Fellow's Award Speech One Mega and Seven Basic Principles For Consumer Research

Gerald Zaltman,
[ to cite ]:
Gerald Zaltman (1991) ,"Fellow's Award Speech One Mega and Seven Basic Principles For Consumer Research", in NA - Advances in Consumer Research Volume 18, eds. Rebecca H. Holman and Michael R. Solomon, Provo, UT : Association for Consumer Research, Pages: 8.

Advances in Consumer Research Volume 18, 1991      Page 8

FELLOW'S AWARD SPEECH

ONE MEGA AND SEVEN BASIC PRINCIPLES FOR CONSUMER RESEARCH

Gerald Zaltman

INTRODUCTION

The honor of receiving this award is exceeded only by the honor of having had the opportunity to work with so many fine people in our field and of having so many others pay attention to my ideas. If the development of ideas is a researcher's primary objective, the conferral of professional recognition is the coin of the realm. This award and the honor of interacting with so many of you have made me feel very enriched today.

Just as many people have learned from me, so have I learned from others in our own and related fields. For example, during the past two years I've become interested in the use of photography as a social science research tool. As others have already demonstrated,- photography has enormous potential for the study of behavior, a potential that will increase even more as digital imaging technologies applied to photography become more available to experimentalists. While photography is not the subject of my remarks today, it provides the orientation for ideas I'd like to share, particularly with newer members of the profession.

TWO LESSONS FROM GREAT PHOTOGRAPHERS

My interest in photography has brought me into contact with some important photographers who have in common two special accomplishments. First, they have mastered the same principles about their craft. Whatever these might be, they are not easily mastered. Many good photographers don't master them at all. Secondly, these photographers share a knack for bending these principles in highly individual but systematic ways.

It is important to point out that photographers who have not mastered these rules also break them but in ways which are less rich, less exciting, and which result in a much less engaging personality in their work. The same can be said of photographers who have mastered them but have not dared to break them or have not learned how.

What I have said about master photographers can probably be said of master painters, thiefs, musicians, CEOs, engineers, carpenters, chefs, and so on. I know it can be said of master consumer researchers. I have collaborated wit,h some of them and participated with many more in numerous panels, task forces, and committees. Like the master photographers, there is a common set of principles which they seem to have learned and then distinctively altered in practice.

A MEGA PRINCIPLE

This brings me to what I would like to share with you today. I would like to say a few words about basic principles for approaching consumer research (and which apply to other endeavors as well).

There is an important mega principle: once mastered, basic principles need to be creatively bent to reflect individuality. Bending principles in creative and productive ways is a highly personal process which cannot be prescribed. For that matter, I have qualms about prescribing basic principles. They are more evident to me in hindsight than they ever were with foresight. I don't know that I ever really thought about them until the past few years when I began teaching a doctoral seminar on theory construction.

For what they are worth, the following principles are among the more important ones 1 have learned from my mentors and have-subsequently bent through trial and error. My adaptation of these principles seem to we guided most of what I consider to be my best work. As just mentioned, they also seem to have been internalized and then altered in distinctive, personal ways by the consumer researchers whose work I regard most highly, however substantively and methodologically different their work is from mine.

SEVEN BASIC PRINCIPLES

Before introducing these principles I'd like to anticipate two responses and ask you to think about questions they raise. One likely response is: "They are pretty obvious". In fact, they are obvious. This prompts the question,- "Why are they so frequently absent from research in our own and other disciplines?"

The second response is: "It is all well and good for a tenured full professor to espouse principles which may be dangerous for someone needing many publications in a short time for promotion and tenure". This raises the question "Why is it that leaders in our field have managed to master and adapt these principles early in their careers^' If they have, others can.

1. Think big and do it now, not later. By thinking big I mean tackle problems or issues where new insights have the potential of changing (a) at least some thinking on the part of many people, or (b) a great deal of thinking on the part of some people. That is, you should ask yourself a two part question, "How much thinking on the part of how many people could change if this research effort yields a new and sound insight?" If you cannot answer, "Lots!" to either part of this question, you need to seriously question whether your research is worth pursuing. There is nothing wrong with being a good carpenter. In fact, that is rather important. But it is still more important to be an architect, too.

Moreover, if you do not engage early in your career in research which has the potential for major impact you are unlikely to do so later. The "Mental Trap of the Small Problem" is very difficult to escape once you have been ensnared. This observation goes against popular wisdom about the impact of tenure on the selection of a research program.

A corollary to this principle is that the ideas being tested should have a reasonable chance of failing. If they are quite likely to be supported, why are you wasting your time with a rather obvious idea?

2. Think fun. Thinking big can be risky. An impactful result may elude you. As a consolation you should at least be able to say doing the work was fun. I mean "fun" the way it is fun to read an engaging novel, participate in sports, or see an involving play. At the end you are disappointed it is over. Here, too, your motivations for doing the research should be questioned if, more evenings than not, you are not eager to get up the next morning to resume work.

Then, too, there is the issue of control. About the only thing we can control is whether most of our research is intrinsically fun. We certainly can't control research outcomes if (a) we are working on complex and messy problems, which is what important problems tend to be, and (b) we are using equal opportunity methodologies, that is, methodologies which allow equally for disconfirming evidence to show up if it is really out there. In fact, major intellectual advances often originate in disconfirming evidence. In fact, it is often the outlier in our results that are the most important phenomena.

Additionally, we really cannot control how our colleagues will respond to our work, particularly when they assume the role of journal referee. So why not at least enjoy what we are doing? It also makes for higher quality work.

3. Have the courage of your convictions when they are felt strongly. While my convictions are wrong often enough, I am wrong still more often when I act on someone else's conviction when it differs from mine. You will receive a lot of advice about what is important to research and how you should go about it. You will be especially tempted by reviewer advice and advice from senior colleagues. This advice is all the more difficult to disregard when it conflicts with your own counsel because it is well intended, comes from a respected source, and usually makes sense. But that doesn't mean it is superior to your particular stance. The more important the issue and the greater the discrepancy between your strongly felt position and someone else's, the more important it is to have the courage of your own conviction.

There is an important qualifying condition for this principle which I will discuss as a fourth principle.

4. Use criticism as a creative tool. Having the courage of your convictions is not the same as being stubborn. The difference lies in how one responds to criticism. When advice is received which contradicts your own position you can accept it immediately, ignore it immediately, or you can use it as a viewing lens for reexamining your own position. So long as criticism and conflicting advice are treated as an occasion to reexamine your position you won't get into too much trouble displaying the courage of your own conviction. To maintain a position without a willingness to step outside of it and question it is stubbornness and, like the too ready abandonment of a conviction, no good is likely to come of it

This brings me to a related fifth principle. But before addressing it, there is a corollary concerning criticism. Honest criticism is most readily used as a creative tool when offered with respect and care. We are dealing, after all, with someone else's valued personal property.

5. Challenge established assumptions. Considerable intellectual progress is a result of challenging assumptions. A look at the intellectual history of various professions and academic disciplines shows that much of what was certified knowledge in a given period was later found to be incorrect or at least substantially more inadequate than believed at the time. The current time period in consumer research is unlikely to be an exception to this observation. So, in addition to trying to conquer ignorance at the frontiers of what we know, do not be reluctant to conquer it within the context of what we think we know.

Above all else, challenge your own assumptions. This requires an ability to stop being a part of an idea and to be able to discard ownership in order to examine it critically. Of course, a sense of ownership and commitment to an idea are very important to its development. Overall though, a greater commitment to the process of having a good idea than to the idea itself is required. It is easier to detect error and to use criticism as a creative tool when you are more committed to the process of being right than to Proving a Particular idea.

6. Have confidence and dedication. Being creative, especially when developing an alternative to an established position, involves many traits. One trait is having confidence that there is a better idea and the dedication to keep working with the raw materials of that idea until an attractive form emerges. Solutions are not so much found like pebbles on a beach or potatoes in a field as they are created. Much of our educational process teaches how to find the single correct answer rather than the more robust process of creating them. I am baffled by the fact that so many exercises intended to improve creativity have predetermined correct answers. The process of creating correct answers as opposed to finding them appears to be scary for educators to address.

Creating ideas is a lot like modeling with clay; one keeps working and reworking it until the right shape emerges. Somewhere within that lump is the creative possibility of a perfect whatever; the task is to get as close to it as possible by strategically and continually taking some clay away and putting some back. Sometimes you do not know exactly what an idea should look like but only that what you have developed so far is not right.

7. Develop wide cognitive peripheral vision. It is very helpful to have exposure to a broad array of ideas via exposure to many people, diverse published works, and activities that are unrelated to any specific professional matter. For example, with respect to people, I have had and continue to have the uncommonly good fortune of working with many bright but otherwise varied mentors, colleagues, and students. And it is no surprise to me that I have learned more from my students than any other group, since they are the most diverse set of professionals one encounters

CONCLUSION

At the outset of my comments I mentioned working with and learning from others. The principles I have shared today were presented as skills important to individual development. However, the principles are also relevant to team research and more importantly, perhaps, to establishing exciting environments for inquiry, be it at the departmental level or university and corporate levels. So, I would like to leave you with a challenge and a caveat.

The challenge is to develop and debate principles for yourself, for your own organizations, and for our profession. Do not, of course, forget to bend or alter them in your own style. But above all else, have the courage to correct or to at least ignore the many conditions that make important principles difficult to maintain and easy to forego. Perhaps that is a second mega principle.

The caveat is a kind of "Catch 22": if pursuit of these principles is motivated largely by matters of professional expediency, such as getting promotion and tenure, they are likely to backfire. Your primary motivation has to be rooted more in the intrinsic enjoyment of the Grand Waltz with these principles than in what occurs at the end of the dance.

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