I had a paper out in January with my social worker colleague Rick Hood, called “Complex systems, explanation and policy: implications of the crisis of replication for public health research”. The journal page is here or you can grab the post-print here. It’s a bit of a manifesto for our research standpoint, and starts to realise a long-held ambition of mine to make statistical thinking (or lack thereof) and philosophy of science talk to one another more.
We start from two problems: the crisis of replication and complex systems. Here’s a fine history of the crisis of replication from Stan chief of staff Andrew Gelman. By complex systems, we mean some dynamic system which is adaptive (responds to inputs) and non-linear (a small input might mean a big change in output, but hey! because it’s adaptive, you can’t guarantee it will keep doing that). In fact, we are in particular interested in systems that contain intelligent agents, because this really messes up research. They know they are being observed and can play games, take short-term hits for long-term goals, etc. Health services, society, large organisations, all fit into this mould.
There have been some excellent writers who have tackled these problems before and we bring in Platt, Gigerenzer, Leamer, Pawson, Manski. I am tempted to give nutshells of their lives’ work but you can get it all in the paper. Sadly, although they devoted a lot of energy and great ideas to making science work better, they are almost unknown among scientists of all stripes. Reviewers said they enjoyed reading the paper and found it fresh, but felt that scientists knew about these problems already and knew how to tackle them. You have to play along and be respectful to reviewers but we thought this was wishful thinking. Bad science is everywhere and a lot of it involves that deadly combination of our two problems; public health (focus of our paper) is more susceptible than most fields because of the complex system (government, health providers, society…) and often multi-faceted interventions requiring social traction to be effective. At the same time it draws on a medical research model that originated in randomised controlled trials, rats and Petri dishes. The reviewers and us disagree on just how far most of that research has evolved from its origins.
My experience of health and social care research in a realist-minded faculty is that the more realist and mixed-method the research gets, and the more nuanced and insightful the conclusions are, the less it is attended to by the very people who should learn from it. Simple statistics and what Manski called “incredible certitude” are much more beguiling. If you do this, that will follow. Believe me.
Then, we bring in a new influence that we think will help a lot with this situation: Peter Lipton. He was a philosopher at Cambridge and his principal contribution to his field was the concept of “inference to the best explanation” (also the title of his excellent book which I picked up somewhat by mistake in Senate House Library one day in 2009, kick starting all of this), which takes Peirce’s abductive reasoning and firms it up into something almost concrete enough to actually guide science and reasoning. The fundamental problem with all these incredible certitude studies is that they achieve statistical inference and take that to be the same thing as explanatory inference. As you know, we are primed to detect signals, and evolved to favour false positives, and have to quantify and use statistics to help us get past that. The same problem arises in explanation, but without the quantification to help.
A good explanation make a statistical inference more credible. It’s what you’re hoping to achieve at the end of Platt’s “strong inference” process of repeated inductive – deductive loops. This is Lipton’s point: as humans, when we try to learn about the world around us, we don’t just accept the likeliest explanation, as statistics provides, but we want it to be “lovely” too. As I used to enjoy having on my university profile of relevant skills (on a few occasions a keen new person in comms would ask me to take it down but I just ignored them until they left for a job elsewhere that didn’t involve pain-in-the-backside academics):
By loveliness, Lipton meant that it gives you explanatory bangs for bucks: it should be simple and it should ideally explain other things beyond the original data. So, Newton’s gravitation is lovely because it has one simple formula and that works for both apples and planets. Relativity seems too hard to comprehend to be lovely, but as the phenomena explained by it stack up, it becomes a winner. Wave-particle duality likewise. In each case, they are accepted not for their success in statistical but explanatory inference. It’s not just laws of physics but more sublunar cause and effect too: if you impose a sugar tax, will people be healthier in years to come? That’s the extended worked example we use in the paper.
Now, there are problems with explanations:
- we don’t know how to search systematically for them
- we don’t know where they come from; they generally just “come to mind”
- we don’t know how to evaluate and choose from alternatives among them
- we usually stop thinking about explanation as soon as we hit a reasonably good candidate, but the more you think, the more refinements you come up with
- we seem to give too much weight to loveliness compared to likelihood
and with loveliness itself too. Firstly, it’s somewhat subjective; consider JFK’s assassination. If you are already interested in conspiracy theories and think that government spooks do all sorts of skullduggery, then the candidate explanation that the CIA did it is lovely – it fits with other explanations you’ve accepted, and perhaps explains other things – they did it because he was about to reveal the aliens at Roswell. If you don’t go for that stuff then it won’t be lovely because there are no such prior beliefs to be co-explained. In neither the CIA candidate nor the Oswald candidate explanation are there enough data to allow likelihood to get in there and help. It would be great if we could meaningfully quantify loveliness and build it into the whole statistical process which was supposed to help us get over our leopard-detecting bias for false positives, but that seems very hard. Lipton, in fact, wrote about this and suggested that it might be possible via Bayesian priors. I’ll come back to this.
So, here’s a couple of examples of loosely formed explanations that got shot from the hip after careful and exacting statistical work.
Long ago, when I was a youngster paying my dues by doing data entry for the UK clinical audit of lung cancer services, we put out a press release about differences by sex in the incidence of different types of tumour. I’m not really sure why, because that’s an epidemiological question and not one for audit, but there ya go. It got picked up in various places and our boss was going to be interviewed on Channel 5 breakfast news. We excitedly tuned in. “Why is there a difference?” asked the interviewer. They had heard the statistical inference and now they wanted an explanation.
Of course, we didn’t know. We just knew it was there, p=whatever. But it is human nature to seek out explanation and to speculate on it. The boss had clearly thought about it already: “It may be the feminine way in which women hold their cigarettes and take small puffs”. Whaaat? Where did that come from? I’d like to say that, before dawn in my shared apartment in Harringay, I buried my face in my hands, but that requires some understanding of these problems which I didn’t acquire until much later, so I probably just frowned slightly at the stereotype. I would have thought, as earnest young scientists do, that any speculation on why was not our business. Now, I realise two things: the scientist should propose explanations lest someone less informed does, and they should talk about them, so that the daft ones can get polished up, not stored until they are released pristine and unconstrained by consensus onto national television. It would be nice if, as our paper suggests, these explanations got pre-specified like statistical hypotheses should be, and thus the study can be protected against the explanatory form of multiple testing.
Then here’s a clip from the International New York Times (erstwhile weekly paper edition in the UK) dated on my 40th birthday (I never stop looking for good stuff to share with you, readers).
It’s all going well until the researcher starts straying from ‘we found an association’ into ‘this is why it happens’. “There are more than a thousand compounds in coffee. There are a few candidates, but I don’t know which is responsible.” The opposite problem happens here: by presupposing that there must be a chemical you can attribute effects to (because that’s what he was shown in med school), we can attribute it to an unknown one, and thus by begging the question back up the statistical inference with a spurious explanatory one. Here, there is a lack of explanation, and that should make us rightly suspicious of the conclusion.
On these foundations, we tentatively propose some steps researchers could take to improve things:
- mixed-methods research, because the qual informs the explanation empirically
- Leamer’s fragility analysis
- pre-specify a mapping of statistical inference to explanation
- have an analysis monitoring committee, like trials have a data monitoring committee
- more use of microsimulation / agent-based modelling
- more use of realist evaluation
Further in the future, we need:
- methodological work on Bayesian hyperpriors for loveliness
- better education, specifically dropping the statistical cookbook and following the ASA GAISE guidelines
This is strong medicine; funders and consumers of research will not give a damn for this time-consuming expense, bosses and collaborators will tell concerned researchers not to bother, and some of it could be so hard as to be practically impossible. In particular, Bayesian hyperpriors for loveliness are in the realm of methodological fancy, although some aspects exist, notably bet-on-sparcity, and I’ll return to that in a future post. But setting that to one side, if researchers do things like our recommendations, then over time we will all learn how to do this sort of thing well, and science will get better.
Wrong. None of this will happen any time soon. And this is, ironically, for the same reason that the problems arise in the first place: science happens in a complex system, and an intervention like ours can have an adverse effect, or no effect at all. Researchers respond to several conflicting forces and the psychosocial drivers of behaviour, stronger than appealing to their good nature, remain unchanged. They still scoff at navel-gazing philosophical writers and lump us into that category, they still get told to publish or perish, and they still get rewarded for publication and impact, regardless of the durability of their work. So if I was to talk about the future in the same form that Gelman wrote about the past, it would be a more pessimistic vision. Deep breath:
A storm hits the city and the lights go out before I can prepare
This crisis is known to scientists in only a few areas, where the problem is particularly egregious (not to say to it won’t one day be revealed to have been bigger elsewhere, like public health, but that in these areas it is both quite bad and quite obvious): social and behavioural psychology most notably, although brain imaging and genetics have their own problems and believe they have fixed it by looking for really small p-values (this, lest you be mistaken, will not help). For most other fields of quantitative scientific endeavour, they don;t even realise they are about to get hit. I recall being introduced to a doctor by a former student when we bumped into each other in a cafe:
“Robert’s a statistician.”
“Oh, good, we need people like you to get the p-values going in the right direction”
Now, I know that was a light-hearted remark, but it shows the first thing that comes to mind with statistics. They have no idea what’s coming.
The whole of downtown looks dark like no one lives there
Statistical practice is so often one of mechanistic calculation. You can use recipes to crank the handle and then classify as significant (go to Oslo, collect Nobel prize) or non-significant (go to Jobcentre, collect welfare). There is no sign of explanation up front; it is grubbed up after the fact. It’s as though all human thought was abandoned the minute they turned on the computer. I just can’t understand why you would do that. Have more pride!
Why does this happen? These are at least some of the psychosocial forces I mentioned earlier:
- The risk is carried by early career people: the junior academic or the budding data scientist. The older mentor is not expected to control every detail, and doesn’t take personal responsibility (it was Fox’s fault!)
- Only a few such analyses are used (maybe one) to evaluate the junior person’s ability
- Impact is valued; a reasonable idea for a whole organisation or programme of work, but not for projects, because there will always be a certain failure rate; paradoxically, this is also why academics play it safe with uninspiring incremental advances
- Discovery and novelty are valued – as above
- This sort of work is badly paid. You have to succeed quickly before you have to drop out and earn some cash.
- The successful ones get the habit and can carry on misbehaving.
There’s a party uptown but I just don’t feel like I belong at all (do I?)
So what would happen when people operating in these psychosocial forces get confronted? We’ve seen some of this already in the recent past. Call the critics bullies, just ignore them, pretend that what they say is hilariously obscure left-bank tosh, say that the conclusion didn’t change anyway, suddenly decide it was only intended to be exploratory, find a junior or sub-contractor scapegoat, say you absolutely agree and make only a superficial change while grandstanding about how noble you are to do so, and of course there are more strategic ways for the bad guys to fight back that I listed previously. Medicine will prove to be much worse than psychology and resistant to (or oblivious of any need to) reform. There are reasons for this:
- it’s full of cliques
- they live and breathe hierarchy from school to retirement
- whatever they tell you, their research is uni-disciplinary
- there’s a DIY ethic that comes from that unfettered confidence in one’s own ability to do whatever anyone else does
- they venerate busyness (no time for learning the niceties) and discovery (just get to the p-value)
I considered politicians with the same list and concluded that we don’t have to worry about them, reform will come from statistics up and post-truth, if such a thing exists, is transient. This might not apply to Trump types, of course, because they are not politicians. Cliques are open to coming and going, there is an expectation of advancing and taking turns in the hierarchy, their research is done by others and they can then blame the experts if it goes wrong, they do nothing themselves, they did humanities courses and venerate turning the idea over and over.
Let me leave you with a quote from the late, great Hans Rosling: “You can’t understand the world without statistics. You can’t understand the world with statistics alone.”
“False Hope” by Laura Marling is (c) Warner / Chappell Music Inc