What are we missing in the study of cultural policy?

I’m continuing to draw suggestions for topics from readers. Mark writes:

As you’ve offered, I’ll throw in a request - “what don’t we know?”. I’m struck that - and I include myself in this - those of us who work on cultural policy have focused in some directions and not in others, for largely path dependency related reasons. My favourite example of this is within the evidence review leading up to the current ACE data strategy, in which the section labelled “Enablers and barriers to talent development in England” (and especially the sub-sections labelled things like “Socio-economic group”) is absolutely full of references to things written by people who work in universities, and the section labelled “International perceptions of the quality of English arts and culture” is almost devoid of same. But more broadly I think there’s lots of current areas that interested parties might be curious about that research and policy just doesn’t have in its headlights at this point.

So an overview of open questions - including ones that people aren’t thinking about - would be very welcome!

This is a great question! My answer is a mix of probably more, and less, of what you’ve asked.

Some preamble: I’ll focus on how social scientists - I’m most familiar with my own field of economics, but have become at least familiar enough with a lot of work from sociology, though I remain a layperson - study cultural policy.

There is a bind from the outset in terms of the distinction between positive and normative analysis. In particular, it is a norm in the social science study of cultural policy that no judgments are made regarding the tastes of individuals, nor should one assume any sort of hierarchies in the quality and importance of artistic works. This is not because the researchers necessarily believe this to be true. It is because the field would be a mess if researchers started importing their own standards and judgments of taste into their work. A French fellow tried to make the case that any such judgments are fake anyway, a fiction designed to preserve social hierarchies and maintain the status of those who could credibly present as having “good taste.” But it is an error (albeit one I have seen from time to time) to leap from “I can’t try to incorporate aesthetic judgments into my social science research, because that is outside of my wheelhouse” to “Nobody can make aesthetic judgments; they’re all (literally) nonsense.” And if one actually does believe it is all nonsense, then there’s not much point in studying cultural policy anyway, except to see it in political-economy terms as a means to provide favours to the upper-middle class, and the only policy recommendation that logically follows is to burn the arts council down.

But arts councils have not burned down, and that is because there is a sense, at least among enough people to matter, that some art in particular is worthy of public support (the exception to this rule is the introduction of “Guaranteed Income for Artist” programs, which fund artists regardless of what they have previously accomplished or what they hope to accomplish - anything will do. I wrote about how this doesn’t make an awful of sense here).

So what can researchers research? The topics that seem to dominate (others might have a different list in mind) are:

• What does arts consumption (or “participation”) look like: how does it break down across different genders, race, formal education, socio-economic status, and so on, and are there noticeable trends?

• How “diverse” are audiences, performers, and arts managers, and if markedly different from the population at large, can we see why?¹

• How does arts activity affect other things: population health, civic participation, local economic development, and so on?

• And, how does the public seem to feel about their being taxed to provide public funding for the arts?²

All of these questions involve normative assumptions, but ones that seem uncontroversial: arts participation, regardless of what, is good; barriers to people from certain classes not having the same opportunities are bad; health and civic participation and economic development are all good. So they avoid the aesthetic judgment problem. But often when I am asked to review these sorts of papers I can’t shake the feeling that there is not much at stake: a magnitude is being estimated, but it doesn’t really matter much what that estimate is. Of course at least some citizens are willing to pay more in taxes to fund public spending on the arts; of course the production and consumption of the arts might have some effects on the non-arts parts of society. But these numbers don’t inform cultural policy. One of the sixty-six things wrong with so-called “economic impact” studies is that it simply makes no difference what number the writer comes up with; the estimates could be off by millions but who cares? The only time we really take note of the actual numbers is when they are absurd: I do not believe that on average a single visit to a museum generates an increase in well-being equivalent to $905. So I think we need to look for topics where there is a hypothesis worth testing that actually means something: it looks like this thing about cultural policy is more likely than that.

I agree with Mark that some research questions remain active through a sort of hysteresis. Social scientists who have been working with a data set want to squeeze what they can from it, and are glad to bring graduate students on board, who then keep the topic alive. It’s time consuming and expensive to develop useable new data.

So, finally, to Mark’s big question: “what don’t we know?” What are we missing out on as a field? I will continue to stick with social science / data-oriented work. Everyone in the field would have a different list, but this is mine. I’m also going to focus on things directly of interest to cultural policy, specifically when it comes to policy involving public expenditures. I’m going to skip over LLMs and AI: the technology is running ahead of policy, and they will both be ahead of research, outdated at the moment of publication.³ Most workshops I have attended on AI and cultural policy have been exercises in speculative fiction, but not much more.

I am not saying there is no work going on in the following areas; just that it would be interesting to see more:

• Many years ago I wrote a book about how arts organizations should think about how to set prices. It was a non-technical how-to (without original research on my part) for arts managers who would not be able to get through the very complex mathematical economics literature on the subject, a primer. But prices are interesting! We see headline stories about theatre prices in those newspapers that still have something we could call an “arts” section. But there’s room for some deep dives into how prices in a particular setting (the West End theatres, for example) have changed over time, and what have been the drivers of those changes, on the demand side and the cost side. Are nonprofit theatres maximizing net revenues with their pricing, or are they doing something else (I always thought this paper was interesting, on discounted Broadway tickets, but it is now over twenty years old). Back in 1981 Henry Hansmann wrote about pricing in the live performing arts and how it might provide a clue into whether arts nonprofits tend to try to maximize the quality of their performances (as this simple but brilliant model from Joseph Newhouse suggests), or quantity of people attending their shows, or the size of the annual budget. This is still a really good question (and I’m not sure of what the answer would be). And it would be important for arts councils to know what it is they are funding; the late Alan Peacock used to say that public funding for the arts must make something happen that wouldn’t otherwise happen, or else what’s the point? So - if we know about the objective functions of recipients of funding a bit better, we can better assess whether the funding makes something worthwhile happen.

• Public funding for the arts, as well as “creative placemaking” policies: what is the evidence regarding accomplishments? I’ve not seen a lot of bog standard program evaluation in the field. A part of the problem, maybe a big part, is that a lot of arts policy research is funded by organizations looking for positive results - the program evaluations I have seen of Guaranteed Income for Artists programs, for example, are, respectfully, shallow and tilted towards finding nice things to say. I think there is more serious policy evaluation going on in the UK, but not enough in North America. What has arts funding here actually accomplished, especially now that we have some “long term” effects?

• This question follows from the last: what do the various policies, new and continuing, indicate about the government’s objective function with respect to funding - what are governments’ revealed preferences? Has policy been simply a matter of decades of “muddling through”, avoiding making anyone upset? Or is there a core principle underlying it all?

Anyway, in the comments people might suggest their own ideas.

1. This is adjacent to the management question, “are diversely-composed teams more effective?” You can’t get federal research funding for this sort of thing in the United States anymore, the topic having been branded with the scarlet W. I don’t find the question particularly “woke”, although I do think research on the topic has long been well into the realm of diminishing returns.

2. These are known as “stated preference” or “contingent valuation” estimates. For various reasons the estimates are pretty dubious, and, as with the footnote above, I think this line of enquiry has hit something of a limit.

3. I will protect the names of the innocent by not going into the writers who wrote papers on how NFTs will change the arts forever.