Estimating Case-Fatality Reduction from Randomized Screening Trials

2.1 Notation and assumptions

We develop our notation in the context of NLST, where eligible individuals were 55–74 year old heavy smokers (current or having quit within the last 15 years, with 30+ pack years of smoking history). The participants were assigned at random to undergo either three annual low-dose helical CT (screening arm) scans or standard chest X-rays (control arm), and followed up for 7 years (NLST Research Team 2011). A simplified representation (ignoring time, corresponding to one baseline screening examination) of the causal relationships in a randomized screening trial is presented in the directed acyclic graph of Figure 1. This resembles the setting considered by Altstein, Li, and Elashoff (2011), where the intermediate variable was the result of a one-time diagnostic procedure. However, in the screening context, our notation has to take into account that both the mortality outcome and the early diagnosis are time-dependent.

Figure 1:

A simplified schematic of the causal relationships in a conventional randomized cancer screening trial. Here Z is an indicator of assignment to (one or more rounds) of screening or control, S is an indicator of receiving screening, P is an indicator of a positive screening result, D is an indicator of screening-induced early diagnosis (e.g. positive screening test followed by a positive cytology or biopsy), R an indicator of subsequent referral to early treatment, and Y an indicator for cancer-specific mortality outcome. Due to the randomization, the relationship between Z and Y can be estimated without confounding bias, but the relationship between R and Y is confounded by the observed covariates X and the unobserved factors U. Even if we ignore the intermediate variables S and P, the screening assignment can still influence the outcome only through early diagnosis, which in turn prompts early treatments, which motivates the use of Z as an instrumental variable. The ellipses and rectangles represent unobserved and observed variables, respectively. Unshaded dashed rectangles represent observed variables that have not been used directly in the analysis, whereas shaded rectangles represent variables used in the estimation.

Following the convention in cancer screening trials (NLST Research Team 2011; Steele and Brewster 2011) and because our focus is on case-fatality, we consider cancer-specific mortality outcomes. However, because several authors have recommended using all-cause mortality as a measure of benefits (Black, Haggstrom, and Gilbert Welch 2002; Penston 2011; Welch and Black 1997), we note that the methods that follow could be easily adapted to all-cause mortality outcomes. The results could also be presented for other-cause mortality if this is of interest. To represent the outcome, let Y1i(t) and Y0i(t)∈{0,1} be the potential (underlying, in the absence of censoring) counting processes for cancer-specific death by time t for individual i under assignment to screening and control respectively. For simplicity, where possible, we suppress the subscript i from the subsequent notation. The process notation is used to shorten the notation in the formulas that follow; the connection to potential event times and types is Yz(t)≡1{Tz≤t,Ez=1}, z ∈{0,1}, where Tz is the potential time of death, and Ez cause of death indicator, with Ez=1 indicating cancer and Ez=2 other cause of death. We suppress the corresponding process notation for other-cause mortality, but note that Y1(t) and Y0(t) remain at zero if other cause death has taken place before cancer-specific death. The observed cancer-specific mortality outcome is given by Y(t)=ZY1(t)+(1−Z)Y0(t) (counterfactual consistency). The intention-to-screen estimand in the conventional screening trial can be defined as the proportional reduction in cancer mortality (preventive etiologic proportion) 1−E[Y1(t)]/E[Y0(t)], or absolute reduction/risk difference E[Y0(t)]−E[Y1(t)], usually estimated at the end of the follow-up period of the trial at t = τ (in NLST the main analysis was carried out after 6 years). In the presence of censoring, which in the context of NLST is mostly administrative due to late entry into the study, the quantities E[Yz(t)], z ∈{0,1} can be estimated through non-parametric estimators for cancer-specific cumulative incidence, taking into account the competing causes of death. In the presence of covariate-dependent censoring, estimates for covariate conditional cumulative incidences E[Yz(t)∣X], z ∈{0,1} can be obtained for example by fitting subdistribution hazard models (Fine and Gray 1999) separately in the screening and control arms. The flow of a conventional screening trial is illustrated in panel (a) of Figure 2.

Instead of the causal effect of screening assignment among the asymptomatic population eligible for screening, here we are interested in the effectiveness of early (following screening induced diagnosis) versus delayed (following symptom induced diagnosis) treatment, in the screening-detectable subpopulation. Such a latent subpopulation cannot be identified at the baseline, but rather, accumulates over time through the repeated screening examinations. To reflect this, we introduce (underlying, in the absence of censoring) counting processes D1(t) and D0(t)∈{0,1} for cancer diagnosis following a positive screen (using the technology in the screening arm of the trial, e.g. CT in NLST), related to the observed process by D(t)=ZD1(t)+(1−Z)D0(t). These processes remain at zero if a death due to any cause, or a non-screening based diagnosis, takes place first. Based on the screening assignment and diagnosis status at time t, we can identify four distinct latent subpopulations (Table 1). The screening assignment can benefit individuals for whom D1(t)=1 and D0(t)=0, but this subpopulation is unobservable. However, if the specific screening technology used in the trial is not readily available outside the screening arm, this will be approximately equivalent to the subpopulation for whom D1(t)=1. For the purposes of estimation, we assume (i) that P(D0(t)=1)≈0.

Now, we can consider the causal effect of early versus delayed treatments in the subpopulation defined by D1(t)=1 (screening-detectable case of cancer). For this purpose, since the diagnosis in itself (like screening) is not an intervention, we still need a well-defined intervention. This is provided by the hypothetical intervention screening trial outlined by Miettinen (2011, p. 117–118) and Miettinen (2015), illustrated in panel (b) of Figure 2. Here screening-detected individuals, accumulated through a predefined screening regimen, are randomized into immediate referral to treatment following the diagnosis (R = 1), or sent home without being informed about the result of the screening or subsequent diagnostic tests (R = 0). This hypothetical randomization of the action following a possible diagnosis can already take place at the onset of the trial, and thus the intervention is not time-dependent, even though the diagnosis status is. Thus, although obviously unethical in practice, this intervention and any potential outcomes indexed with respect to it are well-defined. Further, for the subpopulation for whom D1(t)=1, we can now introduce the potential outcomes

where the first subscript corresponds to the screening assignment and the second to the intervention.

Figure 2:

Illustration of conventional screening trial and Miettinen’s hypothetical intervention trial in terms of potential outcome variables.

For estimation purposes, we assume further (ii) that Y0∗(t)=Y0(t), that is, undergoing screening and diagnostic procedures and being withheld the result of these does not in itself influence the outcome, for example through looking for screening outside the assigned regimen (beyond what the individual would do in the control arm). In a conventional screening trial, R is not randomized, but for lung cancer it makes sense to assume (iii) that early diagnosis is always followed by immediate referral to treatment, so that D1(t)=1⇒R=1. In addition, we assume (iv) monotonicity Y1(t)≤Y0(t) and Y1∗(t)≤Y0∗(t), meaning that neither the screening examinations themselves, or the early treatments can harm the individual. Finally, we assume (v) that D1(t)=0⇒Y1(t)=Y0(t), meaning that screening can only influence the outcome through early diagnosis, the absence of which implying that the two potential outcomes are the same.

The usual causal assumptions, namely strong ignorability (vi)

and its covariate conditional version

are satisfied through the randomized screening assignment. The assumptions are summarized in Table 2.

3.1 Proportional case-fatality reduction

To motivate case-fatality reduction as the quantity of interest in screening trials, Miettinen (2014a) decomposed the joint probability of benefiting from screening into several conditional probabilities. To connect the notation introduced in Section 2.1 to this, we introduce a simplified version ignoring the overdiagnosis component (Figure 3). If N individuals are assigned to screening, the expected number of these benefiting from screening by time t is given by

where the three probabilities from right to left refer to the probability of early diagnosis due to screening (in any of the screening examinations in the interval [0,t]), the probability that the cancer would be fatal in the absence of early treatments, and finally, the probability that early treatments would avert cancer specific death in the interval [0,t]. Below we will show that the leftmost probability is the proportional reduction in case fatality (by time t).

We note that it may seem that conditioning D1(t)=1 will introduce lead time and immortal time into the causal contrast. While it is true that the individual was immortal until the diagnosis, immortality until the same time is present also under control, because, as discussed before, screening can avert death only due to earlier diagnosis (assumption (v)). In other words, before early diagnosis under screening, the two potential outcomes are the same, and immortal time does not imply immortal time bias. As for lead time, lead time bias is avoided because the time origin in the comparison is the same, the time of randomization.

Figure 3:

A probability tree illustrating decomposition of the joint probability of benefiting from screening into conditional probabilities.

As we want to allow for possible covariate-dependent censoring, we consider a covariate conditional version of the leftmost conditional probability. Under the monotonicity assumption (Section 2.1), this can be written as

which is equivalent to the proportional reduction in case fatality for screening-detectable cases of cancer. It is apparent from the last form that this quantity could be estimated directly from data produced by the hypothetical intervention trial depicted in Figure 2 (b), by plugging in estimators for cancer-specific cumulative incidence separately in the intervention (referral to early treatment) and control arms. However, direct estimation based on conventional screening trial data is not possible, since the potential outcome Y0∗(t) is unobserved in the screening arm. However, Miettinen (2014b, p. 157) derived an estimator in terms of quantities estimable from a conventional screening trial. We re-derive this estimator in the present notational framework, to make explicit the assumptions involved, and consider estimation in the presence of censoring and competing risks.

As a side note, while the intervention trial of Figure 2 (b) could be based on a single baseline screening examination, the quantity in eq. (1) in a conventional screening trial of Figure 2 (a) will depend on the screening regimen employed in the trial, due to the repeated screening examinations resulting in a different screening-detectable subpopulation. However, arguably the quantity in eq. (1) is less dependent on the screening regimen than the intention-to-screen estimand because, as we will show in the next section, the latter will directly depend on the probability of being diagnosed through screening.

To express the quantity in eq. (1) in terms of estimable quantities, we can write the t-year cumulative incidences in the screening and control arms as

and

to get

We can now express the quantity in eq. (1) as

Here the terms P(Y(t)=1∣Z=z,X), z ∈{0,1} can be estimated using non-parametric estimators for cumulative incidence in screening and control arms separately (unconditional on the covariates), or Fine & Gray models, fitted separately in the screening and control arms (conditional on the covariates). The latter can accommodate censoring that is dependent on the observed covariates. The term P(Y(t)=1,D(t)=0∣Z=1,X) in the denominator can be estimated by cumulative incidence of cancer-specific death in the screening arm, considering both screening-based cancer diagnosis and other cause deaths as competing risks.

3.2 Absolute case-fatality reduction

For estimating the absolute reduction in case fatality in the latent subpopulation, we adopt the instrumental variable approach. Generally, IV is a variable that is associated with the exposure of interest, but not directly associated with the outcome (Sussman and Hayward 2010). Thus, as discussed before, random assignment in the randomized screening trial is a natural instrumental variable, since it can only influence the outcome through early diagnosis following a positive screen and the subsequent early treatment. As our estimand, we consider the quantity

To express the quantity in eq. (5) in terms of estimable quantities, we can expand the covariate conditional intention-to-screen effect as

By applying the other assumptions discussed in Section 2.1, we further get

giving an expression for the quantity in eq. (5) as

As in Section 3.1, the expectations E[Y(t)∣Z=z,X], z ∈{0,1} in eq. (6) can be estimated as cumulative incidences of cancer-specific mortality in the screening and control arm, considering other cause mortality as competing risks. The expectation E[D(t)∣Z=1,X] can be estimated as the cumulative incidence of screening-induced diagnosis of cancer in the screening arm, considering any-cause mortality and non-screening based cancer diagnoses as competing risks. This cumulative incidence can also be used to estimate the prevalence of being early diagnosed through screening at any given time during the follow-up.

3.3 Alternative assumptions

We note that deriving expression (6) required the exact same assumptions as the expression for proportional case-fatality reduction in Section 3.1, with the exception of the monotonicity assumption, which was needed in Section 3.1 to connect the one minus risk ratio quantity to the probability of benefiting from screening/preventive etiologic proportion. The risk ratio itself, as well as the risk difference herein, can be estimated without the monotonicity assumption.

To make the connection between eq. (6) and the IV estimator more obvious, we note that among those with D0(t)=1 we could introduce the hypothetical intervention and the corresponding potential outcomes Y01(t) and Y00(t), and replace assumption (i) with assumptions P(D1(t)=0,D0(t)=1∣X)=0 and Y01(t)=Y11(t), the former ruling out individuals who would only get screening-detected when not assigned to screening and the latter meaning that the effect of the intervention is the same irrespective of the screening assignment. The latter assumption would together with (ii) correspond to the usual ‘exclusion restriction’ assumption in instrumental variable estimation, and the former to the ‘absence of defiers’ (assumptions 3 and 5 of Angrist, Imbens, and Rubin 1996). Under the alternative assumptions we could express the quantity in eq. (5) as

which has the same form as the IV estimator Angrist, Imbens, and Rubin (1996) proposed for estimation under non-adherence in randomized trials. However, the assumption Y01(t)=Y11(t) would be difficult to justify here as the screening assignment will influence the timing of the early diagnosis and thus the timing of early treatment. Thus, we stick with the assumptions leading to eq. (6), but demonstrate in Section 4 how the alternative estimator above could be used for a sensitivity analysis concerning assumption (i).

We also note assumption (ii) was introduced in our context for the purpose of connecting the causal estimand to the hypothetical intervention in Miettinen’s intervention trial. Since we cannot actually obtain data from such a trial, this assumption mainly requires that we can hypothesize such an intervention (where screening itself and being withheld the result does not change the screenee’s behaviour). Had we instead specified our causal quantity of interest as E[Y0(t)−Y11(t)∣D1(t)−D0(t)=0] (meaning that the reference level of exposure is the control arm exposure), assumption (ii) would not be needed.

3.4 Formulas for marginal effects

We presented the covariate-conditional versions of the formulas to accommodate possible covariate-dependent censoring. However, we might still be interested in the marginal effects in the latent screening-detectable subpopulation. Estimators for these can be obtained through averaging over the covariate distribution of the screening-detected subpopulation in the screening arm, because

For example, to get an estimate for the marginal probability of benefiting from screening in the latent subpopulation, we can write

where the sum is over the empirical covariate distribution of the screening-detected subpopulation in the screening arm, and the numerator and denominator are estimated through

and

We note that former is equivalent to eq. (6). This is because due to assumption (i), P(D1(t)=1,D0(t)=0∣X)≈P(D1(t)=1∣X), and the marginal causal contrast can again be estimated through averaging over the covariate distribution of the screening-detected population in the screening arm as