Causal inference for oncology: past developments and current challenges

2.1 Basic concepts

We begin by defining the notation used throughout this manuscript. Let Z denote treatment, X denote pre-treatment covariates, and Y denote an outcome; each may be indexed by i to indicate a specific individual in a sample of size n or in the population from which the sample is drawn. Define the potential outcome Y(z) as the random variable that records the outcome under the condition where treatment was set to z. In a binary treatment setting, where z takes values 0 and 1, each individual has two potential outcomes, Y(0) and Y(1). Under the assumptions discussed in the following subsection, the observed outcome is Y = (1 − z)Y(0) + zY(1). That is, the observed outcome equals the potential outcome under the treatment actually received; the potential outcome under the treatment not received is often termed a ‘counterfactual’ outcome. This idea of potential outcomes can be traced back to [5] but is more commonly attributed to Rubin [6], who used the notion of counterfactuals to suggest the average treatment effect (ATE), E[Y _i (1) − Y _i (0)], as an estimand of interest. He used potential outcomes to highlight the fairness of the comparison – that individuals, and thus their characteristics, are fixed so that any differences in expected outcomes must be attributed to different treatment conditions. Though Rubin’s early work in causal inference is grounded in educational sciences rather than oncology, the underlying difficulty is the same: many exposures of interest cannot be randomized. The potential outcome framework formalizes the analysis of non-experimental data and, with care, allows one to show that causal effects could be attributed to some causes.

2.2 Causal principles

In addition to focusing on estimands of interest that avoid confounding through conditional or ‘associational’ (but not necessarily causal) contrasts, the potential outcomes framework provides a foundation upon which each step in an analysis can be explicitly defined, from the formulation of the research question to the design of the analytic data set, and finally to the execution of the analysis. In a tutorial focused primarily on point exposures (rather than treatment sequences) and continuous outcomes, Goetghebeur and colleagues [7] outline key steps required to perform an analysis from which causal inferences may be drawn. The primary steps are: (1) define the causal question, which requires formalizing all operational variable definitions (treatment levels, outcome, and population of interest); (2) specify the estimand of interest, a statistical parameter that is the target effect of interest and that ‘answers’ the question defined in the first step; and (3) execute the estimation. The second step, specifying an estimand, typically relies on contrasts (i.e., differences and ratios) of expected potential outcomes. The final step can be done in a variety of ways – the specific methods that can be applied depend on the causal question, and it is unlikely that only a single approach would yield consistent estimators. However, to execute the estimation via any approach, the analyst should explicitly state all assumptions required for identifiability and estimation (including model specifications) and evaluate those assumptions through sensitivity analyses when direct testing of assumptions is not possible.

In the point exposure, continuous outcome setting, there are numerous valid and consistent methods for estimation, most of which rely on the assumption that a sufficient set of confounders, X, has been measured (often referred to as the no unmeasured confounders assumption). For example, traditional regression analyses and direct comparisons in matched or stratified samples can be performed. Methods based on a propensity score [8] can be used when there are concerns about correct specification or incomplete understanding of the outcome model. The propensity score is the coarsest scalar-valued function of pre-treatment covariates, X, that yields conditional independence of the treatment and the covariates, X. Rosenbaum and Rubin [8] demonstrated that for propensity score e(X), both Z ⊥ X|e(x) and Y ( 0 ) , Y ( 1 ) ⊥ Z | e ( x ) hold. From this, it can be shown that the ATE for a continuous outcome can be found by: matching or stratifying on e(X) (rather than the higher-dimensional vector X); using e(X) as a covariate in a regression model; or weighting using inverse probability of treatment weights (see, for example, [8, 9]). When the assumption of no unmeasured confounding cannot be assured, instrumental variable methods can be used as an alternative; however, it is to be noted that these methods simply replace one assumption (no unmeasured confounding) with another (existence of an instrument) [10].

Whatever the approach adopted – and whether reliant on the propensity score or not – identification assumptions are needed. In particular, the Stable Unit Treatment Value Assumption is required, which relies on consistency of the potential and observed outcomes and further requires that an individual’s outcome is affected only by the treatment they receive and not by the treatment received by others. Positivity is also required, which ensures that for every stratum of X, treatment assignment is not uniquely determined. Finally, each method typically makes some assumptions on model specification, specifically that either the outcome model or the propensity score model is correctly specified (at least with respect to the confounding variables).

Estimation using parametric regression, matching, stratification, and inverse weighting extend naturally to discrete outcomes; however, when using parametric regression to estimate the ATE, one must also marginalize over the distribution of X, even when treatment-covariate interactions are not present. In contrast, the extension of propensity score regression to binary and censored outcomes is not straightforward [11, 12] – an important obstacle for their application in oncology research, where uncensored, continuous outcomes are less common. However, the core principles outlined in steps (1) and (2) of the workflow above, which call for the thoughtful specification of the research question and its subsequent linkage to a causal estimand with carefully stated definitions, remain unchanged.

2.3 Special considerations for censored outcomes

As we will see in the examples of the following sections, there are a variety of outcomes of interest in oncology, e.g., cancer rates, mortality, and recurrence. These outcomes are often censored, which poses additional challenges for causal inference. Consider as an example the outcome ‘death due to throat cancer’ and the potential exposure ‘daily use of mouthwash.’ Suppose an individual, i, used mouthwash daily from the age of 20 and died of throat cancer at age 82. What is the counterfactual outcome for this individual? Perhaps had this individual not used mouthwash daily, s/he would never die of throat cancer (Y _i (0) = ∞), but in fact would die at age 70 of heart disease (known to be associated with poor oral hygiene and gum disease).

As argued by Greenland et al. [13], one cannot have a well-defined counterfactual that conditions on the absence of a competing risk. That is, there is no well-defined counterfactual that consists of “no daily use of mouthwash and no death by heart disease.” Alternative approaches have been considered. For instance, Robins [14] allowed for the outcome to be undefined under some treatments or for the potential outcome to be well-defined even if a competing risk would occur and prevent its observation under treatment [15]. Adapting the example in Appendix II of [13] to the example of individual i above, in this latter understanding of a potential outcome, the individual would have developed throat cancer at 90 had they not used mouthwash daily (and thus died of heart disease at 70). Thus, even the starting point of a causal survival analysis requires considerable care. These considerations relate to the estimand of interest, which may focus on the total effect of the treatment on the outcome of interest or on a ‘direct effect’ on the outcome that is not mediated by competing events [16].

The semi-parametric Cox proportional hazards model [17] is widely used in survival analysis; at the time of printing, the original article has been cited nearly 57,000 times, and the use of this approach has become so ubiquitous that it is often done without citing the original proposal. However, hazard ratios have come under considerable criticism for their lack of interpretability [13, 18], [19], [20]. For example, small (possibly clinically unimportant) differences in survival probabilities may translate to large hazard ratios, and hazard ratios, like odds ratios, are not collapsible. Alternative approaches include the restricted mean survival time [20, 21] and (marginal) cumulative incidence [16, 22].

We now turn a particular group of etiological questions that has been the motivation for considerable methodological developments: occupational exposures and their effects on cancer deaths.

3.1 Early thoughts on causality in studies of workplace exposures

Causal inference was a subject of interest for many of the leading thinkers in our field long before it was formalized through potential outcomes. A survey of early studies of potentially hazardous occupational exposures and their influence on cancer risk highlights this history and sheds light on important early developments in causal inference. Such occupational exposure studies are fraught with challenges, due in part to the fact that randomized trials are both prohibitively expensive given the long latency period as well as ethically dubious given the suspicion of harm. Thus, non-experimental cohort studies are the primary source of evidence to examine the effects of possible carcinogenic workplace exposures in humans.

Concerning steps (1) and (2) of the causal analysis workflow given above, great care must be taken when defining the exposure. Is exposure defined as employment for a particular class of employer (mining industry), employment by a specific employer, or maybe employment in a particular role (e.g., the administrative assistant to the owner or the accountant of a mine will not face the same exposures as the miners)? Is exposure continuously measured (years of exposure) or somehow classified by time or intensity?

In a relatively early example of such a study (though by no means the first – see for example [23]), Doll and colleagues [24] based the classification of occupational exposure of gas workers on multiple factors. Specifically, participants were classified as ‘exposed’ if they were employed in the gas industry for more than five years between the ages of 40 and 65 at the point when observation began, and exposed participants were further divided into risk categories according to whether their specific role involved entry into the carbonizing plant regularly (“heavy exposure”), intermittently, or not at all.

In this study, as well as an earlier investigation of cancer risk of nickel workers [25], Doll was careful to consider alternative explanations for the observed relationship between exposure and cancer risk. In the study of gas workers [24], a small substudy was conducted in 10% of the workers to collect information on smoking habits; this allowed the authors to conclude that it was unlikely that confounding was grossly distorting the increased risk associated with heavy exposure. In terms of more general contextual confounding, in the study of nickel workers, Doll chose as ‘controls’ men in other occupations (grouping these into select occupations that included miners of materials other than nickel, steelworkers, coal miners, or all other occupations) from the same geographical areas as the nickel miners “to eliminate differences in the incidence of the two diseases due to non-industrial local factors” [25]. Although the term confounding was never used in these early studies, its presence was acknowledged and accounted for to the greatest extent possible.

The authors were careful to compare their results with those of other similar studies, and other forms of bias were also considered, including ascertainment bias (“The excess did not appear to be due to a bias in favor of diagnosing lung cancer among nickel workers” [25]) and what is now known as the healthy worker effect, which we discuss in the next section. Thus, even in the absence of causal inference as a formal specialization or without a language of its own within statistics, inferences of a causal nature were being drawn about occupational exposures.

It is perhaps, then, not surprising that one of the best-known texts on causality from the medical statistics literature is the 1965 lecture by Sir Austin Bradford Hill given to the recently formed Section of Occupational Medicine of the Royal Society [26]. Reprinted in 2020 [27] and accompanied by a lengthy and varied discussion by luminaries in our field, it is in this pivotal lecture that Bradford Hill gave a series of conditions that may be used to assess whether a relationship is causal. These conditions are often (erroneously) referred to as the Bradford Hill criteria and include strength, consistency, specificity, temporality, biological gradient, plausibility, coherence, experiment, and analogy. It is interesting to note that even though randomization was well-understood at the time, experiment is rather low on the list; perhaps this is because the audience that Bradford Hill was addressing was more likely to find cohort studies more useful.

While informal, the conditions listed by Bradford Hill foreshadow many of the critical developments that followed in the field of causal inference. Specificity is more likely to hold when the exposure is well-defined. Experiment, strength of relationship, and perhaps also biological gradient speak to the need to avoid confounding and other sources of bias. Consistency links to the ideas of “stability” [28] or invariant prediction [29] found in more recent literature. The remaining conditions require a significant understanding of the substantive area in which the research question arises – a need to be, as Bradford Hill previously suggested [30], bilingual in that: “[the statistician] must learn a great deal of medicine and […] not only have facility in speaking two languages, he must be able to think in two.” Without this fluency, many of the modern tools that are now quite standard, such as directed acyclic graphs [31], are of no use without a solid understanding of the context of the research question.

While workplace safety has, thankfully, improved since the earliest studies cited here, there continue to be questions of occupational exposure that have driven more recent methodological developments and entirely new classes of estimators.

3.2 The healthy worker effect and G-methods

The healthy worker effect is an interesting paradox that has been recognized and discussed in occupational epidemiology for more than a century, and formal statistical solutions through counterfactual formulations were proposed as early as the 1980s. Previous authors [32, 33] have cited an 1885 letter from William Ogle to the Registrar-General of England and Wales as the first reference to this issue. In this letter, Ogle noted that mortality rates are occupation dependent, with those employed in more physically demanding work exhibiting lower mortality rates than those who were unemployed or were employed in less physically taxing positions. In the study of workers in the gas industry introduced in the previous section, Doll [24], noted “An alternative explanation is that some selective bias resulted in the inclusion of a relatively healthy group of employees.” That is, the demands of a physical job could act as a selective force in joining or remaining in the workforce that could distort possible risk factors of a particular occupation. Later, in 1976, Fox and Collier [32] pointed to several origins of the selection of healthy workers, two of which are “the selection of a healthy population for employment” and “the survival in the industry of the healthier [workers].”

Early attempts to address this source of bias were themselves subject to bias. For instance, in the study of nickel workers, comparisons were made with men in “all other occupations” – a reference group deemed “the most suitable” – as well as groups of men working in other industries where the work was similar in nature to that of nickel workers (e.g., workers in steel, aluminum, copper, spelter, and so on) that “might also carry a specific risk of lung cancer” [25]. It might be argued, however, that the physical demands of the latter groups are more similar, and thus subject to the same selective pressures, as that in the nickel industry. How, then, to resolve this, if not through the selection of the comparator occupations?

In a series of papers, Robins [15, 34, 35] described the source of bias arising from the healthy worker effect graphically and proposed G-computation to address these biases and consistently estimate meaningful causal parameters. One of the insights that Robins raised is that occupational exposure must be viewed as time-varying and not as a point exposure. In framing the problem in this way, it becomes evident that exposure at one time point may determine subsequent exposure. For example, if exposure makes an individual sick such that they can no longer work, that intermediate variable of “became sick” then determines subsequent workplace exposure. Those individuals left in employment – and thus with the longest period of exposure – may be those least susceptible to the harmful effects, leading to the incorrect conclusion that the longer exposure is protective.

It is now widely understood and accepted that traditional regression models cannot account for variables that are simultaneously mediators (caused by exposure at a given point in time and leading to changes in the outcome) and confounders (affecting both exposure at subsequent time periods and the outcome) [36]. Indeed, since first introducing G-computation, Robins and colleagues have developed a series of methods for estimation of both conditional and marginal effects of longitudinal sequences of exposures [37–43]; see [44, 45] for an excellent survey of the methods and their relative strengths and frailties.

In the next section, we turn our attention away from the past and historical considerations of the causes (etiology) of cancer, and look instead to current and future research questions on treating cancer.