Here are some more thoughts on Hernan and Taubman’s famous 2008 paper, from a chapter I am finalising for the epidemiology entry in a collection on the philosophy of medicine. I realise I have made a similar point in an earlier post on this blog, but I think I am getting closer to a crisp expression. The point concerns the claimed advantage of RCTs for ensuring consistency. Thoughts welcome!
Hernan and Taubman are surely right to warn against too-easy claims about “the effect of obesity on mortality”, when there are multiple ways to reduce obesity, each with different effects on mortality, and perhaps no ethically acceptable way to bring about a sudden change in body mass index from say 30 to 22 (Hernán and Taubman 2008, 22). To this extent, their insistence on assessing causal claims as contrasts to well-defined interventions is useful.
On the other hand, they imply some conclusions that are harder to accept. They suggest, for example, that observational studies are inherently more likely to suffer from this sort of difficulty, and that experimental studies (randomized controlled trials) will ensure that interventions are well-specified. They express their point using the technical term “consistency”:
consistency… can be thought of as the condition that the causal contrast involves two or more well-defined interventions. (Hernán and Taubman 2008, S10)
They go on:
…consistency is a trivial condition in randomized experiments. For example, consider a subject who was assigned to the intervention group … in your randomized trial. By definition, it is true that, had he been assigned to the intervention, his counterfactual out- come would have been equal to his observed outcome. But the condition is not so obvious in observational studies. (Hernán and Taubman 2008, s11)
This is a non-sequitur, however, unless we appeal to a background assumption that an intervention—something that an actual human investigator actually does—is necessarily well-defined. Without this assumption, there is nothing to underwrite the claim that “by definition”, if a subject actually assigned to the intervention had been assigned to the intervention, he would have had the outcome that he actually did have.
Consider the intervention in their paper, one hour of strenuous exercise per day. “Strenuous exercise” is not a well-defined intervention. Weightlifting? Karate? Swimming? The assumption behind their paper seems to be that if an investigator “does” an intervention, it is necessarily well-defined; but on reflection this is obviously not true. An investigator needs to have some knowledge of which features of the intervention might affect the outcome (such as what kind of exercise one performs), and thus need to be controlled, and which don’t (such as how far west of Beijing one lives). Even randomization will not protect against confounding arising from preference for a certain type of exercise (perhaps because people with healthy hearts are predisposed both to choose running and to live longer, for example), unless one knows to randomize the assignment of exercise-types and not to leave it to the subjects’ choice.
This is exactly the same kind of difficulty that Hernan and Taubman press against observational studies. So the contrast they wish to draw, between “trivial” consistency in randomized trials and a much more problematic situation in observational studies, is a mirage. Both can suffer from failure to define interventions.