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2000-Choices, Values, and Frames (Daniel Kahneman, Amos Tversky)
This preface is not the one that Amos Tversky and I intended to write. Soon after Amos learned early in 1996 that he only had a few months to live, we decided to edit a joint book on decision making that would collect much of our work on this topic and congenial research by others. The collection was to be a sequel and companion to a volume on heuristics and biases of judgment that we had edited together with Paul Slovic many years earlier, and a substitute for a book that Amos and I had promised the Russell Sage
Most of the editorial task was completed quickly, although some new pieces that Amos wanted to include – notably one that I was to write – were only completed long after he was gone. The problem of writing a preface was more difficult than finding articles we liked. Our initial aspirations for the preface were high; we were going to write a broad essay presenting a view of how the field had changed in the preceding 20 years. But we ran out of time before we had a presentable product. Amos advised me to “trust the model of me that is in your mind” and write for both of us. This was not advice that I was able to follow: the risk of writing in his name statements
that he might have rejected proved intimidating to the point of paralysis. I chose to take the smaller risk of writing on my own and in a more personal vein than we would have adopted if we had written jointly. My intent is to provide a perspective on some dominant themes of this book by tracing them to the years that we spent working closely together on the problem of choice.
Amos and I began to collaborate in the study of decision making in 1974, soon after completing a review of our earlier work on judgment, which appeared in Science that year. Because I had no expertise in the formal study of choice, in which he was already a star, Amos encouraged me to read the text on mathematical psychology that he had coauthored with his teacher Clyde Coombs and his contemporary Robyn Dawes. The most relevant chapter was concerned with preferences between gambles; it included an introduction to utility theory and an exposition of the Allais paradox. Our discussions of this chapter quickly focused on a remarkable discrepancy: the theoretical analysis implied that the carriers of utility were states of wealth, but the outcomes of gambles were always described as
gains and losses. Some extra assumption was clearly required to bridge the gap – either a spontaneous mental activity that transforms gains and losses into states of wealth, or a highly constrained correspondence between the psychophysics of wealth and the psychophysics of gains and losses. Neither hypothesis seemed appealing. This observation eventually led us to develop
a theory of choice under risk that we called prospect theory (Chapter 2).
Our method of research in those early Jerusalem days was pure fun. We would meet every afternoon for several hours, which we spent inventing interesting pairs of gambles and observing our own intuitive preferences. If we agreed on the same choice, we provisionally assumed that it was characteristic of humankind and went on to investigate its theoretical implications, leaving serious verification for later. This unusual mode of empirical research enabled us to move quickly. In a few giddy months we raced through more than twenty diverse theoretical formulations. Among others, we considered a treatment of risky choice in terms of regret, but we eventually abandoned this approach because it did not elegantly accommodate the pattern of results that we labeled ‘reflection’: changing
the signs of all outcomes in a gamble almost invariably changed the direction of preferences from risk averse to risk seeking or vice versa.
Prospect theory was nearly complete in the spring of 1975; it was then called value theory. A reader familiar with the final version would find almost all the important ideas in that early draft. However, the three additional years that we spent fine-tuning the theory turned out to be essential to its viability. The idea of editing operations, for example, was our answer to many potential counterexamples; it took three years to get to it. Amos was capable of infinite patience. His frequently repeated exhortation “let’s get it right” and the contagious pleasure that he found in the activity of thinking enabled us to persevere in the task of anticipating possible objections – even minor ones – long enough to ensure that they had been resolved, not papered over.
The theory that we constructed was as conservative as possible. We stayed within the decision theoretic framework in which choice between gambles is the model for all decisions. We did not challenge the philosophical analysis of choices in terms of beliefs and desires that underlies utility theory, nor did we question the normative models of rational choice offered by von Neumann and Morgenstern and later by Savage. The goal we set for ourselves was to assemble the minimal set of modifications of expected utility theory that would provide a descriptive account of everything we knew about a severely restricted class of decisions: choices between simple monetary gambles with objectively specified probabilities and at most two nonzero outcomes. Without additional assumptions, prospect theory is not applicable to gambles that have a larger number of outcomes, to gambles on events, or to transactions other than choice; it does not even specify a selling price for monetary gambles. And our hopeful statement that “the extension of equations (1) and (2) to prospects with any number of outcomes is straightforward” (p. 74) turned out to be very optimistic. We got to it some thirteen years later (see Chapter 3), and the extension was not at all straightforward.
It is fair to ask, What is the point of investing so much effort in a theory if its domain of application is so restricted and artificial? The answer is that choice between gambles is the fruit fly of decision theory. It is a very simple case, which contains many essential elements of much larger problems. As with the fruit fly, we study gambles in the hope that the principles that govern the simple case will extend in recognizable form to complex situations. A theory of choice should therefore be evaluated by two distinct criteria, and a successful theory must satisfy both. One requirement is to “get it right” within a precisely specified domain. The theory should be refutable in that domain, and it should be unrefuted. The larger prize, however, lies elsewhere. The principles of the theory should
provide a heuristic benefit in the analysis of more complex decisions, by suggesting hypotheses and by providing templates and labels for the identification of phenomena. For example, although it is surely futile to “test” prospect theory against utility theory in the domain of international relations, the concepts of loss aversion and pseudocertainty are useful tools for understanding strategic decisions. No warranty is implied, of course. The scholars who use the tools to explain more complex decisions do so at their own risk.
Many chapters in the present collection explore one or another of four themes that emerged from our attempt to construct a viable theory of our chosen domain. When we published prospect theory we had a clear view of only the first two of these ideas: the nonlinearity of decision weights and the reference-dependent characteristics of the value function. The third theme, the significance of framing effects, was present in rudimentary form in that article and was articulated soon afterward. The fourth idea, the need to distinguish experienced utility from decision utility, came up early in our conversations but was only developed much later.