Scientists like to claim – rightly – that they’re free to do research into whatever takes their fancy, but getting funding for it is a different matter.
We scientists are very proud of our intellectual freedom. We say, rightly, that we have the freedom to research anything we want. We’re not like office drones in the employ of a company, beholden to their managers. We’re not shackled to projects like the bonded suits in industry. No! We can do research into any damn thing we like.
But in practise, while we might be free to do that research, it can be pretty hard to get funding for it. Just as an artist is free to paint anything they like, but may find that doing portraits is what ultimately pays the bills, we are more constrained than our idealism proclaims.
An entrepreneur can start a business doing absolutely anything – from selling whoopee cushions to offering financial services – but in order to attract money to get that enterprise going and allow it to continue then they can’t just haemorrhage cash. Not every business can be run like Factory Records, and that in itself is held up as a cautionary tale of suicidal artistic utopianism running up against harsh market realities. Getting money to do research will be likeliest if we conform to certain criteria.
Adam Smith, godfather of the free market economy, understood this very well. He saw that businesspeople are driven – consciously or unconsciously – by the need to maximise profit, and will behave accordingly. But in so doing, they create tides in an economy which may have effects unforeseen at the individual level.
“By directing that industry in such a manner as its produce may be of the greatest value,” Smith wrote “he [the businessman] intends only his own gain, and he is in this, as in many other cases, led by an invisible hand to promote an end which was no part of his intention.”
This insight into how actions of self-interested individuals unconsciously affect the larger economy, i.e. how societal benefits are accrued by the primarily self-interested behaviours of many individuals, finds a more cautionary expression when it comes to science funding.
Ask most scientists what kind of research should get funding support and they’ll defend to the hilt the idea that academic freedom is everything, that scientists should be free to pursue whatever ideas they like, and that one can never predict what societal benefits may come from funding research. In this conception, research quality is paramount and the research topic is irrelevant. Let good people do what they want, let them follow where the data leads, and both the scientific community and wider society will ultimately benefit.
Look closely though, and that tends not to match the reality. Peter Medawar put it as bluntly as any Reviewer 2 when he said, “Any scientist of any age who wants to make important discoveries must study important problems. Dull or piffling problems yield dull or piffling answers. It is not enough that a problem should be “interesting.” … The problem must be such that it matters what the answer is – whether to science generally or to mankind”.
If Medawar was your reviewer, good preliminary data and clear hypotheses would not be enough. He’d want to see that you were working on a problem that seemed important. Medawar would never have awarded funding for early work on CRISPR, because the role of small RNAs in bacteria and the travails of the yoghurt industry are unlikely to have struck him as important problems for either science or society.
But Medawar was mistaken. Or rather, if you look at his quotation closely you’ll see that he’s not talking about science, he’s talking about impact. Defining what’s important is different from defining good science. Good science has fairly objective qualities, things like rigour, reproducibility, quality (Medawar presumably took all this for granted). Important science has…importance. It’s cultural, variable. Research into Entamoeba is going to be pretty damn important if everyone around you is living in unsanitary conditions, but not such a big deal if your arse and guts are not at daily risk of inflammation.
But if working on important problems is what matters, then how do we tell what seems to be important? More directly, how do we define what is most important right now?
This kind of question is a no-brainer to any contemporary influencer: What’s important right now is whatever’s sexy, trendy, cool. What’s important is whatever’s getting a lot of attention.
Science funding thereby ends up being fed and sustained by the culture of prestige publishing and breakthrough papers. Breakthrough papers – sexy papers, trendy papers, cool papers – create a sense of new intellectual destinations being made available, so people must rush to join this bandwagon before it leaves the station. You are of course free to apply for money on anything, but it helps if you can point to a recent and supposedly “high-impact” publication as evidence that this is an exciting new thing. In other words, you don’t find the money, you follow it.
This then, is the more far-reaching and arguably more pernicious effect of the blockbuster paper phenomenon. By being in thrall to the idea of “breakthrough” publications, we enable a system that not only capriciously elevates individuals from a pool of equally talented peers, it also has a ripple effect on funding with far wider consequences than the immediate research area. Anyone who has found themselves disputing the findings of a blockbuster paper will know how incredibly hard it is to get a hearing when there is a mad rush going on to profit from the new avenues supposedly opened by it. Probably everyone has had the experience of being recommended to cite a paper that they don’t rate, simply because it has been acclaimed as a “breakthrough” or a “blockbuster” and so therefore cannot be ignored.
Whole research fields can bloom and die and seem to do so increasingly quickly, while the mob moves on in hectic pursuit of wherever the spotlight of funding is pointing. This is not freedom, this is being guided by Smith’s invisible hand.