In Search of Simple Problems

Some of my recent work around behavioural science and behavioural economics might convince some that I am, on balance, 'anti' behaviouralism. To be sure, I am critical. I think there have been purposeful overexaggerations at times, and that there is a politics to the movement that is rarely acknowledged. I think these elements should be explored and amplified. In the long-run, I believe it will help the field. Because, ultimately, I am not 'anti' behaviouralism, or indeed, any field of study. My greatest passion in life is learning, and I take tremendous joy out of indulging in the great range of ideas that people have come up with. I am keen to see what behaviouralism becomes next. I worry that the notion of criticism equating to opposition, a feature that I am sure is more representative of the human condition in general, rather than just our present epoch, leads criticism to suffocate and conformity to proliferate. That is the death of a field, if not of a civilisation.

My thinking about behaviouralism has recently been stimulated, though, by having read Michael Lewis' The Undoing Project, a history (of sorts) of the Kahneman-Tversky collaboration. I enjoyed it--the review will come at some point. And I must confess, with total self-awareness, that I was hooked. Lewis is a wonderful writer, insofar as he is a wonderful storyteller. Having never met Kahneman or Tversky, I cannot comment on whether the characters presented by Lewis in the book are accurate representations of who these people actually were. But they are engaging, likeable, sympathetic characters nonetheless. I was rooting for them, and struck by the sense of tragedy towards the end.

Something else which befell me, though, was a kind of nostalgia. An earlier love for a discipline that I now find myself, sometimes, having to call my own. Lewis does not go into too much detail about the work that Kahneman and Tversky actually did. He describes the two (well, Kahneman) coming up with quirky, off-beat questions, and finding interesting answers. He does not, for instance, dive into the profound beauty (a beauty I am also critical of) within a paper such as Prospect Theory. A layperson might be satisfied with the weird tricks of the behavioural scientist--the one who asks the Linda problem and makes everyone feel so obviously dumb. But these 'tricks' are not the essence of behaviouralism. In my opinion, the 'tricks' are not what motivates those who study human behaviour. To discover a quirk of behaviour, or a bias, is to enhance your career, and--at one time--to land a book deal. It is why so many 'biases' exist today. But I sincerely believe that behavioural scientists are motivated by their desire to understand human behaviour in a quite fundamental way. Not to sell executive training programmes to Goldman Sachs (etc.).

This is what I mean by nostalgia when reading Lewis' book. It developed into something else. The beauty of Kahneman and Tversky's work is that they were looking at fundamental behaviours, and built theories from these fundamentals. They researched loss aversion, for instance. Not whether loss aversion applies in banking, or misinformation, or meal choice, and so on. This is not meant to imply that these domain-specific studies are not valuable. I am quite sure they are. But my point is to highlight a distinction that I feel is meaningful. Behavioural science today is a science of application. There are a range of sociological reasons for this. A wider study might even reveal that most disciplines, following fundamental research, evolve into more granular, applied disciplines--what Kuhn would probably call 'normal science.' But application will rarely scratch the itch that I feel most behavioural scientists wish to scratch, that of understanding (or discovering) something more fundamental about human behaviour. To me--and this may just reveal my great ignorance of the field to which I am most professionally associated--this focus on application, rather than fundamentals, explains why we are still stuck with Kahneman and Tversky. They did great work. But that work is nearly fifty years old. Mental accounting is approaching that anniversary, too. Hyperbolic discounting and present bias are, fittingly, a bit more recent. But they are still thirty years old. Where are the new phenomena? Where are the mysteries that keep behavioural scientists up at night?

The matters that, I am told, increasingly define a post-Nudge era for the discipline are, too, matters of application. The question of agency, for instance, is an important one. But it is a question of usage, of application, not of fundamentals. My own specialism in this space, personalisation, suffers the same critical fault. Personalisation concerns application of behavioural ideas; it is not a topic concerned with the more fundamental patterns of human decision-making. I have also heard about the importance of systems thinking, and this might have some room to run. I think it would be helpful for behavioural scientists shift away from the individual as the unit of analysis. Similarly, to move away from individual behaviours as specimens for dissection, and to instead understand behaviour as a continuous process, with one choice linked to those past, present, and future. But (in my opinion), these ideas infrequently appear in behaviouralist discussions of systems. Ideas remain firmly orientated towards application, rather than something more fundamental (as an aside, the slow invention of cybernetics and systems thinking within behavioural science--fields that are even older than behavioural science--is something I find quite amusing insofar as it demonstrates the blinkering effects that disciplinary scholarship can produce).

And so, captured and enthralled by Lewis' story of Kahneman and Tversky, I finished the book asking myself a question: where are all the simple problems for us to solve? By 'simple problems', I mean fundamental research. Ideas about human behaviour that span domain-specific applications. Asking people if they prefer a gamble now, as a gain, and then later, as a loss, is fundamental research. It is a simple problem. I think my definition is also open to a methodological requirement. Simple problems should be premised on simple mental models and simple hypotheses. They should be drawable/explainable on the back of a napkin. They should also require relatively simple tools (e.g., short surveys of questions) to gain a foundational empirical picture of them. Simple problems should not be simple phenomena--they will, almost be definition, be hugely expansive when fully investigated--but they should come from plain experiences and via accessible channels.

One answer to my question (where are all the simple problems for us to solve?) is that no such problems now remain. This is an idea based in complexity theory. We start with a simple problem, and develop a theory that works pretty well. Over time, that theory is tested in a range of areas, and built upon through extension and adaption. It becomes more complex. Furthermore, other theories that were developed to solve other simple problems come to be tacked onto our theory. We begin to operate with an almost 'metatheory' applicable to a class of problems. As such, over time, scholars of that theory must learn more and more. To focus on the simple problem is to be left behind. Simple problems come to be regarded as veins of gold that are now fully exhausted. Our understanding has taken us away from the simple problem; why are you still standing there? This is all to say, maybe there are no more simple problems for behavioural science to solve. Only complicated ones.

Maybe. But take a different perspective. Yes, many behavioural science ideas are getting on in years. Thirty, fourty, fifty years old, and so on. I am a Herbert Simon head--bounded rationality is eighty years old, and even older if one consults some of Pareto's writing! But, at the same time, these ideas are only decades old. There was a time, in living memory for many people, when we did not understand loss aversion, just as there was a time when we could not manufacture blue LEDs or had to regularly change spark plugs. There was a time, not too long ago, when overpopulation was the crisis of note; where we were paralysed by the question of how to deal with all the horse shit that would, inevitably, swamp our cities. Something that inspires me, even though I will never achieve such intellectual feats, is the knowledge that there are still so many simple problems for us to solve. We are so often consumed by hindsight bias when we think about science and philosophy. It is too easy for us to say all the good ideas are gone, the well has run dry, the low hanging fruit has not only been picked, but has now rotted. It has not! We are simply blessed with knowledge of those splendid ideas. But, by extension, we are also now, at this moment, surrounded by opportunities for even more splendid ideas to emerge. We are overwhelmed by simple problems. We simply have to look for them.

When I think about Kahneman and Tversky (and, again, this is probably a result of Lewis' wonderful characterisation), that is what they did. They did not focus on application. Application was the catalyst for more fundamental questioning. My lament of application in behavioural science, then, is a lament of a reversal of the process. Application must facilitate blind exploration, so that one may stumble upon a simple problem entailing a fundamental revelation. Applying the fundamental relevation will not result in new relevations, only the burial of interesting problems. I want to champion a search for simple problems. They are there to be found. We must endeavour to figure out how.

To this end, and to end, I feel it appropriate to give my own example of a simple problem. I do not know if it is of any merit. I am almost certainly ignorant of a range of perspectives that, had I known better, would have prompted me to bury the idea at the bottom of a sea of self doubt. Alas, I am ignorant, and all the better for it! My simple problem concerns the matter of indecision. We have spent much time trying to understand how people makes decisions. Economists have developed a workable (if hardly compelling) set of ideas around indifference. There is also a literature on choice overload. But I think indecision is different to all these things. It is quite common, in everyday life, to come across a decision wherein the options available are different, but a person cannot reliably/confidently differentiate between them. Maybe they suffer from perfectionism? Maybe the decision is too high stakes? But why is it my wife, so often, cannot decide on which restaurant for us to eat at? There is no perfect choice. There is no indifference, either--indeed, there are differences. The decision is not life or death. And yet... indecision. And why, perhaps more curiously, when I flipped a coin to decide where we eat, does the indecision suddenly vanish, either in satisfaction or immediate rejection? I have my own ideas. Maybe others have ideas, too. I think there is something more to this problem, something more fundamental about decision-making. It is, in my opinion, the kind of simple problem that is worth investigating. There are more to be found, if we look for them.