A method to account for covariate-specific treatment effects when estimating biomarker associations in the presence of endogenous medication use

Abstract

In the modern era, cardiovascular biomarkers are often measured in the presence of medication use, such that the observed biomarker value for the treated participants is different than their underlying natural history value. However, for certain predictors (e.g. age, gender, and genetic exposures) the observed biomarker value is not of primary interest. Rather, we are interested in estimating the association between these predictors and the natural history of the biomarker that would have occurred in the absence of treatment. Nonrandom medication use obscures our ability to estimate this association in cross-sectional observational data. Structural equation methodology (e.g., the treatment effects model), while historically used to estimate treatment effects, has been previously shown to be a reasonable way to correct endogeneity bias when estimating natural biomarker associations. However, the assumption that the effects of medication use on the biomarker are uniform across participants on medication is generally not thought to be reasonable. We derive an extension of the treatment effects model to accommodate effect modification. Based on several simulation studies and an application to data from the Multi-Ethnic Study of Atherosclerosis, we show that our extension substantially improves bias in estimating associations of interest–particularly when effect modifiers are associated with the biomarker or with medication use–without a meaningful cost of efficiency.

Introduction

A common goal in epidemiologic studies is to estimate the association between a predictor such as age, or a single-nucleotide polymorphism (SNP) and a biomarker outcome (e.g., low-density lipoprotein).¹ In modern observational studies, a sizable portion of study participants may be on medication to reduce their natural biomarker values.² However, when studying such associations, there are settings in which the untreated biomarker is of principal interest. For instance, if the predictor of interest is a primordial or long-term variable such as age, gender, race, or a SNP, the association with the natural history of the biomarker that would have occurred in the absence of medication use is generally of greater scientific interest than the association with the observed biomarker. Medication use is nonrandom in that treated participants tend to have higher underlying (off-medication) biomarker values as compared to untreated participants. This is to say that medication use is endogenous. Endogenous medication use acts a contaminant when estimating the “natural history” association (namely, the association in the hypothetical setting where no participants are on medication), causing a specific type of missing data on the outcome of interest.

It is generally understood that simple approaches (e.g., adjustment for medication use in linear regression) are not appropriate for the purposes of estimating the effect of the medication on the biomarker when there is endogeneity.³ However, such approaches are commonly applied in practice for estimating biomarker associations with other variables in the same setting.^1,4-8 Although methodological advances have been made to reduce endogeneity bias when estimating associations between predictors and biomarkers in longitudinal data,^9,10 there is a noted lack of approaches that can be applied in a cross-sectional setting to address this challenge. Cross-sectional data are sometimes the best available for answering a question, particularly for populations in which it is difficult to obtain repeated measures over time (e.g., the homeless). Cost and safety (e.g., radiation exposure) can also limit the ability to obtain repeated measures on certain variables. In cohort studies, measurements on certain biomarkers might also be taken only at a single time point, leaving no alternatives to cross-sectional methods when analyzing those biomarkers.

We have previously proposed use of the treatment effects model (TEM) as a reasonable way to correct endogeneity bias when estimating associations between predictors and biomarkers in cross-sectional data when there is endogenous medication use.^11,12 Note that the phrase “treatment effects model” is the simpler name given to what James Heckman originally referred to as the hybrid model with structural shift; this name arose from the fact that this model was proposed to estimate the average effect of some treatment (medication use in our example) on the outcome of interest. Throughout this research, we are taking a clear departure from the historical use of this modeling framework. The distinction between the original purpose and our proposed use is that we seek to estimate the association between a predictor and the natural history of the biomarker, treating the effects of medication use as a nuisance rather than a quantity of interest.

Prior work was conducted to evaluate the strengths of using the TEM to estimate associations of interest.¹² This research revealed low sensitivity to departures from many of the model’s main assumptions (most interestingly, violations to bivariate normality). One assumption to which the TEM appears to be particularly sensitive is the assumption of uniform treatment effects; namely, the expected difference between the underlying and observed biomarker is assumed to be the same in all treated participants. If a predictor of interest modifies the effects of medication use, the TEM does not provide a consistent estimate of the association between that predictor and the underlying biomarker. Effect modifiers are often to be expected in practice. In LDL, for instance, the effect of medication use is understood to depend upon the class of medication used.¹³ Differential efficacy might also appear across race categories or genetic exposures.¹⁴

Heckman Urzua, and Vytlacil developed instrumental variable (IV) methods for estimation of average treatment effects in the presence of certain forms of random treatment effect heterogeneity.¹⁵ While such a framework can be of use in order to estimate associations between a predictor and a biomarker, little work has been done to accommodate systematic heterogeneity in the effects of medication use, such that the expected treatment effects vary with observable covariates. Moreover, IV approaches rely on the existence of an instrument; such exclusion restrictions are untestable and generally unlikely to hold in cross-sectional observational data. The TEM and other Heckman selection-based models, in contrast, do not demand the existence of an IV in order to estimate the association between a predictor and a biomarker, although they can reduce variability of estimates when they are available.^12,16,17 Our approach to this research is therefore to focus specifically on the TEM framework; we propose an extension to allow covariate-specific effects, accommodating treatment effect modifiers that are associated with the underlying biomarker, with the probability of medication use, or with neither.

This paper is organized as follows: we will derive the proposed model (showing identifiability of parameters), and present a testing procedure for presence of systematic heterogeneity. We will follow up with a number of simulation studies to demonstrate the advantages of accommodating effect modification. We will also illustrate our results with an application to LDL from the Multi-Ethnic Study of Atherosclerosis (MESA). Finally, we will discuss our findings and future directions for research.

The Treatment Effects Model with Covariate-Specific Effects

Notation

Let i = 1,…, N index the independently sampled study participants, each with observed biomarker y_i. Let z_i denote the indicator of medication use for subject i, taking on the value 1 if on medication, and 0 if off medication. Then, denote subjects’ potential outcome y_i(z_i) to be the potential biomarker value under medication use status z_i, so that in particular, y_i = y_i(0) if z_i = 0. Let x_i denote a set of covariates predicting the underlying biomarker. The parameter of interest, β, is the association between x and y(0), so that $\mathbb{E}[y_i(0)\mid {\mathit{x}}_i]={\mathit{x}}_i^T\beta$. Let w_i denote a set of covariates predicting medication use, and v_i a set of covariates predicting the effect of medication use on the biomarker (effect modifiers). These three covariate vectors all allow for an intercept, and they may share common predictors (e.g., age may predict both the biomarker and medication use).

Structural Equations and Identifiability

The treatment effects model with covariate-specific effects can be described as follows: suppose that $y_i(0)={\mathit{x}}_i^T\beta +{ϵ}_i$, where ϵ_i are independent and identically distributed (i.i.d.) normally distributed errors with unknown variance ${\sigma }_y^2$. The probability of medication use can be represented by a probit model: $P(z_i=1\mid {\mathit{w}}_i)=\Phi ({\mathit{w}}_i^T\alpha )$, where Φ denotes the standard normal cumulative distribution function (CDF). Another way to write this is with a latent continuous variable $z_i^{\ast }$, so that $z_i^{\ast }={\mathit{w}}_i^T\alpha +{\gamma }_i$, and γ_i are i.i.d. normally distributed errors of variance ${\sigma }_z^2$. The error terms ϵ_i and γ_i are permitted to be correlated with correlation parameter ρ. Since α and ρ are only identifiable up to a scale factor of σ_z, it is convenient to simply set σ_z = 1, as is standard in probit analysis.¹⁸ Finally, suppose that the observed biomarker can be written as $y_i=y_i(0)-{\mathit{v}}_i^T\eta z_i$, where ${\delta }_i\equiv {\mathit{v}}_i^T\eta$ denotes the covariate-specific effect of medication use. An alternative way to express this is through the on-medication potential outcome: y(1) = y(0) + v^Tη, such that $\mathbb{E}[y(1)\mid \mathit{x},\mathit{v}]={\mathit{x}}^T\beta +{\mathit{v}}^T\eta$. Formally, the errors on y(0) and y(1) conditional on x and v are presumed to be the equal, though we will show in the following section how this assumption can be relaxed by using a robust variance estimator. The covariate-specific effect component is the modification that distinguishes this model from the original TEM, which presumes that $\mathbb{E}[y_i(1)-y_i(0)]=\delta$ for some real-valued parameter δ. The covariates of v may contain continuous variables such as age, or discrete variables such as medication class or dose. Maddala proved that β, η, and ${\sigma }_y^2$ are identifiable when no effect modifiers are present (i.e., when v_i is simply an intercept and η = δ).¹⁹ We follow a similar methodology to sketch a proof that parameters are still identifiable in the presence of effect modifiers.

Let A denote a 2 × 2 nonsingular matrix and Σ the covariance matrix for (ϵ, γ). Let $\tilde{\mathit{x}}$ denote a vector of length p containing all unique predictors in x, w, and v (each having q₁, q₂, and q₃ predictors, respectively), and partition this complete covariate vector into seven total classes: ${\tilde{\mathit{x}}}_{(1)}$, ${\tilde{\mathit{x}}}_{(2)}$, and ${\tilde{\mathit{x}}}_{(3)}$ denote the predictors in x only, w only, and v only, respectively. Then, ${\tilde{\mathit{x}}}_{(4)}$, ${\tilde{\mathit{x}}}_{(5)}$, and ${\tilde{\mathit{x}}}_{(6)}$ denote predictors in x and w but not v, in x and v but not w, and in v and w but not in x, respectively. Finally, ${\tilde{\mathit{x}}}_{(7)}$ denotes the predictors appearing in all x, w, and v. The parameters β, α, and η can be partitioned accordingly as well. If o = (y, z*)^T denotes the (partially observed) outcome vector, and ${\tilde{\mathit{x}}}^{\prime }=(1,\tilde{\mathit{x}},\mathit{v}\times z)$ the covariate vector, the structural equations can be written as $\mathit{A}\mathit{o}-\Gamma {\tilde{\mathit{x}}}^{\prime }=(ϵ,\gamma {)}^T$ for a 2 × (p + q₃ + 1) matrix of coefficients, Γ, given by:

$$\Gamma =\left[\begin{array}{ccccccccc}\hfill 1\hfill & \hfill {\beta }_{(1)}^T\hfill & \hfill 0^T\hfill & \hfill 0^T\hfill & \hfill {\beta }_{(2)}^T\hfill & \hfill {\beta }_{(3)}^T\hfill & \hfill 0^T\hfill & \hfill {\beta }_{(4)}^T\hfill & \hfill {\eta }^T\hfill \\ \hfill 1\hfill & \hfill 0^T\hfill & \hfill {\alpha }_{(1)}^T\hfill & \hfill 0^T\hfill & \hfill {\alpha }_{(2)}^T\hfill & \hfill 0^T\hfill & \hfill {\alpha }_{(3)}^T\hfill & \hfill {\alpha }_{(4)}^T\hfill & \hfill 0^T\hfill \end{array}\right].$$

The system can be simplified to $\mathit{o}=\Pi {\tilde{\mathit{x}}}^{\prime }+({ϵ}^{\prime },{\gamma }^{\prime }{)}^T$, where Π = A⁻¹Γ, and the error vector has covariance matrix Ω ≡ A⁻¹ ΣA^−T. Letting

$$\Lambda =\left[\begin{array}{cc}\hfill 1\hfill & \hfill 0\hfill \\ \hfill 0\hfill & \hfill 1∕{\sigma }_z\hfill \end{array}\right],$$

Maddala shows that when the structural equations can be written in this form, parameters appearing in matrices ΛΠ and ΛΩΛ^T are identifiable.¹⁹ The result that β, η, and ${\sigma }_y^2$ are identifiable follows from setting A to be the 2 × 2 identity matrix.

The TEM presumes that dependence of z on y(0) is explainable by correlation in their respective error terms. Bivariate normality provides weak identifiability of ρ. In the setting of cardiovascular biomarkers, where y(0) may be highly predictive of z, one may wish to accommodate dependence of z on y(0) by including, e.g., λy(0) in the medication use model, as in the upper panel of Figure 1. However, this indirect feedback loop demands an instrument for the y(0) → z association to recover weak identification of ρ, which may not exist in theory or be available in practice. We propose decomposition of the term λy(0) into its systematic and random components as follows:

$$\begin{gathered} z^{\ast }={\mathit{w}}^T\alpha +\lambda y(0)+\gamma \\ ={\mathit{w}}^T\alpha +\lambda {\mathit{x}}^T\beta +\lambda ϵ+\gamma \\ ={\tilde{\mathit{w}}}^T\tilde{\alpha }+\tilde{\gamma }, \end{gathered}$$

such that $\tilde{\mathit{w}}=(1,{\tilde{\mathit{x}}}_{(1)},{\tilde{\mathit{x}}}_{(2)},{\tilde{\mathit{x}}}_{(4)},{\tilde{\mathit{x}}}_{(5)},{\tilde{\mathit{x}}}_{(6)},{\tilde{\mathit{x}}}_{(7)}{)}^T$, and

$$\tilde{\alpha }=\{\begin{array}{cc}\alpha \hfill & \text{for}\text{covariates}\text{in}\mathit{w}\text{only}({\tilde{\mathit{x}}}_{(1)}\text{and}{\tilde{\mathit{x}}}_{(5)}),\hfill \\ \lambda \beta \hfill & \text{for}\text{covariates}\text{in}\mathit{x}\text{only}({\tilde{\mathit{x}}}_{(2)}\text{and}{\tilde{\mathit{x}}}_{(6)}),\hfill \\ \alpha +\lambda \beta \hfill & \text{for}\text{covariates}\text{in}\text{both}\mathit{x}\text{and}\mathit{w}({\tilde{\mathit{x}}}_{(4)}\text{and}{\tilde{\mathit{x}}}_{(7)}).\hfill \end{array}\phantom{\}}$$ (1)

Figure 1.

DAGs illustrating relationship between covariates and outcomes. Upper panel: Our proposed data generation mechanism in which y(0) influences z beyond the error correlation. Lower panel: A depiction of how the CSEM can be fitted to allow for the possibility of the influence of y(0) on z as per the upper panel, but without the feedback loop (all covariates of x and w are placed in the medication use model). Solid black circles indicate observed variables; dashed black circles indicate partially observed variables. The double arrow denotes correlation in the error terms. Note that the covariates of x, w, and v need not be unique, The upper-left arrow between x and y(0) in each DAG corresponds to the association of interest.

Since B(ϵ, γ)^T is bivariate normal for any nonsingular matrix B, the errors $(ϵ,\tilde{\gamma }{)}^T$ are bivariate normal; in this case,

$$\mathit{B}=\left[\begin{array}{cc}\hfill 1\hfill & \hfill 0\hfill \\ \hfill \lambda \hfill & \hfill 1\hfill \end{array}\right]$$

so that the updated variance component is given by ${\tilde{\sigma }}_z^2={\sigma }_z^2+{\lambda }^2{\sigma }_y^2$ and the updated correlation parameter is given by $\tilde{\rho }=(\lambda {\sigma }_y^2+\rho {\sigma }_y{\sigma }_z)∕({\sigma }_y{\tilde{\sigma }}_z)$. Thus, if one places all covariates of x into w (as in the lower panel of Figure 1), α can be estimated without the need to explicitly estimate λ, since we may set ${\tilde{\sigma }}_z=1$ and estimate $\tilde{\rho }$ directly. Estimating $\tilde{\alpha }$ in an unconstrained fashion (i.e., without the restrictions imposed by Equation 1) provides a class of models that includes the possibility that y(0) influences z. Modifying the proof of identifiability of β, η, and σ_y to accommodate inclusion of x into w is trivial in this case; the second row of the matrix Γ would be altered to include more covariates that may be estimated without constraints, and λ need not ever be estimated.

Identification of the natural history association additionally presumes the stable unit treatment value assumption (SUTVA) and consistency assumption; namely, that (y_i(0), y_i(1)) ⊥ z_j for 1 ≤ i ≠ j ≤ N, and y_i = y_i(0)(1 – z_i) + y_i(1)z_i. The former simply says that the potential outcomes are independent of the medication use status of other individuals; the second states that an individual’s observed biomarker is equal to their potential biomarker under his or her medication use status. Finally, we have the unconfoundedness assumption that $\mathbb{E}[y(j)\mid \mathit{x}]=\mathbb{E}[y(j)\mid \mathit{x},z]$ for j = 0, 1.

Maximum Likelihood and Covariance Estimation

Parameters may be estimated through maximum likelihood by jointly modeling the distribution of y_i and z_i; modeling the errors as bivariate normal,¹⁹ and letting θ = (α, β, η, ${\sigma }_y^2$, ρ) denote the parameter vector, the likelihood may be written as:

$$\begin{gathered} {\mathcal{L}}_{\mathit{V},\mathit{W},\mathit{X},\mathit{y},\mathit{z}}(\theta )=\prod _{i=1}^{N}p(y_i\mid z_i)p(z_i) \\ =\prod _{z_i=0}{\int }_{-\infty }^{0}p(y_i)dF(z_i^{\ast }\mid y_i)\prod _{z_i=1}{\int }_0^{\infty }p(y_i)dF(z_i^{\ast }\mid y_i) \\ =\prod _{i=1}^N\{\frac{1}{{\sigma }_y}\varphi \left(\frac{y_i-{\mathit{x}}_i^T\beta +{\mathit{v}}_i^T\eta z_i}{{\sigma }_y}\right)\phantom{\}} \\ \times \Phi \phantom{\{}\left((-1{)}^{1-z_i}\frac{{\mathit{w}}_i^T\alpha +\rho (y_i-{\mathit{x}}_i^T\beta +{\mathit{v}}_i^T\eta z_i)∕{\sigma }_y}{\sqrt{1-{\rho }^2}}\right)\}. \end{gathered}$$

The estimator based on this maximum likelihood approach is consistent and asymptotically efficient.¹¹ We term this model the covariate-specific effects model (CSEM). In order for the log-likelihood to achieve a global maximum on the interior of the parameter space, we require overlap in outcomes between the treatment groups:

$$\bigcap _{j\in \{0,1\}}\left(\underset{z_i=j}{\text{min}}{y}_i,\underset{z_i=j}{\max }{y}_i\right)\ne \varnothing .$$

When using the TEM, the robust variance-covariance estimator as proposed by White was previously found to provide approximately valid inference, both under correct model specification and under modest departures from assumptions.^12,20 We propose utilizing the robust variance estimator rather than the model-based variance estimator in order to accommodate modest forms of misspecification likely encountered in practice (e.g., error heteroscedasticity and probit model misspecification).

Wald Test of Systematic Heterogeneity

In practice, one might be unsure of whether or not certain covariates serve as effect modifiers. As a tool to test for evidence of effect modification, a robust Wald test can be implemented to test the null hypothesis H₀ : η = (η₀, 0, ⋯ , 0)^T against H₁ : (not H₀), for any real-valued η₀. If the parameter vectors α, β, and η are of dimensions (q₁ + 1), (q₂ + 1), and (q₃ + 1), respectively, define

$$\mathit{R}=\left[0_{q_3\times (q_1+q_2+3)}{\mathbf{I}}_{q_3\times q_3}{0}_{q_3\times 2}\right],$$

and, if $\widehat{\theta }$ is the estimate of θ from maximum likelihood and ${\mathit{S}}_N(\widehat{\theta })$ the robust variance estimator, a Wald statistic can be defined by

$$W_N=(\mathit{R}\widehat{\theta }{)}^T({\mathit{RS}}_N(\widehat{\theta }){\mathit{R}}^T{)}^{-1}(\mathit{R}\widehat{\theta }).$$

Under standard likelihood theory, we have that $W_N{\stackrel{}{\to }}_d{\chi }_{q_3}^2$ under H₀, so that W_n may be computed and compared to the (1 – α)-quantile of ${\chi }_{q_3}^2$ in order to test for effect modification.²¹ One may also use this robust Wald test analogously to test individual effect modifiers within v.

Discussion of DAG and Relation to Alternative Approaches

The DAG of Figure 1 provides a reasonable way of describing a realistic data generation mechanism that could give rise to cross-sectional observational data in our problem of interest. We use this DAG to explain why commonly used simpler approaches are not appropriate for estimating β, the association between x and y(0).

One common approach is to simply ignore medication use and fit the mean model $\mathbb{E}[y\mid \mathit{x}]={\mathit{x}}^T{\beta }_I$ using ordinary least squares linear regression.^5,8 This model estimates a different parameter than the one of interest. In particular, ${\beta }_{I,k}=\mathbb{E}[y\mid x_1,\dots ,x_k+1,x_{k+1},\dots ,x_{q_1}]-\mathbb{E}[y\mid \mathit{x}]$ characterizes how the observed biomarker varies in expectation across values of the predictor x_k. While this could be of interest in some settings, it is not a characterization of how the predictor x is associated with the natural history of the biomarker. Instead, β_I is influenced by the prevalence of medication use and the magnitude of its effects on the biomarker. Medication use ultimately mediates the association between x and y, but the natural history association, our parameter of interest, is that which could be directly estimated if no participants were on medication factor (under which y_i = y_i(0) would hold for all i).

Another approach that has been used previously is exclusion of on-medication participants from analysis.⁷ In this analysis, the mean model $\mathbb{E}[y\mid \mathit{x},z=0]={\mathit{x}}^T{\beta }_E$ is fit. This analysis tends to suffer from selection bias, as can be seen from the fact that z and y are correlated even after conditioning on all available covariates. For estimation of the natural history association, we do not wish to condition on z holding a certain value.

Considering the simple setting of uniform treatment effects for the time being, another approach commonly implemented is to adjust for medication use as though a confounder and fit the model $\mathbb{E}[y\mid \mathit{x},z]={\mathit{x}}^T{\beta }_A+{\delta }_A{z}_i$.^4,6 This approach estimates yet a different parameter: ${\beta }_{A,k}=\mathbb{E}[y\mid x_1,\dots ,x_k+1,x_{k+1},\dots ,x_{q_1},z]-\mathbb{E}[y\mid \mathit{x},z]$ describes how the observed biomarker from participants of the same medication use status vary in expectation across levels of the predictor x_k. Note that z does not act as a confounder for the association between x and y(0) since the predictor x and the outcome y(0) are both indirect causes of z. In the setting of treatment effect modification, one might include the covariates v^Tη_Az as opposed to a single parameter δ_Az. In this setting, the coefficient β_Α will have the same interpretation as that of the exclusion approach. We will consider both versions of the adjustment approach going forward.

This demonstrates that neither ignoring z nor conditioning on z are adequate for estimating the natural history association. Instead, estimates from these approaches characterize how participants differ in their observed biomarker values, either marginally or conditionally. The TEM (and our extension to the CSEM) instead models the joint distribution of y and z in order to estimate parameters of interest, under the assumptions of Figure 1. Tobin provides an in-depth examination surrounding the inadequacy of these approaches in the setting of nonrandom medication use.³ Tobin additionally considered other simple approaches such as fixed-addition, whereby a single value is added to the on-medication biomarker. Such an approach can work well if there is valid external or prior information on the effects of medication use, and if medication is similarly effective across participants. However, in the absence of either of these two conditions, this approach is not adequate. We focus on approaches that do not require external information on the effects of medication in the studied population.

Recognizing that the simpler approaches are not sufficient, instrumental variable approaches have also sometimes been used in this setting.¹⁷ In the one-stage approach, we presume (in addition to the standard SUTVA, consistency, and unconfoundedness assumptions) the existance of some instrument w that that satisfies the following properties: (1) w and z are correlated, (2) w ⊥ ϵ∣x. Defining w′ = (1, x^T, w)^T and z′ = (1, x^T, z)^T, the one-stage instrumental variables estimator is given by:

$$({\widehat{\beta }}_{IV}^T,\widehat{\delta }{)}^T={\left[\frac{1}{N}\sum _{i=1}^N{\mathit{w}}_i^{\prime }({\mathit{z}}_i^{\prime }{)}^T\right]}^{-1}\left[\frac{1}{N}\sum _{i=1}^N{\mathit{w}}_i^{\prime }{y}_i\right].$$ (2)

While such estimators can be perfectly reasonable in certain settings where the exclusion restriction is thought to hold, the major challenge is that the assumption of having an instrument is untestable and unlikely to hold in cross-sectional observational data.

Simulation Studies

In the presence of effect modification, the TEM is not correctly specified and hence may not provide consistent estimates of β. However, analytically computing either finite-sample or asymptotic bias of the TEM is not tractable, since the solutions to the likelihood equations do not possess a closed-form expression and must be obtained through computational approximation procedures such as the Newton-Raphson method. The relative advantages of allowing covariate-specific effects can be more effectively illustrated with simulation studies over a wide range of reasonable parameters. In this section, we consider a number of scenarios to address this.

For all scenarios, let N = 5,000 participants, and x₁, x₂, x₃ denote the set of predictors, all distributed i.i.d. $\mathcal{N}(0,1)$. Further let D ~ Bernoulli(p = 0.5). We may think of D as some “dose” or “class” variable that predicts the effect of medication use only. The data generation mechanism for y(0) and z* is given as follows for all simulation studies:

$$\begin{gathered} y_i(0)=50+x_{1i}+x_{2i}+{ϵ}_i \\ {z}_i^{\ast }=-5+x_{1i}+x_{3i}+0.1\times y_i(0)+{\gamma }_i \end{gathered}$$

where ${\sigma }_y^2={\sigma }_z^2=50$ and ρ = 0.5. That is to say that the covariance matrix for ϵ_i and γ_i is given by

$${\Sigma }_i=50\times \left[\begin{array}{cc}\hfill 1\hfill & \hfill 0.5\hfill \\ \hfill 0.5\hfill & \hfill 1\hfill \end{array}\right].$$

Relating back to the notation of the previous section (and in particular, Equation 1), the TEM and CSEM would be fit by including all covariates of x = (1, x₁, x₂)^T into w = (1, x₁, x₃)^T to create the larger covariate vector $\tilde{\mathit{w}}=(1,x_1,x_2,x_3{)}^T$, so that β = (50, 1, 1)^T and $\tilde{\alpha }=(0,1.1,0.1,1)$. This setup yields an approximate 50% prevalence of medication use at each replication. Additionally, $\mathbb{E}[y(0)\mid z_i=1]-\mathbb{E}[y(0)\mid z_i=0]\approx 6.5$ under this setup, and so we select the parameters in all scenarios such that the expected marginal treatment effect (that is, ${\mathbb{E}}_{\mathit{v}}[{\mathit{v}}_i^T\eta ]$) is about 3.75, placing all simulations on a comparable scale in which medication use is modestly effective on average. Based on this setup, the most general form of the data generating mechanism for y can be described by:

$$y_i=y_i(0)-({\eta }_0+{\eta }_1{x}_{1i}+{\eta }_2{x}_{2i}+{\eta }_3{x}_{3i}+{\eta }_4{D}_i)z_i.$$

Each simulation scenario focuses on a particular parameter or range of parameters in order to evaluate one or more of the following under different circumstances: (a) the extent of bias that arises from using the TEM when treatment effect modification is present, (b) the circumstances under which the CSEM reduces bias, and (c) the efficiency cost of using of the CSEM. These results aid us in providing recommendations for when to use the updated CSEM over the original TEM. We also compare these approaches to the classical one-stage IV approach (with x₃ as our true instrument), and the simpler approaches of Ignoring, Excluding, and Adjusting. For the adjustment approach, we consider two versions: (A) no interaction terms for x and z included, and (B) interaction terms included. The purpose of comparing the CSEM to the IV approach is to evaluate whether the IV method is particularly sensitive to effect modification, to demonstrate that the CSEM does not demand the existence of an instrument, and to evaluate potential differences in efficiency when an instrument does exist. The purpose of comparing the CSEM to the simple approaches is to confirm their inappropriateness when seeking to estimate the natural history association, and to evaluate the extent to which TEM can still reduce bias as compared to these approaches when effect modifiers are present. All simulation studies are conducted in R²², and the code for the negative log-likelihood is included in the supplementary material (Appendix I). Figure 2 illustrates which variables in the general simulation setup are also modifiers of the treatment effect for each scenario.

Figure 2.

Illustration of the data generation mechanism in each simulation scenario, depicting how different variables in the general simulation setup modify the effect of medication use. Green backgrounds denote modifiers of the treatment effect magnitude, and are used in place of arrows drawn to the arrow between z and y for variabels x₁, x₂, and x₃.

Scenario 1

In this scenario, we let η = (2.5, 0.5, 0.5, 0.5, 2.5)^T. Under this setup, the effect of medication use on the biomarker varies with all predictors. Again relating back to the notation of the previous section, we have that v_i = (1, x_1i, x_2i, x_3i, D_i)^T. Note that conditional on D_i = 0, the distribution of the effects is $\mathcal{N}(2.5,0.75)$, and conditional on D_i = 1, the distribution of the treatment effects is $\mathcal{N}(5,0.75)$. The subject-specific treatment effect therefore lies between 1 and 6.5 for the vast majority of participants. We conduct two-thousand simulation replicates under this setup. Table 1 presents results for estimation of β. Specifically, we present the estimates (averaged across all replicates), the Monte-Carlo standard error (the standard deviation of all the estimates from each replicate), and the estimated robust standard error estimate (averaged across all replicates).

Table 1.

Results from simulation study under scenario 1. Presented are the simulation estimates, Monte-Carlo standard errors (SE), and estimated robust standard errors ($\widehat{\text{SE}}$)

	β0 = 50			β1 = 1			β2 = 1
Method	Est.	SE	$\widehat{\text{SE}}$	Est.	SE	$\widehat{\text{SE}}$	Est.	SE	$\widehat{\text{SE}}$
CSEM	49.9	0.63	0.66	0.99	0.15	0.16	1.00	0.13	0.13
TEM	50.5	0.38	0.38	0.82	0.10	0.11	0.75	0.10	0.11
Ignore	48.1	0.09	0.09	0.54	0.09	0.09	0.73	0.09	0.09
Exclude	46.8	0.13	0.13	0.63	0.13	0.13	0.97	0.13	0.13
Adjust (A)	46.8	0.12	0.13	0.39	0.09	0.09	0.72	0.09	0.09
Adjust (B)	46.8	0.13	0.13	0.63	0.13	0.13	0.97	0.13	0.13
IV	52.5	1.20	1.19	1.04	0.18	0.18	0.78	0.12	0.12

The CSEM appeares to provide low-bias estimates of β as compared to the other approaches. In particular, estimates obtained from the Ignore, Exclude, and both Adjustment approaches are markedly biased, even under this setting in which the effect of the medication on y(0) is not very large relative to the difference in mean y(0) between participants on and off medication. Interestingly, the TEM appears to provide some bias reduction for estimation of β₁ relative to the simple approaches under this simulation setup, but not as much so for β₂. Likely, this is a consequence of the fact that x₁ is a strong predictor of medication use, and x₂ weakly predicts medication use (through the underlying biomarker). Comparing the bias of these the TEM compared to the CSEM confirms that the TEM can be quite sensitive to departures from the assumption of uniform treatment effects. The one-stage IV approach appears to provide biased estimates of β in the setting of effect modification, although the bias appears to be more extensive for estimation of β₂, much as with the TEM; interestingly, the TEM appears to be more sensitive to departures from the assumption of uniform treatment effects.

Additionally, we note that estimating the additional effect modifier parameters results in a loss of efficiency for the CSEM. However, the potential for bias reduction in this setting is objectively large enough to justify the efficiency loss: we estimate the mean squared error (MSE) in estimating β₁ to be 0.023 for the CSEM, as compared to 0.042 for the TEM; for β₂, the estimated MSE for estimating β₂ is 0.017 for the CSEM and 0.073 for the TEM. The gain in MSE was confirmed to be higher in follow-up simulations in which the overall expected treatment effect was higher. Of note also is that the robust standard error estimates all adequately represent the true repeat-sample standard errors.

To elucidate finite-sample bias for the CSEM, we simulate two-thousand replicates from scenario 1 under different sample sizes varying from N = 200 to N = 10,000. Results for estimation of β₁ and β₂ are depicted in Figure 3. We found evidence of bias for estimation of β₁ when smaller sample sizes are used (e.g., N = 200). Finite-sample bias under this simulation setup is negligible for sample sizes greater than N = 5,000, although even at N = 200, the estimated bias does not exeed that of any of the alternative approaches. For estimation of β₂, finite-sample bias appears to be smaller under this scenario setup, in which x₂ is not as strongly predictive of z.

Figure 3.

Illustration of finite-sample bias when using the CSEM. Point estimates are given based on the average of two-thousand simulation replicates at each sample size, and 95% confidence intervals are given based on the simulated standard error of the estimate (given by the Monte-Carlo based standard deviation divided by $\sqrt{2000}$). For sample sizes of N = 200-500, the CSEM can provide estimates that are modestly biased (although not as much so as the simpler approaches such as the Ignore approach). For sample sizes of larger than N = 5000, the finite-sample bias appears to be negligible in this setting.

The following scenarios focus on covariate-specific effects when they are generated from each predictor individually, in contrast to this example which considered effect modification from all predictors simultaneously. Since the intercept is rarely of interest in an association study, we do not present results on estimation of β₀ it in the studies that follow. Additionally, because the Adjust (B) approach is essentially equivalent to the Exclude approach as far as estimation of β₁ and β₂ are concerned, we do not consider that in the simulation scenarios that follow.

Scenario 2

The purpose of this study is to evaluate bias under a setting in which the source of systematic heterogeneity is a single factor associated with both the biomarker and medication use (in this case, x₁). In this scenario, we let η = (3.75, η₁, 0, 0, 0)^T, and we vary η₁ over a range of values from 0 to 1 (with one-thousand simulation replicates at each value considered). For the CSEM, we do not estimate η₂, η₃, or η₄. Increasing η₁ serves to increase the overall heterogeneity of the effects of medication use and does not alter the average effect of the medication on the biomarker (3.75).

Figure 4 illustrates the estimated bias from each method for β₁ and β₂ across the range of values for η₁. We find that the TEM and CSEM provide low-bias estimates of β₂, as compared to the Ignore, Exclude, and Adjust methods. The lines for these two methods are nearly indistinguishable since x₂ is not associated with the effects of the medication. However, the TEM does not provide valid estimates of β₁ when η₁ > 0; this finding is unsurprising since x₁ is associated with both the underlying biomarker and the effects of medication. Note that the TEM still provides modest advantages in bias as compared to the Ignore, Adjust, and Exclude approaches. In contrast to the TEM, the CSEM provides low bias estimates of β₁. The one-stage IV approach performes almost identically to the TEM. In a follow-up scenario in which x₂ was the sole effect modifier, the reverse pattern was observed for β₁ and β₂.

Figure 4.

Results from simulation scenario 2. The range of values considered for η₁ is shown on the x-axis, and the average estimates for ${\widehat{\beta }}_1$ (left) and ${\widehat{\beta }}_2$ (right) on the y-axis, for each method. Note that the true parameter values are given by β₁ = β₂ = 1.

Scenario 3

The purpose of this study is to evaluate bias under a setting in which the source of systematic heterogeneity is a single factor associated with medication use only (in this case, x₃). In particular, x₃ is not associated with the biomarker. In this scenario, we let η = (3.75, 0, 0, η₃, 0)^T, and we vary η₃ over a range of values from 0 to 1 (with one-thousand simulation replicates at each value considered). For the CSEM, we do not estimate η₁, η₂, or η₄. As with η₁ and η₂, increasing η₃ serves only to increase the heterogeneity of the effects of medication use.

Figure 5 illustrates the estimated bias from each method for β₁ and β₂ across the range of values for η₃. The CSEM provides low-bias estimates of β₁ and β₂, particularly compared to the Ignore, Exclude, and Adjust methods. Interestingly, the TEM shows bias for estimation of β₁ and β₂ when η₃ > 0; this is particularly apparent for β₁. The two determinants of a subject’s treatment effect are ${\mathit{v}}_i^T\eta$ and $z_i=1(z_i^{\ast }>0)$. Since x₃ is associated with both, there is systematic under- or over-correction in the treatment effects if x₃ is not included as an effect modifier (as in the TEM). Unsurprisingly, this creates substantial bias for the one-stage IV approach (particularly for estimation of β₁).

Figure 5.

Results from simulation scenario 3. The range of values considered for η₃ is shown on the x-axis, and the average estimates for ${\widehat{\beta }}_1$ (left) and ${\widehat{\beta }}_2$ (right) on the y-axis, for each method. Note that the true parameter values are given by β₁ = β₂ = 1.

Scenario 4

The purpose of this study is to evaluate bias under a setting in which the source of systematic heterogeneity is the single factor D_i, which is only associated with the magnitude of the medication’s effect (and in particular, not with the biomarker y or with medication use, z). In this scenario, we let η = (η₀, 0, 0, 0, η₄)^T, where η₀ ranges from 0 to 5, and η₄ = 5.5 – 2η₀, so that the marginal effect of medication use is constantly 3.75. We simulate one-thousand replicates at each pair of η₀ and η₄ considered. For the CSEM, we do not estimate η₁, η₂, or η₃.

Figure 6 illustrates the estimated bias from each method for β₁ and β₂ across the range of values for η₀. Interestingly, both the TEM and CSEM provide low-bias estimates of β₁ and β₂ in this setting; the Ignore, Exclude, and Adjust methods provide biased estimates of both parameters. The IV approach appears to provide valid estimates as well, although with slightly greater variability. These patterns were confirmed when D_i was generated continuously rather than as a binary variable, as illustrated in Appendix II of the supplementary materials. This study suggests that the TEM is robust to effect modification when the modifying source only influences the effect of the medication on the biomarker, and is not a predictor of the biomarker itself or medication use.

Figure 6.

Results from simulation scenario 4. The range of values considered for η₀ is shown on the x-axis, and the average estimates for ${\widehat{\beta }}_1$ (left) and ${\widehat{\beta }}_2$ (right) on the y-axis, for each method. Note that the true parameter values are given by β₁ = β₂ = 1.

In addition, we conducted a set of simulations in the setting where x₃ was weakly associated with y(0) (so that it would no longer be an instrument). The details of this simulation and the results are presented in Appendix III of the supplementary materials. In short, we verified that the CSEM does not demand the inclusion of a true instrumental variable, where the IV approach does, consistent with prior findings in similar Heckman-type models, in which there is no need to impose an exclusion restriction.¹⁶

Illustration from the Multi-Ethnic Study of Atherosclerosis: LDL & Hypolipidemic Drugs

The Multi-Ethnic Study of Atherosclerosis (MESA) is a multi-site cohort study of 6,814 men and women ages 45-84 years, designed to give insight into the progression of subclinical cardiovascular disease. Subjects were recruited from six U.S. communities, and were free of clinical cardiovascular disease at entry. The demographic breakdown is as follows: 47% men; 38% white, 28% African-American, 22% Hispanic, and 12% Chinese-American. All subjects provided written informed consent. Details of the sampling, recruitment, and data collection have been reported elsewhere.² We consider the Exam 1 data as an example of a naturally occurring cross-sectional data set.

We consider our motivating example of LDL cholesterol as an illustration of how one might use the CSEM to evaluate age, gender and race/ethnic differences in LDL. Using a complete-case analysis yields a total of N = 6, 658 subjects. At baseline, the prevalence of lipid-lowering drug use was 16.1% (1,072/6,658); the majority of drugs used were statins (988/1,072).

In the medication use (z*) model, we include the following covariates: age, gender, race, diabetes, insurance status, and Framingham Risk Score. Note that participants with diabetes are often placed on lipid-lowering drugs, hence the reason for this adjustment.²³ In addition, differential effects across the races would also be consistent with prior findings.^14,24 We compare the CSEM and TEM to one another, and also compare the results to those from the Ignore, Exclude, both Adjust approaches, and the one-stage IV approach, using health insurance status as the potential “instrument”. For the CSEM only, we considered age, gender, race, and medication class (statin vs. other), and diabetes to be potential effect modifiers.

Results from this example are presented in Table 2. First, we note that the Ignore approach could be naïvely interpreted as conclusive evidence that LDL cholesterol decreases with age; the Exclude and Adjust approaches do not provide sufficient evidence of an increasing or decreasing age trend. Both the CSEM and TEM models provide evidence that older people tend to have higher underlying LDL values, consistent with what we would expect. The one-stage IV approach provides a high estimate of the age-LDL association, but with substantially greater variability than the other approaches. The seven models provide comparable conclusions for the difference in mean LDL between males and females.

Table 2.

Results from LDL-demographic example in the Multi-Ethnic Study of Atherosclerosis. Presented are the estimates and standard errors for all coefficients in the biomarker model from the seven approaches considered. Results are expressed as “Estimate (SE)”

	Ignore	Exclude	Adjust (A)	Adjust (B)	IV	TEM	CSEM
Intercept	126 (2.4)	123 (2.6)	126 (2.4)	123 (2.6)	116 (4.3)	117 (2.6)	119 (2.7)
Age	−0.13 (0.04)	−0.035 (0.04)	−0.13 (0.04)	−0.035 (0.04)	0.19 (0.12)	0.16 (0.04)	0.15 (0.04)
Female	REF	REF	REF	REF	REF	REF	REF
Male	−1.06 (0.77)	−0.92 (0.84)	−1.06 (0.77)	−0.92 (0.84)	−1.00 (0.84)	−1.01 (0.83)	−1.15 (0.89)
White	REF	REF	REF	REF	REF	REF	REF
Black	−2.01 (1.19)	−2.25 (1.07)	−2.01 (1.19)	−2.25 (1.07)	−1.49 (1.11)	−1.44 (1.06)	−2.73 (1.13)
Hispanic	−0.65 (0.97)	1.07 (1.13)	−0.65 (0.97)	1.07 (1.13)	−0.27 (1.46)	−0.096 (1.12)	−0.41 (1.29)
Chinese	2.35 (1.05)	−2.84 (1.28)	2.35 (1.05)	−2.84 (1.28)	−4.24 (1.50)	−4.09 (1.28)	−4.48 (1.35)

The CSEM suggests that the difference in underlying LDL is greater between whites and Blacks than that suggested by the TEM. Although studying differential treatment effect patterns across predictors is not the focus of this paper, it is of particular interest the CSEM estimates the effect of medication use to be 7.8 mg/dL lower in Blacks than in whites (95% CI: [3.25, 12.3]). The effects of medication use were not found to be as different in Hispanics or in Chinese participants as compared to whites. The finding that the coefficient for Blacks is substantially different between the TEM and CSEM (as compared to the other coefficients) is of particular interest as it is consistent with the results of the simulation study; namely, this suggests that effect modifiers have the greatest impact on estimation when they also predict the biomarker.

The robust Wald test for presence of effect modification yields an overall p-value of p = 0.002. Testing each individual factor, medication class and race yielded strong evidence of effect modification (p < 0.001 and p = 0.008, respectively), whereas age, gender, and diabetes status did not achieve significance.

Discussion

In this paper, we have derived and evaluated an extension of the treatment effects model in order to accommodate effect modification when estimating the “natura historyl” association between a predictor of interest and a biomarker in the presence of endogenous medication use. In practice, the effects of medication use may systematically vary with factors such as medication class/dose, or with the predictors of interest. The TEM (and hence the CSEM) can be presented as a system of structural equations. The maximum likelihood approach to estimating parameters of interest allows one to regard the model essentially as a missing-at-random model, in which y(0) is unobservable in participants on medication. In the TEM, the appropriate correction (δ) to y_i is determined by a single value for all participants (this is the assumption of uniform effects), estimated simultaneously with the other parameters. When the effects of medication use vary with predictors of interest in the biomarker model, substantial bias can arise when using the TEM to estimate associations; this occurs because the single estimate of δ applied to on-medication participants systematically under- or over-corrects their observed biomarker values for the effects of medication use. Moreover, if the effect modifier is associated with medication use only, bias is also observed (albeit of lower magnitude in our simulations). The approach taken in the CSEM is to further condition the effects of medication use on potential effect modifiers to mitigate these problems.

Viewing the model extension in this way helps explain our finding that the TEM appears robust to misspecification of effect modifiers associated only with the treatment effects (i.e., when covariates in v do not appear in x or w). In this setting, the mean models for y_i (0) and $z_i^{\ast }$ are still correctly specified, and the variation in the effects of medication use across participants becomes absorbed into the error term in the biomarker model (which can be accounted for with the robust standard error estimator).

Our simulation results confirmed the inadequacy of the simpler approaches (ignoring medication use, excluding on-medication participants from analysis, and adjusting for medication use as a confounder) in the setting of endogenous medication use, and further demonstrated that the TEM can provide biased estimates of the natural association when predictors in the biomarker model modify the effects of the medication on the underlying biomarker. The one-stage IV approach was confirmed to be adequate if one has a valid instrument, but it can be highly sensitive to departures from the assumption that predictors of medication use do not modify the treatment effect. The proposed CSEM nearly eliminates this bias by specifically accommodating the effect modifiers, and does so without requiring an exclusion restriction. Under the setting of a modest average treatment effect, there is an efficiency loss that is inarguably small relative to the large bias reduction achieved, at least when considering measures such the MSE.

Our application to MESA provides results that were consistent with our simulation studies: (a) coefficients corresponding to predictors that strongly modify treatment effect are likely to be the most biased if effect modification is ignored, and (b) the estimates are ostensibly less biased when endogeneity is adequately accounted for (this is suggested by the finding LDL was found to have a positive trend with age in the TEM, CSEM, and IV method (although the IV method did not achieve significance), whereas the simpler approaches failed to confirm this expected result). We acknowledge the existence of two-stage IV approaches that accommodate further variables to be included as instruments. Among the variables that predicted medication use, health insurance status was likely the closest to satisfying the exclusion restriction demanded by the IV approach, and so we opted for the one-stage IV approach as an example. The CSEM does not demand such exclusion restrictions to hold under its alternative set of assumptions. We note that the finding of differential treatment effects in Blacks is not necessary a result of an inherent biologic characteristic–the models considered are incapable of providing evidence to support or reject this hypothesis. Rather, this result could be an artifact of lower adherence rates in this subgroup. Although the source of this difference is unclear, the importance of accounting for race category as a potential effect modifier is not any less important. If the result is in fact simply an artifact of lower adherence, then failure to account for effect modification would still result in systematically over-correcting the biomarker for the effects of medication use in Black participants–the treatment effect is understood to be smaller if adherence rates are lower.

We would additionally like to comment further on the importance of distinguishing between settings in which the observed biomarker or the natural history of the biomarker is of interest. For scientific and clinical problems involving prediction of further adverse cardiac events, the observed biomarker could very well of greater relevance than the hypothetical off-medication value for treated participants. However, when we seek to estimate how groups of individuals differing in primordial or long-term predictors (such as age, race, or a genetic exposure) differ in their biomarker outcomes, consideration of the natural history is of greater scientific relevance. Consider, for instance, the setting of cardiovascular biomarkers such as systolic blood pressure and LDL cholesterol. These are typically the target of reduction in participants with high underlying values. If the medication taken is effective in (at least partially) restoring participants’ values to the values of healthy participants, failure to account for medication use when selecting a model will, in general, result in an attenuated estimate of the association of interest. If medication use is prevalent and sufficiently effective, one might even be led to the erroneous conclusion age is not associated with cardiovascular biomarkers (as seen in our application to MESA). If the goal of the study is to identify important predictors of biomarkers, ignoring medication use will hence lead to severely under-powered study designs.

While we acknowledge that using cross-sectional observational data for quantifying associations poses a range of challenges, we believe that having a reasonable modeling tool such as the CSEM to account for the specific challenge of endogenous medication use with effect modification is important when cross-sectional data are the best available.

Recommendations and Future Directions

Previous work revealed that failure to account for endogeneity can result in bias when estimating the natural history association between a predictor and a biomarker. This follow-up work revealed that this improvement may be partially lost if the predictor of interest modifies the effect of medication use on the biomarker. Therefore, this modeling framework can be a useful tool in order to estimate associations when effect modifiers are thought to be well understood. In particular, this can be useful if there is no reliable instrument available.

On the other hand, there are settings in which effect modifiers might not be we well documented. The use of the robust Wald test can be used as a complimentary tool or an exploratory data analysis procedure to first test for effect modification before applying the TEM (which presumes uniform treatment effects). Based on the results of this research, we recommend using the CSEM in conjunction with the TEM framework in order further reduce bias in estimating associations of interest when endogenous medication use is present.

When effect modifiers are present but are unrelated to the underlying biomarker or to medication use, the advantages to accounting for them is not as clear, unless understanding differential treatment effect patterns is of interest. More work is underway to evaluate the potential advantages to using this model as a tool to understand treatment effect patterns. Further work is being conducted to test the sensitivity of the CSEM to departures from its main assumptions, including the conditional mean independence assumption. Additionally, it will be of interest to further evaluate the CSEM to mean model misspecification, including departures from linearity.