What to do in a discipline once it is clear that it is impossible to base one’s knowledge on anything underlying that can be reasonably accurately measured and when you know that you cannot construct a consistent story that ties all the sub-problems in a field together?

We are at this stage in all areas of economics and social sciences that I know of. As I argued in a previous post, we for purely technical reasons cannot generate useful models of money. Not because we cannot think of the right arguments or because we lack information about how money arose historically, but because what is mathematically solvable and useful in further investigations is so limited.

The same problem has turned up when it concerns models of disequilibrium, social interaction, life-time planning, optimal control of complex organisations, etc.
It is not just theoretically that we keep hitting barriers of tractability. We can’t measure anything with a high degree of accuracy either. Everything we measure, even at the level of brain activity, is not what we really had in mind and is measured very inaccurately with little hope of much improvement.

Individual income, for instance, understood in theory-land as our ability to draw on resources, is in practice measured quite poorly. Individuals themselves don’t know their income all that well, and tax authorities only deal with the monetary part that they can potential grab and miss important chunks even of that. The goods and services we get for free or that have been promised to us (and are hence every bit as much a part of income as a salary) are not included in either the measures of the tax authorities or self-reports. Environmental services that we get now and in the future (sunshine, biodiversity, a happy life for our kids) are even harder to measure, even if some brave researcher attempts to do so. Once you are prepared to think like a philosopher, you get into even more fundamental problems: the concept of individual income presupposes a notion of an ‘individual’ which is an exceptionally tough notion to define and measure if you think about it.

What goes for income goes for everything populating our representations of an economy: ‘peers’, ‘competition’, ‘health’, ‘causes of death’, ‘productivity’, ‘R&D’, ‘technology’, “GDP’, ‘expectations’, the list goes on and on. There is not a single economic notion that can actually be measured with much confidence. It is not that our measures are useless and tell us nothing, but more that they are poor proxies of what we wanted to know. Well-known economists have described this problem in various ways, with Paul Krugman stating in ‘Peddling Prosperity’ “the economy can’t be put in a box”.

In academic environments where truth is valued, you get to hear these things as a starting academic and every young scientist worth their salt closes their ears when they hear this. The search for something that can be said with certainty and that is not subject to the seeming arbitrariness of ‘judgment calls’ is a key motivator for a scientist and to give up at the outset is not healthy for the soul. Hence the realities of the mathematical and measurement barriers between a scientist and the ‘complete truth’ are only squared up to after long exploration, and even then only reluctantly.
What reactions can one have if one accepts that it is indeed beyond us to have a consistent story of economics and that nothing is measured with great precision?

1. True denial of the barriers. With fresh hope, new generations try anew. If you are oblivious to the notion that you have to make decisions, you can quite happily find truth in theory land, though even there you will have to maintain a certain level of unintelligence not to see that most models written down are inconsistent with other models written down. In empirical land there is always the hope that new ways of measuring things will improve accuracy. Brain scans, lab-experiments, national statistics, cohort panels, world-wide consistent datasets, etc., have flooded the market in recent decades. We have never had so much data available at the click of a mouse. There is then always the hope that the next batch of numbers truly measures what we wanted to measure and that hope keeps us going. Of course, the world is also full of people who will quite clearly see all the problems with mainstream economics as it currently is, but think they have already hit upon the crystal ball that makes them privy to the total truth if only the world takes the time to find out about it. When done whole-heartedly that is, in a sense, also a fresh take on the problem.
2. Deceit I: to pretend that the relations found between measured variables is the undoubted truth, mainly in order to get more admiration and resources from the onlookers. Journalists in particular are susceptible to this kind of deceit. They don’t want to be given a hundred measures of the unemployment rate. They want a hard and fast ‘verifiable’ number and they will always find someone to supply it to them.
3. Deceit II: to pretend that what has been found in the world of some theory is actually useful and has been applied in the real world. Statements along these lines include things like ‘The Nobel Prize winner Mirrlees proved income taxes should not be too progressive and his work has had great influence on government’. Ha! Other statements along those lines often heard include ‘the fundamental welfare theorem shows the potential efficiency of markets’. The notion that the incredibly abstract theoretical world of Mirlees and the welfare theorems have much to do with the actual world of taxation and markets is pure hubris on the side of theorists and their acolytes.
4. Deceit III: to have one’s cake and eat it by basing decisions on one thing and defending them based on something else. For instance, the actual reason for economists to increase interest rates when inflation is high is mainly the hope that past experience will repeat itself and not to be the odd one out amongst central bankers by doing something else, whereas the official defence is a tome of models and figures. Similarly, a favourite defense when other people criticise economists for assuming that people are greedy (Homo Economicus) is that economists make no assumptions at all about what people want and allow for each individual to be completely unique in their wants subject only to some regularity conditions of the ‘preferences’. The accuser is then speaking of perceived actions of economic policy makers whereas the defender is thinking of axiomatic preference bundles and other theories that do not actually inform any decisions.
5. Absolutist Retreat: to re-define the discipline as the study of those things that can be known for certain (even if conditional on assumptions that do not overlap) and to refuse to be drawn into statements about policies or implications. This is an honest approach that re-defines economics as an intellectual pursuit rather than an applicable science but of course will elicit the question of the onlooker as to why their taxes should pay for the study of inapplicable and internally inconsistent knowledge.
6. Self-serving RetreatDeceit: to re-define the discipline as the study of those things that can be known for certain but to encourage others to make the leap from the snippets of knowledge to policies and implications. This is an accusation one can level at the ‘randomistas’ in economics who insist that every problem is unique and that one needs randomised trials to get at the truth. Taking that line seriously, nothing they find in any experiment would then be applicable to anyone else (or even the same persons second time around). One might, for instance, argue that we need to experiment with higher minimum wages amongst car-cleaners in Perth to know whether ‘high minimum wages cost jobs’. There is an obvious intuitive appeal to this, but of course if every situation is truly unique then how can one know that a random experiment on one population will have the same outcome on another population, at another time, or even on a larger group at the same time? The answer is that one doesn’t and is hence appealing to the tendency of the onlooker to see more in the number that is produced than is truly there. Hence the ‘result’ on Perth car-cleaners might not apply to all other professions, might not hold at all when feedbacks from such a large change are taken into account, and of course depend anyway on the rather fuzzy notion of what a ‘job’ is and on the ability to keep track of the car-washers included in the Perth experiment (which is usually not a trivial problem in actual experiments: neither the people who agree to be monitored nor the people running the experiments are ‘standard’).
7. Reactionary Retreat: to reject formalism and measurement in its entirety as a bad job and to rely on expert judgment, verbal theories, and a historical database of anecdotes and perceived ‘lessons’. This of course is ultimately even harder to sell to new students (and thus in terms of evolution a dead-end), but has the added disadvantage that formalism and data are not a universally poor fit. There are areas where formalism and measurement have improved our decisions and our understanding. Just because there are no certainties doesn’t mean there aren’t degrees of good and bad guesses and that formalism can help with the guesses.
8. Pragmatism I: to give up on the notion that any large area of economics comes with a consistent story, but to adopt heuristics on how to arrive at local knowledge and local institutions to muddle along. You are then in the business of comparing the outcomes of different processes, which of course is messy in itself, but it allows for a higher-order science of what the more or less successful strategies are (obviously this is only useful in sub-fields).
9. Pragmatism II: to give up on the Grand Truth and to go into a ‘horses for courses’ set-up where one applies formalism in one area, historical knowledge in another, and yet other models and historical stories in another. The ‘unscientific’ aspect of this type of pragmatism is the question of how to decide what model and what data to rely on in which circumstances. The ‘feelers’ amongst us choose their explanatory framework based on gut instinct. Brilliant though some of those individuals may be, it’s not a very useful approach because we can’t teach it to the younger scientists and furthermore it means that the true strategies of the ‘feelers’ are beyond scrutiny and improvement. Hence an attempt to do ‘science’ at the next level is to start to formulate rules-of-thumb, heuristics, and even overt models with measurement to decide on which mental strategy to use in which situation. In short, one then accepts that the sub-models and sub-data are imperfect and inconsistent with other sub-models and sub-data but one nevertheless tries to make some progress by designing and discussing actual formalised rules as to which way of looking at a problem is appropriate when. You are then ultimately in the business of competing schools of thought.

Obviously, my personal favourite is (9). As a result I feel that highly successful ‘intuitive economists’ who on instinct decide how they approach a problem and what the most important characteristics of a new situation are, are duty bound to try and formalise what they do in actuality: to capture their own instinct in heuristics that can be held up to scrutiny. That way one can hope to make some progress in economic thinking after all.