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Interdisciplinary Theory Guided Research in Educational Administration: A Smoggy View from the Valley

by Laurence Iannaccone - 1973

It is the authorís perception that the concern with theory research has faltered. In the past, he has offered three or four standard answers to that question: 1. The concern for theory based research became a movement and ran out of steam; 2. The nature of the research professorship in educational administration; 3. The nature of the research professor in educational administration; 4. The encounter of the movement with the 1960s.

Laurence Iannaccone is chairman of the Graduate School of Administration, University of California at Riverside. This article is a revised version of the Vice Presidential Address to Division A of the American Educational Research Association, Chicago, April, 1972.

One beginning of the interdisciplinary theory movement in educational administration can be found in the impact of three presentations at a National Council of Professors of Educational Administration (NCPEA) meeting in the early 1950s by Arthur Coladarcci, Jacob W. Getzels, and Andrew W. Halpin.1,2 The ripples produced by these speeches were then transmitted by the Kellogg Centers of that decade and the NCPEA. They influenced the University Council of Educational Administration as well. Other early stimuli include W.W. Charters' work, especially his 1952 R.KR. article on the school as a social system,3 Daniel E. Griffith's influence in focusing on decision making,4 and his assessment of research in educational administration.5 Additional reenforcement came from the impact of the University of Chicago's Midwest Center and the development of the Co-op Research Program of the Office of Education within the context of similar research and theory orientations in education generally. All of which increasingly, until the mid-1960s, produced a pseudo-research, a so-called theory movement.

Small though it may have been, a movement is what it was. The combination of dubious theory and suspect research, with the qualities of this movement calling to mind Eric Hoffer's "true believers," says something about the nature of the professorship in educational administration, an easy elite if there ever was one. I should prefer, however, not to slip into one of the established defense mechanisms of educationists, an undiscriminating, painless self-flagellation, which allows for a sense of universal shortcomings without specific blame to any particular group or individual and results customarily in a revival of slogans of doing different as a substitute for behavioral change. Let me instead first point out some of the significant accomplishments of interdisciplinary theory-based research during the last two decades. In the 1950s, an introduction to a triennial review of the research in educational administration concluded that if all the research in the three previous years on educational administration were to disappear, it would not be noticed.6 That statement would not have been true in 1968.

Charters' position that the concepts not the findings of mid-twentieth century sciences are the important product of theory-based research is valid.7 While we know very little of the process by which the researchers' concepts seep into the language and frame of reference of schoolmen, the fact is, they do. In part, my assessment of the thrust toward theory in educational administration is found in this acquisition of concepts. The simple fact that social system concepts are widely used in the field of educational administration, in evaluating the school district, the school building unit, the classroom as social systems—this fact itself—illustrates one accomplishment. Another may be seen in the existence of a sub-field, the politics of education, which simply did not exist as an area of research a decade and a half ago. The refocusing of educational finance (too slowly by half for some of us) is another product of the last two decades. It displays the interdisciplinary aspect, especially of the research theory thrust. The refocusing, whether viewed as from Paul R. Mort to Jesse Burkhead and Charles Benson, or from educational finance to the economics of education, reflects an interdisciplinary theory guided research product.8

One could point to the use of role concepts derived from Jacob W. Getzels' psychological derivation of Parasonian theory.9 The impact of Andrew W. Halpin's work on leader behavior and the climate studies in education may be cited.10 The work of Donald Willower on control ideology is significant.11 Perhaps more significant in the long run will be his work with students. The change from Mort's adaptability studies, concerned almost exclusively with the effects of fiscal variables, to Richard O. Carlson's concern for adoption of innovations related to social system variables in addition to fiscal ones offers additional evidence of the impact of theory. It also testifies in its essential character to the interdisciplinary nature, as well as footnoting the social system frame of reference of that theory-based research thrust.12

The language even of practicing school administrators increasingly reflects, some might say is contaminated by, concepts which earlier appeared in theory related, if not guided, research. Fruitfully fertilized or contaminated—that value judgment I leave to others—these developments indicate the interdisciplinary theory thrust of a decade ago. A change is underway in the orientation of training programs for practitioners. It is a shift from the study of educational administration folklore and the hortatory issuances of the word by a few elite educational administration departments to a wider focus on administrative and organizational behavior. Again, for some of us the rate of change may appear to be glacial, but it is there. Nor am I afraid to predict that, despite the current direction of federal and foundation funding incentives, we will see a continued development of training programs as well as research centering upon concepts of organizational behavior derived from interdisciplinary theory. For the near term, I would look more to the programs developing in less prestigious universities by younger professors than to the elite schools and established professors.

Nevertheless, it is my perception that the concern with theory research has faltered. And so I ask, why? In the past, I have offered three or four standard answers to that question.

1. The concern for theory based research became a movement and ran out of steam.

2. The nature of the research professorship in educational administration.

3. The nature of the research professor in educational administration.

4. The encounter of the movement with the 1960s.

I still think each of these is worth some brief attention and supplies some of the answers. But they do not account for all. I believe the root cause of the failure is that the initial interdisciplinary, theory-guided research approach in educational administration attempted to bypass its first stage of development.

The fact that the concern for theory became a movement, improbable as that seems, tells us more about the nature of educational administration as a field of research than about the nature of interdisciplinary theory-based research. The field of research in educational administration has qualities I think of as inverted Protean and late Athenian. Inverted Protean because just as it begins to grasp something it changes its form. Late Athenian because, like the men St. Paul saw gathered around the unknown God, seeking "some new thing," it is all too superstitious, anxious to choose some new doctrine, with new demi-gods every two years. One manifestation of this quality, I would hypothesize, may be found in testing the proposition that each year of research hi educational administration is better predicted by a content analysis of the Saturday Review or some other widely distributed periodical than any set of academic journals. Ironically, this irreverance for scholarship has led educational administration research into being truly irrelevant. Many of its research proposals are what could be called late contemporary. Its findings produce that slight sense of embarrassment we feel wearing last season's fashions. When the significance of proposed research is defined as its timeliness for contemporary crises in public policies rather than as the concepts and explanations it offers, then not only must its findings be published concurrent with, if not before, crises, but public policy makers must at best be guided by mere findings rather than by understanding. Under these conditions, theory guided research and research based theory can contribute to understanding episodic crises. However, it cannot grow beyond them if it remains enslaved by them.


I have elsewhere applied the concept of a conjunctive domain between practice and scholarship to the educational researcher's world of work.13 The educational administration professorship is located in even more of a conjunctive domain which militates even more against quality research or the development of theory. That world reflects the frustrating difficulties of combining a series of disciplines around one public service with the requirements of focusing upon the institution, its policy makers, and administrators. The researcher hi educational administration is confronted with the demands of the school of education, dominated in its research orientation by a single discipline, psychology, and its preferred, sometimes required, research mode. If he is to do theoretically guided research with a view toward contributions to theory, he needs a solid if not expert grounding in a discipline. The educational administration research professor's task would in any case be difficult. Even more serious, his role is inappropriate to his task. Over a decade ago, in a speech at the NCPEA meetings in Macomb, Illinois, I indicated what I most feared would wreck the chances for the development of significant achievements from the theory-guided research thrust. My fears have been realized. I said then:

. . . I should like to share with you one of my greatest concerns in connection with the use of theory in teaching administration. I fear, that perhaps because of a misunderstanding of what theory is, or because of the inertia of tradition and vested interests, we will add a theory course to programs and wear a theory instructor at our institutions like a prestige symbol, perhaps as evidence that we are up to date, and otherwise go along as we have. This will not work! Theory, by its very nature, because it demands the economical and useful description and explanation of the nature and process of administration, cannot be left out of any course which seeks to increase the students' understanding of Administration. Put another way, theory divorced from its application in administrative practice or the study of administrative practice without theory is indeed not practical—But it is the divorce which is impractical, not theory!"14

The research professorship role is not needed for the main functions of their departments in schools of education today. Those functions may be variously denned as certifying numbers of students as school administrators, providing field services to school administrators and policy makers (as often as possible for outside money), facilitating the career mobility of school administrators, protecting them from the university community, and repairing relations with school boards and administrators after forays into the schools by educational psychologists, and more recently educational sociologists and other "real" educational researchers. Whatever the means for performing such functions, interdisciplinary theory-guided research is only indirectly, if at all, related to them. Hence, I conclude, while the "research professor" may be a highly functional creature to have in the department of educational administration for functions other than research, the research professorship is at bottom a non-role.

The movement and its chameleonic character provide another clue to the nature of the research professor in educational administration. When I use this term I do not refer to men such as I cited earlier. They are among the few to whom I doff my cap in this business of understanding educational administration.

Alas, some two or three

poor heretics in love there be,

Which think to 'stablish dangerous constancy.

But in general, the ephemeral corpus of researchers in educational administration supports the mercurial nature of the field. It is well to remember most research professors in educational administration started out to be practitioners and were seduced into the professorship during their graduate school training in the sixties. Research in educational administration is still largely a matter of doctoral theses by people on the way to something else. And often the few bits done by a young research professor in educational administration after his dissertation provide the base for getting his bag, private consulting facilitated by one or more of these, a light load, a small research center, field consultant operations, tenure, or a department headship. Having arrived, his research ends. Implicit in this career line is the nature of research professor groups for whom the research venture is a ticket not to a better research professorship in a better institution but to a different role. That role is most often an administrative role. The central quality of such a group is administrative other directedness.


Here then we have a movement of people occupying organizational roles irrelevant or even antithetical to their proclaimed cause. Too often they are poorly trained for research. They are, however, eminently endowed with other directedness and a nose for that bitch goddess, success. And they encountered that sensational decade, the sixties. The latter half of it, in particular, nearly destroyed any theory directed research, let alone that more demanding research which develops theory.

A mercurial movement hit its high gear at about the point in time when private and public funding agencies began a series of kaleidoscopic shifts in programs rationalized by descriptions of the desperate demands of education, crisis conditions of classrooms, failures of educational research, and a variety of other reasons but, never, never admitting the possibility that their own poor decisions of each year, reflecting a commitment to educational crisis management, might have something to do with the problems of quality and meaningfulness of educational research. Ford and federal funding freed the educational administration professor from the need to even fake a research interest. Instead, educational administration researchers chased merrily down the trail blazed by granting agencies.

Sometimes American genius captures and expresses itself best in its musicals. We opened the decade with Camelot and moved from it to the "Impossible Dream." This was followed by the false dawning of the Age of Aquarius. The decade closed with that wistful, mocking, haunting, hope-doubt of Jesus Christ, Superstar.

As I look back, I find Houseman's Shropshire Lad's comments appropriate.

there's brisker pipes than poetry.


Ale, man, ale's the stuff to drink

For fellows whom it hurts to think;

Look into the pewter pot

To see the world as the world's not.

Money makes the mare go round. Changing funding patterns determine research and other work activities for all of us some of the time and for some of us all of the time. In educational administration the latter is the larger number. External funding for university research is not an unmixed blessing for any of the parties to the transaction. As noted earlier, the frequent complaint of funding agencies heard in the sixties that the research they bought did not make a difference reflected their own poor purchases. No other field better illustrates the fact that when you buy researchers you get researchers who can be bought.15 The sensational, seductive, and shifting sixties saw more such sales and purchases than educational administrative history had ever seen before. The wonder is that anything was produced. I can cite instance after instance where getting a grant paid much better than worrying about completing a project did. It is not accidental that much of what was cited earlier as achievements of the interdisciplinary theory research thrust did not result from foundation or even less federal funding. Often small projects paid off better than large ones. There was, in some other areas, a negative relationship between the magnitude of funding and the significance of the work produced. Is it any wonder then that as granting agencies moved toward educational crisis management, research professors in educational administration replaced the search for concepts with social concerns and focused on producing solutions instead of understanding problems?

The theory movement had, by the late 1950s and early 1960s, euphorically begun with a search for the holy grail, a single molar theory of educational administration. It was, of course, more talk than search. But more dangerous for the future, the stallion ridden on this search was an adoption of the traditional educational psychological adaptation of the critical experiment mode. How naive and unrealistic can a field get? Not only did the interdisciplinary theory research movement encounter the sensational sixties—it was a reflection of them, too. Above all, the interdisciplinary theory research thrust in educational administration suffered from its own euphoric unrealistic view of its task and its inappropriate definition of its science.

As I look back at where we have been I must say with Houseman:

Oh I have been to Ludlow fair

And left my necktie God knows where.

And carried half way home, or near,

Pints and quarts of Ludlow beer;

Then the world seemed none so bad,

And I myself a sterling lad:

And down in lovely muck I've kin

Happy till I woke again.


The world, it was the old world yet,

I was I, my things were wet.

The task ahead requires a more modest, even plebeian, definition of science than we have claimed to use. Humility is needed to accomplish it. We must walk before we try to run. Above all, we must so define our work that it will allow our research subject (and subjects) to teach us something. The task ahead requires that we break from the traditional research methods which have dominated the research ideology of schools of education and stop pretending that every dissertation is a critical experiment. It is a time for observing the phenomena of educational administration and for letting these influence our definition of our work.

I know we have opened the door a little during the last decade to so-called field studies. More harm than good may so be done. Most of these studies have been consultant reports to school people. For thesis purposes some have had a theory chapter slapped on to them. Such field reports are clearly atheoretical. We have not provided systematic quality training in field methodology. We have not allowed students to substitute in-depth anthropological or sociological field study techniques and methods for the shibboleths of educational research methods. We have research method requirements for them which appear to function very similarly to the language requirement for the Ph.D. Is it any wonder that most of the field studies that result are poor research and that most of our research is considered irrelevant by people who work in the field?

In earlier years, a number of us almost said what needed to be done or said it badly and were not heard. Griffiths and I came close in 1958 when we said "We are at the same stage as were the scientists who studied heat with the concept of caloric as the basis for theorizing. Not until caloric was abandoned and the concept of molecular motion was equated to heat was a science of thermodynamics possible."16 But we too straddled the fence between verificational studies requiring the critical experimental mode and a firm confrontation of the need to describe and conceptually organize such description before moving to verification. Donald Willower, in a U.C.E.A. publication on research some years ago, said it better.17 To his credit, he and his students have quietly gone about the business he saw as needed.

Despite our achievements to date, the black box of research in educational administration is the school and its work, including that of the administrators. We have tested more hypotheses than we have derived from theory. We have related inputs to outputs. We know more about pupil, teacher, and administrator characteristics and about achievement, responses and community reactions than we know about what people do—how they move and live in schools. Given the present state of the art, we know more about the former classes of variables than we can fruitfully use. Until we understand the school as a world of work and why it is what it is, the development of relevant theory in educational administration will continue to falter.

The emphasis on the rigor of theory testing that has too often, as Zetterberg said, "rendered trivial conclusions with efforts toward maximum precision. . . ,"18 has left much to be desired in the way of theory and of theory development. The emphasis on verification and on methodologies appropriate to verification concerned primarily with "how accurate facts can be obtained and how theory can thereby be more rigorously tested" has not been as fruitful as had been hoped in contributing to the development of science and knowledge.19 Nevertheless, the purpose of theory is to provide understanding, knowledge, and science. What has tended to happen has been the redefinition of the term science to signify research of the verificational variety. Thus Kerlinger would define science as the "empirical, systematic, controlled, and critical investigation of theory and its resultant hypothetical propositions."20


The problem that is raised in this current definitional approach has to do with the limits posed on "scientific research." This restrains it from extending beyond the parameters of the quantitative statistical and verificational ideology, thus restricting and falsifying the nature of the scientific enterprise. It tends to exclude qualitative approaches on the basis that they are not amendable to mathematically derived models of analysis. It tends to forego the possibility of developing theory which is based on data and attained through more systematic procedures than serendipity. This is not to say that qualitative methodologies necessarily lead to theoretical formulations. But qualitative methodological approaches have the advantage of not forcing the researcher to a pre-judgment of reality, as in the case of verificational (hypothetico-deductive) approaches. This feature allows for the possibility of reformulating the problem as the research proceeds. It permits one to recast the explanatory scheme by incorporating or rejecting variables or by redefining relationships among variables as those utilized become unsatisfactory.

Field study methodology has also been variously referred to as participant observation, 21,22 the community study method,23,24 case study methodology, qualitative research, and comparative analysis.25 It places a distinct emphasis on what constitutes the scientific method in the social sciences. Reference is made to the epistemological basis of what constitutes proof. Field study methodology is a set of methodological procedures distinct from the statistical-verificational or critical experimental approach. Predictably, educationist discussions of participant observation and the sociological field study have focused upon methodological procedures almost exclusively, which is what one would expect from mere research technicians. The field is evaluated mainly on the basis of criteria derived from canons which do not take into consideration the particular nature of the subject matter of sociological inquiry. The problem of how best to approach the study of man has been referred to as the "most important problem confronting social and psychological sciences. . . ,"26 Most of the literature on field methodology, or participant observation, fails to come to grips with this problem and adopts the approach taken by McCall and Simmons of discussing the methodology of participant observation "at a less heady level, largely eschewing issues of epistemology and focussing rather on concrete issues of method and technique."27 There results, on the part of social scientists generally, a lack of awareness of the properties and the advantages inherent in the approach. Despite recent indications of interest in the approach, McCall and Simmons saw no widespread enthusiasm for it among social scientists:

... it remains true today that sociologists do not in general maintain that there is any special methodological advantage to studying the complicated inner dynamics of a particular case in all details or to seeking out the perspectives or interpretations actually held by subjects themselves.28

Instead, that is precisely what must be done in educational administration if we are to develop the concepts and explanations necessary to produce theory which will be practical, that is, not divorced from its application to administrative practice.

In his "Forward" to Bruyn's Human Perspective in Sociology, Herbert Blumer points out that there exist various and divergent conceptions of what constitutes the scientific method in the social sciences. He puts the reader on guard for what Glaser and Strauss have referred to as the "doctrinaire approach to verification":29

This picture of extensive differences (in conception of what constitutes the method of science) is obscured by the tendency at one or another period of time for a particular conception to acquire prestige and relative dominance— as in the case of the current identification of scientific procedure with "research design" cast in the form of a relationship between independent and dependent variables under conditions of a control group. One should not be deceived by such a seeming approximation to concensus at any given time.30

This prevailing conception exists because social scientists, by and large, believe that the progressive development of the physical and biological sciences since the sixteenth century has forged the basic components of the scientific method "under the test of exacting experience" and thereby has firmly established the "essential character and principles of scientific procedure." The social sciences are seen as beneficiaries to this legacy and are not required to work out the nature of the scientific method through their own effort and in their own field. Similarly, we in educational administration in much less sophisticated ways have attempted to bypass the requirement of working out the nature of scientific method in our own field and through our own efforts. We have naively accepted the constraints of the educational psychologist's adaptation of the critical experiment. We have produced studies which are methodologically bad, theoretically useless, and which are focused on trivial problems.

The basic orientation of participant observation, or field study approach, on the other hand, can be said to follow the proposition that the principal requirement of an empirical science is that the nature of its subject matters must be respected. Schutz makes this point very clearly:

The observational field of the social scientist, however, namely the social reality, has a specific meaning and relevance structure for the human beings living, acting, and thinking therein. By a series of common sense constructs they have preselected and preinterpreted this world which they experience as the reality of their daily lives. It is these thought objects of theirs which determine their behavior by motivating it. The thought objects constructed by the social scientist, in order to grasp this social reality, have to be founded upon the thought objects constructed by the commonsense thinking of men, living their daily life within their social world.31

It is the social world of the school organization which is the observational field of the researcher in educational administration. It is the specific meaning and relevance of structure of the school for the human beings living, acting, and thinking therein which we must grasp. The concepts constructed by us to grasp this social reality have to be grounded upon the.common sense thinking of men and women living their daily lives within the school.

Now we stand in the early years of the sobering seventies. There are some small signs in the wind of a return of interest in theory and research in educational administration. Before the new song becomes, "Those Were The Good Old Days" as sung by Archie Bunker and his wife, I want to enter a demur. Until the needed conceptual development takes place, no new significant theory thrust will be seen in educational administration. The renewed research interest in foundations and in Washington led by the same individuals and clubs will be sterile. Attempts to bypass that tough and not very glamourous job will continue to produce irrelevant practitioner programs in the universities. Efforts by foundations and the federal government to innovate in education rather than first understand schools in order to change them will continue, I like the Italian expression here, to make a hole in water.

1 I am especially indebted to two people for some of the thoughts expressed here: Andrew W. Halpin for his unpublished, "A Foggy View from Olympus," presented to The Southern Regional Council on Educational Administration in 1967, and Jean B. Hache for discussions about field study methodology.

2 Daniel E. Griffiths. Administrative Theory. New York: Appleton-Century-Crofts, 1959, p. 3.

3 W.W. Charters, Jr., “School as a Social System,” Review of Educational Research, Vol. 22, No. 3 October 1952, pp. 41-50.

4 Daniel E. Griffiths. Human Relations in School Administration. New York: Appleton-Century-Crofts, 1956.

5 Daniel E. Griffiths. Research in Educational Administration. New York: Teachers College Bureau of Publications, 1959.

6 Tom Arthur Lamke, "Introduction," Review of Educational Research, Vol. 25, No. 3, June 1955, p. 192.

7 W.W. Charters, Jr., "The Role of the Social Scientist," in Roald F. Campbell and James M. Lipham, eds. Administrative Theory as a Guide to Action. Chicago: Midwest Administration Center, University of Chicago, 1960, pp. 173-180.

8 Paul R. Mort, Walter C. Reusser, and John W. Polley. Public School Finance: It's Background, Structure, and Operation. New York: McGraw-Hill, 1960; and Jesse Burkhead, Bertram M. Gross, and Charles S. Benson. Public School Finance: Economics and Politics. Syracuse, N.Y.: Syracuse University Press, 1964.

9 Jacob W. Getzels, James M. Lipham, and Roald F. Campbell. Educational Administration as a Social Process: Theory, Research, and Practice. New York: Harper & Row, 1968.

10 Andrew W. Halpin. Theory and Research in Administration. New York: MacMillan, 1966.

11 Donald J. Willower. The School and Pupil Control Ideology. University Park, Pa.: Pennsylvania State University, 1967.

12 Richard O. Carlson. Adoption of Educational Innovations. Eugene, Oregon: CASEA, University of Oregon, 1967.

13 Richard A. Dershimer and Laurence lannaccone, "Social and Political Influences on Education Research," in Robert M.W. Travers, eds. Second Handbook of Research on Teaching. Chicago: Rand McNally, 1973, pp. 113-121.

14 Laurence lannaccone, "The Place of Theory in a Preparation Program," unpublished paper presented to the National Conference of Professors of Education at Macomb, Illinois, 1960.

15 Henry Housdorf, "Academic Rites," unpublished manuscript.

16 Daniel E. Griffiths and Laurence lannaccone, "Administrative Theory, Relationships, and Preparation," Review of Educational Research, Vol. 28, No. 4, October 1958, pp. 334-354.

17 Donald J. Willower, "Concept Development and Research," in Jack A. Culbertson and Stephen P. Henchley, eds. Educational Research: New Perspectives. Danville, Ill.: Interstate Printers and Publishers, 1963, pp. 101-111.

18 Hans Lennart Zetterberg. On Theory and Verification in Sociology. Ottowa, N. J.: Bedminster Press, 1965, p. 7.

19 Barrier G. Glaser and Anselm L. Strauss. The Discovery of Grounded Theory: Strategies for Qualitative Research. Chicago: Aldine, 1967.

20 Frederick N. Kerlinger. Foundations of Behavioral Research: Educational and Psychological Inquiry. New York: Holt, Rinehart and Winston, 1964, Ch. 1.

21 Severyn Bruyn. The Human Perspective in Sociology: The Methodology of Participant Observation. Englewood Cliffs, N.J.: Prentice-Hall, 1966.

22 George J. McCall and J.L. Simmons, eds. Issues in Participant Observation^ Text and Reader. Reading, Mass.: Addison-Wesley, 1969.

23 Conrad M. Arensberg, "The Community Study Method," American Journal of Sociology, Vol. 60, No. 2, September 1954, pp. 109-124.

24 Arthur K. Vidich and Joseph Bensman. Small Town in Mass Society. Princeton, N.J.: Princeton University Press, 1958.

25 Glaser and Strauss, op. cit.

26 Herbert Blumer, "Forword," in Bruyn, op. cit., p. iii.

27 McCall and Simmons, op. cit., p. 2.

28 Ibid.

29 Glaser and Strauss, op. cit., p. 7.

30 Blumer, op. cit., p. v.

31 Alfred Schutz, "Concept of Influence and Proof in Participant Observation," American Sociological Review, Vol. 23, December 1958, pp. 652-653.

Cite This Article as: Teachers College Record Volume 75 Number 1, 1973, p. 55-66
https://www.tcrecord.org ID Number: 1471, Date Accessed: 5/25/2022 6:15:09 PM

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About the Author
  • Laurence Iannaccone
    University of California at Riverside
    Laurence lannaccone is chairman of the Graduate School of Administration, University of California at Riverside. This article is a revised version of the Vice Presidential Address to Division A of the American Educational Research Association, Chicago, April, 1972.
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