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2007-5-6 06:30

Autobiography  
Early  years

  I was born in Tel Aviv, in what is now Israel, in 1934, while my  mother was visiting her extended family there; our regular  domicile was in Paris. My parents were Lithuanian Jews, who had  immigrated to France in the early 1920s and had done quite well.  My father was the chief of research in a large chemical factory.  But although my parents loved most things French and had some  French friends, their roots in France were shallow, and they  never felt completely secure. Of course, whatever vestiges of  security they'd had were lost when the Germans swept into France  in 1940. What was probably the first graph I ever drew, in 1941,  showed my family's fortunes as a function of time - and around  1940 the curve crossed into the negative domain.

  I will never know if my vocation as a  psychologist was a result of my early exposure to interesting  gossip, or whether my interest in gossip was an indication of a  budding vocation. Like many other Jews, I suppose, I grew up in a  world that consisted exclusively of people and words, and most of  the words were about people. Nature barely existed, and I never  learned to identify flowers or to appreciate animals. But the  people my mother liked to talk about with her friends and with my  father were fascinating in their complexity. Some people were  better than others, but the best were far from perfect and no one  was simply bad. Most of her stories were touched by irony, and  they all had two sides or more.

In one experience I remember vividly, there  was a rich range of shades. It must have been late 1941 or early  1942. Jews were required to wear the Star of David and to obey a  6 p.m. curfew. I had gone to play with a Christian friend and had  stayed too late. I turned my brown sweater inside out to walk the  few blocks home. As I was walking down an empty street, I saw a  German soldier approaching. He was wearing the black uniform that  I had been told to fear more than others - the one worn by  specially recruited SS soldiers. As I came closer to him, trying  to walk fast, I noticed that he was looking at me intently. Then  he beckoned me over, picked me up, and hugged me. I was terrified  that he would notice the star inside my sweater. He was speaking  to me with great emotion, in German. When he put me down, he  opened his wallet, showed me a picture of a boy, and gave me some  money. I went home more certain than ever that my mother was  right: people were endlessly complicated and interesting.

  My father was picked up in the first  large-scale sweep for Jews, and was interned for six weeks in  Drancy, which had been set up as a way station to the  extermination camps. He was released through the intervention of  his firm, which was directed (a fact I learned only from an  article I read a few years ago) by the financial mainstay of the  Fascist anti-Semitic movement in France in the 1930s. The story  of my father's release, which I never fully understood, also  involved a beautiful woman and a German general who loved her.  Soon afterward, we escaped to Vichy France, and stayed on the  Riviera in relative safety, until the Germans arrived and we  escaped again, to the center of France. My father died of  inadequately treated diabetes, in 1944, just six weeks before the  D-day he had been waiting for so desperately. Soon my mother, my  sister, and I were free, and beginning to hope for the permits  that would allow us to join the rest of our family in  Palestine.

  I had grown up intellectually precocious  and physically inept. The ineptitude must have been quite  remarkable, because during my last term in a French lycée,  in 1946, my eighth-grade physical-education teacher blocked my  inclusion in the Tableau d'Honneur - the Honor Roll - on the  grounds that even his extreme tolerance had limits. I must also  have been quite a pompous child. I had a notebook of essays, with  a title that still makes me blush: "What I write of what I  think." The first essay, written before I turned eleven, was a  discussion of faith. It approvingly quoted Pascal's saying "Faith  is God made perceptible to the heart" ("How right this is!"),  then went on to point out that this genuine spiritual experience  was probably rare and unreliable, and that cathedrals and organ  music had been created to generate a more reliable, ersatz  version of the thrills of faith. The child who wrote this had  some aptitude for psychology, and a great need for a normal  life.

  Adolescence

  The move to Palestine completely altered my experience of life,  partly because I was held back a year and enrolled in the eighth  grade for a second time - which meant that I was no longer the  youngest or the weakest boy in the class. And I had friends.  Within a few months of my arrival, I had found happier ways of  passing time than by writing essays to myself. I had much  intellectual excitement in high school, but it was induced by  great teachers and shared with like-minded peers. It was good for  me not to be exceptional anymore.

  At age seventeen, I had some decisions to  make about my military service. I applied to a unit that would  allow me to defer my service until I had completed my first  degree; this entailed spending the summers in officer-training  school, and part of my military service using my professional  skills. By that time I had decided, with some difficulty, that I  would be a psychologist. The questions that interested me in my  teens were philosophical - the meaning of life, the existence of  God, and the reasons not to misbehave. But I was discovering that  I was more interested in what made people believe in God than I  was in whether God existed, and I was more curious about the  origins of people's peculiar convictions about right and wrong  than I was about ethics. When I went for vocational guidance,  psychology emerged as the top recommendation, with economics not  too far behind.

  I got my first degree from the Hebrew  University in Jerusalem, in two years, with a major in  psychology and a minor in mathematics. I was mediocre in math,  especially in comparison with some of the people I was studying  with - several of whom went on to become world-class  mathematicians. But psychology was wonderful. As a first-year  student, I encountered the writings of the social psychologist  Kurt Lewin and was deeply influenced by his maps of the life  space, in which motivation was represented as a force field  acting on the individual from the outside, pushing and pulling in  various directions. Fifty years later, I still draw on Lewin's  analysis of how to induce changes in behavior for my introductory  lecture to graduate students at the Woodrow Wilson  School of Public Affairs at Princeton. I was  also fascinated by my early exposures to neuropsychology. There  were the weekly lectures of our revered teacher Yeshayahu  Leibowitz - I once went to one of his lectures with a fever of 41  degrees Celsius; they were simply not to be missed. And there was  a visit by the German neurosurgeon Kurt Goldstein, who claimed  that large wounds to the brain eliminated the capacity for  abstraction and turned people into concrete thinkers.  Furthermore, and most exciting, as Goldstein described them, the  boundaries that separated abstract from concrete were not the  ones that philosophers would have set. We now know that there was  little substance to Goldstein's assertions, but at the time the  idea of basing conceptual distinctions on neurological  observations was so thrilling that I seriously considered  switching to medicine in order to study neurology. The Chief of  Neurosurgery at the Hadassah Hospital, who was a neighbor, wisely  talked me out of that plan by pointing out that the study of  medicine was too demanding to be undertaken as a means to any  goal other than practice.

  The military experience

  In 1954, I was drafted as a second lieutenant, and after an  eventful year as a platoon leader I was transferred to the  Psychology branch of the Israel Defense Forces. There, one of my  occasional duties was to participate in the assessment of  candidates for officer training. We used methods that had been  developed by the British Army in the Second World War. One test  involved a leaderless group challenge, in which eight candidates,  with all insignia of rank removed and only numbers to identify  them, were asked to lift a telephone pole from the ground and  were then led to an obstacle, such as a 2.5-meter wall, where  they were told to get to the other side of the wall without the  pole touching either the ground or the wall, and without any of  them touching the wall. If one of these things happened, they had  to declare it and start again. Two of us would watch the  exercise, which often took half an hour or more. We were looking  for manifestations of the candidates' characters, and we saw  plenty: true leaders, loyal followers, empty boasters, wimps -  there were all kinds. Under the stress of the event, we felt, the  soldiers' true nature would reveal itself, and we would be able  to tell who would be a good leader and who would not. But the  trouble was that, in fact, we could not tell. Every month or so  we had a "statistics day," during which we would get feedback  from the officer-training school, indicating the accuracy of our  ratings of candidates' potential. The story was always the same:  our ability to predict performance at the school was negligible.  But the next day, there would be another batch of candidates to  be taken to the obstacle field, where we would face them with the  wall and see their true natures revealed. I was so impressed by  the complete lack of connection between the statistical  information and the compelling experience of insight that I  coined a term for it: "the illusion of validity." Almost twenty  years later, this term made it into the technical literature  (Kahneman and Tversky, 1973). It was the first cognitive illusion  I discovered.

  Closely related to the illusion of validity  was another feature of our discussions about the candidates we  observed: our willingness to make extreme predictions about their  future performance on the basis of a small sample of behavior. In  fact, the issue of willingness did not arise, because we did not  really distinguish predictions from observations. The soldier who  took over when the group was in trouble and led the team over the  wall was a leader at that moment, and if we asked ourselves how  he would perform in officer-training, or on the battlefield, the  best bet was simply that he would be as good a leader then as he  was now. Any other prediction seemed inconsistent with the  evidence. As I understood clearly only when I taught statistics  some years later, the idea that predictions should be less  extreme than the information on which they are based is deeply  counterintuitive.

  The theme of intuitive prediction came up  again, when I was given the major assignment for my service in  the Unit: to develop a method for interviewing all combat-unit  recruits, in order to screen the unfit and help allocate soldiers  to specific duties. An interviewing system was already in place,  administered by a small cadre of interviewers, mostly young  women, themselves recent graduates from good high schools, who  had been selected for their outstanding performance in  psychometric tests and for their interest in psychology. The  interviewers were instructed to form a general impression of a  recruit and then to provide some global ratings of how well the  recruit was expected to perform in a combat unit. Here again, the  statistics of validity were dismal. The interviewers' ratings did  not predict with substantial accuracy any of the criteria in  which we were interested.

  My assignment involved two tasks: first, to  figure out whether there were personality dimensions that  mattered more in some combat jobs than in others, and then to  develop interviewing guidelines that would identify those  dimensions. To perform the first task, I visited units of  infantry, artillery, armor, and others, and collected global  evaluations of the performance of the soldiers in each unit, as  well as ratings on several personality dimensions. It was a  hopeless task, but I didn't realize that then. Instead, spending  weeks and months on complex analyses using a manual Monroe  calculator with a rather iffy handle, I invented a statistical  technique for the analysis of multi-attribute heteroscedastic  data, which I used to produce a complex description of the  psychological requirements of the various units. I was  capitalizing on chance, but the technique had enough charm for  one of my graduate-school teachers, the eminent personnel  psychologist Edwin Ghiselli, to write it up in what became my  first published article. This was the beginning of a lifelong  interest in the statistics of prediction and description.

  I had devised personality profiles for a  criterion measure, and now I needed to propose a predictive  interview. The year was 1955, just after the publication of  "Clinical versus statistical prediction" (Meehl, 1954), Paul  Meehl's classic book in which he showed that clinical prediction  was consistently inferior to actuarial prediction. Someone must  have given me the book to read, and it certainly had a big effect  on me. I developed a structured interview schedule with a set of  questions about various aspects of civilian life, which the  interviewers were to use to generate ratings about six different  aspects of personality (including, I remember, such things as  "masculine pride" and "sense of obligation"). Soon I had a  near-mutiny on my hands. The cadre of interviewers, who had taken  pride in the exercise of their clinical skills, felt that they  were being reduced to unthinking robots, and my confident  declarations -"Just make sure that you are reliable, and leave  validity to me"-did not satisfy them. So I gave in. I told them  that after completing "my" six ratings as instructed, they were  free to exercise their clinical judgment by generating a global  evaluation of the recruit's potential in any way they pleased. A  few months later, we obtained our first validity data, using  ratings of the recruits' performance as a criterion. Validity was  much higher than it had been. My recollection is that we achieved  correlations of close to .30, in contrast to about .10 with the  previous methods. The most instructive finding was that the  interviewers' global evaluation, produced at the end of a  structured interview, was by far the most predictive of all the  ratings they made. Trying to be reliable had made them valid. The  puzzles with which I struggled at that time were the seed of the  paper on the psychology of intuitive prediction that Amos Tversky  and I published much later.

  The interview system has remained in use,  with little modification, for many decades. And if it appears odd  that a twenty-one-year-old lieutenant would be asked to set up an  interviewing system for an army, one should remember that the  state of Israel and its institutions were only seven years old at  the time, that improvisation was the norm, and that  professionalism did not exist. My immediate supervisor was a man  with brilliant analytical skills, who had trained in chemistry  but was entirely self-taught in statistics and psychology. And  with a B.A. in the appropriate field, I was the best-trained  professional psychologist in the military.

  Graduate school years

  I came out of the Army in 1956. The academic planners at the  Hebrew University had decided to grant me a fellowship to obtain  a PhD abroad, so that I would be able to return and teach in the  psychology department. But they wanted me to acquire some  additional polish before facing the bigger world. Because the  psychology department had temporarily closed, I took some courses  in philosophy, did some research, and read psychology on my own  for a year. In January of 1958, my wife, Irah, and I landed at  the San Francisco airport, where the now famous sociologist  Amitai Etzioni was waiting to take us to Berkeley, to the  Flamingo Motel on University Avenue, and to the beginning of our  graduate careers.

  My experience of graduate school was quite  different from that of students today. The main landmarks were  examinations, including an enormous multiple-choice test that  covered all of psychology. (A long list of classic studies  preceded by the question "Which of the following is not a study  of latent learning?" comes to mind.) There was less emphasis on  formal apprenticeship, and virtually no pressure to publish while  in school. We took quite a few courses and read broadly. I  remember a comment of Professor Rosenweig's on the occasion of my  oral exam. I should enjoy my current state, he advised, because I  would never again know as much psychology. He was right.
  I was an eclectic student. I took a course  on subliminal perception from Richard Lazarus, and wrote with him  a speculative article on the temporal development of percepts,  which was soundly and correctly rejected. From that subject I  came to an interest in the more technical aspects of vision and I  spent some time learning about optical benches from Tom  Cornsweet. I audited the clinical sequence, and learned about  personality tests from Jack Block and from Harrison Gough. I took  classes on Wittgenstein in the philosophy department. I dabbled  in the philosophy of science. There was no particular rhyme or  reason to what I was doing, but I was having fun.

  My most significant intellectual experience  during those years did not occur in graduate school. In the  summer of 1958, my wife and I drove across the United States to  spend a few months at the Austen Riggs Clinic in Stockbridge,  Massachusetts, where I studied with the well-known psychoanalytic  theorist David Rapaport, who had befriended me on a visit to  Jerusalem a few years earlier. Rapaport believed that  psychoanalysis contained the elements of a valid theory of memory  and thought. The core ideas of that theory, he argued, were laid  out in the seventh chapter of Freud's "Interpretation of Dreams,"  which sketches a model of mental energy (cathexis). With the  other young people in Rapaport's circle, I studied that chapter  like a Talmudic text, and tried to derive from it experimental  predictions about short-term memory. This was a wonderful  experience, and I would have gone back if Rapaport had not died  suddenly later that year. I had enormous respect for his fierce  mind. Fifteen years after that summer, I published a book  entitled "Attention and Effort," which contained a theory of  attention as a limited resource. I realized only while writing  the acknowledgments for the book that I had revisited the terrain  to which Rapaport had first led me.

  Austen Riggs was a major intellectual  center for psychoanalysis, dedicated primarily to the treatment  of dysfunctional descendants of wealthy families. I was allowed  into the case conferences, which were normally scheduled on  Fridays, usually to evaluate a patient who had spent a month of  live-in observation at the clinic. Those attending would have  received and read, the night before, a folder with detailed notes  from every department about the person in question. There would  be a lively exchange of impressions among the staff, which  included the fabled Erik Erikson. Then the patient would come in  for a group interview, which was followed by a brilliant  discussion. On one of those Fridays, the meeting took place and  was conducted as usual, despite the fact that the patient had  committed suicide during the night. It was a remarkably honest  and open discussion, marked by the contradiction between the  powerful retrospective sense of the inevitability of the event  and the obvious fact that the event had not been foreseen. This  was another cognitive illusion to be understood. Many years  later, Baruch Fischhoff wrote, under my and Amos Tversky's  supervision, a beautiful PhD thesis that illuminated the  hindsight effect.

  In the spring of 1961, I wrote my  dissertation on a statistical and experimental analysis of the  relations between adjectives in the semantic differential. This  allowed me to engage in two of my favorite pursuits: the analysis  of complex correlational structures and FORTRAN programming. One  of the programs I wrote would take twenty minutes to run on the  university mainframe, and I could tell whether it was working  properly by the sequence of movement on the seven tape units that  it used. I wrote the thesis in eight days, typing directly on the  purple "ditto" sheets that we used for duplication at the time.  That was probably the last time I wrote anything without pain.  The paper itself, by sharp contrast, was so convoluted and dreary  that my teacher, Susan Ervin, memorably described the experience  of reading it as "wading through wet mush." I spent the summer of  1961 in the ophthalmology department, doing research on contour  interference. And then it was time to go home to Jerusalem, and  start teaching in the psychology department at the Hebrew  University.

  Training to become a  professional

  I loved teaching undergraduates and I was good at it. The  experience was consistently gratifying because the students were  so good: they were selected on the basis of a highly competitive  entrance exam, and most were easily PhD material. I took charge  of the basic first-year statistics class and, for some years,  taught both that course and the second-year course in research  methods, which also included a large dose of statistics. To teach  effectively I did a lot of serious thinking about valid  intuitions on which I could draw and erroneous intuitions that I  should teach students to overcome. I had no idea, of course, but  I was laying the foundation for a program of research on judgment  under uncertainty. Another course I was teaching concerned the  psychology of perception, which also contributed quite directly  to the same program.

  I had learned a lot in Berkeley, but I felt  that I had not been adequately trained to do research. I  therefore decided that in order to acquire the basic skills I  would need to have a proper laboratory and do regular science - I  needed to be a solid short-order cook before I could aspire to  become a chef. So I set up a vision lab, and over the next few  years I turned out competent work on energy integration in visual  acuity. At the same time, I was trying to develop a research  program to study affiliative motivation in children, using an  approach that I called a "psychology of single questions." My  model for this kind of psychology was research reported by Walter  Mischel (1961a, 1961b) in which he devised two questions that he  posed to samples of children in Caribbean islands: "You can have  this (small) lollipop today, or this (large) lollipop tomorrow,"  and "Now let's pretend that there is a magic man … who  could change you into anything that you would want to be, what  you would want to be?" The answer to the latter question was  scored 1, if it referred to a profession or to an  achievement-related trait, otherwise 0. The responses to these  lovely questions turned out to be plausibly correlated with  numerous characteristics of the child and the child's background.  I found this inspiring: Mischel had succeeded in creating a link  between an important psychological concept and a simple operation  to measure it. There was (and still is) almost nothing like it in  psychology, where concepts are commonly associated with  procedures that can be described only by long lists or by  convoluted paragraphs of prose.

  I got quite nice results in my one-question  studies, but never wrote up any of the work, because I had set  myself impossible standards: in order not to pollute the  literature, I wanted to report only findings that I had  replicated in detail at least once, and the replications were  never quite perfect. I realized only gradually that my  aspirations demanded more statistical power and therefore much  larger samples than I was intuitively inclined to run. This  observation also came in handy some time later.

  My achievements in research in these early  years were quite humdrum, but I was excited by several  opportunities to bring psychology to bear on the real world. For  these tasks, I teamed up with a colleague and friend, Ozer  Schild. Together, we designed a training program for  functionaries who were to introduce new immigrants from  underdeveloped countries, such as Yemen, to modern farming  practices (Kahneman and Schild, 1966). We also developed a  training course for instructors in the flight school of the Air  Force. Our faith in the usefulness of psychology was great, but  we were also well aware of the difficulties of changing behavior  without changing institutions and incentives. We may have done  some good, and we certainly learned a lot.

  I had the most satisfying Eureka experience  of my career while attempting to teach flight instructors that  praise is more effective than punishment for promoting  skill-learning. When I had finished my enthusiastic speech, one  of the most seasoned instructors in the audience raised his hand  and made his own short speech, which began by conceding that  positive reinforcement might be good for the birds, but went on  to deny that it was optimal for flight cadets. He said, "On many  occasions I have praised flight cadets for clean execution of  some aerobatic maneuver, and in general when they try it again,  they do worse. On the other hand, I have often screamed at cadets  for bad execution, and in general they do better the next time.  So please don't tell us that reinforcement works and punishment  does not, because the opposite is the case." This was a joyous  moment, in which I understood an important truth about the world:  because we tend to reward others when they do well and punish  them when they do badly, and because there is regression to the  mean, it is part of the human condition that we are statistically  punished for rewarding others and rewarded for punishing them. I  immediately arranged a demonstration in which each participant  tossed two coins at a target behind his back, without any  feedback. We measured the distances from the target and could see  that those who had done best the first time had mostly  deteriorated on their second try, and vice versa. But I knew that  this demonstration would not undo the effects of lifelong  exposure to a perverse contingency.

  My first experience of truly successful  research came in 1965, when I was on sabbatical leave at the  University of  Michigan, where I had been invited by Jerry Blum, who had a  lab in which volunteer participants performed various cognitive  tasks while in the grip of powerful emotional states induced by  hypnosis. Dilation of the pupil is one of the manifestations of  emotional arousal, and I therefore became interested in the  causes and consequences of changes of pupil size. Blum had a  graduate student called Jackson Beatty. Using primitive  equipment, Beatty and I made a real discovery: when people were  exposed to a series of digits they had to remember, their pupils  dilated steadily as they listened to the digits, and contracted  steadily when they recited the series. A more difficult  transformation task (adding 1 to each of a series of four digits)  caused a much larger dilation of the pupil. We quickly published  these results, and within a year had completed four articles, two  of which appeared in Science. Mental effort remained the  focus of my research during the subsequent year, which I spent at  Harvard.  During that year, I also heard a brilliant talk on experimental  studies of attention by a star English psychologist named Anne  Treisman, who would become my wife twelve years later. I was so  impressed that I committed myself to write a chapter on attention  for a Handbook in Cognitive Psychology. The Handbook was never  published, and my chapter eventually became a rather ambitious  book. The work on vision that I did that year was also more  interesting than the work I had been doing in Jerusalem. When I  returned home in 1967, I was, finally, a well-trained research  psychologist.

  The collaboration with Amos  Tversky

  From 1968 to 1969, I taught a graduate seminar on the  applications of psychology to real-world problems. In what turned  out to be a life-changing event, I asked my younger colleague  Amos Tversky to tell the class about what was going on in his  field of judgment and decision-making. Amos told us about the  work of his former mentor, Ward Edwards, whose lab was using a  research paradigm in which the subject is shown two bookbags  filled with poker chips. The bags are said to differ in their  composition (e.g., 70:30 or 30:70 white/red). One of them is  randomly chosen, and the participant is given an opportunity to  sample successively from it, and required to indicate after each  trial the probability that it came from the predominantly red  bag. Edwards had concluded from the results that people are  "conservative Bayesians": they almost always adjust their  confidence interval in the proper direction, but rarely far  enough. A lively discussion developed around Amos's talk. The  idea that people were conservative Bayesian did not seem to fit  with the everyday observation of people commonly jumping to  conclusions. It also appeared unlikely that the results obtained  in the sequential sampling paradigm would extend to the  situation, arguably more typical, in which sample evidence is  delivered all at once. Finally, the label of 'conservative  Bayesian' suggested the implausible image of a process that gets  the correct answer, then adulterates it with a bias. I learned  recently that one of Amos's friends met him that day and heard  about our conversation, which Amos described as having severely  shaken his faith in the neo-Bayesian idea. I do remember that  Amos and I decided to meet for lunch to discuss our hunches about  the manner in which probabilities are "really" judged. There we  exchanged personal accounts of our own recurrent errors of  judgment in this domain, and decided to study the statistical  intuitions of experts.

  I spent the summer of 1969 doing research  at the Applied Psychological Research Unit in Cambridge, England.  Amos stopped there for a few days on his way to the United  States. I had drafted a questionnaire on intuitions about  sampling variability and statistical power, which was based  largely on my personal experiences of incorrect research planning  and unsuccessful replications. The questionnaire consisted of a  set of questions, each of which could stand on its own - this was  to be another attempt to do psychology with single questions.  Amos went off and administered the questionnaire to participants  at a meeting of the Mathematical Psychology Association, and a  few weeks later we met in Jerusalem to look at the results and  write a paper.

  The experience was magical. I had enjoyed  collaborative work before, but this was something different. Amos  was often described by people who knew him as the smartest person  they knew. He was also very funny, with an endless supply of  jokes appropriate to every nuance of a situation. In his  presence, I became funny as well, and the result was that we  could spend hours of solid work in continuous mirth. The paper we  wrote was deliberately humorous - we described a prevalent belief  in the "law of small numbers," according to which the law of  large numbers extends to small numbers as well. Although we never  wrote another humorous paper, we continued to find amusement in  our work - I have probably shared more than half of the laughs of  my life with Amos.

  And we were not just having fun. I quickly  discovered that Amos had a remedy for everything I found  difficult about writing. No wet-mush problem for him: he had an  uncanny sense of direction. With him, movement was always  forward. Progress might be slow, but each of the myriad of  successive drafts that we produced was an improvement - this was  not something I could take for granted when working on my own.  Amos's work was always characterized by confidence and by a crisp  elegance, and it was a joy to find those characteristics now  attached to my ideas as well. As we were writing our first paper,  I was conscious of how much better it was than the more hesitant  piece I would have written by myself. I don't know exactly what  it was that Amos found to like in our collaboration - we were not  in the habit of trading compliments -but clearly he was also  having a good time. We were a team, and we remained in that mode  for well over a decade. The Nobel Prize was awarded for work that  we produced during that period of intense collaboration.

  At the beginning of our collaboration, we  quickly established a rhythm that we maintained during all our  years together. Amos was a night person, and I was a morning  person. This made it natural for us to meet for lunch and a long  afternoon together, and still have time to do our separate  things. We spent hours each day, just talking. When Amos's first  son Oren, then fifteen months old, was told that his father was  at work, he volunteered the comment "Aba talk Danny." We were not  only working, of course - we talked of everything under the sun,  and got to know each other's mind almost as well as our own. We  could (and often did) finish each other's sentences and complete  the joke that the other had wanted to tell, but somehow we also  kept surprising each other.

  We did almost all the work on our joint  projects while physically together, including the drafting of  questionnaires and papers. And we avoided any explicit division  of labor. Our principle was to discuss every disagreement until  it had been resolved to mutual satisfaction, and we had  tie-breaking rules for only two topics: whether or not an item  should be included in the list of references (Amos had the  casting vote), and who should resolve any issue of English  grammar (my dominion). We did not initially have a concept of a  senior author. We tossed a coin to determine the order of  authorship of our first paper, and alternated from then on until  the pattern of our collaboration changed in the 1980s.

  One consequence of this mode of work was  that all our ideas were jointly owned. Our interactions were so  frequent and so intense that there was never much point in  distinguishing between the discussions that primed an idea, the  act of uttering it, and the subsequent elaboration of it. I  believe that many scholars have had the experience of discovering  that they had expressed (sometimes even published) an idea long  before they really understood its significance. It takes time to  appreciate and develop a new thought. Some of the greatest joys  of our collaboration-and probably much of its success - came from  our ability to elaborate each other's nascent thoughts: if I  expressed a half-formed idea, I knew that Amos would be there to  understand it, probably more clearly than I did, and that if it  had merit he would see it. Like most people, I am somewhat  cautious about exposing tentative thoughts to others - I must  first make sure that they are not idiotic. In the best years of  the collaboration, this caution was completely absent. The mutual  trust and the complete lack of defensiveness that we achieved  were particularly remarkable because both of us - Amos even more  than I - were known to be severe critics. Our magic worked only  when we were by ourselves. We soon learned that joint  collaboration with any third party should be avoided, because we  became competitive in a threesome.

  Amos and I shared the wonder of together  owning a goose that could lay golden eggs - a joint mind that was  better than our separate minds. The statistical record confirms  that our joint work was superior, or at least more influential,  than the work we did individually (Laibson and Zeckhauser, 1998).  Amos and I published eight journal articles during our peak years  (1971-1981), of which five had been cited more than a thousand  times by the end of 2002. Of our separate works, which in total  number about 200, only Amos' theory of similarity (Tversky, 1977)  and my book on attention (Kahneman, 1973) exceeded that  threshold. The special style of our collaborative work was  recognized early by a referee of our first theoretical paper (on  representativeness), who caused it to be rejected by  Psychological Review. The eminent psychologist who wrote  that review - his anonymity was betrayed years later - pointed  out that he was familiar with the separate lines of work that  Amos and I had been pursuing, and considered both quite  respectable. However, he added the unusual remark that we seemed  to bring out the worst in each other, and certainly should not  collaborate. He found most objectionable our method of using  multiple single questions as evidence - and he was quite wrong  there as well.

  The Science '74 article and the  rationality debate

  From 1971 to 1972, Amos and I were at the Oregon  Research Institute (ORI) in Eugene, a year that was by far  the most productive of my life. We did a considerable amount of  research and writing on the availability heuristic, on the  psychology of prediction, and on the phenomena of anchoring and  overconfidence - thereby fully earning the label "dynamic duo"  that our colleagues attached to us. Working evenings and nights,  I also completely rewrote my book on Attention and Effort,  which went to the publisher that year, and remains my most  significant independent contribution to psychology.

  At ORI, I came into contact for the first  time with an exciting community of researchers that Amos had  known since his student days at Michigan: Paul Slovic, Sarah  Lichtenstein, and Robyn Dawes. Lewis Goldberg was also there, and  I learned much from his work on clinical and actuarial judgment,  and from Paul Hoffman's ideas about paramorphic modeling. ORI was  one of the major centers of judgment research, and I had the  occasion to meet quite a few of the significant figures of the  field when they came visiting, Ken Hammond among them.

  Some time after our return from Eugene,  Amos and I settled down to review what we had learned about three  heuristics of judgment (representativeness, availability, and  anchoring) and about a list of a dozen biases associated with  these heuristics. We spent a delightful year in which we did  little but work on a single article. On our usual schedule of  spending afternoons together, a day in which we advanced by a  sentence or two was considered quite productive. Our enjoyment of  the process gave us unlimited patience, and we wrote as if the  precise choice of every word were a matter of great moment.

  We published the article in Science  because we thought that the prevalence of systematic biases in  intuitive assessments and predictions could possibly be of  interest to scholars outside psychology. This interest, however,  could not be taken for granted, as I learned in an encounter with  a well-known American philosopher at a party in Jerusalem. Mutual  friends had encouraged us to talk about the research that Amos  and I were doing, but almost as soon as I began my story he  turned away, saying, "I am not really interested in the  psychology of stupidity."

  The Science article turned out to be  a rarity: an empirical psychological article that (some)  philosophers and (a few) economists could and did take seriously.  What was it that made readers of the article more willing to  listen than the philosopher at the party? I attribute the unusual  attention at least as much to the medium as to the message. Amos  and I had continued to practice the psychology of single  questions, and the Science article - like others we wrote  - incorporated questions that were cited verbatim in the text.  These questions, I believe, personally engaged the readers and  convinced them that we were concerned not with the stupidity of  Joe Public but with a much more interesting issue: the  susceptibility to erroneous intuitions of intelligent,  sophisticated, and perceptive individuals such as themselves.  Whatever the reason, the article soon became a standard reference  as an attack on the rational-agent model, and it spawned a large  literature in cognitive science, philosophy, and psychology. We  had not anticipated that outcome.

  I realized only recently how fortunate we  were not to have aimed deliberately at the large target we  happened to hit. If we had intended the article as a challenge to  the rational model, we would have written it differently, and the  challenge would have been less effective. An essay on rationality  would have required a definition of that concept, a treatment of  boundary conditions for the occurrence of biases, and a  discussion of many other topics about which we had nothing of  interest to say. The result would have been less crisp, less  provocative, and ultimately less defensible. As it was, we  offered a progress report on our study of judgment under  uncertainty, which included much solid evidence. All inferences  about human rationality were drawn by the readers themselves.

  The conclusions that readers drew were  often too strong, mostly because existential quantifiers, as they  are prone to do, disappeared in the transmission. Whereas we had  shown that (some, not all) judgments about uncertain events are  mediated by heuristics, which (sometimes, not always) produce  predictable biases, we were often read as having claimed that  people cannot think straight. The fact that men had walked on the  moon was used more than once as an argument against our position.  Because our treatment was mistakenly taken to be inclusive, our  silences became significant. For example, the fact that we had  written nothing about the role of social factors in judgment was  taken as an indication that we thought these factors were  unimportant. I suppose that we could have prevented at least some  of these misunderstandings, but the cost of doing so would have  been too high.

  The interpretation of our work as a broad  attack on human rationality - rather than as a critique of the  rational-agent model - attracted much opposition, some quite  harsh and dismissive. Some of the critiques were normative,  arguing that we compared judgments to inappropriate normative  standards (Cohen, 1981; Gigerenzer, 1991, 1996). We were also  accused of spreading a tendentious and misleading message that  exaggerated the flaws of human cognition (Lopes, 1991, and many  others). The idea of systematic bias was rejected as unsound on  evolutionary grounds (Cosmides & Tooby, 1996). Some authors  dismissed the research as a collection of artificial puzzles  designed to fool undergraduates. Numerous experiments were  conducted over the years, to show that cognitive illusions could  "be made to disappear" and that heuristics had been invented to  explain "biases that do not exist" (Gigerenzer, 1991). After  participating in a few published skirmishes in the early 80's,  Amos and I adopted a policy of not criticizing the critiques of  our work, although we eventually felt compelled to make an  exception (Kahneman and Tversky, 1996).

  A young colleague and I recently reviewed  the experimental literature, and concluded that the empirical  controversy about the reality of cognitive illusions dissolves  when viewed in the perspective of a dual-process model (Kahneman  and Frederick, 2002). The essence of such a model is that  judgments can be produced in two ways (and in various mixtures of  the two): a rapid, associative, automatic, and effortless  intuitive process (sometimes called System 1), and a slower,  rule-governed, deliberate and effortful process (System 2)  (Sloman, 1996; Stanovich and West, 1999). System 2 'knows" some  of the rules that intuitive reasoning is prone to violate, and  sometimes intervenes to correct or replace erroneous intuitive  judgments. Thus, errors of intuition occur when two conditions  are satisfied: System 1 generates the error and System 2 fails to  correct. In this view, the experiments in which cognitive  illusions were "made to disappear" did so by facilitating the  corrective operations of System 2. They tell us little about the  intuitive judgments that are suppressed.

  If the controversy is so simply resolved,  why was it not resolved in 1971, or in 1974? The answer that  Frederick and I proposed refers to the conversational context in  which the early work was done:
  

    A comprehensive psychology of intuitive judgment cannot    ignore such controlled thinking, because intuition can be    overridden or corrected by self-critical operations, and    because intuitive answers are not always available. But this    sensible position seemed irrelevant in the early days of    research on judgment heuristics. The authors of the "law of    small numbers" saw no need to examine correct statistical    reasoning. They believed that including easy questions in the    design would insult the participants and bore the readers. More    generally, the early studies of heuristics and biases displayed    little interest in the conditions under which intuitive    reasoning is preempted or overridden - controlled reasoning    leading to correct answers was seen as a default case that    needed no explaining. A lack of concern for boundary conditions    is typical of "young" research programs, which naturally focus    on demonstrating new and unexpected effects, not on making them    disappear. (Kahneman and Frederick, 2002, p. 50).
  

  What happened, I suppose, is that because  the 1974 paper was influential it altered the context in which it  was read in subsequent years. Its being misunderstood was a  direct consequence of its being taken seriously. I wonder how  often this occurs.

  Amos and I always dismissed the criticism  that our focus on biases reflected a generally pessimistic view  of the human mind. We argued that this criticism confuses the  medium of bias research with a message about rationality. This  confusion was indeed common. In one of our demonstrations of the  availability heuristic, for example, we asked respondents to  compare the frequency with which some letters appeared in the  first and in the third position in words. We selected letters  that in fact appeared more frequently in the third position, and  showed that even for these letters the first position was judged  more frequent, as would be predicted on the idea that it is  easier to search through a mental dictionary by the first letter.  The experiment was used by some critics as an example of our own  confirmation bias, because we had demonstrated availability only  in cases in which this heuristic led to bias. But this criticism  assumes that our aim was to demonstrate biases, and misses the  point of what we were trying to do. Our aim was to show that the  availability heuristic controls frequency estimates even when  that heuristic leads to error - an argument that cannot be  made when the heuristic leads to correct responses, as it often  does.

  There is no denying, however, that the name  of our method and approach created a strong association between  heuristics and biases, and thereby contributed to giving  heuristics a bad name, which we did not intend. I recently came  to realize that the association of heuristics and biases has  affected me as well. In the course of an exchange of messages  with Ralph Hertwig (no fan of heuristics and biases), I noticed  that the phrase "judging by representativeness" was in my mind a  label for a cluster of errors in intuitive statistical judgment.  Judging probability by representativeness is indeed associated  with systematic errors. But a large component of the process is  the judgment of representativeness, and that judgment is  often subtle and highly skilled. The feat of the master chess  player who instantly recognizes a position as "white mates in  three" is an instance of judgment of representativeness. The  undergraduate who instantly recognizes that enjoyment of puns is  more representative of a computer scientist than of an accountant  is also exhibiting high skill in a social and cultural judgment.  My long-standing failure to associate specific benefits to the  concept of representativeness was a revealing mistake.

  What did I learn from the controversy about  heuristics and biases? Like most protagonists in debates, I have  few memories of having changed my mind under adversarial  pressure, but I have certainly learned more than I know. For  example, I am now quick to reject any description of our work as  demonstrating human irrationality. When the occasion arises, I  carefully explain that research on heuristics and biases only  refutes an unrealistic conception of rationality, which  identifies it as comprehensive coherence. Was I always so  careful? Probably not. In my current view, the study of judgment  biases requires attention to the interplay between intuitive and  reflective thinking, which sometimes allows biased judgments and  sometimes overrides or corrects them. Was this always as clear to  me as it is now? Probably not. Finally, I am now very impressed  by the observation I mentioned earlier, that the most highly  skilled cognitive performances are intuitive, and that many  complex judgments share the speed, confidence and accuracy of  routine perception. This observation is not new to me, but did it  always loom as large in my views as it now does? Almost certainly  not.

  As my obvious struggle with this topic  reveals, I thoroughly dislike controversies where it is clear  that no minds will be changed. I feel diminished by losing my  objectivity when in point-scoring mode, and downright humiliated  when I get angry. Indeed, my phobia for professional anger is  such that I have allowed myself for many years the luxury of  refusing to referee papers that might arouse that emotion: If the  tone is snide, or the review of the facts more tendentious than  normal, I return the paper back to the editor without commenting  on it. I consider myself fortunate not to have had too many of  the nasty experiences of professional quarrels, and am grateful  for the occasional encounters with open minds across lines of  sharp debate (Ayton, 1998; Klein, 2000).

  Prospect theory

  After the publication of our paper on judgment in Science  in 1974, Amos suggested that we study decision-making together.  This was a field in which he was already an established star, and  about which I knew very little. For an introduction, he suggested  that I read the relevant chapters of the text "Mathematical  Psychology," of which he was a co-author (Coombs, Dawes and  Tversky, 1970). Utility theory and the paradoxes of Allais and  Ellsberg were discussed in the book, along with some of the  classic experiments in which major figures in the field had  joined in an effort to measure the utility function for money by  eliciting choices between simple gambles.

  I learned from the book that the name of  the game was the construction of a theory that would explain  Allais's paradox parsimoniously. As psychological questions go,  this was not a difficult one, because Allais's famous problems  are, in effect, an elegant way to demonstrate that the subjective  response to probability is not linear. The subjective  non-linearity is obvious: the difference between probabilities of  .10 and .11 is clearly less impressive than the difference  between 0 and .01, or between .99 and 1.00. The difficulty and  the paradox exist only for decision theorists, because the  non-linear response to probability produces preferences that  violate compelling axioms of rational choice and are therefore  incompatible with standard expected utility theory. The natural  response of a decision theorist to the Allais paradox, certainly  in 1975 and probably even today, would be to search for a new set  of axioms that have normative appeal and yet permit the  non-linearity. The natural response of psychologists was to set  aside the issue of rationality and to develop a descriptive  theory of the preferences that people actually have, regardless  of whether or not these preferences can be justified.

  The task we set for ourselves was to  account for observed preferences in the quaintly restricted  universe within which the debate about the theory of choice has  traditionally been conducted: monetary gambles with few outcomes  (all positive), and definite probabilities. This was an empirical  question, and data were needed. Amos and I solved the data  collection problem with a method that was both efficient and  pleasant. We spent our hours together inventing interesting  choices and examining our preferences. If we agreed on the same  choice we provisionally assumed that other people would also  accept it, and we went on to explore its theoretical  implications. This unusual method enabled us to move quickly, and  we constructed and discarded models at a dizzying rate. I have a  distinct memory of a model that was numbered 37, but cannot vouch  for the accuracy of our count.

  As was the case in our work on judgment,  our central insights were acquired early and, as was the case in  our work on judgment, we spent a vast amount of time and effort  before publishing a paper that summarized those insights  (Kahneman and Tversky, 1979). The first insight came as a result  of my naïveté. When reading the mathematical psychology  textbook, I was puzzled by the fact that all the choice problems  were described in terms of gains and losses (actually, almost  always gains), whereas the utility functions that were supposed  to explain the choices were drawn with wealth as the abscissa.  This seemed unnatural, and psychologically unlikely. We  immediately decided to adopt changes and/or differences as  carriers of utility. We had no inkling that this obvious move was  truly fundamental, or that it would open the path to behavioral  economics. Harry Markowitz, who won the Nobel Prize in economics  in 1990, had proposed changes of wealth as carriers of utility in  1952, but he did not take this idea very far.

  The shifts from wealth to changes of wealth  as carriers of utility is significant because of a property of  preferences that we later labeled loss-aversion: the  response to losses is consistently much more intense than the  response to corresponding gains, with a sharp kink in the value  function at the reference point. Loss aversion is manifest in the  extraordinary reluctance to accept risk that is observed when  people are offered a gamble on the toss of a coin: most will  reject a gamble in which they might lose $20, unless they are  offered more than $40 if they win. The concept of loss aversion  was, I believe, our most useful contribution to the study of  decision making. The asymmetry between gains and losses solves  quite a few puzzles, including the widely noted and economically  irrational distinction that people draw between opportunity costs  and 'real' losses. Loss aversion also helps explain why  real-estate markets dry up for long periods when prices are down,  and it contributes to the explanation of a widespread bias  favoring the status quo in decision making. Finally, the  asymmetric consideration of gains and losses extends to the  domain of moral intuitions, in which imposing losses and failing  to share gains are evaluated quite differently. But of course,  none of that was visible to Amos and me when we first decided to  assume a kinked value function - we needed that kink to account  for choices between gambles.

  Another set of early insights came when  Amos suggested that we flip the signs of outcomes in the problems  we had been considering. The result was exciting. We immediately  detected a remarkable pattern, which we called "reflection":  changing the signs of all outcomes in a pair of gambles almost  always caused the preference to change from risk averse to risk  seeking, or viceversa. For example, we both preferred a sure gain  of $900 over a .9 probability of gaining $1,000 (or nothing), but  we preferred a gamble with a .9 probability of losing $1,000 over  a sure loss of $900. We were not the first to observe this  pattern. Raiffa (1968) and Williams (1966) knew about the  prevalence of risk-seeking in the negative domain. But ours was  apparently the first serious attempt to make something of it.

  We soon had a draft of a theory of risky  choice, which we called "value theory" and presented at a  conference in the spring of 1975. We then spent about three years  polishing it, until we were ready to submit the article for  publication. Our effort during those years was divided between  the tasks of exploring interesting implications of our  theoretical formulation and developing answers to all plausible  objections. To amuse ourselves, we invented the specter of an  ambitious graduate student looking for flaws, and we labored to  make that student's task as thankless as possible. The most novel  idea of prospect theory occurred to us in that defensive context.  It came quite late, as we were preparing the final version of the  paper. We were concerned with the fact that a straightforward  application of our model implied that the value of the prospect  ($100, .01; $100, .01) is larger than the value of ($100, .02).  The prediction is wrong, of course, because most decision makers  will spontaneously transform the former prospect into the latter  and treat them as equivalent in subsequent operations of  evaluation and choice. To eliminate the problem we proposed that  decision-makers, prior to evaluating the prospects, perform an  editing operation that collects similar outcomes and adds their  probabilities. We went on to propose several other editing  operations that provided an explicit and psychologically  plausible defense against a variety of superficial  counter-examples to the core of the theory. We had succeeded in  making life quite difficult for that pedantic graduate student.  But we had also made a truly significant advance, by making it  explicit that the objects of choice are mental representations,  not objective states of the world. This was a large step toward  the development of a concept of framing, and eventually toward a  new critique of the model of the rational agent.

  When we were ready to submit the work for  publication, we deliberately chose a meaningless name for our  theory: "prospect theory." We reasoned that if the theory ever  became well known, having a distinctive label would be an  advantage. This was probably wise.

  I looked at the 1975 draft recently, and  was struck by how similar it is to the paper that was eventually  published, and also by how different the two papers are. Most of  the key ideas, most of the key examples, and much of the wording  were there in the early draft. But that draft lacks the authority  that was gained during the years that we spent anticipating  objections. "Value theory" would not have survived the close  scrutiny that a significant article ultimately gets from  generations of scholars and students, who only are obnoxious if  you give them a chance.

  We published the paper in  Econometrica. The choice of venue turned out to be  important; the identical paper, published in Psychological  Review, would likely have had little impact on economics. But  our decision was not guided by a wish to influence economics.  Econometrica just happened to be the journal where the  best papers on decision-making to date had been published, and we  were aspiring to be in that company.

  And there was another way in which the  impact of prospect theory depended crucially on the medium, as  well as the message. Prospect theory was a formal theory, and its  formal nature was the key to the impact it had in economics.  Every discipline of social science, I believe, has some ritual  tests of competence, which must be passed before a piece of work  is considered worthy of attention. Such tests are necessary to  prevent information overload, and they are also important aspects  of the tribal life of the disciplines. In particular, they allow  insiders to ignore just about anything that is done by members of  other tribes, and to feel no scholarly guilt about doing so. To  serve this screening function efficiently, the competence tests  usually focus on some aspect of form or method, and have little  or nothing to do with substance. Prospect theory passed such a  test in economics, and its observations became a legitimate  (though optional) part of the scholarly discourse in that  discipline. It is a strange and rather arbitrary process that  selects some pieces of scientific writing for relatively enduring  fame while committing most of what is published to almost  immediate oblivion.

  Framing and mental accounting

  Amos and I completed prospect theory during the academic year of  1977 to 1978, which I spent at the Center for Advanced Studies at  Stanford,  while he was visiting the psychology department there. Around  that time, we began work on our next project, which became the  study of framing. This was also the year in which the second most  important professional friendship in my life - with Richard  Thaler - had its start.

  A framing effect is demonstrated by  constructing two transparently equivalent versions of a given  problem, which nevertheless yield predictably different choices.  The standard example of a framing problem, which was developed  quite early, is the 'lives saved, lives lost' question, which  offers a choice between two public-health programs proposed to  deal with an epidemic that is threatening 600 lives: one program  will save 200 lives, the other has a 1/3 chance of saving all 600  lives and a 2/3 chance of saving none. In this version, people  prefer the program that will save 200 lives for sure. In the  second version, one program will result in 400 deaths, the other  has a 2/3 chance of 600 deaths and a 1/3 chance of no deaths. In  this formulation most people prefer the gamble. If the same  respondents are given the two problems on separate occasions,  many give incompatible responses. When confronted with their  inconsistency, people are quite embarrassed. They are also quite  helpless to resolve the inconsistency, because there are no moral  intuitions to guide a choice between different sizes of a  surviving population.

  Amos and I began creating pairs of problems  that revealed framing effects while working on prospect theory.  We used them to show sensitivity to gains and losses (as in the  lives example), and to illustrate the inadequacy of a formulation  in which the only relevant outcomes are final states. In that  article, we also showed that a single-stage gamble could be  rearranged as a two-stage gamble in a manner that left the  bottom-line probabilities and outcomes unchanged but reversed  preferences. Later, we developed examples in which respondents  are asked to make simultaneous choices in two problems, A and B.  One of the problems involves gains and elicits a risk-averse  choice; the other problem involves losses and elicits  risk-seeking. A majority of respondents made both these choices.  However, the problems were constructed so that the combination of  choices that people made was actually dominated by the  combination of the options they had rejected.

  These are not parlor-game demonstrations of  human stupidity. The ease with which framing effects can be  demonstrated reveals a fundamental limitation of the human mind.  In a rational-agent model, the agent's mind functions just as she  would like it to function. Framing effects violate that basic  requirement: the respondents who exhibit susceptibility to  framing effects wish their minds were able to avoid them. We were  able to conceive of only two kinds of mind that would avoid  framing effects: (1) If responses to all outcomes and  probabilities were strictly linear, the procedures that we used  to produce framing effects would fail. (2) If individuals  maintained a single canonical and all-inclusive view of their  outcomes, truly equivalent problems would be treated  equivalently. Both conditions are obviously impossible. Framing  effects violate a basic requirement of rationality which we  called invariance (Kahneman and Tversky, 1984) and Arrow (1982)  called extensionality. It took us a long time and several  iterations to develop a forceful statement of this contribution  to the rationality debate, which we presented several years after  our framing paper (Tversky and Kahneman, 1986).

  Another advance that we made in our first  framing article was the inclusion of riskless choice problems  among our demonstrations of framing. In making that move, we had  help from a new friend. Richard Thaler was a young economist,  blessed with a sharp and irreverent mind. While still in graduate  school, he had trained his ironic eye on his own discipline and  had collected a set of pithy anecdotes demonstrating obvious  failures of basic tenets of economic theory in the behavior of  people in general - and of his very conservative professors in  Rochester in particular. One key observation was the endowment  effect, which Dick illustrated with the example of the owner of a  bottle of old wine, who would refuse to sell it for $200 but  would not pay as much as $100 to replace it if it broke. Sometime  in 1976, a copy of the 1975 draft of prospect theory got into  Dick's hands, and that event made a significant difference to our  lives. Dick realized that the endowment effect, which is a  genuine puzzle in the context of standard economic theory, is  readily explained by two assumptions derived from prospect  theory. First, the carriers of utility are not states (owning or  not owning the wine), but changes - getting the wine or giving it  up. And giving up is weighted more than getting, by loss  aversion. When Dick learned that Amos and I would be in Stanford  in 1977/8, he secured a visiting appointment at the Stanford  branch of the National Bureau of Economic Research, which is  located on the same hill as the Center for Advanced Studies. We  soon became friends, and have ever since had a considerable  influence on each other's thinking.

  The endowment effect was not the only thing  we learned from Dick. He had also developed a list of phenomena  of what we now call "mental accounting." Mental accounting  describes how people violate rationality by failing to maintain a  comprehensive view of outcomes, and by failing to treat money as  fungible. Dick showed how people segregate their decisions into  separate accounts, then struggle to keep each of these accounts  in the black. One of his compelling examples was the couple who  drove through a blizzard to a basketball game because they had  already paid for the tickets, though they would have stayed at  home if the tickets had been free. As this example illustrates,  Dick had independently developed the skill of doing "one-question  economics." He inspired me to invent another story, in which a  person who comes to the theater realizes that he has lost his  ticket (in one version), or an amount of cash equal to the ticket  value (in another version). People report that they would be very  likely still to buy a ticket if they had lost the cash,  presumably because the loss has been charged to general revenue.  On the other hand, they describe themselves as quite likely to go  home if they have lost an already purchased ticket, presumably  because they do not want to pay twice to see the same show.

  Behavioral economics

  Our interaction with Thaler eventually proved to be more fruitful  than we could have imagined at the time, and it was a major  factor in my receiving the Nobel Prize. The committee cited me  "for having integrated insights from psychological research into  economic science ….". Although I do not wish to renounce  any credit for my contribution, I should say that in my view the  work of integration was actually done mostly by Thaler and the  group of young economists that quickly began to form around him,  starting with Colin Camerer and George Loewenstein, and followed  by the likes of Matthew Rabin, David Laibson, Terry Odean, and  Sendhil Mullainathan. Amos and I provided quite a few of the  initial ideas that were eventually integrated into the thinking  of some economists, and prospect theory undoubtedly afforded some  legitimacy to the enterprise of drawing on psychology as a source  of realistic assumptions about economic agents. But the founding  text of behavioral economics was the first article in which  Thaler (1980) presented a series of vignettes that challenged  fundamental tenets of consumer theory. And the respectability  that behavioral economics now enjoys within the discipline was  secured, I believe, by some important discoveries Dick made in  what is now called behavioral finance, and by the series of  "Anomalies" columns that he published in every issue of the  Journal of Economic Perspectives from 1987 to 1990, and  has continued to write occasionally since that time.

  In 1982, Amos and I attended a meeting of  the Cognitive Science Society in Rochester, where we had a drink  with Eric Wanner, a psychologist who was then vice-president of  the Sloan Foundation. Eric told us that he was interested in  promoting the integration of psychology and economics, and asked  for our advice on ways to go about it. I have a clear memory of  the answer we gave him. We thought that there was no way to  "spend a lot of money honestly" on such a project, because  interest in interdisciplinary work could not be coerced. We also  thought that it was pointless to encourage psychologists to make  themselves heard by economists, but that it could be useful to  encourage and support the few economists who were interested in  listening. Thaler's name surely came up. Soon after that  conversation, Wanner became the president of the Russell Sage  Foundation, and he brought the psychology/economics project with  him. The first grant that he made in that program was for Dick  Thaler to spend an academic year (1984-85) visiting me at the  University of  British Columbia, in Vancouver.

  That year was one of the best in my career.  We worked as a trio that also included the economist Jack  Knetsch, with whom I had already started constructing surveys on  a variety of issues, including valuation of the environment and  public views about fairness in the marketplace. Jack had done  experimental studies of the endowment effect and had seen the  implications of that effect for the Coase theorem and for issues  of environmental policy. We made a very good team: Jack's wisdom  and imperturbable calm withstood the stress of Dick's boisterous  temperament and of my perfectionist anxieties and intellectual  restlessness.

  We did a lot together that year. We  conducted a series of market experiments involving real goods  (the "mugs" studies), which eventually became a standard in that  literature (Kahneman, Knetsch and Thaler, 1990). We also  conducted multiple surveys in which we used experimentally varied  vignettes to identify the rules of fairness that the public would  apply to merchants, landlords, and employers (Kahneman, Knetsch  and Thaler, 1986a). Our central observation was that in many  contexts the existing situation (e.g., price, rent, or wage)  defines a "reference transaction," to which the transactor  (consumer, tenant, and employee) has an entitlement - the  violation of such entitlements is considered unfair and may evoke  retaliation. For example, cutting the wages of an employee merely  because he could be replaced by someone who would accept a lower  wage is unfair, although paying a lower wage to the replacement  of an employee who quit is entirely acceptable. We submitted the  paper to the American Economic Review and were utterly  surprised by the outcome: the paper was accepted without  revision. Luckily for us, the editor had asked two economists  quite open to our approach to review the paper. We later learned  that one of the referees was George Akerlof and the  other was Alan Olmstead, who had studied the failures of markets  to clear during an acute gas shortage.

  One question that arose during this  research was whether people would be wiling to pay something to  punish another agent who treated them "unfairly", and in some  circumstances would share a windfall with a stranger in an effort  to be "fair". We decided to investigate these ideas using  experiments for real stakes. The games that we invented for this  purpose have become known as the ultimatum game and the dictator  game. Alas, while writing up our second paper on fairness  (Kahneman, Knetsch and Thaler, 1986b) we learned that we had been  scooped on the ultimatum game by Werner Guth and his colleagues,  who had published experiments using the same design a few years  earlier. I remember being quite crestfallen when I learned this.  I would have been even more depressed if I had known how  important the ultimatum game would eventually become.

  Most of the economics I know I learned that  year, from Jack and Dick, my two willing teachers, and from what  was in fact my first experience of communicating across tribal  boundaries. I was also much impressed by an experimental game  that Dick Thaler, James Brander, and I invented and called the N*  game. The game is played by a group of, say, fifteen people. On  each trial, a number 0< N* <15 is announced. The  participants then make simultaneous choices of whether or not to  "enter." Those who decide to enter announce their choice  simultaneously. The payoff to the N entrants depends on their  number, according to the following formula: $.25(N* - N). We  played the game a few times, once with the faculty of the  psychology department at U.B.C. The results, although not  surprising to an economist, struck me as magical. Within very few  trials, a pattern emerged in which the number of entrants, N, was  within 1 or 2 of N*, with no obvious systematic tendency to be  higher or lower than N*. The group was doing the right thing  collectively, although conversations with the participants and  the obvious statistical analyses did not reveal any consistent  strategies that made sense. It took me some time to realize that  the magic we were observing was an equilibrium: the pattern we  saw existed because no other pattern could be sustained. This  idea had not been in my intellectual bag of tools. We never  formally published the N* game - I described it informally in  Kahneman (1987) - but it has been taken up by others (Erev &  Rapoport, 1998).

  That was the closest my research ever came  to core economics, and since that time I have been mostly  cheering Thaler and behavioral economics from the sidelines.  There has been much to cheer about. As a mark of the progress  that has been made, I recall a seminar in psychology and  economics that I co-taught with George Akerlof, after Anne  Treisman and I had moved from the University of British Columbia  to Berkeley in 1986. I remember being struck by the reverence  with which the rationality assumption was treated even by a free  thinker such as George, and also by his frequent warnings to the  students that they should not let themselves be seduced by the  material we were presenting, lest their careers be permanently  damaged. His advice to them was to stick to what he called  "meat-and-potatoes economics," at least until their careers were  secure. This opinion was quite common at the time. When Matthew  Rabin joined the Berkeley economics department as a young  assistant professor and chose to immerse himself in psychology,  many considered the move professional suicide. Some fifteen years  later, Rabin had earned the Clark medal, and George Akerlof had  delivered a Nobel lecture entitled "Behavioral  Macroeconomics."

  Eric Wanner and the Russell Sage Foundation  continued to support behavioral economics over the years. I was  instrumental in the idea of using some of that support to set up  a summer school for graduate students and young faculty in that  field, and I helped Dick Thaler and Colin Camerer organize the  first one, in 1994. When the fifth summer school convened in  2002, David Laibson, who had been a participant in 1994, was  tenured at Harvard and was one of the three organizers. Terrance  Odean and Sendhil Mullainathan, who had also participated as  students, came back to lecture as successful researchers with  positions in two of the best universities in the world. It was a  remarkable experience to hear Matthew Rabin teach a set of  guidelines for developing theories in behavioral economics -  including the suggestion that the standard economic model should  be a special case of the more complex and general models that  were to be constructed. We had come a long way.

  Although behavioral economics has enjoyed  much more rapid progress and gained more respectability in  economics than appeared possible fifteen years ago, it is still a  minority approach and its influence on most fields of economics  is negligible. Many economists believe that it is a passing fad,  and some hope that it will be. The future may prove them right.  But many bright young economists are now betting their careers on  the expectation that the current trend will last. And such  expectations have a way of being self-fulfilling.

  Later years

  Anne Treisman and I married and moved together to U.B.C. in 1978,  and Amos and Barbara Tversky settled in Stanford that year. Amos  and I were then at the peak of our joint game, and completely  committed to our collaboration. For a few years, we managed to  maintain it, by spending every second weekend together and by  placing multiple phone calls each day, some lasting several  hours. We completed the study of framing in that mode, as well as  a study of the 'conjunction fallacy' in judgment (Tversky and  Kahneman, 1983). But eventually the goose that had laid the  golden eggs languished, and our collaboration tapered off.  Although this outcome now appears inevitable, it came as a  painful surprise to us. We had completely failed to appreciate  how critically our successful interaction had depended on our  being together at the birth of every significant idea, on our  rejection of any formal division of labor, and on the infinite  patience that became a luxury when we could meet only  periodically. We struggled for years to revive the magic we had  lost, but in vain.

  We were again trying when Amos died. When  he learned in the early months of 1996 that he had only a few  months to live, we decided to edit a joint book on  decision-making that would cover some of the progress that had  been made since we had started working together on the topic more  than twenty years before (Kahneman and Tversky, 2000). We planned  an ambitious preface as a joint project, but I think we both knew  from the beginning that we would not be granted enough time to  complete it. The preface I wrote alone was probably my most  painful writing experience.

During the intervening years, of course, we  had continued to work, sometimes together sometimes with other  collaborators. Amos took the lead in our most important joint  piece, an extension of prospect theory to the multipleoutcome  case in the spirit of rank-dependent models. He also carried out  spectacular studies of the role of argument and conflict in  decision-making, in collaborations with Eldar Shafir and with  Itamar Simonson, as well as influential work on violations of  procedural invariance in collaborations with Shmuel Sattath and  with Paul Slovic. He engaged in a deep exploration of the  mathematical structure of decision theories with Peter Wakker.  And, in his last years, Amos was absorbed in the development of  support theory, a general approach to thinking under uncertainty  that his students have continued to explore. These are only his  major programmatic research efforts in the field of  decision-making - he did much more.

  I, too, kept busy, and also kept moving.  Anne Treisman and I moved to UC Berkeley in 1986, and from there  to Princeton in 1993, where I happily took a split appointment  that located me part-time in the Woodrow Wilson  School of Public Affairs. Moving East also made it easier to  maintain frequent contacts with friends, children and adored  grandchildren in Israel.

  Over the years I enjoyed productive  collaborations with Dale Miller in the development of a theory of  counterfactual thinking (Kahneman and Miller, 1986), and with  Anne Treisman, in studies of visual attention and object  perception. In addition to the work on fairness and on the  endowment effect that we did with Dick Thaler, Jack Knetsch and I  carried out studies of the valuation of public goods that became  quite controversial and had a great influence on my own thinking.  Further studies of that problem with Ilana Ritov eventually led  to the idea that the translation of attitudes into dollars  involves the almost arbitrary choice of a scale factor, leading  some people who have quite similar values to state very different  values of their willingness to pay, for no good reason (Kahneman,  Ritov and Schkade, 1999). With David Schkade and the famous  jurist Cass Sunstein I extended this idea into a program of  research on arbitrariness in punitive damage decisions, which may  yet have some influence on policy (Sunstein, Kahneman, Schkade  and Ritov, 2002).

  The focus of my research for the past  fifteen years has been the study of various aspects of  experienced utility - the measure of the utility of outcomes as  people actually live them. The concept of utility in which I am  interested was the one that Bentham and Edgeworth had in mind.  However, experienced utility largely disappeared from economic  discourse in the twentieth century, in favor of a notion that I  call decision utility, which is inferred from choices and used to  explain choices. The distinction could be of little relevance for  fully rational agents, who presumably maximize experienced  utility as well as decision utility. But if rationality cannot be  assumed, the quality of consequences becomes worth measuring and  the maximization of experienced utility becomes a testable  proposition. Indeed, my colleagues and I have carried out  experiments in which this proposition was falsified. These  experiments exploit a simple rule that governs the assignment of  remembered utility to past episodes in which an agent is  passively exposed to a pleasant or unpleasant experience, such as  watching a horrible film or an amusing one (Frederickson and  Kahneman, 1993), or undergoing a colonoscopy (Redelmeier and  Kahneman, 1993). Remembered utility turns out to be determined  largely by the peak intensity of the pleasure or discomfort  experienced during the episode, and by the intensity of pleasure  or discomfort when the episode ended. The duration of the episode  has almost no effect on its remembered utility. In accord with  this rule, an episode of 60 seconds during which one hand is  immersed in painfully cold water will leave a more aversive  memory than a longer episode, in which the same 60 seconds are  followed by another 30 seconds during which the temperature rises  slightly. Although the extra 30 seconds are painful, they provide  an improved end. When experimental participants are exposed to  the two episodes, then given a choice of which to repeat, most  choose the longer one (Kahneman, Fredrickson, Schreiber and  Redelmeier, 1993). In these and in other experiments of the same  kind (Schreiber and Kahneman, 2000), people make wrong choices  between experiences to which they may be exposed, because they  are systematically wrong about their affective memories Our  evidence contradicts the standard rational model, which does not  distinguish between experienced utility and decision utility. I  have presented it as a new type of challenge to the assumption of  rationality (Kahneman, 1994).

  Most of my empirical work in recent years  has been done in collaboration with my friend David Schkade. The  current topic of our research is a study of well-being that  builds on my previous research on experienced utility. We have  assembled a multi-disciplinary team for an attempt to develop  tools for measuring welfare, with the design specification that  economists should be willing to take the measurements  seriously.

  Another major effort went into an essay  that attempted to update the notion of judgment heuristics. That  work was done in close collaboration with a young colleague,  Shane Frederick. In the pains we took in the choice of every word  it came close to matching my experiences with Amos (Kahneman and  Frederick, 2002). My Nobel lecture is an extension of that  essay.

  One line of work that I hope may become  influential is the development of a procedure of adversarial  collaboration, which I have championed as a substitute for  the format of critique-reply-rejoinder in which debates are  currently conducted in the social sciences.1 Both as a participant and as a reader I  have been appalled by the absurdly adversarial nature of these  exchanges, in which hardly anyone ever admits an error or  acknowledges learning anything from the other. Adversarial  collaboration involves a good-faith effort to conduct debates by  carrying out joint research - in some cases there may be a need  for an agreed arbiter to lead the project and collect the data.  Because there is no expectation of the contestants reaching  complete agreement at the end of the exercise, adversarial  collaborations will usually lead to an unusual type of joint  publication, in which disagreements are laid out as part of a  jointly authored paper. I have had three adversarial  collaborations, with Tom Gilovich and Victoria Medvec (Gilovich,  Medvec and Kahneman, 1998), with Ralph Hertwig (where Barbara  Mellers was the agreed arbiter, see Mellers, Hertwig and  Kahneman, 2001), and with a group of experimental economists in  the UK (Bateman et al., 2003). An appendix in the Mellers  et al. article proposes a detailed protocol for the  conduct of adversarial collaboration. In another case I did not  succeed in convincing two colleagues that we should engage in an  adversarial collaboration, but we jointly developed another  procedure that is also more constructive than the reply-rejoinder  format. They wrote a critique of one of my lines of work, but  instead of following up with the usual exchange of unpleasant  comments we decided to write a joint piece, which started by a  statement of what we did agree on, then went on to a series of  short debates about issues on which we disagreed (Ariely,  Kahneman, & Loewenstein, 2000). I hope that more efficient  procedures for the conduct of controversies will be part of my  legacy.

  Part 2 - Eulogy for Amos Tversky (June  5, 1996)

  People who make a difference do not die alone. Something dies in  everyone who was affected by them. Amos made a great deal of  difference, and when he died, life was dimmed and diminished for  many of us.

  There is less intelligence in the world.  There is less wit. There are many questions that will never be  answered with the same inimitable combination of depth and  clarity. There are standards that will not be defended with the  same mix of principle and good sense. Life has become poorer.

  There is a large Amos-shaped gap in the  mosaic, and it will not be filled. It cannot be filled because  Amos shaped his own place in the world, he shaped his life, and  even his dying. And in shaping his life and his world, he changed  the world and the life of many around him.

  Amos was the freest person I have known,  and he was able to be free because he was also one of the most  disciplined.

  Some of you may have tried to make Amos do  something he did not want to do. I don't think that there are  many with successes to recount. Unlike many of us, Amos could not  be coerced or embarrassed into chores or empty rituals. In that  sense he was free, and the object of envy for many of us. But the  other side of freedom is the ability to find joy in what one  does, and the ability to adapt creatively to the inevitable. I  will say more about the joy later. The supreme test of Amos's  ability to accept what cannot be changed came in the last few  months. Amos loved living. Death, at a cruelly young age was  imposed on him, before his children's lives had fully taken  shape, before his work was done. But he managed to die as he had  lived - free. He died as he intended. He wanted to work to the  last, and he did. He wanted to keep his privacy, and he did. He  wanted to help his family through their ordeal, and he did. He  wanted to hear the voices of his friends one last time, and he  found a way to do that through the letters that he read with  pleasure, sadness and pride, to the end.

  There are many forms of courage, and Amos  had them all. The indomitable serenity of his last few months is  one. The civic courage of adopting principled and unpopular  positions is another, and he had that too. And then there is the  heroic, almost reckless courage, and he had that too.

  My first memory of Amos goes back to 1957,  when someone pointed out to me a thin and handsome lieutenant,  wearing the red beret of the paratroopers, who had just taken the  competitive entrance exam to the undergraduate program in  Psychology at Hebrew University. The handsome lieutenant looked  very pale, I remember. He had been wounded.

  The paratrooper unit to which he belonged  had been performing an exercise with live fire in front of the  general staff of the Israel Defense Forces and all the military  attaches. Amos was a platoon commander. He sent one of his  soldiers carrying a long metal tube loaded with an explosive  charge, which was to be slid under the barbed wire of the  position they were attacking, and was to be detonated to create  an opening for the attacking troops. The soldier moved forward,  placed the explosive charge, and lit the fuse. And then he froze,  standing upright in the grip of some unaccountable attack of  panic. The fuse was short and the soldier was certainly about to  be killed. Amos leapt from behind the rock he was using for  cover, ran to the soldier, and managed to jump at him and bring  him down just before the charge exploded. This was how he was  wounded. Those who have been soldiers will recognize this act as  one of almost unbelievable presence of mind and bravery. It was  awarded the highest citation available in the Israeli army.

  Amos almost never mentioned this incident,  but some years ago, in the context of one of our frequent  conversations about the importance of memory in our lives, he  mentioned it and said that it had greatly affected him. We can  probably appreciate what it means for a 20-year old to have  passed a supreme test, to have done the impossible. We can  understand how one could draw strength from such an event,  especially if - as was the case for Amos - achieving the almost  impossible was not a once-off thing. Amos achieved the almost  impossible many times, in different contexts.
  Amos' almost impossible achievements, as  you all know, extended to the academic life. Amos derived some  quiet pleasure from one aspect of his record: by a large margin,  he published more articles in Psychological Review, the  prestigious theory journal of the discipline, than anyone else in  the history of that journal, which goes back more than 100 years.  He had two pieces in press in Psychological Review when he  died.

  But other aspects of the record are even  more telling than this statistic. The number of gems and enduring  classics sets Amos apart even more. His early work on  transitivity violations, elimination by aspects, similarity, the  work we did together on judgment, prospect theory and framing,  the Hot Hand, the beautiful work on the disjunction effect and  Argument-Based Choice, and most recently an achievement of which  Amos was particularly proud: Support Theory.

  How did he do it? There are many stories  one could tell. Amos' lifelong habit of working alone at night  while others slept surely helped, but that wouldn't quite do it.  Then there was that mind - the bright beam of light that would  clear out an idea from the fog of other people's words, the  inventiveness that could come up with six different ways of doing  anything that needed to be done. You might think that having the  best mind in the field and the most efficient work style would  suffice. But there was more.

  Amos had simply perfect taste in choosing  problems, and he never wasted much time on anything that was not  destined to matter. He also had an unfailing compass that always  kept him going forward. I can attest to that from long  experience.

  It is not uncommon for me to write dozens  of drafts of a paper, but I am never quite sure that they are  actually improving, and often I wander in circles. Almost  everything I wrote with Amos also went through dozens of drafts,  but when you worked with Amos you just knew. There would be many  drafts, and they would get steadily better.
  Amos and I wrote an article in  Science in 1974. It took us a year. We would meet at the  van Leer Institute in Jerusalem for 4-6 hours a day.  On a good day we would mark a net advance of a sentence or two.  It was worth every minute. And I have never had so much fun. When  we started work on Prospect Theory it was 1974, and in about 6  months we had been through 30- odd versions of the theory and had  a paper ready for a conference. The paper had about 90% of the  ideas of Prospect Theory, and quite properly did not impress  anyone. We spent the better part of the following four years  debugging it, trying to anticipate every objection.

  What kept us at it was a phrase that Amos  often used: "Let's do it right". There was never any hurry, any  thought of compromising quality for speed. We could do it because  Amos said the work was important, and you could trust him when he  said that. We could also do it because the process was so  intensely enjoyable.

  But even that is not all. To understand  Amos' genius - not a word I use lightly - you have to consider a  phrase that he was using increasingly often in the last few  years: "Let us take what the terrain gives". In his growing  wisdom Amos believed that Psychology is almost impossible,  because there is just not all that much we can say that is both  important and demonstrably true. "Let us take what the terrain  gives" meant not over-reaching, not believing that setting a  problem implies it can be solved.

  The unique ability Amos had - no one else I  know comes close - was to find the one place where the terrain  will yield (for Amos, usually gold) - and then to take it all.  This skill in taking it all is what made so many of Amos' papers  not only classics, but definitive. What Amos had done did not  need redoing.

  Whether or not to over-reach was a source  of frequent, and frequently productive tension between Amos and  me over nearly 30 years. I have always wanted to do more than  could be done without risk of error, and have always taken pride  in preferring to be approximately right rather than precisely  wrong. Amos thought that if you pick the terrain properly you  won't have to choose, because you can be precisely right. And  time and time again he managed to be precisely right on things  that mattered. Wisdom was part of his genius.

  Fun was also part of Amos' genius. Solving  problems was a lifelong source of intense joy for him, and the  fact that he was richly rewarded for his problem solving never  undermined that joy.

  Much of the joy was social. Almost all of  Amos' work was collaborative. He enjoyed working with colleagues  and students, and he was supremely good at it. And his joy was  infectious. The 12 or 13 years in which most of our work was  joint were years of interpersonal and intellectual bliss.  Everything was interesting, almost everything was funny, and  there was the recurrent joy of seeing an idea take shape. So many  times in those years we shared the magical experience of one of  us saying something which the other would understand more deeply  than the speaker had done. Contrary to the old laws of  information theory, it was common for us to find that more  information was received than had been sent. I have almost never  had that experience with anyone else. If you have not had it, you  don't know how marvelous collaboration can be ...

References
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