Tag Archives: causality

Book: B Smart, “Concepts and Causes in the Philosophy of Disease”

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Recently published with Palgrave Macmillan: Concepts and Causes in the Philosophy of Disease, by Benjamin Smart. A very interesting short book that aims to summarise and progress some of the central recent work in the philosophy of medicine, concerning the nature of health and disease, causality in medicine, the classification of diseases and the relation between medicine and public health.

On Amazon: http://www.amazon.co.uk/gp/search?index=books&linkCode=qs&keywords=9781137552938

On the Palgrave site: http://www.palgrave.com/page/detail/?k=9781137552914

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

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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?

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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?

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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/tint) and 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

Is the Methodological Axiom of the Potential Outcomes Approach Circular?

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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.

A Tale of Two Papers

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I’m on my way back from the World Epi Congress in Anchorage, where causation and causal inference have been central topics of discussion. I wrote previously about a paper (Hernan and Taubman 2008) suggesting that obesity is not a cause of mortality. There is another, more recent paper published in July of this year, suggesting, more or less, that race is not a cause of health outcomes – or at least that it’s not a cause that can feature in causal models (Vanderweele and Robinson 2014). I can’t do justice to the paper here, of course, but I think this is a fair, if crude, summary of the strategy.

This paper is an interesting comparator for the 2008 obesity paper (Hernan and Taubman 2008). It shares the idea that there is a close link between (a) what can be humanly intervened on, (b) what counterfactuals we can entertain, and (c) what causes we can meaningfully talk about. This is a radical view about causation, much stronger than any position held by any contemporary philosopher of whom I’m aware. Philosophers who do think that agency or intervention are central to the concept of causation treat the interventions as in-principle ones, not things humans could actually do.

Yet feasibility of manipulating a variable really does seem to be a driver in this literature. In the paper on race, the authors consider what variables form the subject of humanly possible interventions, and suggest that rather than ask about the effect of race, we should ask what effect is left over after these factors are modelled and controlled for, under the umbrella of socioeconomic status. That sounds to me a bit like saying that we should identify the effects of being female on job candidates’ success by seeing what’s left after controlling for skirt wearing, longer average hair length, shorter stature, higher pitched voice, female names, etc. In other words, it’s very strange indeed. Perhaps it could be useful in some circumstances, but it doesn’t really get us any further with the question of interest – how to quantify the health effects of race, sex, and so forth.

Clearly, there are many conceptual difficulties with this line of reasoning. A good commentary was published with the paper (Glymour and Glymour 2014) which really dismantles the logic of the paper. But I think there are a number of deeper and more pervasive misunderstandings to be cleared up, misunderstandings which help explain why papers like this are being written at all. One is confusion between causation and causal inference; another is confusion between causal inference and particular methods of causal inference; and a third is a mix-up between fitting your methodological tool to your problem, and your problem to your tool.

The last point is particularly striking. What’s so interesting about these two papers (2008 & 2014) is that they seem to be trying to fit research problems to methods, not trying to develop methods to solve problems – even though this is ostensibly what they (at least VW&R 20114) are trying to do. To me, this is strongly reminiscent of Thomas Kuhn’s picture of science, according to which an “exemplary” bit of science occurs, and initiates a “paradigm”, which is a shared set of tools for solving “puzzles”. Kuhn was primarily influenced by physics, but this way of seeing things seems quite apt to explain what is otherwise, from the outside, really quite a remarkable, even bizarre about-turn. Age, sex, race – these are staple objects of epidemiological study as determinants of health; and they don’t fit easily into the potential outcomes paradigm. It’s fascinating to watch the subsequent negotiation. But I’m quite glad that it doesn’t look like epidemiologists are going to stop talking about these things any time soon.

References

Glymour C and Glymour MR. 2014. ‘Race and Sex Are Causes.’ Epidemiology 25 (4): 488-490.

Hernan M and Taubman S. 2008. ‘Does obesity shorten life? The importance of well-defined interventions to answer causal questions.’ International Journal of Obesity 32: S8–S14.

VanderWeele TJ and Robinson WR. 2014. ‘On the Causal Interpretation of Race in Regressions Adjusting for Confounding and Mediating Variables.’ Epidemiology 25(4): 473-484.

Potential Outcomes: Separating Insight from Ideology

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I’m in Anchorage, preparing for the World Congress of Epidemiology. One of the sessions I’m speaking at is a consultation for the next edition of the Dictionary of Epidemiology. It’s a strange and delightful document, this Dictionary: since it sets out to define not only individual words but also the discipline of epidemiology as a whole. Thus it contains both mundane and metaphysics entries, from “death certificate” to “causality”. I’m billed to talk about “Defining Measures of Causal Strength”. There’s a lot to say: the current entries under causal-related terms could use some disciplining. But I’m particularly interested in orienting myself with regards to the “potential outcomes” view of causation, which seems to be the current big thing among epidemiologists.

The potential outcomes view is associated in particular with Miguel Hernan, a very smart epidemiologist at Harvard, and he has a number of nice papers on it. (I hope I don’t need to say that what follows is not a personal attack: I have great respect for Hernan, and am stimulated by his work. I’m just taking his view as exemplary of the potential-outcomes approach, in the way that philosophers typically do.)

In particular I’ve been engaged in a close reading of a paper on obesity by Hernan and Taubman (2008). Their view, as expressed in that paper, is an interesting mix of pragmatism and idealism. On the one (pragmatic) hand, they argue that causal questions are often ill-formed, and thus unanswerable. There is no answer to the question “What is the effect of body-mass index (BMI) on all-cause mortality?” because the different ways to intervene on BMI may result in different effects on mortality. Diet, exercise, a combination of diet and exercise, smoking, chopping off a limb – these are all ways to reduce BMI. Until we have specified which intervention we have in mind, we cannot meaningfully quantify the contribution of BMI to mortality.

This much is highly reminiscent of contrastivist theories of causation in philosophy. Contrastivist theories take causation to consist in counterfactual dependence, but differ from counterfactual theories in taking the form of causal statements to be implicitly contrastive: not “c causes e” but “c rather than C* causes e rather than E*”, where C* and E* are classes of events that could occur in the absence of c and e respectively. Against this background, Hernan and Taubman’s point is simply that, for an epidemiological investigator, it matters what contrast class we have in mind when we seek to estimate the size of an effect. This is a good point, especially in a context where one hopes to act on a causal finding. One had better be sure that one knows, not only that there is a causal connection between a given exposure and outcome, but also what will happen if a given intervention replaces the factor under investigation. I have called the failure to appreciate this point The Causal Fallacy and linked it to easy errors in prediction (see this previous post and Broadbent 2013, 82).

But there is another more troubling side to the view as it is expressed in this paper: that randomized controlled trials offer a protection against this error, and somehow force us to specify our interventions precisely. The argument for this claim is striking, but on reflection I fear it is specious.

Hernan and Taubman make a striking point: they say that an observational study might appear to be able to answer the question “What is the effect of BMI on all-cause mortality?” via a statistical analysis of data on BMI and mortality, while randomized controlled trials would not be able to answer this question directly: they would only be able to answer questions like: “What is the effect of reducing BMI via dietary interventions? / via exercise? / via both?” This apparent shortcoming of RCTs is, of course, a strength in disguise: the observational study is in fact not so informative, since it does not distinguish the effects of different ways of reducing BMI; while the RCTs do give us this information.

This argument is fallacious, however, for the following reasons.

  1. An observational study that includes the same information as the RCTs on the methods of reducing BMI would also be able to distinguish between the effects of these interventions.
  2. It is true that one could conduct an observational study which ignored the possibility that different methods of reducing BMI might themselves have affect mortality. But that would be a bad study, since it would ignore the effects of known confounders. A good study would take these things into account.
  3. Conversely, it is a mistake to suppose that RCTs offer protection against this sort of error. The BMI case is a special one, precisely because there are so many ways to intervene to reduce BMI and we know that these could affect mortality. In truth, there are many ways to make any intervention. One may take a pill or a capsule or a suppository, on the equator or in the tropics, before or after a meal, and so on. Even in an RCT, the intervention is not fully specified. Rather, we simply assume that the differences don’t matter, or that if they do, they are “cancelled out” by the randomisation process.
  4. Randomized controlled trials are not controlled in the manner of true controlled experiments; rather, randomization is a surrogate for controlling. We hope that all the many differences between the circumstances of each intervention in the treatment group will either have no effect or, if they do, will have effects that are randomly distributed so as not to obscure the effect of the treatment. But in principle, it is still possible that this hope is not fulfilled. At a p-value of 0.05 this will happen in one RCT in 20; and perhaps more often in published RCTs, given publication bias (i.e. the fact that null results are harder to publish).

These are familiar points in the philosophical literature on randomised controlled trials (see esp. Worrall 2002). The point I wish to pull out is this. On the one hand, Hernan’s emphasis on getting a well-defined contrastive question is insightful and important. But on the other hand, it is wrong to think that RCTs solve the problem. True, in an RCT you must make an intervention. But it does not follow that one’s intervention is well-specified. There might be all sorts of features of the particular way that you intervene that could skew the results. And conversely, plug the corresponding “how it happened” info into a cohort study, and you will be able to obtain the same sorts of discrimination between these methods.

On top of all this, the focus on the methods of individual studies obscures the most important point of all: that convincing evidence comes from a multitude of studies. Just as an RCT allows us to assume that differences between individuals are evenly distributed and thus ignorable, so a multitude of methodologically inferior studies can provide very strong evidence if their methodological shortcomings are different. This is the kind of situation Hill responded to with his guidelines (NOT criteria!) for inferring causality (Hill 1965). Similarly, ad hoc arguments against each possible alternative explanation can add up to a compelling case, as in the classic paper by Cornfield and colleagues on smoking and lung cancer (Cornfield et al 1959). The recent insights of the potential outcomes approach are valuable and important, but they augment rather than replace these familiar, older insights.

References

Broadbent, A. 2013. Philosophy of Epidemiology. Basingstoke and New York: Palgrave Macmillan.

Cornfield J, Haenszel W, Hammond EC, Lilienfeld AM, Shimkin MB and Wynder EL. 1959. Smoking and lung cancer: recent evidence and a discussion of some questions. Journal of the National Cancer Institute 22: 173-203.

Hernan, MA and Taubman, SL. 2008. Does obesity shorten life? The importance of well-defined interventions to answer causal questions. International Journal of Obesity 32: S8-S14.

Hill, Austin Bradford. 1965. The environment and disease: association or causation? Proceedings of the Royal Society of Medicine 58: 259-300.

Worrall, J. 2002. What Evidence in Evidence-Based Medicine? The British Journal of the Philosophy of Science 58: 451-488.