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Uses and misuses of causal language

In this issue of BJOG, Hilary Brown and colleagues report on a study from southwestern Ontario, Canada, entitled: ‘Biological determinants of spontaneous late preterm and early term birth: a retrospective cohort study’. I was one of the two original reviewers of this article. The other reviewer strongly objected to the use of the term ‘biological determinants’ in the paper. The editors agreed with the reviewer and requested a revision in terminology, but the authors insisted on retaining the term ‘to distinguish medical predictors from social predictors. . . and behavioural predictors. . . which are also associated with preterm birth’. The editors acceded to the authors’ wishes but asked me to weigh in this mini-controversy with a mini-commentary. Rather than limiting my comments to ‘biological determinants’, however, I will broaden them to the uses and misuses of causal language in health research. This issue is relevant to the paper by Brown et al. and to other studies published in BJOG, but is also applicable to clinical and public health research in general. In particular, I will discuss the use of the terms ‘predictor’, ‘risk factor’, ‘determinant’ and ‘cause’. Most clinical readers – particularly those without formal training in epidemiology or biostatistics – tend to use and interpret these terms interchangeably. A cause has been defined in logic, mathematics and statistics by means of a counterfactual conditional: a factor X is a cause of outcome Y in a population if Y would not have occurred (the conditional part) if exposed persons in that population had not been exposed, i.e. counter to the fact of what actually occurred (the counterfactual part). As the formal definition of causality depends on something that has not occurred, epidemiologists and biostatisticians use the exchangeability principle to investigate cause and effect. In a two-arm randomised controlled trial (RCT), the groups randomised to the experimental and control treatments are believed to be exchangeable, because exposure (treatment) is determined entirely by chance. In observational studies, however, exposure is not randomly allocated by the investigator, and exchangeability therefore depends on the absence of confounding factors (third factors that can cause both exposure and outcome) when comparing outcomes in the exposed and unexposed groups. Many clinicians therefore claim that only RCTs can ‘prove’ cause and effect. Although the RCT is the accepted gold standard for demonstrating causal effects of treatments and other exposures, it remains imperfect. Perfection in research involving human beings is elusive; even RCTs depend on concealment of allocation, adequacy of blinding, minimisation of random measurement error, unbiased losses to follow-up and adherence to treatment and the absence of publication bias, deliberate fraud and bad luck (type 1 and type 2 errors). Conversely, observational studies are capable of identifying true causes. It is obviously unethical and infeasible to randomise people to smoke or not smoke cigarettes. Yet, the strong association between cigarette smoking and lung cancer has been robustly demonstrated in numerous observational studies carried out in varied populations, and lung cancer incidence and mortality rates have paralleled cigarette use so closely that no reasonable scientist, clinician or public health official can doubt their causal relationship. Obstetricians are similarly convinced of the causal effects of maternal cigarette smoking on fetal growth restriction, preterm birth and stillbirth. Some research aims to identify the causal pathways leading to health outcomes. Potential causes can be temporally ordered as ‘upstream’ or ‘downstream’; upstream factors cause the downstream factors, which, in turn, cause the outcome. In recent years, directed acyclic graphs (DAGs)