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Be creative and playful with ideas: An interview with Danny Miller

Research Professor, HEC Montreal and Chair in Family Business and Strategy, University of Alberta

It so happens that Danny’s office at HEC is two doors down from mine. Imagine that! “the” Danny Miller is now my colleague and hallway buddy.  I mean, Danny is up there in the academic management pantheon alongside Henry Mintzberg, Bill Starbuck, Karl Weick, Dick Scott, Kathy Eisenhardt, and so on. These are the guys (and gals!) whose stuff you read as “classics” in graduate seminars, whose talks you go out of your way to attend at conferences. And what a super nice guy he is! He more than graciously acquiesced to being interviewed for this blog, although he initially seemed unconvinced that he would have anything interesting or terribly insightful to say. It turns out that he was quite wrong on that – we talked for two hours, and easily could have gone on.  And what a fascinating conversation it was!  My only reserve is that he makes writing and publishing sound so easy… if only it were so for the rest of us!  I hope you enjoy it.

So why don’t we start with an easy question. Where do you get your ideas?

I have no idea.  I can tell you that I don’t get them from journals.  I don’t get them from reading in our field, at least, not any longer.  And I don’t get them from any clearly identifiable outside source.  Sometimes I get new ideas on the basis of what I’ve already done.  I’ll think, “You could look at it this way or you could put these two things together and it will have a more powerful message or a more revealing insight.”  Because of my dyslexia, I read far less management literature than many of my colleagues.  So I don’t find that I benefit greatly from the academic journals.  When I was a PhD student and early in my career I did find the journals useful, because it was important to learn what was out there and to read the classics.  I still read the classics.  But given how hard it is for me to read, reading is a resource I allocate very carefully – but not narrowly.  Now I’m reading about Eleanor and Franklin Roosevelt’s activities during the Second World War.  I’m reading about Cornelius Vanderbilt and Kissinger’s foreign policy influence. And it’s not that I’m especially interested in US politics or US history.  These just seemed to be interesting books.  Last year I was reading things on neurobiology and how the mind works.  That too was just out of curiosity.

Let’s backtrack just a little.  Of the many, many articles that you’ve written, do you have any favourites?

I have favourites but they’re different from the ones that get cited a lot by the field. One of my favourites is The Simplicity of Competitive Repertoires.  It’s a study with Ming-Jer Chen on the competitive strategies of US airline firms — the national carriers — and it’s the clearest case that I’ve ever seen of superstitious learning.  I think it’s very revealing. Ming-Jer gathered this incredible database of every external competitive move of every airline over eight years, post deregulation. These were price increases, price decreases, changes in route structure, changes in advertising.  You name it — 32 types of moves on a daily basis. So we thought “Why don’t we look at what happens to the repertoires of companies post-deregulation as a function of their environment and past success?”

So where did that idea come from? 

Well, I had written an essay entitled The Architecture of Simplicity.  And I had written a book, The Icarus Paradox.  These were in fact about superstitious learning and the pernicious effects of success — about how good performance can trick firms into thinking they know why they’ve excelled.  Although success can guide useful learning along dimensions that firms obsessively monitor, it also induces them to focus too narrowly and ignore other critical variables that they track less carefully.  And so we thought, “Let’s look at an entire industry and see if the more successful companies show more rapidly shrinking competitive repertoires”. As a function of their success, are they using fewer kinds of competitive moves?  Does one type of move come to dominate?  Is there greater variance in the frequency of their types of moves?  In other words, one can track various measures of evolving simplicity and see if these were a function of prior success.  They were.  We also found that success increases and then decreases as a function of the size of the repertoire – showing useful learning eventually being overtaken by the superstitious variety.

Because their repertoire is getting more and more narrow.

And it gets them into trouble. So that paper is one of my absolute favourites.


Because empirically, it’s incredibly solid. Because the data on objective competitive moves are so concrete. There are no perceptual filters from managers to rationalize or distort the findings.  Also the study is about all the national carriers in an entire industry over an eight year period and it shows a phenomenon that I think is really important. I’m sorry to say that the paper has been only modestly cited!

Where did the ideas for the Icarus Paradox and The Architecture of Simplicity come from?

The idea for The Icarus Paradox came all at once – but after many years of related work.  My early work on organizational configurations revealed some very common successful and unsuccessful types. What was important about these configurations was that they could be richly characterized and were few in number.  So if you gave me four or five features, I could classify firms within a type and then predict many of their other features.  That’s useful.  It was also possible to collect a different sample of companies and find the very same configurations.  So the configurations were very predictive.  [In fact, configurations showed a type of ordering in data that one cannot find using linear multivariate methods.  The mathematical analogue for the data pattern is a snake-like surface in a multi-dimensional vector space.  I had the good fortune to work with Peter Friesen, a mathematical economist, who was instrumental in making the work rigorous and establishing the robustness of the configurations algebraically]. When in subsequent work we tracked how firms within particular configurations change over time we found that they tended to exhibit long periods of momentum.  So bureaucracies tended to become more bureaucratic, having, say more rules and procedures, more policies and levels of hierarchy, more focus on stable markets — that kind of thing.  Change was constant.

Yeah, but in a certain direction.

Right. And it was the same with innovative firms.  They were changing all the time — but becoming more innovative, often going too far in that direction and squandering resources on useless novelties.  They had to reverse course. And those changes can be very costly. They’re resisted for economic, cognitive, political and social reasons.  And we found that the only time these companies could reverse momentum and move to a new or more balanced configuration was to have a change in leadership and experience very poor performance over a long period.  In part because it’s so costly, risky and difficult to reverse direction, many firms stay within configuration until their extremes, their focus, their dysfunction, is so great that they can’t do anything but change.  And that was the basis for Icarus – successful firms continue along the same ever narrowing path until they reach excesses that cause their downfall.   Alone and with Peter we wrote several conceptual and empirical papers on organizational change.   Then we did one on innovation inspired in part by Rogers and Shoemaker’s book on the diffusion of innovation.  Their book reviewed the debates on the drivers of innovation and found that information processing was a key driver.  The problem was that you had 40-odd studies saying it boosted innovation, and many other studies saying the opposite. And we thought, well maybe if you’re an innovative company and you’re innovating too much, information will slow you down.  And if you’re some bureaucracy and you’re innovating too little, information will induce you to do more.  So we did this study, another that I liked, confirming that.

Which paper is that?

Innovation in Conservative and Entrepreneurial Firms.  A sister-paper was called The Correlates of Entrepreneurship in Three Types of Firms.  And the reason people found that significant is because I came up with a definition of entrepreneurship and a way of measuring it that no one had thought of before. This is the basis of the popular concept “entrepreneurial orientation”.  What I found is that what drove entrepreneurship in simple companies was the personality of the founder.  What drove it in planning bureaucracies was strategy making processes. What drove it in innovative adhocracies was structure and environment.  So we had very different drivers and different configurations.  Much of that material on configurations, change and prediction came together to provide the fodder for The Icarus Paradox. Well actually, the first book on these topics was Organizations: A Quantum View, which put together for an academic audience all of the findings we’ve been talking about. And then the Icarus book came about because it hit me all at once that we could tell a beautiful story, encapsulating for managers the message of our previous decade of research using examples from companies that everybody knows.  I remember that moment.  I was sitting at LaGuardia Airport and I started smiling.  I thought, “I think I have half the book. I mean, it was just so real and I thought, “It will write itself.”  I wrote it in four weeks.


Well, I wrote most of it in four weeks and then I was dickering around a little bit because I needed to put in some boilerplate stuff.  But I had the examples.  I knew which cases I wanted, and I could see the trajectories. The book is built around four trajectories leading to excess, each of them showing superstitious learning and the perils of excellence but in very different types of firms – different configurations.

It sounds like you do a lot of relational thinking. One thing leads to another that leads to another and you see patterns…

That’s true. There’s a lot of continuity even though I sometimes don’t recognize it quickly.

Ok, so let’s say you’ve made this decision that you’re going to write a book. Let’s say it’s the Icarus book.  Now what? 

Well in that particular case I got a bunch of cases together because that is what we needed. And I went through them. Most of them were from Fortune and Harvard Business School stuff.  And then I had sort of an outline. I mean, it was obvious to me that the outline would have to deal with a certain type of evolution in different dimensions of organizations.

This was all in your head?


Do you ever write your outlines down?

Rarely. Now, because my short term memory is not very good, while I’m writing I’ll sometimes write down a couple of words to remind me that I need to address a point.

So I’ll do that.  But I don’t really use outlines because I know what the basic structure has to be and I know what the categories will be. It’s not like I have 500 categories.  There are going to be six or seven and then I need to fill them in.  And I need to fill them in with a particular type of information, a particular line of argument.

Would this be the same if you were writing an article for a journal?

Yes.  But our The Neurotic Organization book was different because we were doing it chapter by chapter.  Each chapter had a different structure and it was about a different topic.   That was not the case with the Icarus book which had an integrated message shown in different manifestations.  So each chapter followed pretty much the same outline, but involving different characters and trajectories. The same types of things drove the trajectories, but different stories with different outcomes and different types of organizational situations.  So that was easy.  Once you had one chapter structured, you pretty much had them all. You just kept repeating the same pattern a few times.  Add an introduction and a conclusion, and that’s it.

Did you start from the beginning and then went through it systematically, chapter by chapter?

No, I never start with the introductory chapter, which needs to be strong and integrative and often is hardest to write.  I started with chapter 2, the first trajectory.  And then I did all the trajectories.  And then a theory chapter because, you know, people like theory stuff, just general principles that we could take from this study, and then some remedial-prescriptive aspects because the book was intended for practitioners. And that was it.  It wasn’t really hard to do.

When you write a book in four weeks, how many hours of writing a day are we talking about?

Many.  It’s very efficient.  I don’t know, 12 hours, 14 hours. You eat, you sleep and you write. Seven days.  Actually, I might take a day off because I still liked to bike so I used to go out on a bike ride and stuff.  The work is intense but it’s not tiring.  The only indication I had that the writing process might be tiring was that I never slept better. I would put my head on the pillow, and I was gone.  And I’d wake up only when it was time to get up.  And that’s how I love it.  I long for those days. You wake up and you know exactly where you are in the text. I didn’t even have to use tricks, like where you stop writing in the middle of a paragraph because you already know how to continue.  I didn’t have to do that.

Are you suggesting it doesn’t always work out that way?

That was a rare experience. The Managing for the Long Run book we did on family business with Isabelle (Le Breton-Miller) was much harder to write.  First of all, we hadn’t done the research in advance.  Secondly, we didn’t know the field that well.  Thirdly, these companies were creatures we didn’t really understand. And family businesses are very secretive.  It was hard to find good source material. We also had an “axe to grind” constraint because we wanted to find family firms that represented a more humane, sustainable, stakeholder-conscious form of management. Given the short-term orientations and opportunistic behaviour of many publicly listed companies, we were looking for an alternative long-term management approach – in this case among family businesses that had been around for over 100 years.  We thought “They’ve done well by their stakeholders or they wouldn’t have thrived for this long — so let’s look at them”.  That was the idea.  We were searching for a different model of management at work.  We kind of found it, but it’s always messier than you want it to be.  The book also took a long time to write because we did the research while writing. And it is a bit repetitive because it is built on configurations that overlap thematically.  But I think it’s a valuable book that makes some socially important points.  It is now printed in seven languages.

What about when you’re writing an article?  

Well, there’s a piece I wrote on Paradigm Prisons, which is a critical essay that was generated by my dissatisfaction with our field.  I think our field is too insular.  Too many of us are theory-obsessed and don’t care about problems in the real world.  We write for a very narrow group of people using jargon. And so as a field we become irrelevant to society.  What we have is a paradoxical situation in which our management field, which often has the stated aims of improving broader society, is becoming irrelevant. At the same time disciplines such as finance, which tends to cater to narrower, more opportunistic motives, relates more intimately to practice and so enjoys a forceful presence in the business world.

So these are more opinion pieces.

They ARE opinion pieces.  There isn’t very much research that goes into them except to look up research in other fields to find alternative models.  In Paradigm Prisons, I argue that organization theory is dominated by fewer and fewer paradigms. Many journals now insist on theory development and reject purely empirical contributions. That can be counterproductive.  In the article I talk about the field of medicine and show that three of the biggest discoveries of the last few centuries were pre-theoretical.  One was Semmelweis’ discovery of a remedy for puerperal fever.  Many mothers were dying after giving birth and no one knew why.  Semmelweis noticed a pattern — in one room many were always dying, in the other room relatively few. And so Semmelweis tried to find out why by changing things — the sheets, the layout, even the clientele.  All with no result.  Finally, he reversed the working shifts of the doctors visiting the mothers and found that the doctors who had just been in contact with cadavers were linked to the sick mothers.  Then he could control the mortality rate by alternating rounds sequences: 18% in the doomed ward, 0.3% in the other.  And by forcing doctors to wash their hands before entering the maternity ward, he reduced mortality almost to zero. His brute empiricism had paid off handsomely even though he had no viable theory to explain his results. Unfortunately, the hospital rejected the new procedure as they couldn’t explain its effectiveness – they had no theory.  Their disdain for empirics in favour of conceptual convention cost a lot of lives.  In fact, Semmelweis got fired because he was said to be attributing some ghostly force to the dead.   No one had yet heard of bacteria.  A few years later Semmelweis himself died of sepsis in a hospital.

So had you read these stories and then saw the link with management? 

No, I was motivated by dissatisfaction with our field and then went in search of lessons from the history of other disciplines.  Actually, I knew the Semmelweis story because I was interested in the history of medicine.  I also knew about Banting and Best’s work on diabetes, and Fleming’s on penicillin – all discussed in the essay.  These doctors found important regularities in nature that were of consequence to disease.  They didn’t know why they occurred but found a way to stop them. When you read the philosophy of science, they always tell you that it’s the theories that change. The observations don’t change very much, even in quantum theory. I mean, Newtonian predictions still hold.  It’s only when you get beyond a certain scale that they don’t. So pay attention to empirical fact and be useful.  Don’t always back off to the theory. The theory’s going to change. Einstein was the same way when he rejected quantum theory, but he was wrong.  He said, “God doesn’t play dice with the universe.” Well, he does. And it’s ugly. There’s randomness in the machine. But Einstein didn’t accept it. And he was, even in those days, one of the greatest physicists of the day. He didn’t accept it. So beauty in theorizing isn’t necessarily the criteria. Truth and beauty are not always the same.

Why don’t we talk a bit about the review process. How do you deal with response letters?

Well, it depends.  It depends on whether I have co-authors and what stage they’re at in their careers. Because if they’re early in their careers, I’d feel less willing to dismiss the reviewers and move on, which is often my first reaction. Early in my career, it was a mix. Some reviews I took very seriously. If I thought they contained useful comments, I worked very hard to address them.  Otherwise I was more dismissive and just moved on.

What do you mean by move on?

Just go to a different journal.

So you wouldn’t even attempt to respond to an R&R if you felt the requests were unreasonable?

Correct. I would say that that was the case more often than not. My attitude has been: “This is what I want to say and how I want to say it”.  Unless reviewers find some flaw – in the data, the arguments, the method, even the writing clarity.  I’ll take that seriously.  But sometimes reviewers want to send you off in a completely different direction with a different theory – one that is often allied to their own “hot topic”.  I have resisted that.  So even early in my career, the articles I liked the best tended to go into journals that were less prestigious. And the papers that I thought were less original, less controversial, less innovative, and related more closely to what was already out there — those were the ones that got into the most prestigious journals.

But when you’re writing with someone where getting an article in one of these journals is important for their career, you’ll respond a little bit differently? You’re more willing to help and try to make it happen?

Up to a point, but I’m not going to ruin the paper. And it isn’t so much that I’m stubborn about the correctness of my ideas, because I’m not.  And I’ve changed my mind about a lot of things.  But I’m stubborn about my right to present a decent case.  I may be wrong, but if my case or position is as strong as most of the stuff that’s out there, and it’s important, then at least I deserve to be heard. And if the paper is fresh and interesting, and you could even show it to people who are not in the field and they say it’s interesting, then it deserves to be published.  In fact, I think that’s an important test. I mean, if your friends from outside the field look at your stuff and say, “Huh?” or “Who cares”, that’s not good — especially in an applied field like ours. Our work or at least its topic and purpose should be understandable by any reasonably intelligent person.

Do you have your stuff read by people around you at all?

Hardly ever.

So you don’t do the whole friendly review thing.

No. Hardly at all. I occasionally do it. You’re supposed to do it. But it’s just that I’m going to get very different comments from different people – and those can tempt you to lose focus or originality.  Also, I don’t want to be hassling my friends. Sometimes I will seek advice selectively. If I’m uncertain about something, or someone I know well has worked on something closely related to my topic I may ask for comments.  But not often.  If there are glitches in what I’m writing, I’ll often catch them or whoever I’m working with will.

So you’re at a stage now where you probably don’t need it. 

In any case, I’ve never really done much of it.  Although I should say that I’ve worked with really good people. I worked with Peter Friesen and he was a very tough reviewer and taskmaster.  We’d have many arguments but these made our papers a lot better. And Peter and I were so different — from such different backgrounds and skills, which was very helpful.  I could do stuff he might have difficulty with and vice versa.  So there was always significant scrutiny by someone really smart. By no means was this a one man show. I did do a few things alone, but much of my work was with really good people.

What was his background?

Physics and math. And then mathematical economics. And I also worked with Manfred Kets de Vries, who is a psychoanalyst who studies leadership, with Ming-Jer Chen an expert in competitive dynamics and Chinese culture and philosophy, and with Isabelle Le Breton who has an HR background.

So you like to combine perspectives?

Well, I find it’s very refreshing and it’s fun. I was talking to Ming-Jer and he said, “You have to tell people that you’re an academic entrepreneur because you look for opportunities and launch projects in all these different areas and you learn from them and play with ideas”.  Luckily, we are blessed with a job in which we’re supposed to be creative and playful.  We’re supposed to take chances.  And by being here (at HEC), I am allowed to take chances. It’s not like we have to produce three A articles a year like they might at Stanford. In fact, a friend of mine came to McGill precisely because he could attempt more risky and significant projects. He received job offers from Columbia and Chicago, but was afraid he’d be too much under the gun there. He’d have to do the easy stuff. He wouldn’t be able to take chances.

But couldn’t you just fit into that mould for a while and then once you get tenure…

From the people I see and know in some of our schools, going solely for short-term results to get tenure is a corrupting influence because, first of all, you develop bad work habits and your creativity becomes rusty.  And secondly you come to not like research because doing that kind of opportunistic research isn’t a lot of fun.  Put those obstacles together with emerging consulting opportunities and administrative distractions and you leave research altogether. I mean, how many people my age still do research?

In terms of writing style, who do you admire most?

For convincing revelation, I would say Erving Goffman who is also a super-original thinker, an acutely perceptive researcher, and whose skills at social observation are simply beyond reach. His ability to characterize how people interact is genius at work.  For originality of perspective I would chose James Thompson, Bill Starbuck and Jim March.  For practical importance I would pick Jay Galbraith and Dick Rumelt.   For expository clarity and organization I would say Chick Perrow, Henry Mintzberg, Jim Collins and Don Hambrick.

What are your thoughts around this whole notion of identity as a researcher?

Well, personally I have no capacity to assume a fixed research identity. I would get bored if I stuck with anything for too long.  You know, once I’ve done it, I’ve done it.  It’s time to look for something different. On the other hand, I’m not a dabbler.  I’ll spend five or ten years on a set of related ideas.  I mean, we did tons of stuff on configurations, change, executive effects, competitive dynamics and family business.  In the last case we’ve got, I don’t know, almost twenty articles and a book. So that’s not a dabble, but it’s not my life’s work. I’m already revisiting competitive dynamics, this time in Asian firms, because I find the topic interesting. Also, we might do some neurophysiological work to see what’s going through people’s mind as they make decisions to get more of an “inside view”.  So a few different paths.

We’re running out of time, so let me ask you one last question: What advice do you have for those of us just starting out at this game? 

Think of what your accomplishments will look like to you when you’re my age. Are you going to be proud of them or are you going to just say, “Well, I managed to keep my job and play the game.” In a way, it’s a matter of trying to reduce the amount of cognitive dissonance you’ll have as your life proceeds. I mean, you want to do something that you’re going to be proud of and it’s hard.  I was diagnosed with a serious condition before I began to write the Quantum book and I thought that was the last thing I would ever do.  So I was driven.  I put all of my effort into working on the book — to argue and illustrate a different way of studying and characterizing organizations and change. I don’t think I did the perfect job, but with Peter’s help I did my best, given the resources we had at the time.  At almost the same time with Manfred I wrote The Neurotic Organization.  And I look at those books today after so many years and I’m still proud of them.  That’s a nice feeling.


Bill Starbuck told me never to give anyone career advice.  He claimed, with justification, that mine was an unorthodox career and approach and that others should avoid following in my footsteps.  “Too risky”, he said.  I believe he’s probably correct.  D.M.

Interviewed and edited by Charlotte Cloutier.


Kets de Vries, Manfred and Danny Miller (1984); The Neurotic Organization; Jossey-Bass: San Francisco, CA.

Miller, Danny (1983) The correlates of entrepreneurship in three types of firms; Management Science; 29 (7); p. 770.

Miller, Danny (1990); The Icarus Paradox: How Exceptional Companies Bring About Their Own Downfall; Harper-Collins.

Miller, Danny (2007); Paradigm prison:  Or in praise of atheoretic research; Strategic Organization; 5 (2); p. 177.

Miller, Danny and Peter Friesen (1982); Innovation in conservative and entrepreneurial firms:  Two models of strategic momentum; Strategic Management Journal; 3 (1); p. 1.

Miller, Danny and Peter H. Friesen (1984); Organizations:  A Quantum View; Prentice-Hall.

Miller, Danny and Isabelle LeBreton-Miller (2005); Managing for the Long Run:  Lessons in Competitive Advantage from Great Family Businesses; Harvard Business School Press: Cambridge, MA.

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