Research Heroes: Jay Edward Russo

RussoThis week’s Research Hero is Prof. Jay Edward Russo. Prof. Russo received his PhD in Cognitive Psychology from University of Michigan. He has been working at Cornell University since 1985, and holds the S.C. Johnson Family Professor of Management at the business school. He has also been on the Faculty of the University of Chicago, the University of California, San Diego as well as holding visiting positions at Bocconi University (Milan), Carnegie-Mellon, and Duke, and Penn (The Wharton School). Prof. Russo’s research focuses on managerial and consumer decision making and one of his most important contributions is the work in information distortion and process tracing methods. Prof. Russo has published extensively in prestigious journals as well as co-authoring Winning Decisions (2002) and Decision Traps (1989). He has been on the editorial boards of leading journals such as Journal of Behavioral Decision Making, Journal of Consumer Psychology, Journal of Marketing, Journal of Personality and Social Psychology, Psychological Science, and many more. He has also done consulting work for National Bureau of Federal Trade Commission, GTE Laboratories and General Motors Research Laboratories. 

I wish someone had told me at the beginning of my career…Throughout your career, but especially prior to tenure, you will very likely be forced to make a tradeoff between good science and careerist tactics. A research topic that may contribute most to understanding J/DM may not be one that is currently well recognized and accepted by the field. The more novel the topic of one’s research, the more challenging will be its path to publication in journals, to grant support, and to other markers of acceptance by the field. The likelihood of lots of published papers is far greater if you work on currently accepted topics. You will need the publications, maybe many of them, to achieve careerist goals, especially tenure. The price to good science may be work that is incremental at best and “backfill” at worst.  I urge you to be fully aware of the tradeoffs that you make between better science and career advantage.

I most admire academically… because…
Herb Simon because he aimed so high as a scholar and as a citizen of his university and of the world at large– and because he was so successful as both scientist and a citizen.

The best research project I have worked on during my career…/the project that I am most proud of/ that has inspired me most….I stumbled on the phenomenon of decision makers’ distorting new information to support the currently leading alternative. I investigated this predecisional distortion of information for a decade or so, revealing some of its manifestations, boundaries, and consequences. One strategy for good science is to try to identify the underlying causes that explain why a phenomenon occurs, in the hope that even one of those causes may be fundamental enough to explain other phenomena as well. The attempt to explain predecisional distortion led to work that identified the goal of cognitive consistency as the main driver. This work relied on multiple methods, including some new to me (semantic priming and a lexical decision task) or simply new (in-progress assessment of goal activation). The result was unexpected and quite clear: only cognitive consistency caused information distortion, with alternative goals like saving effort playing no role at all. Subsequent work has confirmed that the goal of cognitive consistency is at least one driver of several other J/DM phenomena, thus validating the scientist’s strategy of seeking depth of explanation.

The worst research project I have worked on during my career…/the one project that I should never had done…There is no one project that I regret. Rather my regret is working on too many projects, drawn to each one because it was so genuinely interesting. I probably should have focused on those that were both most interesting and most important.

The most amazing or memorable experience when I was doing research….After so many decades of research (five), there are many experiences; but it is more categories than individual events that come to mind in responding to this question. For instance, when I was younger, it was a great pleasure to have a senior scholar whom I respected proffer kind words about my work. Now I have the pleasure of supporting young researchers, reminding them that it may take several good ideas to find one both worthwhile and feasible and to remember in their enthusiasm and impatience that science is slow.

The one story I always wanted to tell but never had a chance…“There’s nothing new here.” These were the words of all three reviewers of one of the first submitted manuscripts on information distortion. Fortunately, each one identified a different well-known phenomenon of which information distortion was asserted to be merely another (unnecessary!) illustration. I do not recall the exact three, but early in this research stream the following were offered: attitude extremity/polarization, cognitive dissonance, confirmation bias, the desirability bias (wishful thinking), the halo effect, and the prior belief effect. Fortunately, the editor was sensitive to the unusual combination of reviewers’ complete agreement (“reject this manuscript”) and complete disagreement (“just another example of [three distinctly different phenomena]”). As a result, he gave me and my co-authors the chance to explain why there was, in fact, something new in the phenomenon of information distortion. The subsequent explanation was accepted, along with the manuscript. The lesson I took from this experience was how reviewers (which means most of us) can so naturally filter our judgments through our own lenses. The question that I ask myself is whether I have applied that lesson consistently when I evaluate others’ work. The answer: probably not, but I do keep trying.

A research project I wish I had done… And why did I not do it…I cannot claim to have no regrets whatsoever (that would be hubris), but none of them involve a research project that I regret not attempting.

If I weren’t doing this, I would be…Likely retired, an unpleasant thought. There is still tread left, so please don’t retire me.

The biggest challenge for our field in the next 10 years…One challenge is to encompass the growing breadth of J/DM phenomena and methods. Among the phenomena are those that are nonconscious, emotional, and contextual. Among the methods are those of neuroscience and of process tracing. In considering the opportunities and barriers to adopting these newer research topics and methods, I recall the observation that so often seems best to characterize a field’s response to such a situation, “We love progress; it’s change we hate”. My belief is that J/DM researchers, senior as well as junior, can master new methods and solve new problems. My hope is that more than a few will.

A second challenge is paradigmatic. J/DM emerged as a field by testing the optimal models of economics and statistics, especially EU and Bayesian updating. Violations of these models engendered the anomalies paradigm that has characterized J/DM for the last four decades. Let me suggest a challenge in the form of a question: what would J/DM look like if studied the way other higher-order psychological phenomena are approached, such as problem solving/reasoning and language comprehension? That is, what if we built theories of cognitive (and other) processes from process (and other) data, but without specifying optimal performance? Indeed, if we view behavior as driven by multiple goals not all of which are even conscious, can we really specify optimal performance? What if, instead, we viewed our subjects as adapting to the task environment that we scientists create in order to perform sufficiently well rather than optimally?  Great progress has been achieved in understanding how people read without the use of an optimal model of language comprehension. Might similar progress occur in J/DM by focusing less on how our observations compare to optimality criteria and more on the complexity of decision makers’ attempt to achieve multiple goals simultaneously?

My advice for young researchers at the start of their career is…Learn how to select research problems, not just how to solve them.   Try to be strategic in how you approach your topics, colleagues, and journals.  Often I’ve seen a graduate student (or a credentialed researcher) happy just to find a candidate problem: “That would make a dissertation topic.” or “That could be publishable”. With my own students who are ready to find a dissertation problem, I ask them to identify three potential topics, to research each one for at least one week, and to evaluate their comparative merits. Then, and only then, do I want them to pick one.

Understand the J/DM paradigm in which you are working and think about whether a different one, maybe a newer one, might yield greater contributions to the field. Are input-output data sufficient, or would process data yield more insight? Is this the time or topic to bring in neuroscience? Should the analysis move from the attributes of the alternatives considered in a decision to the benefits that those attributes convey, or even to the goals that those benefits help to achieve? One of books that most influenced my graduate training is Thomas Kuhn’s Structure of Scientific Revolutions, which focused on scientific paradigms. I still begin my doctoral seminar by asking students to read it.

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Research Heroes: Karl Halvor Teigen

TeigenGraduated as a psychologist from the University of Oslo in 1966, where he is now an emeritus professor in general psychology. He also held positions in cognitive psychology at the universities of Bergen and Tromsø (Norway) where he was for some years the northernmost professor of psychology in the world (until a colleague beat him with half a mile). He is a past president of EADM, and has received an honorary doctorate from the University of Bergen. His main research interests concern probability judgments, including verbal probabilities, social cognition (counterfactual thinking), and the history of psychology.

I wish someone had told me at the beginning of my career… that I would have a career! I also wish I had been strongly encouraged to go abroad and to attend international conferences. Norwegian psychology at the time I graduated was quite provincial. In 1967 it was considered a big leap even to move from one Norwegian city (Oslo) to another (Bergen). It took me more than 15 years before I dared to step out on the international scene, so I now have to continue research far into senility to make up for those lost years.

I most admire academically … As a young student I came across “Chance, skill and luck” by John Cohen (Penguin books, 1960). I admired his studies of psychological probability which he combined with a rich historical perspective. In fact this was a book I would have liked to write myself. Later came Kahneman and Tversky who did similar studies even better, except leaving out the historical aspect. It is in such cases hard to distinguish between envy and admiration, but it has fortunately been shown that benign envy outperforms admiration (Van de Ven, Zeelenberg & Pieters, 2011), so I can confess my benign envy for a number of scholars inside and outside of our field. 

The best research project I have worked on during my career…/the project that I am most proud of/ that has inspired me most….Many years ago I became puzzled by the fact that newspaper articles about “lucky” people (with the exception of occasional lottery winners) almost invariably described accident victims. When I asked students to give autobiographical instances of their own luck, they produced similar, rather negative instances. Degrees of luck seemed to be almost completely determined by the discrepancy between what happened and what could have happened, that is, by close and worse counterfactuals. The closer and the worse they are, the luckier you feel. This issue has haunted me for years, partly because of its popular appeal (journalists love it), and partly because it can be linked to several other themes, like risk perception, counterfactual thinking, probability judgments, superstitions, and gratitude. But its main fascination resides in the observation that people seem to know it, through the stories they tell and the judgments they pass, yet our findings make them puzzled and surprised.

The worst research project I have worked on during my career…/the one project that I should never had done…I once had to conduct a research project with students and decided to spare them for background reading by finding a topic that had never been experimentally investigated before. It turned out that nobody had at that time studied “sighing” in healthy adults (it had been studied in patients with panic disorder and in rats), so we had to invent our own “sigh-cology”, for instance by observing participants working on insoluble puzzles. They had to give up every new attempt, and they sighed. I wrote a paper which, to my surprise, was accepted for publication, but did not exactly revolutionize the (nonexistent) field. It would have remained a forgotten oddity, when I suddenly received an invitation to receive the Ig Nobel prize in psychology from Improbable Research “for trying to understand why, in everyday life, people sigh”. So I had to go to Harvard for a parodical celebration of “research that makes people laugh and then think”. Or in our case: to make people think and then sigh.

The most amazing or memorable experience when I was doing research….There have been several such experiences. Doing research often feels like trying to force open a door that appears to be slightly ajar. You have an idea, a theory, an intuition that you feel could work, but the door proves surprisingly resistant to all applications of the foot-in-the-door technique.  Then there are moments where the door simply needs a gentle push before swinging wide open. Such moments, when you get more than you asked for, are the researcher’s peak events. I experienced one almost 40 years ago when I first “discovered” that people consistently violated the 100% limit when estimating probabilities for several mutually exclusive alternatives. Again when I found that most people have to be unlucky to feel lucky, as described above; that they attach more confidence to specific (fallible) rather than to general (true) statements, that they think that events are more unlikely when they happen than when they do not occur, that negative outcomes are less surprising than equivalent positive ones, and several other robust paradoxes that seemingly defy common sense.

The one story I always wanted to tell but never had a chance…Peter Ayton already told the story of the spider in Cambridge, which I can confirm (although we may disagree about the details).  I also experienced in Cambridge (same SPUDM meeting I believe) my most successful presentation; the audience seemed more attentive to what I had to say than ever before (or since), showing their keen interest with synchronized head movements to the right and to the left, following me like a bunch of hypnotized cobras. Only after the talk I discovered I had been standing in front of the projector, obstructing their view of the screen.

A research project I wish I had done… And why did I not do it…I am fascinated by the role chance plays in shaping our lives, from the small details that make our day amusing, to more momentous decisions about marriage and career. We once carried out a set of pilot interviews with colleagues, asking them about their choices of research themes. They seemed to believe in the idea of a recurrent theme, or common thread running through their professional life, but when we pushed it further back they typically responded: “It all began quite accidentally”.  We did not follow this up, for methodological, theoretical, and perhaps even philosophical reasons, but I wish there was a neat and tractable way to observe chance at work in real-life settings. Perhaps I will stumble over one, accidentally.

 If I wasn’t doing this, I would be…perhaps a historian – of ideas, or of art. But every time I have had a brief encounter with these fields I have thanked God that I belong to a discipline where one can do experimental work, not restrained by events already settled in a hazy past, and where hypotheses can actively be put to test. To indulge in my historical interests I have published quite a bit on the history of psychology.

The biggest challenge for our field in the next 10 years… To disentangle the psychology of judgment from the psychology of decision making. These are in my opinion two overlapping themes rather than a single field. And even if I am strongly in favor the cross-disciplinary applications of JDM in economics, management, political science, medicine, and law, I feel it extremely important that it should keep and perhaps expand its psychological roots.

 My advice for young researchers at the start of their career is… (1) Travel and seek new research environments; (2) realize that your freedom of choice concerning themes, ideas, theories, methods, and approaches is greater than you think; (3) listen to advice, so that you can disregard it on purpose, and have something to tell when Elina, Neda or their successor ask you, 20 years from now, what you had wished someone had told you at the beginning of your career (they did).

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Research Heroes: Ellen Peters

peters

This week’s Research Hero is Prof. Ellen Peters. Prof. Peters received her M.S. and Ph.D. from the Department of Psychology, University of Oregon in 1994 and 1998, respectively. She is currently a professor in the Psychology Department at The Ohio State University. She works extensively with the National Cancer Institute and the Food and Drug Administration to advance the science of human decision making. Prof. Peters’ research focuses on how affective, intuitive, and deliberative processes help people to make decisions in an increasingly complex world. She studies numeracy and number processing, how affect and emotion influence information processing and decisions, and how information processing and decision making change across the adult life span. Prof. Peters has received over 10 academic awards, been on the editorial board of various academic journals, published numerous articles and continues to be one of the experts in medical decision making. 

I wish someone had told me at the beginning of my career… how much fun research can be. It is serious business in some ways, but the process of discovering something new about the human mind is simply fascinating. What we study is so much more complex than other “hard” sciences that it continues to amaze me that we can and do find some order in the chaos.

I most admire academically… I most admire people who combine great scientific rigor with a desire (and actions) to do some good in the world because we only get one life time to try to make a difference.  There are many examples including Paul Slovic, Elke Weber, Baruch Fischhoff, Eric Johnson, Laura Carstensen, Karen Emmons, and countless others (my apologies if I forgot to name you).

The best research project I have worked on during my career… is about something we called evaluative categories and how they influence judgments and choices about health insurance plans and hospitals. It started off as a topic that looked really boring (sorry Judy Hibbard!); it ended up being a great blend of basic and applied research. Although it’s among my favorite projects, it took the longest to publish!

The worst research project I have worked on during my career… I’ve learned something from all of them.

The most amazing or memorable experience when I was doing research… This experience is my most memorable but also the saddest. It also taught me a lot about the research process. We were doing a study for HCFA (Medicare) with older adults subjects.  I was doing cognitive interviews with some materials in a senior center. One of my participants was having some surprising difficulty with a relatively easy task. As we talked about it, she suddenly broke down crying.  It turned out that her husband had died about a year ago and he had always made these kinds of insurance and other money decisions for them. What I thought was a simply comprehension task was filled with grief and powerful narrative for her. The “decision” she faced was completely different from the one that I thought I had given her.

The one story I always wanted to tell but never had a chance… I think I’ve told them!

A research project I wish I had done… Any time I have wanted to do a research project, I have done it. We’ve gone to Africa and Peru, worked with older adults and younger, and have studied theoretical topics from affect and emotion to numeracy and applied topics from health-plan choices to donation behaviors to climate change.

If I wasn’t doing this, I would be…Writing fiction or running a restaurant with my husband.

The biggest challenge for our field in the next 10 years… Be relevant. Develop theory because this is what is needed. At the same time, the theory needs to matter to “something that matters.”

My advice for young researchers at the start of their career is… Pay attention to opportunities and take some risks.  Whether the opportunities you find actually benefit you is probabilistic (just like everything else in life), but taking a chance is often worth it.

Do what you enjoy or feel is important to society, hopefully both.  If you’re lucky, you’ll get to enjoy doing most of it. I’ve been really lucky.

It’s good to have your own money – spend time writing and rewriting grant proposals.

Departmental website

Research Heroes: Robert B. Cialdini

CialdiniThis week’s Research Hero is Robert B. Cialdini, Regents’ Emeritus Professor of Psychology and Marketing at Arizona State University. Prof Cialdini’s research focuses on, but is not limited to, social influences and persuasion. He is the recipient of the Distinguished Scientific Achievement Award of the Society for Consumer Psychology, the Donald T. Campbell Award for Distinguished Contributions to Social Psychology, the (inaugural) Peitho Award for Distinguished Contributions to the Science of Social Influence, the Distinguished Scientist Award of the Society of Experimental Social Psychology, and has been elected president of the Society of Personality and Social Psychology. Professor Cialdini’s book Influence: Science and Practice, which was the result of a three-year program of study into the reasons that people comply with requests in everyday settings, has sold over two million copies while appearing in numerous editions and twenty-eight languages.

I wish someone had told me at the beginning of my career to avoid being overcommitted and, thereby, constantly rushed. In my experience, it is the single self-inflicted problem that, when left to expand, has most undermined the joy of doing research.

I most admire academically William McGuire because he was the consummate combination of big-picture theorist and precise-picture experimentalist.

The project that I am most proud of took me out of my comfort zone as a researcher predicting (mostly from theoretical formulations) the responses of experimental subjects (mostly college students) in controlled settings (mostly laboratories) and put me, as a kind of secret agent, in the training programs of the influence professionals of our society. There, I recorded the lessons taught to aspiring salespeople, marketers, advertisers, managers, fund-raisers, public relations specialists, and recruiters. My intent was to find out which practices were roundly judged to work powerfully time after time, figuring that thriving influence organizations would instruct their influence agents in those techniques. So I answered the organizations’ newspaper ads for trainees or otherwise arranged to be present in their classrooms, notebook in hand, ready to absorb the wisdom born of longstanding experience in the business of persuasion.  That experience of going to the field for evidence, rather than only to the laboratory, changed my perspective on the most productive ways to study the social influence process.

The one project that I should never had done, in keeping with my answer to question #1, was always the one that was so attractive that I agreed to it even though I already had too many projects on my plate to accept another. The consequence was that, invariably, all the projects suffered from my inability to give each the time, energy, and focus it deserved.

The most amazing or memorable experience when I was doing research occurred during one of a series of meetings with the local blood services organization to get their assistance with a research project investigating how to get citizens to give blood. Although we thought that we had made a compelling case for mutual benefit, the organization’s chief administrator hung back from authorizing our project. It wasn’t until a junior member of his staff quietly informed us of the reason for her boss’s reluctance that we understood what we had left out of our persuasive approach. “None of you has given blood yet,” she whispered during a break in the meeting. Mildly chastised but properly enlightened, we asked just before the meeting’s close how we might contribute to the organization’s important goals by donating a pint or two of blood ourselves. An opportunity was arranged, blood was drained, and full approval of our project followed within the week.

The one story I always wanted to tell but never had a chance doesn’t exist, as I am an inveterate story-teller.

A research project I wish I had done would have followed up empirically on a theoretical piece I wrote a few years ago in which I offered a rationale—beyond the traditional one based on the economic consequences of a damaged reputation—for why organizations should steer sharply away from unethical persuasive practices: Those practices will lend themselves to the attraction and retention of employees who find cheating personally acceptable and who will ultimately cheat the organization as a consequence. Fortunately along with a pair of brilliant collaborators, Jessica Li and Adriana Samper, I am finally beginning that project.

If I wasn’t doing this, I would be looking for a way to do this.

The biggest challenge for our field in the next 10 years is demonstrating convincingly to individuals outside of the academic research community the value of our thinking, findings, and (research-based) approach to the problems they confront regularly.

My advice for young researchers at the start of their career is always have a foil. For maximum scholarly impact, never test your hypothesis just against the null. Always test it against at least one competing conceptual hypothesis.

I got interested in doing research on social influence because I was raised in an entirely Italian family, in a predominantly Polish neighborhood, in a historically German city (Milwaukee), in an otherwise rural state. I often ascribe my interest in the social influence process to an early recognition that the groups populating those settings had to be approached somewhat differently in order to obtain their assent, sometimes to the identical request. It also struck me that one reason for this complication was that the social norms—the characteristic tendencies and codes of conduct of the groups—differed. Therefore, if I wanted to maximize compliance with a request from a member of one or another of these groups, it would be wise to take into account the dominant social norms of that particular unit.

My recommendations for young researchers interested in studying social influence is get into the field. It’s possible to do soundly conducted, properly controlled studies and experiments in naturally-occurring settings. It might be substantially more inconvenient; but, provided the work is soundly conducted and properly controlled, the data will be more meaningful—and the effort consequently worth it.

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Research Heroes: Gerd Gigerenzer

gigerenzer_gerd_rgb_2006_webThis week on Research Heroes we’re featuring professor Gerd Gigerenzer who is Director at the Max Planck Institute for Human Development in Berlin and former Professor of Psychology at the University of Chicago. He has won the AAAS Prize for the best article in the behavioral sciences and the Association of American Publishers Prize for the best book in the social and behavioral sciences. His award-winning popular books Calculated Risks: How To Know When Numbers Deceive You, and Gut Feelings: The Intelligence of the Unconscious have been translated into 18 languages and his academic books include The Empire of Chance,Simple Heuristics That Make Us Smart, Rationality for Mortals, and Bounded Rationality: The Adaptive Toolbox (with Reinhard Selten, a Nobel Laureate in economics). Together with the Bank of England, he works on the project “Simple heuristics for a safer world.” He has trained managers, U.S. Federal Judges and German physicians in decision-making and understanding risk and uncertainty. 

I wish that someone had told me at the beginning that research and writing is more fun than playing Jazz and Dixieland (my previous career).

I most admire academically Herbert Simon, because he was no respecter of disciplinary boundaries. There are two ways to do research: one is to identify with a discipline, and to research whatever topics others do; the other is to identify with a problem, and use the knowledge and methods from various disciplines to solve it. Real innovation almost always comes from problem-oriented research.

Asking about the best research project I have worked is like asking me to single out a Wagner opera as my favorite – like the operas, the projects mostly build on each other and form a single body of work.

The worst research project I was involved in: In the early phases of discovering cognitive heuristics, some researchers at my center were overly enthusiastic about the predictive accuracy of a particular heuristic in forecasting sports results. Fortunately for us, the press followed its usual pattern of announcing a dramatic result and just as quickly forgetting it.

The most memorable experience when I was doing research was Ulrich Hoffrage’s and my totally unexpected discovery of the “less-is-more” effect. Initially we were dismayed by this counter-intuitive result, which ruined the experiment in question, but answering the question of how it could be so led to the fast-and-frugal heuristics program.

The one story I always wanted to tell: Up to now my audiences have been kind enough to listen to all of my stories. My books Rationality for Mortals and Gut Feelings are full of stories about research.

A research project I wish I had done: Hmm. When I trained about 1,000 physicians as part of a Continuing Medical Education program to understand risk und uncertainty, I learned that about 80% of physicians are statistically illiterate. I always wondered why medical schools don’t teach medical students to understand evidence, and why most patients, including academics, nevertheless blindly trust their doctors. And why so few psychologists are willing to leave their labs and go out and teach doctors. That would be an important research project I always wanted to do. And probably will.

If I weren’t doing this, I would be a guitar or piano player with my former jazz band.

The biggest challenge for our field in the next 10 years lies in studying how one should rationally deal with unknown risks (“uncertainty”), as opposed to known risks (“risk”). Uncertainty means that not all alternatives, consequences and probabilities are known – as in most of our decisions. Under uncertainty, one cannot optimize and has to rely on smart heuristics. Probability theory and logic are the tools for known risks; heuristics and intuition are those for uncertainty. This distinction is not always respected, and there are still many who believe that subjective probability theory would be the only tool that is needed to make good decisions.

My advice: If you are average and unimaginative, do what the others do and pursue a decent career. If you are brilliant and smart, try to think deep, be bold and take professional risks. 

Departmental website

Research Heroes: Max Bazerman

Bazerman_25aThis week’s Research Hero is Prof. Max Bazerman, Jesse Isidor Straus Professor of Business Administration at Harvard Business School. He is also affiliated with Harvard Kennedy School of Government, the Psychology Department, and the Program on Negotiation. Prof Bazerman’s research focuses on but is not limited to decision making, ethics, and negotiation. He has coedited more than 200 articles and 16 books, including Negotiation Genius, Predictable Surprises: The Disasters You Should Have Seen Coming, and How to Prevent Them, and the sixth edition of Judgment in Managerial Decision Making. He has international collaborations with over 25 countries and 50 companies in United States. Prof. Bazerman is also famous for being the one who introduced the science of negotiation in Business schools. He has received many awards, to name a few recent ones: honorary doctorate from the University of London (London Business School), being named as one of Ethisphere’s 100 Most Influential in Business Ethics, one of Daily Kos’ Heroes from the Bush Era for going public about how the Bush Administration corrupted the RICO Tobacco trial, and the 2008 Distinguished Educator Award from the Academy of Management.

I wish someone had told me at the beginning of my career…

a) All good papers find homes

b) If the reviewer is being “stupid”, it is probably your writing that allows them to be “stupid”.  The solutions isn’t hoping for smart reviewers, but taking the perspective of the reviewer, and writing so that they see the brilliance in your work.  (and, if you don’t have those writing skills, find an editor)

I most admire academically… because…


a) Kahneman and Tversky, for outlining the most influential research direction in the social sciences

b) Thaler and Sunstein, for nudging us to how to put this brilliance into practice to make the world a better place

The best research project I have worked on during my career...the project that I am most proud of/ that has inspired me most….
The next project, which I do not even know about as I write this, that one of my brilliant doctoral students lures me into joining.

The worst research project I have worked on during my career…the one project that I should never had done…
My empirical work has co-authors, so I am going to refuse to answer this one.

The most amazing or memorable experience when I was doing research….The common occurrence of a brilliant doctoral student coming into my office to inform me about how wrong I am – again!

The one story I always wanted to tell but never had a chance…
I have told all my stories worth telling

A research project I wish I had done… And why did I not do it…Kern, M. and Chugh, D. (2009).  Bounded ethicality: The perils of loss framing.  Psychological Science, 20(3), 378-384. The paper is brilliant, simple, and important.  And, it is about things I know about.  I can’t figure out why I didn’t do this before Kern and Chugh.  I love this paper!

If I wasn’t doing this, I would be...less happy.

The biggest challenge for our field in the next 10 years…Changing our methods to cope with the insightful and important work of John, Leslie K., George Loewenstein, and Drazen Prelec. Measuring the Prevalence of Questionable Research Practices with Incentives for Truth-telling. Psychological Science (2012). Simmons, Joseph P.,  Leif D. Nelson and Uri Simonsohn.  False-Positive Psychology : Undisclosed Flexibility in Data Collection and Analysis Allows Presenting. Psychological Science (2011). My generation messed up, and led to the acceptance of bad practices with too many cute false positives.  We need to clean up our act, and the faster the better.

My advice for young researchers at the start of their career is… Don’t p-hack (see Simmons et al., 2011).  The world is changing, detecting p-hacking is easy, and the value on integrity in research is going up very quickly.

Prof. Bazerman’s Wikipedia page

Research Heroes: Barry Schwartz

This week’s research hero is prof. Barry Schwartz of Swarthmore College. schwartzProf. Schwartz received his PhD from University of Pennsylvania and his research addresses morality, decision making, and reasoning. He has published a number of books, among other the praised “Paradox of Choice”. He is also active in publishing in scientific journals and editorials in the New York Times where he applies research in psychology to current events. 

I wish someone had told me at the beginning of my career…To take more math.  I spent my undergraduate days taking every psych course there was. Then I twiddled my thumbs in grad school while other students caught up.  I should have done lots more math.

I most admire academically… I won’t mention names, but the people I most admire academically are people who are willing to be wrong in public.  Everyone seems to think that the worst thing you can do is be wrong.  I think the worst thing you can do is be trivial.  This is reflected in journal submission reviews, tenure reviews and grant reviews. It’s a pity. People willing to make mistakes in public are the people who really move the field forward.

The best research project I have worked on during my career… I think the best paper I ever wrote was not an empirical paper, but the result of a collaboration with two philosopher colleagues.  We wrote a paper that tried to embed the work of B.F. Skinner in the historical context of the growth of the factory, and of “scientific management” in the U.S.  It’s an old paper (1978), and in those days my empirical work was focused on identifying the limits of Skinner’s view of the world.  This project made me appreciate that there was no guarantee that claims that were empirically false would die–of “natural causes.”  They could live if society believed them and then shaped its institutions in the image of these claims.  Many years later I published a paper in Psych Science, prompted by the book, “The Bell Curve,” that made a similar point and called the phenomenon “ideology,” after Karl Marx’s notion of “false consciousness.”  Working on this paper changed the way I think about psychological phenomena in general.  It actually contributed to two of my books, “The Battle for Human Nature,” and “The Costs of Living.”

The worst research project I have worked on during my career… I did a whole bunch of pretty trivial things in my days working from within the Skinnerian worldview.  Happily, they were pretty trivial even at the time, so no one was led on wild goose chases.

The most amazing or memorable experience when I was doing research….In my paper on “maximizing” (JPSP, 2002), we did a study of the ultimatum game that I thought had no chance of working.  It worked!  It was quite clever, borrowing a methodology developed by Marcel Zeelenberg and Jane Beatty.  Alas, this is a part of the paper that nobody writes about.

The one story I always wanted to tell but never had a chance…Well, I have told this story.  I taught a course in “motivation” almost 40 years ago.  I gave everyone a B and they knew this on day 1.  There was still a midterm, a final and a term paper, all of them graded, but people got a B no matter what.  This was designed to have students scrutinize their own motives in being students. For the first five weeks, everything was great.  But then midterms in other courses rolled around, students in my course fell behind, and they never caught up, growing increasingly embarrassed as the semester wore on.  I think I ended up with three (quite good) papers in a class of 40.  It was not a successful experiment.

If I wasn’t doing this, I would be… Well, I’d be a writer.  In the last 25 years, what I have found most satisfying, by far, is writing books (and the occasional article) for non-professional audiences.  My aim is to make the mysterious world of psychological research comprehensible and to show readers why it matters.  I’ve written four such books thus far and plan to start a fifth this summer.

The biggest challenge for our field in the next 10 years…

This will seem iconoclastic, but I think there are four challenges:

1. Too much data.  I think it would be good to declare a moratorium on new data until we understand the data we already have.  Five years, let’s say (I told you I’d be iconoclastic).

2.  Far too much worship of neuroscience.

3. People whose education is far too specialized and who then perpetuate this specialization in the students they train.

4. An incentive structure for success that is close to a disaster.  It’s all about having publication lists as long as your arms and about publishing papers that are “flawless.”  As long as this persists, all the concern about “p-hacking” in the world will not induce people to do research that matters and do it honestly and openly.

My advice for young researchers at the start of their career is…Take lots of math, be willing to make mistakes in public, and work on things that matter.  I certainly can’t guarantee that this will lead to a successful career.  But if it does, it will be a career worth having.

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