Often in randomized trials to evaluate the effect of a treatment, inference is hampered by possible selection bias induced by conditioning on or adjusting for a variable measured post-randomization. For instance, in randomized clinical trials where some study participants do not comply with their treatment assignment, investigators are often interested in the effect of treatment in participants who were compliant. One approach that avoids potential selection bias induced by conditioning on a post-randomization variable is to focus inference on the causal effect within a principal strata of interest, i.e., the principal effect (Frangakis and Rubin 2002). Principal strata are defined by the pair of potential outcomes under either treatment assignment of the post-randomization variable. For instance, in the setting of non-compliance the principal stratum of interest may be study participants who would comply with their randomization assignment regardless of whether assigned to treatment or control (Angrist et al. 1996). In vaccine trials, a principal stratum of interest may be individuals who would be infected at a certain time regardless of vaccine status (Shepherd et al. 2011). In studies of interventions to prevent mother-to-child transmission (MTCT) of HIV through breastfeeding, a principal stratum of interest is infants who would be uninfected at a certain time regardless of treatment (Nolen and Hudgens 2011; Long and Hudgens 2012). There are many other settings where inference about treatment effects within certain principal strata may be of interest; see VanderWeele (2011) for a recent overview. A primary goal in these settings is often to better understand a treatment’s effect by drawing inference about effects within subgroups defined by the principal strata. The principal stratification approach is less helpful for decision making, as principal stratum membership is generally not identifiable prior to treatment (Joffe 2011).

In many instances, even after treatment assignment individual principal strata membership is not identifiable from the observable data without strong assumptions because only one of the two post-randomization variable potential outcomes is ever observed for an individual. In turn, the principal effect of interest is not identifiable. One approach to cope with lack of identifiability is to conduct sensitivity analysis wherein some model is assumed, indexed by an unidentifiable parameter conditional on which the principal effect is identifiable from the observable data. Inference about the principal effect is then conducted conditional on some value of the unidentifiable parameter and sensitivity of the inference is examined by considering different values of the parameter. An alternative approach entails drawing inference about bounds on the principal effects, e.g., Zhang and Rubin (2003), Cheng and Small (2006). Informally, these extreme bounds provide the smallest and largest possible values of the principal effect consistent with the observed data distribution. This approach is appealing in that typically bounds can be obtained under minimal assumptions. However, in many cases the bounds may be quite wide and therefore not particularly informative about the principal effect.

Grilli and Mealli (2008) derived nonparametric bounds on principal effects under a number of different assumptions. They suggested these bounds can be improved (or narrowed) by creating bounds within strata defined by a baseline covariate and combining these stratum specific bounds by taking a weighted average to obtain new adjusted bounds on the principal effect. Grilli and Mealli employed this approach in the analysis of data from an employment study with mixed results: the adjusted bounds were an improvement on only one side of the unadjusted bounds, i.e., the adjusted upper bound was less than the unadjusted upper bound but the adjusted lower bound was also less than the unadjusted lower bound. The reason for only partial improvement was not addressed. More recent work by Lee (2009) and Mealli and Pacini (2012) indicate the adjusted bounds will never be wider than the unadjusted bounds and sometimes the adjusted bounds will be strictly narrower than the unadjusted bounds. In this paper we characterize the exact circumstances for which adjusting for a baseline covariate leads to improved bounds.

The outline of the remainder of this paper is as follows. In Section 2, notation and assumptions are introduced. Section 3 explains the lack of identifiability of the principal effect and in Section 4 the unadjusted bounds are reviewed. Section 5 defines the adjusted bounds based on a weighted average of bounds within levels of the baseline covariate. Section 6 contains the main result of this paper, giving necessary and sufficient conditions under which the covariate adjusted bounds improve upon (i.e., are narrower than) the unadjusted bounds. In Section 7 large sample inferential methods are discussed. In Section 8, the adjusted and unadjusted bounds are compared using data from a recent, large MTCT study. Conditions in which adjusting for the covariate leads to identification of the principal effect are discussed in Section 9. A brief discussion is given in Section 10. Proofs of the propositions in Section 6 are given in the Web Appendix A.

To motivate, throughout we consider the MTCT example where infants of HIV positive mothers are randomized at birth (i.e., baseline or time 0) to treatment or control. Suppose n infants are enrolled in a MTCT study and for i = 1, …, n let Z_i denote the randomization assignment for infant i. Without loss of generality let Z_i = 0 correspond to control and Z_i = 1 correspond to treatment. Let X_i be some binary variable measured at baseline (prior to randomization) taking on values 0 or 1. For simplicity X_i is assumed to be binary for now, although the results derived below will apply for any baseline categorical covariate with a finite number of levels. The primary endpoint in MTCT studies is typically HIV infection of the infant by some time point τ (e.g., six months) after baseline. Denote the presence or absence of the primary endpoint by Y_i, where Y_i = 1 indicates infant i became infected by τ and otherwise Y_i = 0. Because the goal of treatment is to prevent breast milk transmission of HIV, investigators are primarily interested in infant HIV infections that occur before τ but after some time τ₀ > 0 (e.g., τ₀ = 2 weeks), as infections prior to τ₀ are likely due to in utero or peripartum transmission and not breastfeeding. Let S_i denote whether infant i is infected by τ₀, where S_i = 1 if infant i is HIV infected by τ₀ and S_i = 0 otherwise. Let S_i(z) denote the potential value of S_i when assigned treatment z for z = 0, 1 such that S_i = (1 − Z_i)S_i(0) + Z_iS_i(1). Define Y_i(z) similarly. Assume the treatment assignment of an infant does not affect the potential outcomes of other infants (i.e., there is no interference) and that there are not multiple forms of treatment.

An analysis of the effect of treatment that simply excludes infants infected by τ₀ (i.e., S_i = 1) is subject to selection bias. That is, because the set (or population) of infants that would be infected by τ₀ when assigned treatment Z_i = 1 is not necessarily the same as the set of infants that would be infected by τ₀ if assigned control Z_i = 0, direct comparisons between trial arms that exclude infants infected by τ₀ in general do not have a causal interpretation. To avoid such selection bias, the principal stratification framework may be adopted (Frangakis and Rubin 2002). Principal strata are defined by sets of infants with the same potential outcome pair (S_i(0) = s₀, S_i(1) = s₁). Define the always infected (AI) principal stratum to be infants with s₀ = s₁ = 1, i.e., infants who would be infected at τ₀ regardless of randomization assignment. Similarly define the harmed stratum as those infants with s₀ = 0, s₁ = 1; the protected stratum as those infants with s₀ = 1, s₁ = 0; and the never infected (NI) stratum as those infants with s₀ = s₁ = 0. Based on considerations described above, investigators conducting MTCT trials are interested in the NI stratum. The causal estimand of interest, the principal effect, is the effect of treatment on Y_i in infants who would be uninfected at τ₀ under either randomization assignment, namely

Below we consider large sample bounds for CE that do and do not adjust for the baseline covariate X_i. Throughout we assume

where ⊥ denotes independence. Assumption 1 will hold in randomized trials. Monotonicity assumes that treatment does no harm with respect to the intermediate variable S_i, i.e., there are no infants who would be infected by τ₀ only if treated. Under Assumption 2, there are only three possible principal strata: AI, NI, and protected.

In this section we consider identifiability of CE. Let θ_zst = Pr[Y_i(z) = 1|S_i(1) = s, S_i(0) = t], π_z = Pr[Y_i(z) = 1|S_i(z) = 0], and γ = Pr[S_i(0) = 0|S_i(1) = 0], such that CE = θ₁₀₀ − θ₀₀₀. Assume γ > 0 as otherwise the NI stratum is empty with probability 1. Under Assumptions 1 and 2, θ₀₀₀ = Pr[Y_i = 1|S_i = 0, Z_i = 0], which is identifiable from the observed data. However, θ₁₀₀ is not identifiable. Following Hudgens and Halloran (2006) note

i.e.,

Under Assumption 1, π₁ is identifiable. Under Assumptions 1 and 2, γ is identifiable because

On the other hand, θ₁₀₀ and θ₁₀₁ are not identifiable because infants who were assigned treatment and uninfected at τ₀ are a mixture of infants from the protected and NI strata. Solving (1) for θ₁₀₀ yields

Equation (2) describes a line with intercept π₁/γ and slope −(1 − γ)/γ. Any pair of points (θ₁₀₁, θ₁₀₀) in the unit square that are on this line will give rise to the same observed data distribution.

Note that CE is identifiable if and only if γ = 1, π₁ = 1, or π₁ = 0. If γ = 1, then (2) is a horizontal line with intercept π₁ and thus θ₁₀₀ = π₁. Note γ = 1 is equivalent to Pr[S_i(0) = 0] = Pr[S_i(1) = 0], i.e., treatment has no effect on the intermediate variable S_i. If π₁ = 1, then (1) implies θ₁₀₀ = 1; geometrically this corresponds to the line (2) intersecting the unit square at the upper right corner (1,1). In words, π₁ = 1 means that all treated infants who are uninfected at τ₀ will become infected by τ. Likewise, if π₁ = 0, then (1) implies θ₁₀₀ = 0, corresponding to the line (2) intersecting the unit square at the origin (0,0). In words, π₁ = 0 means that all treated infants who are uninfected at τ₀ will not become infected by τ. Otherwise, if γ < 1 and 0 < π₁ < 1, under Assumptions 1 and 2, CE is not identifiable from the observable random variables. On the other hand, θ₀₀₀, π₁, and γ are identifiable, implying the observed data distribution does reveal some information about possible values for CE, i.e., CE is partially identifiable. The focus of the sequel is on large sample bounds, i.e., the smallest and largest possible values of CE that are consistent with the observed data law.

In this section, we present large sample bounds for CE (Zhang and Rubin 2003; Hudgens et al. 2003) that ignore the baseline covariate X. The large sample bounds for CE are found by first bounding θ₁₀₀. The upper bound for θ₁₀₀ is obtained by assuming θ₁₀₁ = 0 or θ₁₀₀ = 1. Likewise, the lower bound for θ₁₀₀ is obtained by assuming θ₁₀₁ = 1 or θ₁₀₀ = 0. These bounds can be envisaged as corresponding to the points where the line (2) intersects the unit square (Hudgens and Halloran 2006). In particular, the upper and lower bounds are

Bounds for CE are found by replacing θ₁₀₀ by θ100u and θ100l, i.e., CEu=θ100u-θ000 and CEl=θ100l-θ000. These bounds will be referred to as “unadjusted” bounds because no information from the covariate is used.

To illustrate, let the probabilities corresponding to a fictitious trial of MTCT of HIV be γ = 0.95, π₁ = 0.02, and π₀ = 0.05. Using (3), for this trial θ100l=max{(0.02-(1-0.95))/0.95,0}=0 and θ100u=min{0.02/0.95,1}=0.021 (note here and in the sequel that reported numerical results are rounded, in this case to the third decimal place). This gives the unadjusted bounds as [CE^l, CE^u] = [0–0.05, 0.021–0.05] = [−0.05, −0.029] because θ₀₀₀ = π₀. In this example the bounds exclude zero, implying treatment reduces the risk of Y = 1 in the NI stratum. Let the probabilities for a second fictitious trial be γ = 0.80, π₁ = 0.85, and π₀ = 0.95. Then θ100u=1 and θ100l=0.813, implying the unadjusted bounds are [CE^l, CE^u] = [−0.137, 0.05]. These two fictitious trials will be revisited in the next section.

Next we consider the method proposed by Grilli and Mealli (2008) for adjusting the large sample bounds using the binary baseline covariate X, i.e., bounds will be obtained within strata defined by X and then weighted averages of the stratum specific bounds will be computed. Let θ_zstx = Pr[Y_i(z) = 1|S_i(1) = s, S_i(0) = t, X_i = x], γ_x = Pr[S_i(0) = 0|S_i(1) = 0, X_i = x], π_zx = Pr[Y_i(z) = 1|S_i(1) = 0, X_i = x], ϕ_x = Pr[X_i = x|S_i(1) = S_i(0) = 0], and λ_x = Pr[X_i = x|S_i(1) = 0]. Throughout it is assumed that Pr[S_i(1) = 0, S_i(0) = t, X_i = x] > 0 for x, t = 0, 1 such that the conditional probabilities θ_z0tx, γ_x, and π_zx are all well defined. This assumption also implies γ_x > 0, ϕ_x > 0 and λ_x > 0 for x = 0, 1. Note

(4)θ100=∑xθ100xϕx, where here and in the sequel ∑x=∑x=01. As in the unadjusted case, θ_100x is not identifiable but using arguments analogous to (2) for X_i = x

(5)θ100x=π1xγx-1-γxγxθ101x, and identifiable upper and lower bounds for θ_100x are

Under Assumptions 1 and 2, ϕ_x is identifiable because Pr[X_i = x|Z_i = 0, S_i = 0] = Pr[X_i = x|S_i(0) = 0] = Pr[X_i = x|S_i(1) = S_i(0) = 0]. Therefore, identifiable bounds for θ₁₀₀ can be obtained by combining (4) and (6), namely

This leads to adjusted bounds CEXu=θ100Xu-θ000 and CEXl=θ100Xl-θ000.

Table 1 contains the values of two different binary baseline covariates, X₁ and X₂, for each of the fictional trials discussed in Section 4. For the first trial and X₁, by (6) we have θ1000u=min{0.035/0.995,1}=0.035,θ1000l=max{(0.035-(1-0.995))/0.995,0}=0.030,θ1001u=0.011, and θ1001l=0. Thus, θ100Xu=0.035×0.419+0.011×0.581=0.021 and θ100Xl=0.013. Therefore, there is improvement to the lower bound of CE but not to the upper bound when adjusting for X₁, and thus the unadjusted bounds [CE^l, CE^u] = [−0.05, −0.029] are wider than the adjusted bounds [CEX1l,CEX1u]=[-0.037,-0.029]. On the other hand, adjusting by X₂ in the first trial does not yield an improvement since θ100Xu=0.021=θ100u and θ100Xl=0=θ100l.

For the second trial and X₁, θ1000u=0.854,θ1000l=0.730,θ1001u=1, and θ1001l=0.878. Thus, θ100Xu=0.935 and θ100Xl=0.813. Here adjusting for X₁ yields a smaller upper bound resulting in narrower bounds, i.e., [CE^l, CE^u] = [−0.137, 0.05] to [CEX1l,CEX1u]=[-0.137,-0.015]. Moreover, the adjusted upper bound is less than the null value of 0, indicating treatment has an effect in the NI principal stratum; such a conclusion was not possible prior to adjusting for X₁. On the other hand, adjusting for X₂ in the second trial yields no improvement in the bounds because θ100Xu=1=θ100u and θ100Xl=0.813=θ100l.

A graphical depiction of the unadjusted and adjusted bounds is given in Figure 1. The unadjusted bounds correspond to where the solid lines intersect the unit square. Bounds within strata defined by X correspond to where the dashed and dotted lines intersect the unit square. The adjusted bounds, represented by ○ and +, are weighted averages of these stratum specific bounds. For example, in the upper left panel corresponding to trial 1 and X₁, we see that θ100Xl is greater than θ100l because the vertical value of + is greater than zero, the point where the solid line intersects the horizontal axis.

The examples in the preceding section illustrate that adjusting for a baseline covariate may or may not improve the bounds on CE. In this section, we give necessary and sufficient conditions for when the adjusted bounds (7) will be narrower than the unadjusted bounds of (3). Proofs of all propositions are given in Web Appendix A.

The unadjusted and adjusted bounds can be consistently estimated by plugging in consistent estimators of the component parameters of the bounds. Specifically, let

γ^=min{∑(1-Si)(1-Zi)/∑(1-Zi)∑(1-Si)Zi/∑Zi,1} and

γ^x=min{∑(1-Si)(1-Zi)I(Xi=x)/∑(1-Zi)I(Xi=x)∑(1-Si)ZiI(Xi=x)/∑ZiI(Xi=x),1}, where ∑=∑i=1n and I() is the usual indicator function. Likewise, let ϕ̂_x = Σ(1 − S_i)(1 − Z_i)I(X_i = x)/Σ(1 − S_i)(1 − Z_i), π̂_z = ΣY_i(1 − S_i)I(Z_i = z)/Σ(1 − S_i)I(Z_i = z), and π̂_zx = ΣY_i(1 − S_i)I(Z_i = z, X_i = x)/Σ(1 − S_i)I(Z_i = z, X_i = x). In the data example presented in Section 8 below, individuals drop out of the study prior to evaluation of Y_i so that the simple moment estimators π̂_z and π̂_zx given above will not be possible to compute. We ignore this complication for now and will return to this issue below.

Consistent estimators of the unadjusted bounds are CE^l=θ^100l-θ^000 and CE^u=θ^100u-θ^000 where θ^100l and θ^100u are obtained by plugging in π̂₁ and γ̂ into (3) and θ̂₀₀₀ = π̂₀. Similarly, letting θ^100xl and θ^100xu denote (6) evaluated at π̂_1x and γ̂_x, consistent estimators of the unadjusted bounds are CE^Xl=θ100Xl-θ^000 and CE^Xu=θ^100Xu-θ^000 where θ^100Xl and θ^100Xu are obtained by plugging in ϕ̂_x, θ^100xu, and θ^100xl into (7).

These estimated bounds reflect ignorance due to partial identifiability but do not account for uncertainty due to sampling variability; such uncertainty intervals can be constructed using the approach of Imbens and Manski (2004) and Vansteelandt et al. (2006). In particular, Lee (2009) proved the estimated unadjusted bounds CE^l and CE^u are asymptotically normal under standard regularity conditions and provided that Pr[S_i(1) < S_i(0)] > 0, i.e., treatment has a protective effect on the intermediate variable S_i. Under these conditions, a (1 − α) × 100% pointwise uncertainty interval for CE is given by

(10)[CE^l-cα/2∗var^{CE^l}1/2,CE^u+cα/2∗var^{CE^u}1/2] where cα/2∗ can be computed using equation (4.3) of Vansteelandt et al. (2006), and var^{CE^l} and var^{CE^u} are consistent estimators of var{CE^l} and var{CE^u}. As n → ∞, the interval (10) will contain CE with probability (1 −α). A pointwise uncertainty interval based on the estimated adjusted bounds can be constructed analogously.

The Breastfeeding, Antiretroviral, and Nutrition (BAN) study was a randomized clinical trial to assess interventions for the prevention of breast milk transmission of HIV in 2369 HIV infected mothers and their infants in Lilongwe, Malawi (Chasela et al. 2010). There were three arms in the BAN study: daily antiretroviral therapy (ART) for the infant, daily ART for the mother, or control. While the primary analysis of the study considered comparisons of both ART arms to control, we will focus on comparing the infant ART and control arms only. The primary endpoint of BAN was infant HIV infection by τ = 28 weeks, so we let Y_i = 1 if the infant was HIV positive by 28 weeks and Y_i = 0 otherwise. Per protocol, infants who died or were infected in the first two weeks post-treatment were to be excluded from the primary analysis. Let S_i = 1 if the infant became HIV positive or died by τ₀ = 2 weeks, S_i = 0 otherwise. An analysis that compares randomization groups conditional on S_i = 0 is subject to selection bias. Instead we let the target of inference be CE, the change in risk of infection by 28 weeks due to infant ART in infants who would be HIV negative and alive at two weeks regardless of randomization assignment. Below estimated unadjusted bounds for CE are compared with estimated adjusted bounds based on a binary variable X_i indicating low birth weight (< 2.5 kg), i.e., X_i = 1 if the infant was of low birth weight, 0 otherwise.

Table 2 presents data on S and X from BAN by randomization arm. The proportion of infants who die or become HIV infected by two weeks is somewhat higher in the control group (5.7% versus 4.6%), although the difference is not statistically significant (Fisher’s exact test two-sided p = 0.35). That the proportion was higher in the control group supports the monotonicity assumption. Because some mother-infant pairs dropped out of the study prior to 28 weeks, the simple moment estimators of π_z and π_zx given in Section 7 cannot be computed. In the absence of competing risks and informative censoring, π_x and π_zx can be consistently estimated using the Kalpan-Meier estimator. However, in the BAN study death and breastfeeding cessation prior to HIV infection were competing risks. Therefore the Aalen-Johansen estimator (Aalen and Johansen 1978) for the cumulative incidence function can be used to estimate π_z and π_zx; see Long and Hudgens (2012) for additional details. The Aalen-Johansen estimates (ignoring X) were π̂₀ = 0.0581 and π̂₁ = 0.0141. Using these estimates, the estimated unadjusted lower and upper bounds of CE are [CE^l,CE^u]=[-0.0556,-0.0438]. Stratifying by X, the Aalen-Johansen estimators for each randomization arm were π̂₀₀ = 0.0609, π̂₀₁ = 0.0233, π̂₁₀ = 0.0107, and π̂₁₁ = 0.0604. Therefore the estimated adjusted lower and upper bounds are [CE^Xl,CE^Xu]=[-0.0482,-0.0431].

In this example, the estimated adjusted lower bound is greater than the estimated unadjusted lower bound, which is expected based on Proposition 3 and the fact X_i satisfies (9) empirically, i.e., π̂₁₀ > (1 − γ̂₀) and π̂₁₁ < (1 − γ̂₁). On the other hand, the estimated adjusted upper bound is greater than the estimated unadjusted upper bound, empirically contradicting Proposition 1. That the estimated adjusted upper bound is not less than the estimated unadjusted upper bound is actually not surprising based on Proposition 2 and the fact X_i does not satisfy (8) empirically, in particular π̂_1x < γ̂_x for x = 0, 1. This suggests the adjusted and unadjusted upper bounds are equal, in which case no particular ordering between the adjusted and unadjusted estimators might be expected. Grilli and Mealli (2008) reported a similar finding in an analysis of employment data of university students. This apparent contradiction between the estimated bounds and Proposition 1 suggests alternative adjusted estimators of the bounds, namely CE∼Xl=max{CE^l,CE^Xl} and CE∼Xu=min{CE^u,CE^Xu}. These estimators are consistent for CEXl and CEXu and by construction will always empirically satisfy Proposition 1, i.e., will always be at least as narrow as the estimated unadjusted bounds. For the BAN data, [CE∼Xl,CE∼Xu]=[-0.0482,-0.0438]. That is, by adjusting for the baseline covariate X indicating lower birth weight, the estimated bounds on CE are 63% narrower than the estimated unadjusted bounds.

Uncertainty intervals corresponding to the estimated unadjusted and adjusted bounds were computed using (10) with bootstrap variance estimates (as in Long and Hudgens 2012). For the unadjusted bounds, the estimated 95% pointwise uncertainty interval equals [−0.076, −0.025]. Corresponding to the estimated adjusted bounds [ CE∼Xl,CE∼Xu] based on the low birth weight indicator, the estimated 95% pointwise uncertainty interval equals [−0.069, −0.024], i.e., adjusting for low birth weight also results in a narrower estimated uncertainty interval.

As noted at the end of Section 3, in the absence of covariate X, CE is identifiable if and only if one of the following three conditions occur: γ = 1, π₁ = 1, or π₀ = 0. When at least one of these conditions holds, CE is identifiable and θ100u=θ100l, i.e., the bounds collapse to a single point. In this section we consider conditions under which adjusting for the binary covariate X renders CE identifiable in the sense that the adjusted bounds collapse to a point, i.e., CEXl=CEXu. By the form of the adjusted bounds given in (7) and the assumption ϕ_x > 0 for x = 0, 1, it follows that the adjusted bounds yield a single point if and only if

(11)γx=1,π1x=1,orπ1x=0 for x = 0 and x = 1.

Ding et al. (2011) also considered identifiability of a principal effect when outcomes are truncated by death, which is mathematically identical to the problem considered here. In addition to Assumptions 1 and 2 above, Ding et al. provided two additional assumptions which are sufficient for identifiability: (i) X_i ⊥ Y_i|{S_i(0), S_i(1), Z_i} and (ii) Pr[X_i = x|S_i(0) = S_i(1) = 0] ≠ Pr[X_i = x|S_i(0) = 1, S_i(1) = 0]. Unfortunately, assumption (i), which under Assumption 1 can be equivalently stated as X_i ⊥ Y_i(z)|{S_i(0), S_i(1)} for z = 0, 1, is in general not subject to empirical test based on the observable data. Ding et al. also gave sufficient identifiability conditions that do not require (i) but instead require that X takes on at least three levels or is continuous and that the mean of Y satisfies a particular linear model.

In contrast, condition (11) can be assessed from the observable data because γ_x and π_1x are identifiable under Assumptions 1 and 2 only. Moreover, (11) suggests a strategy for selecting X. In particular, if a covariate X can be found such that (11) holds for x = 0, 1, then CE will be identifiable. If no such covariate is available, then selecting X such that (11) approximately holds for x = 0, 1 should yield adjusted bounds with width close to zero. For instance, in the MTCT from the previous section, the low birth weight indicator covariate X yields γ̂₀ = 1.000, i.e., (11) empirically holds for x = 0; while (11) does not hold empirically for x = 1, π̂₁₁ = 0.0604 is not too far from zero and indeed the birth weight adjusted bounds for CE are substantially narrower than the unadjusted bounds.

Finally, we note two special cases where X_i identifies CE. First, suppose X_i = 1 if and only if S_i(0) = S_i(1) = 0, i.e., X_i is a perfect predictor of membership in the NI principal stratum. Then trivially CE is identifiable under Assumption 1 alone by the stratum of individuals with X_i = 1. This first case is related to the “principal score,” i.e., the probability an individual is within a principal stratum conditional on one or more covariates (Jo and Stuart, 2009). In practice, principal scores are not known but predicted based on fitted models using the observed data. For example, in the MTCT setting a model for Pr[S_i(0) = S_i(1) = 0|X_i = x] can be fit using data from infants assigned Z_i = 0 because under Assumptions 1 and 2 such infants are in the NI stratum if and only if S_i = 0. If a set of one or more baseline covariates (not necessarily binary or even discrete) can be found such that the principal scores for the NI stratum equal zero or one for each individual, then CE is identified by the stratum of individuals with principal scores equal to one. In practice this may not be possible; however, if covariates can be found such that the principal scores for the NI stratum are all close to zero or one, i.e., the principal scores are highly predictive of NI stratum membership, then the adjusted bounds constructed by stratifying on a dichotomization of the principal score should have width near zero. For the second special case, suppose Y_i = 1 if and only if X_i = 1, i.e., X_i is a perfect predictor of Y_i. Then π₁₀ = 0 and π₁₁ = 1 implying (11) holds for x = 0 and x = 1 and therefore CEXl=CEXu. In settings where Z_i has an effect on Y_i and Z_i is assigned randomly, no such perfect predictor X_i will exist (because X_i is measured pre-randomization), such that the second case seems to have little practical implication.

In this paper we considered whether bounds on principal effects can be improved by adjusting for a categorical baseline covariate. Necessary and sufficient conditions were derived for which the covariate adjusted bounds will be sharper (i.e., narrower) than the unadjusted bounds. The methods were illustrated using data from a study of interventions to prevent mother-to-child transmission of HIV through breastfeeding. Using a baseline covariate indicating low birth weight, the estimated adjusted bounds for the principal effect of interest were 63% narrower than the estimated unadjusted bounds.

The veracity of the analysis of the BAN trial depends on several key assumptions. Assumption 1, independent treatment assignment, is reasonable because infants were randomly assigned treatment. Assumption 2, monotonicity, implies that the treatment is no worse than control for any individual in terms of the intermediate variable S. As mentioned in Section 8 this assumption is supported by the observed data. Additionally, the BAN study principal investigator, Dr. Charles van der Horst, has indicated that monotonicity is reasonable (personal communication). However, in other settings this assumption may be unrealistic. For example, monotonicity might be considered questionable in an analysis comparing the two active arms of the BAN trial, i.e., infant ART versus maternal ART. In such settings, bounds that do not require the monotonicity assumption would be needed.

There are several possible avenues of related future research. One possible direction entails studying how adjusting for covariates affects the efficiency with which the bounds are estimated. For example, is it possible that certain covariates could be advantageous to adjust for with respect to sharpening bounds, but disadvantageous to adjust for in terms of efficiency? In the presence of multiple baseline covariates, future research could explore a formal approach for determining which covariates to adjust for (or include in a principal score model) and how to subsequently draw valid inference accounting for the covariate selection process. Related to Assumption 2, future research could examine relations between adjusted and unadjusted bounds when monotonicity is assumed for the primary endpoint Y.