In support of Daniel Major-Smith’s latest paper, Exploring causality from observational data: An example assessing whether religiosiy promotes cooperation.

As evolutionary human scientists, we care about causality. We usually want to know whether something causes something else, rather than whether things are just correlated. We want to know whether aspects of our culture, social structure or ecology cause a given behaviour, as opposed to being merely associated with it, for instance. Experiments are the gold standard for assessing causality, but for obvious reasons cannot answer everything, especially many of the evolutionary questions we’re interested in – Randomising infants to be raised as religious or not, for instance, would be both impossible and ethically questionable (to put it mildly!).

That leaves observational research. Often derided as being ‘just correlational’ (which is true, but misses the point), observational research is much-maligned and frequently derided as incapable of assessing causality. Sometimes, however – if the stars align and the fates smile upon us – it is possible to infer causality from observational research; in these fleeting dream-like moments, correlation really is causation.

That’s the good news.

The bad news is that this rests on several assumptions, many of which are impossible to prove. This means that even if correlation is causation, it’s often impossible to know for sure. To understate the situation, this is less than ideal.

So what can we do? A first step is to understand the assumptions required for valid causal inferences from observational data and try our best to meet them, and as a second step apply sensitivity analyses to interrogate these assumptions and explore whether their violation might impact a study’s conclusions. If these sensitivity analyses do not substantially alter interpretation, then a stronger case can be made that the observed association may in fact be causal; however, if results change dramatically then a causal interpretation may not be justified. In the associated paper, I detail three of these assumptions and present sensitivity analyses which can be used to examine whether they impact a study’s conclusions or not. For example R code demonstrating these issues and sensitivity analyses via simple simulations, see: https://github.com/djsmith-90/AnalysisCode_BloodDonation_B4030/tree/main/SimulatedExample.

Throughout, I use the causal question “Does religiosity promote cooperative behaviour?” as a motivating example – a Trojan horse, if you will, luring readers in with the promise of exploring religion and cooperation, while surreptitiously imparting knowledge about causal inference and sensitivity analyses – to illustrate these methods. Using data from the parental generation of the Avon Longitudinal Study of Parents and Children, a UK birth cohort study (http://www.bristol.ac.uk/alspac/), I assessed whether three aspects of religiosity – religious belief, affiliation and attendance – were associated with, and may plausibly cause, cooperation, with ‘ever donated blood’ as the measure of cooperation (as this was a Registered Report, all analyses were pre-specified prior to analysis).

Assumption #1: No confounder misspecification

A confounder causes the exposure (independent variable) and outcome (dependent variable). A mediator is caused by the exposure which in turn causes the outcome. A collider is caused by both the exposure and outcome (figure 1). To get unbiased casual estimates, we want to adjust for all confounders – which removes bias – and avoid adjusting for mediators and colliders – which introduces bias.

Figure 1: Directed acyclic graph describing different causal structures and how they can be encoded in such causal graphs. The arrows represent the direction of causality; for instance, the arrow from ‘Exposure’ to ‘Outcome’ indicates that the exposure causes the outcome. Using directed acyclic graphs to represent the assumed causal structure of the data can help identify whether covariates are confounders, mediators and/or colliders, and therefore which variables to statistically adjust for to return an unbiased causal estimate, given the assumptions embedded in the causal graph.

If that all sounds too straightforward, you’re probably right.

Alas, reality is unfortunately much more complicated, as the true causal structure can be difficult to know with certainty, especially from cross-sectional data. So we have to make assumptions. These assumptions should be justified (e.g., from previous literature, theory, educated guesses), and can be represented using directed acyclic graphs, like figure 1. If the true confounding structure is unknown – e.g., a potential confounder may also be a potential mediator – one approach is to explore different confounding structures to see how results change based on these different assumptions.

In our paper, we compared models with covariates assumed to only be confounders (e.g., age, ethnicity and socioeconomic position) vs models with covariates assumed to only be confounders and covariates assumed to be potentially confounders and/or mediators (e.g., marital status and parity). Differences between these models were minor, suggesting that bias due to mis-specified confounding may be minimal (figure 2).

Figure 2: Results of the complete-case (black) and multiple imputation (red) analyses for each religiosity exposure with cooperation (blood donation) as the outcome for mothers. The ‘confounders only’ scenario adjusts only for assumed confounders, while the ‘confounders and/or mediators’ scenario adjusts for both assumed confounders and variables which may be both confounders and mediators.

Assumption #2: No unmeasured confounding

In addition to model misspecification of measured confounders, another source of bias is unmeasured confounding. That is, if a confounder was overlooked, or simply not measured, this may threaten causal inference due to an open pathway between the exposure and outcome via this unmeasured confounder. Fortunately, sensitivity analyses have been developed to explore the level of unmeasured confounding necessary to alter a study’s conclusions. If the level of unmeasured confounding necessary to overturn the observed result is small, we may have little confidence in the conclusions; alternatively, if the level of unmeasured confounding necessary to alter conclusions is large, results may be robust to even a high degree of unmeasured confounding.

In our example, we observed a small positive association between religious attendance and donating blood (figure 2). However, small amounts of unmeasured confounding could explain away this association, weakening the evidence for a causal relationship, especially as important confounders which may cause both religiosity and cooperation – such as personality – could not be assessed here.

Assumption #3: No selection bias due to missing data

A third threat to causal inferences from observational data is missing data. This can result in selection bias if the outcome, or the outcome and the exposure, predict missingness. This bias occurs because complete-case analyses (i.e., the fully-observed data) implicitly condition on a collider, potentially inducing a spurious association between the exposure and outcome. Methods such as multiple imputation can help overcome this bias by imputing missing data, but they rest on various assumptions, which again are impossible to verify (the assumptions are rather nuanced and have borderline-impenetrable names like ‘Missing-At-Random’, so I won’t detail these assumptions here; see the paper for a full explanation).

Our multiple imputation results were similar to those of the complete-case analysis (figure 2). This suggests that either there was little bias due to selection in the complete-case analysis, or that multiple imputation did not remove this bias. Additional multiple imputation sensitivity analyses, which made different assumptions about the selection mechanisms, had little impact regarding study interpretation. Selection bias was therefore unlikely to alter the observed pattern of results.

The main aim of the paper is to demonstrate that it is possible to infer causality from observational data – at least in theory – but in practice it is difficult to demonstrate definitively. Nonetheless, as we are often interested in causal, as opposed to correlational, questions, we need to take a causal approach seriously. Sensitivity analyses, such as those described above, can be used to explore and interrogate these assumptions and help assess whether a causal interpretation may be plausible or not.

In terms of our specific research question – “Does religiosity promote cooperative behaviour?” – there was little evidence that religious beliefs or affiliation cause blood donations. There was a positive association between religious attendance and blood donation, although this could plausibly be explained by unmeasured confounding, meaning that the evidence for a causal relationship is rather weak.

I hope that sensitivity analyses such as these become more mainstream in the evolutionary human sciences, and that we become much less casual when discussing causality.

Author biography: Daniel Major-Smith is a somewhat-lapsed evolutionary anthropologist who now spends most of his time working as an epidemiologist. He is currently a Senior Research Associate in Population Health Sciences at the University of Bristol, and works on various topics, including selection bias, life course epidemiology and relations between religion, health and behaviour. Outside of academia, he fosters cats and potters around his garden pleading with his vegetables to grow.

References/Further reading:

Hernán MA, Robins JM (2020). Causal Inference: What If. Boca Raton: Chapman & Hall/CRC. https://www.hsph.harvard.edu/miguel-hernan/causal-inference-book/ (the bible of all things causal inference)

Pearl, J., & Mackenzie, D. (2018). The book of why: the new science of cause and effect. Basic books. https://en.wikipedia.org/wiki/The_Book_of_Why (a more accessible introduction to causality)

Hernán, M. A. (2018). The C-word: scientific euphemisms do not improve causal inference from observational data. American journal of public health, 108(5), 616-619. https://ajph.aphapublications.org/doi/full/10.2105/AJPH.2018.304337 (on the importance of being clear about causality and not being afraid of the C-word)

McElreath, R. (2020). Statistical rethinking: A Bayesian course with examples in R and Stan. Chapman and Hall/CRC. https://xcelab.net/rm/statistical-rethinking/ (fab introduction to all things statistics, with a focus on causal inference)

VanderWeele, T. J., & Ding, P. (2017). Sensitivity analysis in observational research: introducing the E-value. Annals of internal medicine, 167(4), 268-274. https://www.acpjournals.org/doi/full/10.7326/M16-2607 (E-value sensitivity analysis for unmeasured confounding)

Harada, M. (2013). Generalized sensitivity analysis and application to quasi-experiments. Working Paper. https://ideas.repec.org/c/boc/bocode/s457497.html (Generalised Sensitivity Analysis method for unmeasured confounding; only available in Stata)

Munafò, M. R., Tilling, K., Taylor, A. E., Evans, D. M., & Davey Smith, G. (2018). Collider scope: when selection bias can substantially influence observed associations. International journal of epidemiology, 47(1), 226-235. https://academic.oup.com/ije/article/47/1/226/4259077 (introduction to selection/collider bias)