. Even if we assume merely that at least all rape cases in a given jurisdiction heard by the same judge are “the same,” we would be unlikely to collect data on enough instances of that kind of legal case to gain much inferential leverage from their aggregate results.

Mock jury studies let us replicate the hearing of a given legal case with multiple juries and potentially with alternative judges, attorneys, and jurisdictional peculiarities. Mock studies certainly have their limitations, used alone. But they also offer lots of intellectual leverage on otherwise intractible questions about juries and jurors, if they are used in sensible combinations with studies of other types.

I will not belabor further the many good methodological and conceptual reasons that one might want to study such “unnatural” units, along with rather than instead of studies of such natural groups. Instead, I will argue that, if we want to build a systematic body of knowledge about task performance of work groups in organizations, we had better not reject, out of hand, any opportunities to gain major methodological leverage on that relatively intractible topic. Our Humean logic and positivistic methods are, at best, relatively blunt instruments for acquiring knowledge and increasing our confidence in that knowledge. If we want to study anything at all complex, and we begin that effort by restricting ourselves both to a very limited set of positivistic tools and to using only naturally occurring instances of the phenomena to be studied, we are burdening ourselves with an unnecessary, perhaps fatal, handicap. The topic is tough in any case. We will need all the help we can get.

Classifying Variations in Group Tasks. Cutting across these distinctions about the group's status as a natural or concocted group is the matter of what the group does: its tasks or goals or span of activities. When we set up a work crew or a task force, we set it up to do something—and, by implication, not to do many other things that such a group could do. The research literature on groups reflects a bewildering array of tasks that have been the focus of such studies. At the same time, that literature reflects surprisingly little consideration of how group task performance depends on variations in the tasks that are performed.

There have been surprisingly few attempts to develop systematic ways to classify group tasks. I have tried to build a task typology based on the best of those past efforts (McGrath, 1984). That task classification schema specifies four related task performance processes: to generate, to choose, to resolve, and to execute. Each of those performance processes embodies two related subtypes:

1. Generating plans (planning tasks)
2. Generating ideas (creativity tasks)
3. Choosing correct answers (problem-solving or intellective tasks)
4. Choosing preferred answers (decision-making tasks)
5. Resolving conflicts of viewpoint (cognitive conflict tasks)
6. Resolving conflicts of interest (mixed-motive or negotiating tasks)
7. Executing tasks requiring competition against another group (contests or battles)
8. Executing tasks requiring competition against standards of excellence (performances)

Those eight task types are related to one another in a form that resembles a circumplex. Furthermore, I believe, the operating rules by which groups do business vary systematically across that circumplex, and these four task performance processes are systematically related to socioemotional stages of group development. If so, then this task circumplex (or some improved version of it, perhaps) can serve as another template (along with the group typology already discussed) for framing our questions and qualifying our generalizations about groups. (See McGrath, 1984, especially chapter 5, for a more detailed presentation of this task typology).

Work groups in organizations do tasks of all eight types but not with equal frequency. One way in which this task typology may help us plan for the systematic study of groups at work is to highlight how the frequency distribution of these types of tasks for naturally occurring groups is quite different than the frequency distribution for types of tasks included in our studies. Research on group task performance has dealt mainly with problem-solving and decision-making tasks (types 3 and 4) and to a lesser extent, with the resolution of conflicting interests and the allocation of rewards (type 6). There was a flurry of work, a few years back, on so-called creativity tasks (type 2). But in the workaday world of groups at work, I wonder how often most workers do anything that they would regard as problem solving or decision making or bargaining or allocation of payoffs? That world, I think, is much more densely filled with tasks of quite different types: tasks that involve performances and competitions (types 7 and 8) and planning tasks (type 1). These types of tasks are strikingly absent from the group research literature.

A second way in which we might use this task typology to help our study of groups at work is by building on the idea that group performance is a function of different rules of combination of member inputs for different types of tasks. There are strong tendencies for results of problem-solving groups (type 3) to reflect a “truth wins” or a “truth supported wins” combination rule, for decision-making groups such as (mock) juries (type 4) to reflect a “strong majority” rule, and for groups engaged in coalition-forming and allocation tasks (type 6) to reflect use of some form of minimum-winning-coalition rule (Davis, Laughlin, and Komorita, 1976). I have conjectured (McGrath, 1984) that groups engaged in intergroup competitions (type 7) reflect a conjunctive combinatorial rule, to wit: that the team with the “strongest weakest link” will win. If these or other specific operating rules are accurate descriptions for task performance of groups doing tasks of different types, then people interested in research on task performance of work groups in organizations had better take task type into account in all their empirical and theoretical activities. Otherwise, they will be faced with the same kind of dichotomous choice posed earlier in the discussion about generalization versus particularity across variations in groups. Without some conception of task type differences, we must choose either to be willing to generalize across all groups regardless of task or not to be willing to generalize at all across groups that have even very minor differences in tasks. We must avoid confronting ourselves with such choices of “to be … or not to be ….”

Inclusion of a Broad Band of Content. One further implication of the diversity of tasks in the group area and of the high level of variation that is accounted for by yet unspecified features of groups is that we need to bring to our study of groups a broadband conception of what the relevant phenomena are. We need a study of groups that is broader than just task performance; broader, too, than just cognition; broader, indeed, than any single process currently in fashion in the supporting behavioral sciences. If we are to study work groups in organizations as intact social systems, we must study all of the processes that go on in that “system”—not only cognitive and decision-making processes but also motivational, behavioral, and conative processes, as well as affective, evaluative, and emotional processes, plus whatever else goes on in those systems. Much of the tone of the conference on which this book is based seemed to imply that the study of work groups in organizations ought to study only task performance processes. I think that is a misguided exclusivity. A successful field of study dealing with work groups in organizations certainly must treat the group's task performances as of special interest. At the same time, we would undercut that enterprise, I believe, if we insisted that task performance be the only set of processes of interest within those intact social systems. If we are to study, successfully, work groups in organizations, we must do it not by studying the work of groups but by studying groups at work.

Substantive Requirements

The central substantive issues in any topical area revolve around what the important phenomena are and how they are to be construed. In the present case, if work groups in organizations are to be viewed as intact social systems, interdependent with their surroundings, then we need to study such groups in ways that allow us to learn about group behavior in relation to that context.

One crucial feature of the context is its temporal structure. Furthermore, one crucial aspect of group behavior is its temporal patterning. Hence, we need to study work groups dynamically; that is, we need to take into account temporal features of the group's context, as well as temporal patterns in the group's behavior. Furthermore, the phenomena of most central concern are the processes by which groups do what they do, not the inputs to those performances and not the products or outcomes of them.

Group Behavior in Context. The need to study group behavior as it occurs within the group's time/place/thing context has methodological and conceptual implications as well as substantive ones. On the methodological side, we must reckon with the potential distortion, as well as the massive reduction in potential information gain, that can result from cutting our phenomena out of their context. That issue has been raised obliquely in earlier sections; it is a far more complex question than the simple argument about whether to study groups in the lab or the field.

The context question is also a matter of conceptual strategy. If we are to take a view of groups that stresses their status as intact social systems, we need to think of group behavior as action within a complex context with which the focal system (the group) is intricately interdependent. This is true for the study of groups in general, I would argue. It is even more the case for the study of work groups within organizations. The embedding organization is a crucial part of any workgroup's context, and the pattern of mutual interdependence between the group and the surrounding organization is a crucial part of the pattern of substantive phenomena to be explored.

A number of the contributors to this volume made indirect reference to these contextual issues. One would certainly infer from Schwartzman's (Chapter Seven) general point of view that she would insist on a full treatment of group context. Hackman and Walton (Chapters Three and Five) also seem to assume the importance of context; it is an inevitable consequence of their concern with groups as intact social systems. Davis and Kerr (Chapter Nine) recognize contextual problems as particularly intractible in specific empirical instances and see this intractibility as adding urgency to the use of powerful formal models that let us transcend those particulars. Goodman (Chapter Four) treats contextual complexity as a critical feature of our field that prevents us from generalizing and requires us to follow the ideographic approach he advocates.

Temporal Patterns. One important facet of that critical contextual fabric is its temporal structure, and here perhaps more than anywhere else we have simply failed to deal with it. We have long talked about group dynamics, which originally had a time-based meaning, but we have certainly been sparing in our practice of it. Moreover, there are at least two sides to the temporal question. One is more or less a methodological issue: We must take seriously the idea of studying groups over time and of paying attention to the ways in which they change over time quite apart from our experimental activities. We have long recognized the need for longitudinal studies—and recognized some of their major limitations and difficulties. But we have not practiced them much. And when we have, it has most often been in the form of a simple before-after design that leaves much of the causal process to the imagination of the researcher. (The group research area is not especially notable in its lack of attention to these temporal matters. Virtually all of the behavioral sciences have given short shrift to time. See McGrath and Kelly, forthcoming.)

The other face of the temporal issue is that there is much temporal patterning in the group's behavior, and we need to deal more adequately with such temporal factors that are a part of the phenomena themselves. This is one area in which group research has been making some progress in recent years. There have been several major efforts to study the temporal flow of interpersonal interaction. Some of these (Jaffe and Feldstein, 1970; Dabbs, 1983; Warner, 1979) have concentrated on the temporal pattern of sounds and silences. Others (Gottman, 1979a, 1979b) have also been concerned with the content of that interaction and with patterns of mutual influence. Both of those sets of work have drawn on sophisticated data collection systems involving complex computer-aided audio-visual recording systems, and sophisticated data analysis methods such as Fourier analyses. Still others (for example, Kelly and McGrath, 1985; McGrath and Kelly, forthcoming; McGrath, Kelly, and Machatka, 1984; Warner, 1979, 1984) have developed conceptual models of temporal processes (“social entrainment”) by which group members influence one another, and by which they are collectively influenced by outside forces. The latter work has also shown such entrainment effects for group task performance processes, effects that are manifested in interaction patterns, in productivity rate and in aspects of product quality. This, of course, is at the heart of the study of groups at work.

Focus on Group Process. That we have given so little attention to temporal factors in the study of groups is closely related to our emphasis on structure rather than process. In spite of considerable lip service to the idea of group dynamics, mainly what we have studied has been group statics, and we have used relatively simple input-output models to do so. We have talked about process to a moderate extent, but, as with multiple methods and use of theory, there has been at best a very loose coupling of talk to action.

As with dynamics, we must begin to take seriously the idea of process. We often try to finesse the process issue by assuming that all important aspects of process can be captured in a “series of states,” if only that series is just fine grained enough. We seldom obtain a very fine-grained set of measures in any case; most often we have only a “snapshot” or two. But, I am arguing here, even if we did have data from a series of occasions that offered a very fine-grained picture of a time-ordered “series of states,” we would probably still miss much of the essence of the underlying process(es) because we continue to think about ongoing process as if it were nothing but (that is, merely) a succession of states.

That kind of interpretation in the group area is analogous to viewing the growth process as nothing but a series of measurements of height and weight. Such a series of “states” is not a good representation of process, however accurate those measurements and however small the time interval between successive measures. Growth is more than that. The current and recurrent status of a set of processes (a system or subsystem) can be assessed by such measures. Differences from one measure to the next represent an assessment of change in the status of the system. Number of inches and number of pounds reflect the state of the system at the time of those measurements. Change in inches per day and change in pounds per day are indexes of growth of that system. But they do not provide a description, much less an explanation, of the growth process itself.

The results of the studies of temporal patterning noted above, particularly the work on “social entrainment” noted there, point up one major reason why we often fail to study process even when we get a fine-grained time-ordered series of measures of the phenomena in question. Much of group behavior is cyclical rather than linear. Those cycles indicate underlying periodicities or rhythms that themselves are a function of a variety of factors (group size, task type, verbal proclivities of members, past history, and so forth). If we regard our observations as involving a temporally ordered series of “states,” even if that series is relatively fine grained temporally, we are not likely to interpret those observations as involving recurrent cycles. Instead, such data are likely to be analyzed in terms of differences between successive measures (that is, as before-after changes) or perhaps as an early-middle-late sequence. If the underlying processes are really recurrent cycles (for example, sine waves), the pattern of such differences will be chaotic, even if the recurrent cycles are quite regular. Such chaotic values would be likely unless we just happened to use the period of the cycle as the interval between our measures. If we did the latter, we would find no differences at all. If behavior is rhythmic, we will not find out about it in designs geared to assessing only linear changes over time.

Some of the work that shows promise in this domain begins with the premise that many features of behavior of individuals and groups are periodic; those studies search for the phase, periodicity, and intensity of those temporal patterns. (See, for example, Dabbs, 1983; Kelly and McGrath, 1985; Jaffe and Feldstein, 1970; McGrath and Kelly, forthcoming; Warner, 1979, 1984). A next step in that chain of logic, after temporal patterns have been identified and verified, is to try to manipulate conditions (of composition, structure, situation, and the like) so as to modulate those rhythms in predictable ways. From results of those activities, one may be able to infer the pattern of periodicities underlying the behaviors, the nature of the underlying processes that are driving those behavioral rhythms, and the nature of the processes by which those rhythms can be modified. Such an approach, it seems to me, is a way to study group processes within a dynamic, contextual framework.

Concluding Comments

The past fifty-some years of intensive study of small-group processes and structure has yielded much valuable research information. But there has been much chaff among the wheat. Furthermore, the recent annual yield of information has been far below the bumper crops of some years of the past. However, those recent smaller crops may have a higher-quality product; we may be better positioned, nowadays, to assess and use the information that we gain from small-group research.

From a far less informed position, I would venture that the situation is very much the same in the study of work in organizations. We have gained much from the past, and we currently are generating research information at a reduced rate but perhaps of a higher quality.

If we are going to take seriously the idea of a field of study that is, more or less, the intersection of those two areas—small group research and research on work in organizations—then we should also be concerned with how researchers in that “new” area of study—research on the task performance of work groups in organizations—can best gain from the past research efforts of those two underlying areas while at the same time avoiding their most serious pitfalls. This chapter has been addressed to those concerns and has dealt with them by postulating a series of requirements, or critical needs, for building such a field of study.

I have argued for ten such critical needs. Some of those requirements are methodological: We need to develop better data collection tools and use broader research strategies, including a stronger focus on theory. Some of those requirements are conceptual: We need to study groups as intact systems at a group level, to deal with the variation in types of groups and types of tasks, and to include a broader range of content as part of the phenomena of interest. Some of the critical requirements are substantive: We need to study groups in context, to give much more attention to temporal features of both the context and the group's behavior, and to focus on group process rather than group structure or outcomes.

If we give only lip service to those critical needs—as has too often been the case in many areas of the behavioral sciences in the past—then we will surely not get to harvest a bumper crop of high-grade information. On the other hand, if we take all ten critical needs seriously, and do our best to meet them, we still may not get a good crop. In research, there is no guarantee that a whole field will not turn out to be barren.

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