Using a Surrogate Marker for Early Testing of a Treatment Effect

Summary:

The development of methods to identify, validate and use surrogate markers to test for a treatment effect has been an area of intense research interest given the potential for valid surrogate markers to reduce the required costs and follow-up times of future studies. Several quantities and procedures have been proposed to assess the utility of a surrogate marker. However, few methods have been proposed to address how one might use the surrogate marker information to test for a treatment effect at an earlier time point, especially in settings where the primary outcome and the surrogate marker are subject to censoring. In this paper, we propose a novel test statistic to test for a treatment effect using surrogate marker information measured prior to the end of the study in a time-to-event outcome setting. We propose a robust nonparametric estimation procedure and propose inference procedures. In addition, we evaluate the power for the design of a future study based on surrogate marker information. We illustrate the proposed procedure and relative power of the proposed test compared to a test performed at the end of the study using simulation studies and an application to data from the Diabetes Prevention Program.

1. Introduction

The use of short term treatment response to make inferences about long term treatment effects and assist in earlier decision making has been an area of active methodological research. Recently, the general public’s interest in this area of research has grown dramatically due to two recent public health crises: the Ebola virus and the Zika virus. There are no proven vaccines or treatments available to the public for either of these viruses, and research organizations are striving to find effective solutions. However, the development and testing of vaccines and treatments often require years of research. Rigorous testing is essential to ensure that treatments are safe, effective, and do not lead to unintended consequences. However, in many clinical settings, there are often early indications based on biomarkers or intermediate outcomes that could potentially be used to infer about the treatment effect on the primary outcome. That is, the use of valid “surrogate” markers or outcomes may have the potential to allow for earlier testing for a treatment effect, thus reducing needed follow-up and costs.

A broad range of methods and measures for assessing the value of surrogate markers have been developed. Most notably, Prentice (1989) laid the foundation for this work by proposing a definition for a valid surrogate marker and operational criteria for the identification of valid surrogate markers. Building on top of Prentice (1989), several authors have proposed parametric and non-parametric approaches to quantify the proportion of treatment effect on the primary outcome that is explained by the treatment effect on the surrogate marker (Freedman et al., 1992; Wang and Taylor, 2002; Taylor et al., 2005; Parast et al., 2017). In a principal stratification framework, various quantities have been proposed to assess the utility of a surrogate marker including dissociative effects, associative effects, average causal necessity, average causal sufficiency, and the causal effect predictiveness surface (Frangakis and Rubin, 2002; Huang and Gilbert, 2011; Gilbert and Hudgens, 2008; Conlon et al., 2014; Gabriel and Gilbert, 2014). These quantities are often for use in a single study setting, as opposed to a meta-analytic setting where multiple studies are available to investigate the surrogate marker and where alternative measures have been developed to validate surrogacy (Buyse and Molenberghs, 1998; Daniels and Hughes, 1997).

In terms of using surrogate marker information to test for a treatment effect, several methods have been proposed to increase efficiency through the use of surrogate marker or intermediate event information, when combined with the primary outcome at the end of a study (Pepe, 1992; Venkatraman and Begg, 1999; Parast et al., 2014; Robins and Rotnitzky, 1992; Rotnitzky and Robins, 1995). In contrast to these previous approaches that generally assume that at least a subgroup of patients have complete follow-up, we focus on a setting where follow-up is only up to a fixed intermediate time point at which the surrogate marker is measured and primary outcome information is only available up to that point. No existing methods that we are aware of aim to test for a treatment effect earlier using the surrogate information. Certainly, one may consider testing for a treatment effect by simply assessing the treatment effect on the surrogate marker distribution. However, it is generally not clear how to translate the magnitude of the treatment effect on the surrogate marker into that on the primary outcome. Furthermore, when there are additional complications such as surrogate markers only being measurable for survivors, there is a lack of guidance on how to construct a comparison for the distribution of the surrogate marker between two arms.

In this paper, we develop a novel framework to test for a treatment effect using early measurements of a univariate surrogate marker in a time-to-event outcome setting. We propose robust nonparametric testing and inference procedures. We describe how our proposed quantity can be interpreted in terms of a lower bound for the treatment effect on the primary outcome. In addition, we demonstrate how the proposed test statistic can be used to calculate power or sample size needed for a future study. Here, we assume that the marker has been previously well established as a valid surrogate marker, both clinically and statistically. We illustrate the proposed procedures using simulations as well as data from the Diabetes Prevention Program (DPP).

2. Use of Surrogate Information to Test for a Treatment Effect

2.1. Setting and Notation

We focus on the setting where data from a previous study, Study A, are available past a time of interest, t. We aim to use Study A to help test for a treatment effect in a subsequent Study B, where individuals are followed up to time t₀ < t (Figure 1). Let G be the binary treatment indicator with G = g indicating treatment g for g = 0, 1 and we assume throughout that subjects are randomly assigned. Let $T_k^{(g)}$ denote the time to the primary outcome, and $S_k^{(g)}$ denote the surrogate marker value measured at time t₀, under treatment g, in study k ∈ {A, B}. Throughout, we define the treatment effect for Study k, ∆_k (t), as the difference in survival rates by time t under treatment 1 versus under treatment 0,

$${\mathrm{\Delta }}_k(t)=E\{I(T_k^{(1)}>t)\}-E\{I(T_k^{(0)}>t)\}=P(T_k^{(1)}>t)-P(T_k^{(0)}>t),\hspace{1em}\text{for}\hspace{0.17em}k\in \{A,B\}.$$

Figure 1.

The setting addressed in this paper is one in which information about the primary outcome up to t and information about the surrogate marker values at t₀ are available from Study A, while in Study B, only information about the primary outcome up to t₀ and surrogate marker values at t₀ are available

We assume that the control groups (g = 0) of the two studies are similar, but the treated groups (g = 1) need not be similar. This Study A must have both the same primary outcome and surrogate marker as Study B. The existence of such a Study A is reasonable since such a study must exist for the establishment of the surrogacy of the marker of interest.

2.2. Assumptions

Given that our setting rests on the existence of a valid surrogate marker, we first explicitly state our definition of a valid surrogate marker. We define a valid surrogate marker for Study B for the primary outcome T as one that meets the following assumptions:

(C1) $P(T_B^{(0)}>t|T_B^{(0)}>t_0,S_B^{(0)}=s)$ is a monotone function of s;

(C2) $P(S_B^{(1)}>s,T_B^{(1)}>t_0)⩾P(S_B^{(0)}>s,T_B^{(0)}>t_0)$ for all s;

(C3) $P(T_B^{(1)}>t|T_B^{(1)}>t_0,S_B^{(1)}=s)⩾P(T_B^{(0)}>t|T_B^{(0)}>t_0,S_B^{(0)}=s)$ for all s;

(C4) A large proportion of the treatment effect on the primary outcome can be explained by the treatment effect on the surrogate marker.

Assumptions (C1)-(C3) are parallel to those required in Wang and Taylor (2002) and Parast et al. (2017) and protect against the surrogate paradox situation (VanderWeele, 2013). Assumption (C1) implies that the surrogate marker at time t₀ is either “positively” or “negatively” related to the time of the primary outcome, (C2) implies that there is a positive treatment effect on the surrogate marker, (C3) implies that there is a non-negative residual treatment effect beyond that on the surrogate marker and (C4) guarantees the strength of the surrogate marker of interest.

These assumptions, discussed further in Web Appendix A, are reasonable if this surrogate marker has been previously shown as a valid surrogate marker. Unfortunately, these assumptions are not empirically testable as it would require follow-up past t₀ in Study B, which is not available. Some recent work has focused on developing sensitivity analyses for potential violation of these assumptions; we discuss this further in the Discussion. As previously mentioned, Prentice (1989) has proposed a definition for a valid surrogate marker; a marker deemed to be valid according to the Prentice definition would also satisfy Assumptions (C1)-(C3), but the converse does not hold.

Our testing approach, described in Section 2.3, will require an additional assumption:

(C5) $P(T_B^{(0)}>t|T_B^{(0)}>t_0,S_B^{(0)}=s)=P(T_A^{(0)}>t|T_A^{(0)}>t_0,S_A^{(0)}=s)$ for all s,

which implies that in the control groups, Studies A and B share the same conditional risk function for T given S among those who have not yet experienced the primary outcome by t₀. This assumption may be reasonable when, for example, the control condition in Study A and Study B are the same, such as “usual care”, for the same or similar study population. We discuss this further in the Discussion. Importantly, such an assumption is not required to hold for the treatment groups.

Our nonparametric estimation procedure, described in Section 2.4, will require the following regularity assumptions:

(C6) Censoring must be independent of T and S given G,

(C7) A common compact support Ω_S is assumed for S in g = 0, 1 and k = A, B

(C8) $P(T_A^{(g)}>t)>0$ and $P(T_B^{(g)}>t_0)>0$, g = 0, 1.

2.3. Test Statistic Based on Surrogate Information

Given that the main motivation for identifying and validating surrogate outcomes is to allow for an earlier test for a treatment effect, we propose a method to use (i) information collected in Study A about the relationship between the surrogate marker and the primary outcome and (ii) information collected up to t₀ in Study B, to test for a treatment effect in Study B:

$$H_0:{\mathrm{\Delta }}_B(t)\equiv P(T_B^{(1)}>t)-P(T_B^{(0)}>t)=0.$$

That is, the null hypothesis is that there is no difference in survival rates to time t between the two treatment groups in Study B. Our goal is to test H₀ at an earlier timepoint t₀ where t₀ < t. We aim to achieve this goal in a way that (a) does not require strict model assumptions concerning the relationship between $T_k^{(g)}$ and $S_k^{(g)}$, and (b) allows individuals to experience the primary outcome (e.g. die) before t₀ and hence, have unobservable S_B (which would be common in practice where some individuals do experience the primary outcome early in a study). To achieve this goal, we first decompose the survival rate at time t in each treatment group into the marginal survival to t₀ and the conditional survival,

$$P(T_B^{(g)}>t)=P(T_B^{(g)}>t_0)P(T_B^{(g)}>t|T_B^{(g)}>t_0)=P(T_B^{(g)}>t_0)\int r_B^{(g)}(t|s,t_0)d{F}_B^{(g)}(s|t_0)$$

where $r_k^{(g)}(t|s,t_0)=P(T_k^{(g)}>t|T_k^{(g)}>t_0,S_k^{(g)}=s)$ and $F_B^{(g)}(s|t_0)=P(S_B^{(g)}⩽s|T_B^{(g)}>t_0)$.

Thus, we can then express the treatment effect, ∆_B(t) as

$${\mathrm{\Delta }}_B(t)=\mathcal{G}\{T_B^{(1)},S_B^{(1)},r_B^{(1)}\}-\mathcal{G}\{T_B^{(0)},S_B^{(0)},r_B^{(0)}\},$$

$$\text{where}\hspace{1em}\mathcal{G}\{T_B^{(g)},S_B^{(g)},r\}=P(T_B^{(g)}>t_0)\int r(t|s,t_0)d{F}_B^{(g)}(s|t_0)$$

for a given function r(t|s, t₀). By expressing ∆_B (t) in this way, one can see that the only component of ∆_B (t) that requires information after t₀ is r(t|s, t₀). In addition, based on Assumption (C5) which states that $r_B^{(0)}(t|s,t_0)=r_A^{(0)}(t|s,t_0)$, we take advantage of the fact that $r_B^{(0)}(t|s,t_0)$ is estimable using only observations from the control group (g = 0) of Study A. This motivates us to define a measure for the “early” treatment effect for Study B, “early” in the sense that it is estimable at the earlier time t₀ < t, as

$${\mathrm{\Delta }}_{EB}(t,t_0)\equiv \mathcal{G}\{T_B^{(1)},S_B^{(1)},r_B^{(0)}\}-\mathcal{G}\{T_B^{(0)},S_B^{(0)},r_B^{(0)}\}=\mathcal{G}\{T_B^{(1)},S_B^{(1)},r_A^{(0)}\}-\mathcal{G}\{T_B^{(0)},S_B^{(0)},r_A^{(0)}\}.$$

Note that beyond $r_A^{(0)}$, this treatment effect only depends on the distribution of the primary outcome and the surrogate marker observed up to t₀ in Study B:

$$\{T_B^{(g)}I(T_B^{(g)}<t_0),S_B^{(g)}I(T_B^{(g)}⩾t_0)\},g=0,1,$$

and is thus, identifiable based on the observed information available at t₀ in Study B. Instead of the original null hypothesis H₀ : ∆_B (t) = 0, we aim to test the null hypothesis concerning the surrogate marker

$$H_0^{(S_B)}:{\mathrm{\Delta }}_{EB}(t,t_0)=0$$

in Study B. To ensure the validity of this test with respect to the original null hypothesis, we require that ∆_B (t) = 0 ⇒ ∆_EB (t, t₀) = 0. In Web Appendix A, we show that this requirement indeed holds under Assumptions (C1)-(C3) and (C5). Importantly, by using the same r(t|s, t₀) in $\mathcal{G}\{T_B^{(g)},S_B^{(g)},r\}$ for g = 0, 1 in defining ∆_EB (t, t₀), we show that this earlier treatment effect is smaller than if we used the true conditional probabilities within each treatment group. That is, ∆_EB (t, t₀) is always less than or equal to ∆_B (t) (i.e. ∆_EB (t, t₀) ⩽ ∆_B (t)) and is thus a conservative measure of ∆_B (t). Therefore, ∆_EB(t, t₀) can be considered a meaningful quantity in that it represents a lower bound of the treatment effect on the primary outcome at time t, which is of ultimate clinical interest.

We define our test statistic for $H_0^{(S_B)}$ based on the early treatment effect as $Z_{EB}(t,t_0)=\sqrt{n_B}{\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)/{\widehat{\sigma }}_{EB}(t,t_0)$, where ${\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)$ is a root-n consistent estimate of ∆_EB(t, t₀) and ${\widehat{\sigma }}_{EB}{(t,t_0)}^2$ is the estimated variance of $\sqrt{n_B}\{{\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)-{\mathrm{\Delta }}_{EB}(t,t_0)\}$. We reject $H_0^{(S_B)}$ (and H₀) when |Z_EB(t, t₀)| is large. In the next section, we propose robust procedures to obtain ${\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)$ and ${\widehat{\sigma }}_{EB}(t,t_0)$.

2.4. Estimation and Inference

To derive our estimation and testing procedures, we assume that the observed data from the gth treatment group and kth study consist of n_kg independent identically distributed random vectors, $\{(X_{ki}^{(g)},{\delta }_{ki}^{(g)},S_{ki}^{(g)}I(X_{ki}^{(g)}>t_0)),i=1,\dots ,n_{kg}\}$, for g = 0, 1; k = A, B, where $X_k^{(g)}=\min (T_k^{(g)},C_k^{(g)})$, ${\delta }_k^{(g)}=I(T_k^{(g)}<C_k^{(g)})$, $C_k^{(g)}$ denotes the censoring time assumed to be independent of $(T_k^{(g)},S_k^{(g)})$ (Assumption C6), and $S_k^{(g)}$ is only observable and appropriately defined if the subject is still at risk by t₀. Let n_k = n_k1+n_k0 be the number of individuals in Study k ∈ {A, B}. To estimate ∆_EB(t, t₀), we let ${\widehat{r}}_A^{(0)}(t|s,t_0)=\exp \{-{\widehat{\mathrm{\Lambda }}}_A^{(0)}(t|s,t_0)\}$, where

$${\widehat{\mathrm{\Lambda }}}_A^{(0)}(t|t_0,s)={\int }_{t_0}^t\frac{{\sum }_{i=1}^{n_{A0}}I(X_{Ai}^{(0)}>t_0)K_h\{\gamma (S_{Ai}^{(0)})-\gamma (s)\}d{N}_{Ai}^{(0)}(z)}{{\sum }_{i=1}^{n_{A0}}{K}_h\{\gamma (S_{Ai}^{(0)})-\gamma (s)\}{Y}_{Ai}^{(0)}(z)}$$

is a consistent estimate of ${\mathrm{\Lambda }}_A^{(0)}(t|t_0,s)=-\log [r_A^{(0)}(t|t_0,s)]$, $Y_{Ai}^{(0)}(t)=I(X_{Ai}^{(0)}⩾t)$, $N_{Ai}^{(0)}(t)=I(X_{Ai}^{(0)}⩽t){\delta }_{Ai}^{(0)}$, K(·) is a smooth symmetric density function, K_h(x) = K(x/h)/h and γ(·) is a given monotone transformation function. For the bandwidth h, we require the standard undersmoothing assumption of $h=O(n_g^{-v})$ with ν ∈ (1/4, 1/2) in order to reduce bias. In practice, one may first obtain an optimal bandwidth h_opt based on plug-in estimators or cross-validation and then use $h=h_{opt}{n}_{A1}^{-c_0}$ for some c₀ ∈ (1/20, 1/4)/ In all numerical examples, we chose h_opt proposed in Scott (1992) and c₀ = 0.11, and used either the identity or log transformation for γ(·).

Subsequently, we estimate $\mathcal{G}\{T_B^{(g)},S_B^{(g)},r_A^{(0)}\}=P(T_B^{(g)}>t_0)\int r_A^{(0)}(t|s,t_0)d{F}_B^{(g)}(s|t_0)$ as

$$\widehat{\mathcal{G}}\{X_B^{(g)},S_B^{(g)},{\widehat{r}}_A^{(0)}\}=n_{Bg}^{-1}\sum _{i=1}^{n_{Bg}}{\widehat{r}}_A^{(0)}(t|S_{Bi}^{(g)},t_0)\frac{I(X_{Bi}^{(g)}>t_0)}{{\widehat{W}}_{Bg}^C(t_0)}$$

and estimate ∆_EB(t,t₀) as ${\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)=\widehat{\mathcal{G}}\{X_B^{(1)},S_B^{(1)},{\widehat{r}}_A^{(0)}\}-\widehat{\mathcal{G}}\{X_B^{(0)},S_B^{(0)},{\widehat{r}}_A^{(0)}\}$ where ${\widehat{W}}_{kg}^C(u)$ is the Kaplan-Meier (KM) estimator of $W_{kg}^C(u)=P(C_k^{(g)}>u)$ for k = A, B and g = 0, 1. In Web Appendix B, we show that ${\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)$ is a consistent estimator of ∆_EB(t,t₀) and $\sqrt{n_B}\{{\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)-{\mathrm{\Delta }}_{EB}(t,t_0)\}$ weakly converges to a mean zero normal distribution with variance ${\sigma }_{EB}^2(t,t_0)$ as min(n_A, n_B) → ∞. We propose to obtain an estimate of σ_EB(t,t₀), ${\widehat{\sigma }}_{EB}(t,t_0)$, using a perturbation-resampling approach described in the Appendix B.

It then follows that the test statistic $Z_{EB}(t,t_0)=\sqrt{n_B}{\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)/{\widehat{\sigma }}_{EB}(t,t_0)$ has a N(0; 1) distribution asymptotically under H₀.We can thus reject H₀ when |Z_EB(t, t₀)| > Φ⁻¹(1−α/2) to attain a type I error of α level. Importantly, the proposed inference procedure only requires the availability of data from the control group from Study A.

Remark 1 The estimate ${\widehat{\sigma }}_{EB}(t,t_0)$ obtained via the perturbation-resampling method can be used for both testing of $H_0^{(S_B)}$ and constructing CIs for ∆_EB(t; t₀): If we are only interested in testing $H_0^{(S_B)}$, it would be adequate to consistently estimate the variance of ${\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)$ under the null hypothesis that $\left\{T_B^{(0)}I(T_B^{(0)}⩽t_0),S_B^{(0)}I(T_B^{(0)}>t_0)\right\}$ and $\left\{T_B^{(1)}I(T_B^{(1)}⩽t_0),S_B^{(1)}I(T_B^{(1)}>t_0)\right\}$ have identical distributions. In Web Appendix B, we show that the asymptotic variance of $\sqrt{n_B}\{{\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)-{\mathrm{\Delta }}_{EB}(t,t_0)\}$ under the null can be consistently estimated as

$${\widehat{\sigma }}_{EB0}^2(t,t_0)=\sum _{g=0}^1\frac{1}{{}^{{\pi }_{Bg}}}\left(\frac{{\widehat{\mu }}_{B2}(t,t_0)}{{\widehat{W}}_{Bg}^C(t_0)}-{\widehat{\mu }}_{B1}{(t,t_0)}^2\left\{1+{\int }_0^{t_0}\frac{d{\widehat{\mathrm{\Lambda }}}_{Bg}^C(u)}{{\widehat{W}}_{Bg}^X(u)}\right\}\right),$$ (1)

where ${\widehat{\mathrm{\Lambda }}}_{kg}^C(u)=-\log \{{\widehat{W}}_{kg}^C(u)\}$, ${\widehat{W}}_{kg}^X(u)$ is the empirical survival function of $X_k^{(g)}$, and

$${\widehat{\mu }}_{Bm}(t,t_0)=\sum _{g=0}^1\frac{{\pi }_{Bg}}{n_{Bg}}\sum _{i=1}^{n_{Bg}}\frac{{\widehat{r}}_A^{(0)}{(t|S_{Bi}^{(g)},t_0)}^{m}I(X_{Bi}^{(g)}>t_0)}{{\widehat{W}}_{Bg}^C(t_0)}.$$

An interesting fact is that the variability of ${\widehat{r}}_A^{(0)}(t|s,t_0)$ does not contribute to the asymptotic null variance of ${\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)$, which allows its explicit estimation without relying on more computational intensive resampling perturbation methods.

Remark 2 It is possible to use ${\widehat{\mathrm{\Delta }}}_{E_B}(t,t_0)$ to recover an estimate of the treatment effect, ∆B(t); details are provided in Web Appendix C.

Remark 3 In some cases, one may wish to condition on Study A, i.e. assume Study A is fixed. This may be of interest when, for example, considering power calculations discussed in Section 3. When the data from Study A are fixed, we can instead test a modified null hypothesis:

$${\tilde{H}}_0^{(S_B)}:{\mathrm{\Delta }}_{EB}(t,t_0|{\widehat{r}}_A^{(0)})\equiv \mathcal{G}\{T_B^{(1)},S_B^{(1)},{\widehat{r}}_A^{(0)}\}-\mathcal{G}\{T_B^{(0)},S_B^{(0)},{\widehat{r}}_A^{(0)}\}=0.$$

Note that ∆_B(t) = 0 also implies that ${\mathrm{\Delta }}_{EB}(t,t_0|{\widehat{r}}_A^{(0)})=0$ (see Web Appendix A). Therefore, the test of ${\tilde{H}}_0^{(S_B)}:{\mathrm{\Delta }}_{EB}(t,t_0|{\widehat{r}}_A^{(0)})=0$ is also valid for testing the presence of the treatment effect on the primary endpoint. However, ${\mathrm{\Delta }}_{EB}(t,t_0|{\widehat{r}}_A^{(0)})=0$ is now only a lower bound of ∆_B(t) in a stochastic and asymptotic sense, i.e., $P_A\{{\mathrm{\Delta }}_{EB}(t,t_0|{\widehat{r}}_A^{(0)})<{\mathrm{\Delta }}_B(t)\}\to 1$ as n_A → ∞, where P_A denotes the probability measure for observations from Study A. If ${\widehat{r}}_A^{(0)}$ is a poor estimator of $r_A^{(0)}$, ${\mathrm{\Delta }}_{EB}(t,t_0|{\widehat{r}}_A^{(0)})$ may not be a lower bound of ∆_B(t).

To construct a valid test for ${\tilde{H}}_0^{(S_B)}$, note that since $|{\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)-{\mathrm{\Delta }}_{EB}(t,t_0|{\widehat{r}}_A^{(0)})|\to 0$ in probability as n_B → ∞ for any realization of ${\widehat{r}}_A^{(0)}$, ${\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)$ may also serve as a consistent estimator of ${\mathrm{\Delta }}_{EB}(t,t_0|{\widehat{r}}_A^{(0)})$. However, the corresponding variance estimation procedure requires modification due to the conditioning on ${\widehat{r}}_A^{(0)}$. Interestingly, it can be shown that under the null, ${\widehat{\sigma }}_{EB0}^2(t,t_0)$ given in (1) is a consistent estimate of the conditional variance

$$\begin{gathered} {\sigma }_{EB}^2(t,t_0|{\widehat{r}}_A^{(0)})=\underset{n_B\to \infty }{\lim }\text{Var}\left(\sqrt{n_B}{\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)|{\widehat{r}}_A^{(0)}\right) \\ \hspace{1em}\hspace{1em}\hspace{1em}\hspace{1em}\hspace{1em}=\sum _{g=0}^1\frac{1}{{\pi }_{Bg}}\left(\frac{{\mu }_{B2}^{(g)}(t,t_0|{\widehat{r}}_A)}{W_{Bg}^C(t_0)}-{\mu }_{B1}^{(g)}{(t,t_0|{\widehat{r}}_A)}^2\left\{1+{\int }_0^{t_0}\frac{{\lambda }_{Bg}^C(u)du}{W_{Bg}^X(u)}\right\}\right), \end{gathered}$$

where ${\mu }_{Bm}^{(g)}(t,t_0|{\widehat{r}}_A)=E\left\{{\widehat{r}}_A{(t|S_B^{(g)},t_0)}^{m}I(T_B^{(g)}>t_0)|{\widehat{r}}_A\right\}$, m = 1, 2. Thus, in this setting, we reject the null when $|Z_{EB}^{*}(t,t_0)|>{\mathrm{\Phi }}^{-1}(1-\alpha /2)$ with $Z_{EB}^{*}(t,t_0)=\sqrt{n_B}{\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)/{\widehat{\sigma }}_{EB0}(t,t_0)$.

3. Planning a Future Study

3.1. Power and Sample Size

We now consider how one might use Study A information to plan Study B. That is, we take a step back and assume that only data from Study A are available; Study B has not yet been conducted. The null and alternative hypotheses of interest are:

$$H_0\hspace{1em}:\hspace{1em}{\mathrm{\Delta }}_B(t)\equiv P(T_B^{(1)}>t)-P(T_B^{(0)}>t)=0$$

$H_1:{\Delta }_B(t)=\psi$ where we assume ψ > 0 without loss of generality.

In this section, we focus specifically on testing H₀ by operationally testing the null hypothesis ${\tilde{H}}_0^{(S_B)}:{\mathrm{\Delta }}_{EB}(t,t_0|{\widehat{r}}_A^{(0)})=0$. We do not consider $H_0^{(S_B)}$ (which would treat the data from Study A as random) but the procedure we propose below could be extended to focus on $H_0^{(S_B)}$ as well. The power of our proposed test statistic, $Z_{EB}^{*}(t,t_0)$, at a type I error rate of 0.05 is thus

$${\mathcal{P}}_{EB}(\psi |t,t_0)=P\left(\sqrt{n_B}\frac{|{\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)|}{{\sigma }_{EB}(t,t_0|{\widehat{r}}_A^{(0)})}>1.96|{\mathrm{\Delta }}_B(t)=\psi ,{\widehat{r}}_A^{(0)}\right).$$ (2)

Since we are planning Study B, we assume only data from Study A are available for power calculations. To use Study A to guide the study design we assume

(D1) ${\mathrm{\Delta }}_{EB}(t,t_0|{\widehat{r}}_A^{(0)})/{\mathrm{\Delta }}_B(t)$ equals the observed proportion of treatment effect explained by the surrogate marker in Study A,${\widehat{R}}_{SA}(t,t_0)$;

(D2) $\{T_A^{(0)}I(T_A^{(0)}<t_0),S_A^{(0)}I(T_A^{(0)}⩾t_0)\}$ and $\{T_B^{(0)}I(T_B^{(0)}<t_0),S_B^{(0)}I(T_B^{(0)}⩾t_0)\}$ have identical distributions.

Here, ${\widehat{R}}_{SA}(t,t_0)={\widehat{\mathrm{\Delta }}}_{EA}(t,t_0)/{\widehat{\mathrm{\Delta }}}_A(t)$, where ${\mathrm{\Delta }}_{EA}(t,t_0)=\mathcal{G}\{T_A^{(1)},S_A^{(1)},r_A^{(0)}\}-\mathcal{G}\{T_A^{(0)},S_A^{(0)},r_A^{(0)}\}$, ${\widehat{\mathrm{\Delta }}}_{EA}(t,t_0)$ is parallel to ${\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)$ except replacing $\widehat{\mathcal{G}}\{T_A^{(0)},S_A^{(0)},r_A^{(0)}\}$ by $n_{A0}^{-1}{\sum }_{i=1}^{n_{A0}}{\widehat{W}}_{A0}^C{(t)}^{-1}I(X_{Ai}^{(0)}>t)$, and

$${\widehat{\mathrm{\Delta }}}_A(t)=n_{A1}^{-1}\sum _{i=1}^{n_{A1}}I(X_{Ai}^{(1)}>t)/{\widehat{W}}_{A1}^C(t)-n_{A0}^{-1}\sum _{i=1}^{n_{A0}}I(X_{Ai}^{(0)}>t)/{\widehat{W}}_{A0}^C(t).$$

(D1) implies that the proportion of the treatment effect on the primary endpoint explained by the surrogate marker in Study B is the same as that observed in Study A. (D2) and (C5) together imply that the joint distributions of the surrogate marker and survival time up to t in the control arm of both studies are identical. It is important to note that these are strong assumptions; however, such strict assumptions are often made when calculating power for a future study. Specifically, if a previous study has been completed and is being used to inform the power calculation, similar assumptions are usually made, assuming some parallel features between the previous study and the future study.

Under (D1) and (D2), the expected power of Study B with n_B subjects given Study A is

$${\mathcal{P}}_{EB}(\psi |t,t_0)=1-\mathrm{\Phi }\{1.96-\sqrt{n_B}{\widehat{R}}_{SA}(t,t_0)\psi /{\sigma }_{EB}(t,t_0|{\widehat{r}}_A^{(0))}\}.$$

To estimate ${\sigma }_{EB}(t,t_0|{\widehat{r}}_A^{(0)})$ using Study A data only, note that under the null hypothesis, ${\mu }_{Bm}^{(1)}(t,t_0|{\widehat{r}}_A)={\mu }_{Bm}^{(0)}(t,t_0|{\widehat{r}}_A)$ and thus, ${\sigma }_{EB}^2(t,t_0|{\widehat{r}}_A^{(0)})$ can be further simplified as

$$\sum _{g=0}^1\frac{n_B}{n_{Bg}}\left[\frac{{\mu }_{B2}^{(0)}(t,t_0|{\widehat{r}}_A^{(0)})}{W_{Bg}^C(t_0)}-{\mu }_{B1}^{(0)}{(t,t_0|{\widehat{r}}_A^{(0)})}^2\left\{1+{\int }_0^{t_0}\frac{{\lambda }_{Bg}^C(u)du}{W_{B0}^T(u)W_{Bg}^C(u)}\right\}\right],$$

where $W_{Bg}^T(u)=P(T_B^{(g)}>u)$. It follows from (D2) that ${\mu }_{Bm}^{(0)}(t,t_0|{\widehat{r}}_A^{(0)})$ can be estimated by

$${\widehat{\mu }}_{ABm}^{(0)}(t,t_0,|{\widehat{r}}_A^{(0)})=n_{A0}^{-1}\sum _{i=1}^{n_{A0}}\frac{{\widehat{r}}_A^{(0)}{(t|S_{Ai}^{(0)},t_0)}^{m}I(X_{Ai}^{(0)}>t_0)}{{\widehat{W}}_{A0}^C(t_0)}$$

using observations from the control arm of Study A and thus, a consistent estimator of ${\sigma }_{EB}^2(t,t_0|{\widehat{r}}_A^{(0)})$ is ${\widehat{\sigma }}_{EB0}^2(t,t_0|{\widehat{r}}_A^{(0)},W_B^C)$, defined as

$$\frac{1}{{\pi }_{B0}{\pi }_{B1}}\left[\frac{{\widehat{\mu }}_{AB2}^{(0)}(t,t_0,|{\widehat{r}}_A^{(0)})}{W_B^C(t_0)}-{\widehat{\mu }}_{AB1}^{(0)}{(t,t_0,|{\widehat{r}}_A^{(0)})}^2\left\{1+{\int }_0^{t_0}\frac{{\lambda }_B^C(u)du}{{\widehat{W}}_{A0}^T(u)W_B^C(u)}\right\}\right]$$ (3)

assuming that $W_{Bg}^C(t)=W_B^C(t)$ in both arms, where ${\widehat{W}}_{A0}^T(\cdot )$ is the KM estimator of the survival function of $T_A^{(0)}$. Therefore, the power can be estimated as

$${\widehat{\mathcal{P}}}_{EB}(\psi |t,t_0)=1-\mathrm{\Phi }\left\{1.96-\frac{\sqrt{n_B}{\widehat{R}}_{SA}(t,t_0)\psi }{{\widehat{\sigma }}_{EB0}(t,t_0|{\widehat{r}}_A^{(0)},W_B^C)}\right\}.$$ (4)

The sample size needed in Study B to achieve a power of 100(1 − β)% is then

$$n_B={\left\{{\widehat{\sigma }}_{EB0}(t,t_0|{\widehat{r}}_A^{(0)},W_B^C)\left(\frac{1.96-{\mathrm{\Phi }}^{-1}(\beta )}{{\widehat{R}}_{SA}(t,t_0)\psi }\right)\right\}}^2.$$ (5)

In Section 4 we illustrate this power calculation for multiple t₀ by examining the estimated power for testing the null hypothesis using ${\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)$ at a fixed sample size. Additionally, we evaluate this power calculation to ensure that it is a reasonable approximation to the true power if Study B was carried out up to t₀ and the proposed test statistic was used.

When the outcome rate is low i.e., $P(T_B^{(g)}>t)$ is close to 1, as is often the case in settings where the surrogate marker would be useful, ${\widehat{\mu }}_{ABm}^{(0)}(t,t_0,|{\widehat{r}}_A^{(0)})$ may not be a good approximation of ${\mu }_{Bm}^{(0)}(t,t_0,|{\widehat{r}}_A^{(0)})$ under the specified alternative. In such a case, we propose to adjust the variance estimator used in the sample size calculation as described in Web Appendix D.

4. Simulation Studies

We conducted simulation studies under three settings. Data were generated such that participants may experience the primary outcome or be censored before t₀; S is only available for participants still under observation at t₀. Throughout, n_A0 = n_A1 = 1000 and n_B0 = n_B1 = 800 , we use a gaussian kernel, t = 1, the results summarize 1000 replications and estimates are obtained across a range of t₀ ∈ (0.25, 0.50, 0.75).

In simulation setting (i), we assumed no treatment effect and generated data from $S_k^{(g)}$ ~ Gamma(shape = 2, scale = 2.2), and $T_k^{(g)}=U/(0.08+0.002\times S_k^{(g)})$ where U ~ Exponential(rate = 1). In simulation setting (ii), data were generated as $S_k^{(0)}$ ~ Gamma(shape = 2, scale = 2.2), and $T_k^{(0)}=U/(0.08+0.002\times S_k^{(0)})$, $S_k^{(1)}$ ~ Gamma(shape = 2, scale = 2.0), and $T_k^{(1)}=U/(0.04+0.001\times S_k^{(1)})$. For both settings, the censoring in both groups was simulated from an Exponential(0.5), and $S_k^{(g)}$ is only observable if $T_k^{(g)}\wedge C_k^{(g)}>t_0$. In setting (i), $P(T_k^{(g)}>t)=0.92$, g = 0, 1 and there is no treatment effect. In setting (ii), $P(T_k^{(1)}>t)=0.96$ and $P(T_k^{(0)}>t)=0.92$, and the underlying treatment effect is ${\mathrm{\Delta }}_k(t)=0.04$. In setting (iii), Study A and Study B group 0 data are generated exactly as in setting (ii) but Study B group 1 data are generated as $S_B^{(1)}$ ~ Gamma(shape = 2, scale = 2), and $T_B^{(1)}=U/(0.03+0.001\times S_k^{(1)})$ with censoring simulated from an Exponential(0.45) in both groups. In this setting $P(T_B^{(1)}>t)=0.97$, $P(T_B^{(0)}>t)=0.92$, and ∆_B(t) = 0.05. This setting reflects the fact that we only require certain similarities between the two studies for the control group (Assumption (C5)). For all three settings the survival rate is purposefully chosen to be high because this is exactly the situation where using a surrogate marker would be of interest, since few individuals experience the primary outcome before t. In Web Appendix E, we provide additional simulation results for settings with lower survival rates and illustrate similar performance in those settings.

Importantly, it can be shown that all simulation settings meet Assumptions (C1)-(C3) and (C5)-(C8). The proportion of treatment effect explained by the surrogate information at t₀ increases with t₀ and was purposefully made to be low for earlier time points. For example, in setting (ii), R_SB(t; t₀) = 0.26; 0.5; 0.75 for t₀ = 0.25; 0.5; 0.75 respectively. Therefore Assumption (C4) technically only holds for t₀ = 0.75; this was done in an effort to show the loss in terms of power when R_SB(t; t₀) is low, as is shown in Table 1.

Table 1.

Performance of our proposed estimation for ∆_EB(t; t₀) and the perturbation-resampling approach to obtain ${\widehat{\sigma }}_{EB}(t,t_0)$, in terms of bias, empirical standard error (ESE), average standard error (ASE) using ${\widehat{\sigma }}_{EB}(t,t_0)$, coverage of the 95% confidence intervals, and Type 1 error/power under three settings, setting (i) (null setting), setting (ii), and setting (iii); performance of ${\widehat{\sigma }}_{EB0}$ from Remark 1, where the standard error (SE) is derived under the null, and corresponding Type 1 error/power when this estimate is used for testing is also shown.

	Setting (i)
	t0 = 0.25	t0 = 0.50	t0 = 0.75
Bias	−0.0001	−0.0002	−0.0001
ESE	0.0072	0.0108	0.0132
ASE	0.0076	0.0107	0.0134
Coverage	0.9570	0.9460	0.9540
Type 1 error	0.0360	0.0480	0.0410
SE derived under the null
${\widehat{\sigma }}_{EB0}/\sqrt{n_B}$	0.0073	0.0106	0.0134
Type 1 error	0.0420	0.0520	0.0440
	Setting (ii)
	t0 = 0.25	t0 = 0.50	t0 = 0.75
Bias	0.0000	0.0002	0.0000
ESE	0.0065	0.0091	0.0114
ASE	0.0068	0.0095	0.0118
Coverage	0.9580	0.9600	0.9560
Power	0.3310	0.6230	0.7650
SE derived under the null
${\widehat{\sigma }}_{EB0}/\sqrt{n_B}$	0.0064	0.0092	0.0117
Power	0.3850	0.6520	0.7760
	Setting (iii)
	t0 = 0.25	t0 = 0.50	t0 = 0.75
Bias	0.0001	0.0001	0.0000
ESE	0.0061	0.0086	0.0108
ASE	0.0066	0.0091	0.0112
Coverage	0.9550	0.9570	0.9540
Power	0.5170	0.8410	0.9420
SE derived under the null
${\widehat{\sigma }}_{EB0}/\sqrt{n_B}$	0.0061	0.0088	0.0111
Power	0.5880	0.8590	0.9440

For each simulation setting, we first examine the finite sample performance of our estimate ${\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)$ and the perturbation-resampling procedure for obtaining ${\widehat{\sigma }}_{EB}(t,t_0)$, an estimate of σ_EB(t,t₀). We examine bias, the empirical standard error (ESE) of ${\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)$, the average standard error (ASE) using ${\widehat{\sigma }}_{EB}(t,t_0)$, coverage of the 95% CIs for ∆_EB(t, t₀), and Type I error/power. We also examine the estimate ${\widehat{\sigma }}_{EB0}^2(t,t_0)$ described in Remark 1 and the corresponding Type 1 error/power when this quantity is used for hypothesis testing. Table 1 shows results for all three settings. These results demonstrate good finite sample performance of our method, with standard error estimates using the perturbation-resampling approach similar to the empirical estimates, small bias, good coverage, and Type 1 error rates close to 0.05. The ${\widehat{\sigma }}_{EB0}^2(t,t_0)$ quantity described in Remark 1 produces similar estimates as the perturbation approach and results in similar Type 1 error and power estimates.

Next, we examine the power calculations described in Section 3 where Study A information is used to plan Study B. Using a single Study A dataset generated under setting (ii), we calculate the estimated power for a future Study B at t₀ = 0.25, 0.50, 0.75, 1.0 with a fixed sample size of n_B = 2500. For calculations in setting (ii), we let $\psi ={\widehat{\mathrm{\Delta }}}_A(t)$ whereas for calculations in setting (iii), we let $\psi =1.25{\widehat{\mathrm{\Delta }}}_A(t)$. Note that this specification for ψ reflects the truth since ∆_B(t) = 0.04 in setting (ii) and ∆_B(t) = 0.05 in setting (iii). This would parallel a situation in practice where a future study is being planned but researchers are expecting the effect size to be slightly more or less than what has previously been seen. The resulting power estimates, shown in the top row for each simulation setting in Table 2, suggest that in both settings, power increases as t₀ increases. When t₀ = 1, our test is equivalent to simply testing for a difference in survival probability without using surrogate marker information since t = 1. For each t₀, we then simulate 1000 replications of Study B with n_B = 2500 and calculate the empirical power i.e. the proportion of replications where the null hypothesis was rejected when our proposed test statistic was used; these quantities are shown in the second row of each setting in Table 2. For all t₀, the estimated power is close to the empirical power.

Table 2.

Given Study A, estimated power for Study B using the proposed approach with a sample size of 2,500 and empirical power at this sample size in settings (ii) and (iii)

	Setting (ii)
	t0 = 0.25	t0 = 0.50	t0 = 0.75	t0 = 1.0
Estimated power	0.732	0.905	0.955	0.979
Empirical power in Study B	0.695	0.879	0.940	0.980
	Setting (iii)
	t0 = 0.25	t0 = 0.50	t0 = 0.75	t0 = 1.0
Estimated power	0.924	0.990	0.998	1.000
Empirical power in Study B	0.867	0.976	0.995	1.000

Lastly, we illustrate how these calculations can be used to visually describe the expected power at a fixed sample size across t₀ or alternatively, required sample size for a fixed desired power across t₀. Figure 2 shows the estimated power when n_B = 2,500, 1,500 or 500 for setting (ii) and demonstrates the expected power loss with each sample size at earlier testing time points; such a figure could be used to assess the optimal stopping point depending on the minimum acceptable power for the study in settings where the sample size is fixed due to practical constraints. Figure 3 shows the needed sample size for power = 0.70, 0.80 or 0.90 for setting (ii); such a figure could be used to assess how much of an increase in sample size would be needed to test at an earlier time point while retaining adequate power.

Figure 2.

Estimated power for testing in Study B using the proposed testing procedure with n_B =2,500, 1,500, or 500 across multiple t₀

Figure 3.

Needed sample size for testing in Study B using the proposed testing procedure for power = 0.70, 0.80, or 0.90 across multiple t₀

5. Example

We illustrate our procedures using a randomized clinical trial, the DPP, designed to investigate the efficacy of various treatments on the prevention of type 2 diabetes in high-risk adults (DPPG, 1999, 2002). DPP data are publicly available through the the National Institute of Diabetes and Digestive and Kidney Diseases Central Repository. Participants were randomly assigned to one of four groups: metformin, troglitazone, lifestyle intervention or placebo; we focus on the comparison of the metformin group (1,027) vs. placebo (1,030). The primary endpoint was time to diabetes as defined by the DPP protocol and we define the treatment effect, ∆(t), as the difference in 1 minus the cumulative incidence of diabetes at t = 2 years after randomization, shown in Figure 4. The term “survival” is avoided, because diabetes is not a terminal event. The estimated P (T > t) was 0.852 in the metformin group and 0.776 in the placebo group, with $\widehat{\mathrm{\Delta }}(t)=0.076$. We illustrate our proposed procedures conditioning on the assumed prior establishment of fasting plasma glucose (FPG) as a valid surrogate marker for a diabetes diagnosis (Simental-Mendía et al., 2008; Singh and Saxena, 2010; Caveney and Cohen, 2011). Though our assumptions (C1-C4) in this paper are untestable directly, this evidence base implies that these assumptions are likely to hold.

Figure 4.

Diabetes Prevention Program Study; 1 minus the cumulative incidence of diabetes within each treatment group, with a vertical line drawn at about t = 2 years

We first consider use of this study as Study A, where we plan to use this study to plan a future study where we will use the proposed testing procedure to test for a treatment effect at t₀ = 1 year using FPG information. Using our proposed procedures, the recommended sample size per arm for 80% power for a future Study B if testing were to occur at t₀ = 1 year would be 456. Specifically, to obtain this sample size we applied the calculation shown in (5) where ${\widehat{\sigma }}_{EB0}(t,t_0|{\widehat{r}}_A^{(0)},W_B^C)=0.53$ , β = 0.80, ${\widehat{R}}_{SA}(t,t_0)=0.65$ and ψ= 0.076 (the observed $\widehat{\mathrm{\Delta }}(t)$). If testing were instead done at t = 2 years using only survival information, the recommended sample size per arm would be 409. This suggests that the follow-up time may be cut in half with only a 11% increase in sample size.

To illustrate the actual testing procedure, we artificially split our study data in half such that one random half is used as Study A and the other random half is used as Study B, and we assume that Study B follow-up ends at 1 year. This results in a little over 500 individuals within each treatment group in Study B. Using our proposed procedure, the earlier treatment effect estimate, ${\widehat{\mathrm{\Delta }}}_{EB}(t,t_0)=0.0531$ with a 95% confidence interval (0.0160, 0.0887), and testing the null hypothesis leads us to reject the null hypothesis with p = 0.004. If we continue to follow the patients in Study B for one additional year, the estimated treatment effect at t = 2 years is ${\widehat{\mathrm{\Delta }}}_B(t)=0.0724$ with a 95% confidence interval (0.0194, 0.1205) and p = 0.005.

6. Discussion

We proposed a novel procedure to use surrogate marker information to test for a treatment effect at an earlier time point in a time-to-event outcome setting. This approach has the potential to result in less required follow-up time for randomized studies. The proposed estimator of the earlier treatment effect can also be interpreted as a lower bound of the treatment effect on the primary endpoint of interest. An R package implementing the methods described here, named SurrogateTest, is available on CRAN; see Web Appendix F.

While we address a problem within a setting that involves more than one randomized study and incorporates results from the first study into designing and analyzing the second study, it is worth noting that this is distinct from one that would be addressed within a group sequential monitoring setup, where the new test is generally a continuation of the previous tests. (Pocock, 1977; Jennison and Turnbull, 1999; Bartroff et al., 2012).

Our approach does have some limitations. First, the nonparametric estimation approach requires relatively large sample sizes; parametric methods could be considered when the sample size is small. Second, several assumptions are required, namely (C1)-(C5) throughout, (C6-C8) for the estimation of our test statistic, and (D1)-(D2) for future study planning. While strict, these assumptions are similarly required in other work focusing on surrogate markers and aim to rule out the surrogate paradox (VanderWeele, 2013; Wang and Taylor, 2002; Taylor et al., 2005). Recent work such as Elliott et al. (2015) aims to provide practical assessments and sensitivity analyses to examine the potential for such a situation; further work focused on providing such tools that can be used in practice is warranted. Assumption (C5) in particular is a strong assumption and warrants some discussion. Even if the control conditions in both studies were exactly the same, differences in study populations could result in a violation of this assumption. In such a situation, one potential solution is to recover the comparability of the control arms in two studies via a propensity score method.

Our proposed procedure relies on the existence and availability of data from both studies A and B. While the existence of such a pair of studies is reasonable, the public availability of individual level data from randomized trials is rare. We illustrated our proposed testing procedure by randomly splitting the DPP data into two sets to represent studies A and B due to lack of data availability. In fact, there are at least two studies that were conducted after DPP that would fit this setting, as a potential Study B, the Canadian Normoglycemia Outcomes Evaluation (CANOE) trial (Zinman et al., 2010) and the Indian Diabetes Prevention Programme (Ramachandran et al., 2006). Both studies were done on adults at high risk for diabetes, had a similar placebo arm, collected fasting plasma glucose every 6 months, and had a primary outcome of a diabetes diagnosis; differences in patient characteristics between studies could have potentially been accounted for using propensity score methods. Unfortunately, data from these two studies are not publicly available and study investigators were unwilling to share de-identified data to illustrate these methods. After extensive efforts, we obtained data on two similar yet not highly comparable clinical trials from the AIDS clinical trials group (ACTG). We now provide results in Web Appendix G from our proposed methods using data from these two studies. Limitations of the analyses based on these two studies are also discussed in detail. In order for surrogate markers to be able to be used to improve the design and efficiency of future studies, increased understanding of the importance of data sharing is needed.