Tobacco and epidemiology in Korea: old tricks, new answers?

Today I participated in a seminar hosted by the National Health Insurance Service (NHIS) of Korea, which is roughly the equivalent of the NHS in the UK, although the health systems differ. The seminar concerned a recent lawsuit in which tobacco companies were sued by the NHIS for the costs of treating lung cancer patients. The suit is part of a larger drive to get a grip on smoking in Korea, where over 40% of males smoke, and a packet of 20 cigarettes costs 4500 Korean Won (about USD 4.10 or UKP 2.80). The NHIS recently suffered a blow at the Supreme Court, where the ruling was somewhat luke-warm about a causal link between smoking and lung cancer in general, and moreover argued that such a link would anyway fail to prove anything about the two specific plaintiffs in the case at hand.

I was struck by the familiarity of some of the arguments that are apparently being used by the tobacco companies. For example, the Supreme Court has been convinced that diseases come in two kinds, specific and non-specific, and that since lung-cancer is a non-specific disease, it is wrong to seek to apply measures of attributability (excess/attributable fraction, population excess/attributable fraction) at all.

This is reminiscent of the use of non-specificity in the 1950s, when it was seen as a problem for the causal hypothesis that smoking causes lung cancer. It also gives rise to a strategy which is legally sound but dubious from a public health perspective, namely, first going for lung cancer, and leaving other health-risks of smoking for later. This is legally sound because lung cancer exhibits the highest relative risk of the smoking-related diseases, and perhaps it is good PR too because cancer of any kind catches the imagination. But the health burden of lung cancer is low, even in a population where smoking is relatively prevalent, since lung cancer is a rare disease even among smokers.

The health burden of heart disease, at the other end of the spectrum, is very large, and even though smoking less than doubles this risk (RR about 1.7), the base rate of heart disease is so high that this amounts to a very significant public health problem. I do not know what the right response to this complex of problems is: clearly, high-profile court cases are have an impact that extends far beyond their outcome, and also the reason that people stop smoking, or accept legislation, need not be an accurate reflection of the true risks in order for those risks to be mitigated. (If you stop smoking to avoid lung cancer, you also avoid heart disease, which is a much better reason to stop smoking from the perspective of a rational individual motivated to avoid fatal disease.) Nonetheless I am struck by the way that legal and health policy objectives interact here.

I was also interested to hear that the case of McTear was a significant blow to the Korean case because of its findings about causality, which indeed are exactly those of the Korean case. That case is not well regarded in the UK, and not authoritative (being first instance), so it is interesting – and unfortunate – that it has had an effect here.

The event was an extremely good-spirited affair, and the other speakers had some interesting things to say. My book, in Korean, received a significant plug, not least, I suspect, because the audience not understanding much of my talk, were repeatedly referred to it for more detail. The most shocking thing about the event was to hear the same obfuscatory strategies that are now history in Europe and America being used, to good effect, by the very same companies in this part of the world. It is one thing to defend a case on grounds that one believes, but there is not anyone who still reasonably believes that smoking does not cause lung cancer, which seems to be the initial burden that plaintiffs in this sort of case need to prove. It is a bit like being asked to begin your case against a scaffolder who dropped a metal bar on your head with a proof of the law of gravity, and then being asked to prove that the general evidence concerning gravity proves that gravity was the cause in this particular case, given that not all downward motions are caused by gravity. – Not exactly like that, of course, but not exactly unlike, either.

On the positive side, I am hoping that a clear explanation of the reasoning behind the PC Inequality that I favour might help with the next stage of the case, although I am unclear what that stage might be.

Is consistency trivial in randomized controlled trials?

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.

Workshop, Helsinki: What do diseases and financial crises have in common?

AID Forum: “Epidemiology: an approach with multidisciplinary applicability”

(Unfamiliar with AID forum? For the very idea and the programme of Agora for Interdisciplinary Debate, see www.helsinki.fi/tint/aid.htm)

DISCUSSED BY:

Mervi Toivanen (economics, Bank of Finland)

Jaakko Kaprio (genetic epidemiology, U of Helsinki)

Alex Broadbent (philosophy of science, U of Johannesburg)

Moderated by Academy professor Uskali Mäki

Session jointly organised by TINT (www.helsinki.fi/tintand the Finnish Epidemiological Society (www.finepi.org)

TIME AND PLACE:

Monday 9 February, 16:15-18

University Main Building, 3rd Floor, Room 5

http://www.helsinki.fi/teknos/opetustilat/keskusta/f33/ls5.htm

TOPIC: What do diseases and financial crises have in common?

Epidemiology has traditionally been used to model the spreading of diseases in populations at risk. By applying parameters related to agents’ responses to infection and network of contacts it helps to study how diseases occur, why they spread and how one could prevent epidemic outbreaks. For decades, epidemiology has studied also non-communicable diseases, such as cancer, cardiovascular disease, addictions and accidents. Descriptive epidemiology focuses on providing accurate information on the occurrence (incidence, prevalence and survival) of the condition. Etiological epidemiology seeks to identify the determinants be they infectious agents, environmental or social exposures, or genetic variants. A central goal is to identify determinants amenable to intervention, and hence prevention of disease.

There is thus a need to consider both reverse causation and confounding as possible alternative explanations to a causal one. Novel designs are providing new tools to address these issues. But epidemiology also provides an approach that has broad applicability to a number of domains covered by multiple disciplines. For example, it is widely and successfully used to explain the propagation of computer viruses, macroeconomic expectations and rumours in a population over time.

As a consequence, epidemiological concepts such as “super-spreader” have found their way also to economic literature that deals with financial stability issues. There is an obvious analogy between the prevention of diseases and the design of economic policies against the threat of financial crises. The purpose of this session is to discuss the applicability of epidemiology across various domains and the possibilities to mutually benefit from common concepts and methods.

QUESTIONS:

1. Why is epidemiology so broadly applicable?

2. What similarities and differences prevail between these various disciplinary applications?

3. What can they learn from one another, and could the cooperation within disciplines be enhanced?

4. How could the endorsement of concepts and ideas across disciplines be improved?

5. Can epidemiology help to resolve causality?

READINGS:

Alex Broadent, Philosophy of Epidemiology (Palgrave Macmillan 2013)

http://www.palgrave.com/page/detail/?sf1=id_product&st1=535877

Alex Broadbent’s blog on the philosophy of epidemiology:

https://philosepi.wordpress.com/

Rothman KJ, Greenland S, Lash TL. Modern Epidemiology 3rd edition.

Lippincott, Philadelphia 2008

D’Onofrio BM, Lahey BB, Turkheimer E, Lichtenstein P. Critical need for family-based, quasi-experimental designs in integrating genetic and social science research. Am J Public Health. 2013 Oct;103 Suppl 1:S46-55. doi:10.2105/AJPH.2013.301252.

Taylor, AE, Davies, NM, Ware, JJ, Vanderweele, T, Smith, GD & Munafò, MR 2014, ‘Mendelian randomization in health research: Using appropriate genetic variants and avoiding biased estimates’. Economics and Human Biology, vol 13., pp. 99-106

Engholm G, Ferlay J, Christensen N, Kejs AMT, Johannesen TB, Khan S, Milter MC, Ólafsdóttir E, Petersen T, Pukkala E, Stenz F, Storm HH. NORDCAN: Cancer Incidence, Mortality, Prevalence and Survival in the Nordic Countries, Version 7.0 (17.12.2014). Association of the Nordic Cancer Registries. Danish Cancer Society. Available from http://www.ancr.nu.

Andrew G. Haldane, Rethinking of financial networks; Speech by Mr Haldane, Executive Director, Financial Stability, Bank of England, at the Financial Student Association, Amsterdam, 28 April 2009: http://www.bis.org/review/r090505e.pdf

Antonios Garas et al., Worldwide spreading of economic crisis: http://iopscience.iop.org/1367-2630/12/11/113043/pdf/1367-2630_12_11_113043.pdf

Christopher D. Carroll, The epidemiology of macroeconomic expectations: http://www.econ2.jhu.edu/people/ccarroll/epidemiologySFI.pdf

Two recent papers

I’ve had two papers come out this month (/year!):

‘Risk Relativism and Physical Law’ in Journal of Epidemiology and Community Health – http://jech.bmj.com/content/69/1/92?etoc

‘Disease as a theoretical concept: The case of HPV-itis’ in Studies in History and Philosophy of Biological and Biomedical Sciences – http://www.sciencedirect.com/science/article/pii/S1369848614000910

Interventionism vs contrastivism about causation

I am trying to summarise (for a paper to be submitted to an epidemiology journal) the differences and similarities between interventionism (a la Woodward, Hitchcock) and contrastivism (a la Schaffer, perhaps Menzies) about causation. Are the following comments fair, and fairly comprehensive?

1) The two approaches share the view that the significance of causal claims is relative to some specified scenario in which some other specified event occurs rather than the cause (unlike pure counterfactual theories, which do not require any such specification).

2) Contrastivism (a la Schaffer) is primarily a semantic thesis about the meaning of “cause” and cognates. Specifically, contrastivism is committed to a descriptive thesis about ordinary talk, namely that “C causes E” implies “C rather than C* causes E rather than E*”, while interventionism is not committed to this (though compatible with it).

3) Interventionism seeks to explicate or shed light on characteristic patterns of counterfactual dependence that surround the instantiation of causes (without fully reducing causation to counterfactual dependence). Contrastivism does not seek to do this (though is compatible with doing so).

4) Both accounts are amenable to “cause” being left ultimately unanalysed, and proponents of each (e.g. Schaffer, Woodward) have expressed pessimism about the prospects of reducing causes to counterfactual dependence.

Comments/thoughts welcome. Thanks.

Is the Methodological Axiom of the Potential Outcomes Approach Circular?

Hernan, VanderWeele, and others argue that causation (or a causal question) is well-defined when interventions are well-specified. I take this to be a sort of methodological axiom of the approach.

But what is a well-specified intervention?

Consider an example from Hernan & Taubman’s influential 2008 paper on obesity. In that paper, BMI is shown up as failing to correspond to a well-specified intervention; better-specifed interventions include one hour of strenuous physical exercise per day (among others).

But what kind of exercise? One hour of running? Powerlifting? Yoga? Boxing?

It might matter – it might turn out that, say, boxing and running for an hour a day reduce BMI by similar amounts but that one of them is associated with longer life. Or it might turn out not to matter. Either way, it would be a matter of empirical inquiry.

This has two consequences for the mantra that well-defined causal questions require well-specified interventions.

First, as I’ve pointed out before on this blog, it means that experimental studies don’t necessarily guarantee well-specified interventions. Just because you can do it doesn’t mean you know what you are doing. The differences you might think don’t matter might matter: different strains of broccoli might have totally different effects on mortality, etc.

Second, more fundamentally, it means that the whole approach is circular. You need a well-specified intervention for a good empirical inquiry into causes and you need good empirical inquiry into causes to know whether your intervention is well-specified.

To me this seems to be a potentially fatal consequence for the claim that well-defined causal questions require well-specified interventions. For if that were true, we would be trapped in a circle, and could never have any well-specified interventions, and thus no well-defined causal questions either. Therefore either we really are trapped in that circle; or we can have well-defined causal questions, in which case, it is false that these always require well-specified interventions.

This is a line of argument I’m developing at present, inspired in part by Vandebroucke and Pearce’s critique of the “methodological revolution” at the recent WCE 2014 in Anchorage. I would welcome comments.