The Use of Bayesian Hierarchical Models for Adaptive Randomization in Biomarker-Driven Phase II Studies

Abstract

The role of biomarkers has increased in cancer clinical trials such that novel designs are needed to efficiently answer questions of both drug effects and biomarker performance. We advocate Bayesian hierarchical models for response-adaptive randomized phase II studies integrating single or multiple biomarkers. Prior selection allows one to control a gradual and seamless transition from randomized-blocks to marker-enrichment during the trial. Adaptive randomization is an efficient design for evaluating treatment efficacy within biomarker subgroups, with less variable final sample sizes when compared to nested staged designs. Inference based on the Bayesian hierarchical model also has improved performance in identifying the sub-population where therapeutics are effective over independent analyses done within each biomarker subgroup.

1. Introduction

Clinical trials in cancer are designed to rigorously monitor and assess health interventions, whether as observational studies or randomized controlled trials. With expansive research in tumor biology over the past decades, cancer has increasingly been recognized as a biologically heterogeneous disease (Golub et al., 1999; Perou et al., 2000; Vogelstein and Kinzler, 2004). Tissue and specimen collection are now commonplace in therapeutic trials, to answer correlative scientific objectives about the disease process and patient-specific responses. At the same time, the availability and decreasing costs of high-throughput technologies have enabled the evaluation of the entire genome, and of other cellular compartments such as the transcriptome, proteome, metabolome, or secretome, and has vastly increased the amount of molecular data derived from biospecimen. Guidelines have been issued on the collection and use of biospecimen for biomarker development (McShane et al., 2005; Schmitt et al., 2004; Simon et al., 2009); and ultimately, the molecular characterization of tumors has been postulated as providing information at the individual patient level to optimize care, and be a critical component of personalized medicine (Hamburg and Collins, 2010).

Biomarkers are broadly defined as chemical, physical, or biological assessments used as an indicator of a patients disease state. Their application in medicine is delineated as: prognostic markers providing information about the overall risk of a clinical outcome (e.g., cancer recurrence); or predictive markers providing information about the specific effect of a therapeutic intervention (e.g., response to a targeted therapy, or treatment-related toxicity). Many laboratory-based assays have been proposed as prognostic or predictive biomarkers of cancer (Ross et al., 2003; Amado et al., 2008), and some have been shown to have both prognostic and predictive value in specific clinical settings (Albain et al., 2010). Molecular assays can also serve as surrogate markers when they correlate with clinical outcomes of primary interest (e.g., overall survival). Thus, they can substitute as an earlier endpoint for evaluating therapeutic benefit, or be incorporated into the design that directs ongoing treatment regimen. For example, based on the results of ACOSOG Z1031 (Ellis et al., 2011), Ki-76 is proposed in the neoadjuvant ALTERNATE trial as a surrogate for response so that it directs the treatment course of patients on trial (DeCensi et al., 2011).

Traditionally, the predictive and prognostic value of molecular assays have been investigated in a retrospective manner, where biospecimen are banked during the course of the trial and evaluated on completion. This allows for a variety of study designs, e.g., nested case-control that can draw from larger randomized or observational studies when clinical outcome is rare (Pepe et al., 2001), or when laboratory resources are limited. However, only a prospective application of the biotechnologies will fully evaluate their clinical utility as an assay. This includes the accessibility of the biospecimen, evaluation of quality control of the assay, and the feasibility of making determinations from the molecular output (Simon et al., 2009).

Response-adaptive trials designs have been advocated as a way to allocate patients such that more patients receive the better treatment. Wei and Durham (1978) extended the stochastic play-the-winner process of Zelen (1969) to randomization using urn models. These strategies were later used in developing the randomized Polya urn (Durham et al., 1998) and drop-the-loser rules (Ivanova, 2003) and the concept of optimal allocation was introduced by Rosenberger et al. (2001). As a second general approach, the doubly adaptive biased coin design was introduced by Eisele and Woodroofe (1995) and was further developed by Hu and Zhang (2004) among others.

Bayesian methods for clinical trials have been well established in the statistical literature. For interim monitoring of trials, Spiegelhalter et al. (1986) advocated the use of predictive power for making decisions of early stopping. The Bayesian model was also used to determine sample size requirements during trial development (Spiegelhalter and Freedman, 1986). Many subsequent methods were developed for sample size determination as summarized in the review given by Adcock (1997). Bayesian models have been proposed for alternative study designs including noninferiority trials of therapeutics and medical devices (Spiegel-halter et al., 2004; Chen et al., 2011), seamless phase II/III designs (Inoue et al., 2002), and adaptive designs that drop treatment arms or modify randomization (Berry, 2005, 2006).

Under the Bayesian paradigm, Kass and Steffey (1989) established as a class “conditionally independent hierarchical models” for observations drawn from distinct units (e.g., sites, clusters, or geographic regions). More recently, this class of models has been proposed for phase II and III clinical trials with integral biomarkers. Thall et al. (2003) proposed the use of a hierarchical model for single arm phase II trials when subjects have multiple subtypes of the disease. Zhou et al. (2008) extended the hierarchical structure to consider multiple treatments in a probit regression model for the randomized phase II trial: Biomarker-integrated approaches of targeted therapy of lung cancer elimination (BATTLE). The book by Berry (2011) includes several illustrations for using hierarchical models to borrow information across components of a trial, and most recently, the Bayesian paradigm is used to consider an evolving series of novel therapeutics and biomarkers in I-SPY 2: An Adaptive Breast Cancer Trial Design in the Setting of Neoadjuvant Chemotherapy (Barker et al., 2009).

In the following sections, we state the motivation for considering adaptive-randomization (AR) strategies for biomarker-driven trials in the phase II setting. Using the general notation of Kass and Steffey (1989) we define the Bayesian components of the trial. We then use simulation to summarize operating characteristics under a variety of scenarios that represent combinations of predictive biomarkers. In particular, we argue that informative prior distributions are needed for AR and interim monitoring to control treatment assignment early in the trial, while final evaluations of efficacy should rely on noninformative priors when the frequentist paradigm for inference is desired. Lastly, using a specific investigation of a novel targeted therapy in metastatic breast cancer, we contrast the performance of the adaptive approach against traditional staged designs for phase IIs nested within the biomarker-defined subgroups (Mandrekar and Sargent, 2010).

2. Motivation

In cancer clinical trials, the research and regulatory environment have divided the process for evaluating new therapeutics into four phases, with phase II and III studies designated for giving preliminary and definitive evidence of efficacy, respectively. For efficacy trials that incorporate prospective biomarkers, the National Cancer Institute has designated two types. Integrated studies involve assays clearly identified as part of the primary objective of a clinical trial, and are often intended to validate biomarkers prior to their use in future trials. As such, they should be hypothesis-testing in nature, and not hypothesis-generating and motivated by discovery. Assays are to be performed in real time and include complete plans for specimen collection, laboratory measurements, and statistical analysis. Integral studies have many of the same elements, but are also designed such that the assay must be completed before patients can proceed on the trial. Examples include biomarkers to establish eligibility, biomarkers used for patient stratification, and biomarkers that inform treatment assignment. The most common trial designs with integral biomarkers are listed below, with representative schema in Figure 1 (Freidlin et al., 2010).

Figure 1.

Schema for integral biomarker trials designs that incorporate randomized treatment arms, including randomized-block (left panel), marker-enrichment (top-right), and marker-directed designs (bottom-right).

• – Randomized-block designs are where the biomarker is used to define a stratification factor for randomization, but equivalent schemes are used within strata, such that globally, treatment assignment does not vary by biomarker status.

• – Marker-enrichment designs are used to select a sub-population for investigation, whether it be a predictive marker for patient sensitivity to treatment, or prognostic markers to identify high-risk patients in which a new therapeutic may have the most clinical benefit.

• – Marker-directed designs are where treatment assignment is determined by the integral biomarker; for example, assigning marker positive patients to the hypothesized optimal treatment (predictive marker), or to the more aggressive treatment (prognostic marker).

In deciding among the different integral biomarker designs, one must weigh the relative importance of validating the prognostic or predictive value of the biomarker, vs. using the information it provides to optimize efficacy of the treatments. Randomized-block designs provide the only direct evidence of marker performance, but are less efficient in terms of evaluating efficacy within target biomarker subgroups when compared to marker-directed designs. Conversely, it can be argued that in the phase II setting, where the goal is to provide evidence of efficacy for future phase III studies, marker-directed designs are restrictive in terms of the possible outcomes from conducting the study. A positive level of efficacy would lead to a randomized controlled trial within the marker subgroup, while insufficient levels of efficacy would not support moving to any phase III study. Based on these distinctions, the sensitivity and specificity of the assays should be known in advance of selecting between a randomized-block or marker-directed design. With this information, the efficiency of enrichment can be weighed against the fact that some patients who truly benefit from treatments would be excluded from receiving the regimen.

Because these are difficult considerations when developing phase II trials for new drugs or indications, we propose an adaptive strategy which allows for efficacy to be evaluated across all targeted subpopulations in an efficient manner. In essence, these methods allow for a single trial to gradually and seamlessly transition from a randomized-block design to a marker-directed design. As a result, more patients are randomized to optimal therapy when, and only when, biomarkers are predictive. The actual size of the trial will also vary less than a randomized-block design that uses multistage tests to reach similar levels of efficiency. Lastly, by using Bayesian models, trial flexibility that is induced by the data-driven adaptations will be taken into account in the statistical inferences.

3. A Phase II Response-Adaptive Design

In a randomized phase II trial with integral biomarkers, suppose we have K patient subgroups that are mutually exclusive and exhaustive for all possible assay results. A total of J treatment regimens are to be considered in the randomized trial, whether they be designated as experimental or control arms. The primary objective is to evaluate the efficacy of each drug within the biomarker subgroups, i.e., a noncomparative multiarm phase II (Rubinstein et al., 2005; Mandrekar and Sargent, 2010).

Here, the primary clinical endpoint is considered to be a binary outcome, y ∈ {0, 1}. The target response rate of an effective treatment in a given subgroup will be defined as π_1,jk, while an unacceptable response rate is defined as π_0,jk. Without loss of generality, we will assume throughout that there are common target rates of interest:

$${\pi }_{1,jk}={\pi }_1\text{and}{\pi }_{0,jk}={\pi }_0\forall jk.$$

Although we note that for prognostic markers, it may be more applicable to have different targets for the high- and low-risk patient subgroups.

Under the formulation of Kass and Steffey (1989), a random vector of n observations, y_n, is conditionally independent given parameters, θ. Further, conditional on hyperparameters, φ, the {θ_i} are i.i.d., such that the elements of y_n are exchangeable with a common density p(⋅).

$$y_n|\theta ~p(y_n|\theta )=\prod _{i=1}^{n}p(y_i|{\theta }_i)$$

$$\theta |\phi ~p(\theta |\phi )=\prod _{i=1}^{n}p({\theta }_i|\phi )$$

3.1. Hierarchical Model for Binary Data

Let j denote treatment arm, j = 1 …J; and k denote biomarker group, k = 1 …K. Nested within treatment j and biomarker k, patients are indexed by i, i = 1 …n_jk, n_j = Σ_k n_jk, and n = Σ_j n_j. We will use n to refer to the number of patients at any point during enrollment up to a final sample size, N. The observed responses are denoted as

$$y_{ijk}=\{\begin{array}{cc}1& \text{if patient}i\text{with marker}k\text{had a response to treatment}j\\ 0& \text{otherwise}\end{array}.$$

Let π_ijk be the response probability for y_ijk and a binary model with the link function θ_ijk = f(π_ijk). The proposed hierarchical structure for multiple treatment and biomarker groups is

$${\theta }_{ijk}~N({\mu }_{jk},1)$$

$${\mu }_{jk}~N({\phi }_j,{\sigma }^2)$$

$${\phi }_j~N(\alpha ,{\tau }^2)$$

with hyperparameters, φ = {α, σ², τ²}. The variance parameter σ² controls the extent of borrowing across marker groups within each treatment; α and τ² represent the second-stage prior distribution to the hierarchical model.

Bayesian binary hierarchical models are well characerized, and can be implemented in specialized software including BUGS (Lunn et al., 2000) or JAGS (Plummer, 2008). For the special case of a probit model, f(⋅) = Φ⁻¹(⋅), the Gaussian priors are conjugate such that the full conditional distributions have closed forms. Correcting for an error that appears in Zhou et al. (2008) and keeping hyperparamaters unspecified, they take the form

$${\theta }_{ijk}|y_{ijk},{\mu }_{jk}\propto \{\begin{array}{cc}N({\mu }_{jk},1)\cdot I(-\infty ,0)& y_{ijk}=0\\ N({\mu }_{jk},1)\cdot I(0,\infty )& y_{ijk}=1\end{array}$$

$${\mu }_{jk}|{\theta }_{ijk},{\phi }_j~N(\frac{{\sigma }^2\cdot {\sum }_{i=1}^{n_{ij}}{\theta }_{ijk}+{\phi }_j}{n_{jk}\cdot {\sigma }^2+1},\frac{1}{n_{jk}+{\sigma }^{-2}})$$

$${\phi }_j|{\mu }_{jk}~N(\frac{{\tau }^2\cdot {\sum }_{k=1}^K{n}_{jk}\cdot {\mu }_{jk}+\alpha }{n_j\cdot {\tau }^2+1},\frac{1}{n_j+{\tau }^{-2}}).$$

We provide the Gibbs sampler for the probit model in the statistical language and environment R (see Appendix for source code). This code was used to run the simulations on scalable computing resources at the author institution.

3.2. Adaptive Randomization

Because the general hypothesis is that patients with certain biomarker profiles respond differently to the targeted treatments, randomization is conditional on biomarker group. Without a prior assumption of increased efficacy of certain treatments, equal randomization (ER) occurs at the beginning of the trial. After at least one patient is assessed for response in each treatment by biomarker group {n_jk ≥ 1}, the trial moves to AR. Under the Bayesian paradigm, randomization ratios at each step in enrollment, r_n, are based on posterior distributions for θ. The functional relationship one chooses for θ and r_n was described by Rosenberger (1993) as the treatment effect mapping.

Here, we formulate two mappings to 0. Let Ω_k,n represent the subset of nonsuspended treatments for marker group k at the time of randomization for patient n. For the BATTLE trial, randomization was based proportionally on the posterior mean for the response rate to each treatment

$${\mathrm{r}}_{jk,n}=\frac{{\widehat{\pi }}_{jk,n}}{{\sum }_{w\in {\Omega }_{k.n}}{\widehat{\pi }}_{wk,n}}$$

where π̂_jk,n = E[f⁻¹(μ_jk)∣y_n]. With noninformative priors to the model, this formulation (we term “ratio-mapping”) is equivalent to the sequential maximum likelihood procedure (Rosenberger et al., 2001). Alternatively, one could base randomization on the probability a treatment is superior to all others (we term “max-mapping”),

$${\mathrm{r}}_{jk,n}=Pr(\prod _{\begin{array}{c}{j}^{\prime }\ne j\\ j^{\prime }\in {\Omega }_{k,n}\end{array}}{\mu }_{jk,n}>{\mu }_{j^{\prime }k,n}|y_n)$$

which is derived from the full posterior distribution to θ. In contrasting the two formulations, we note that max-mapping will always approach 1 when one therapy is superior to all others, whereas the value ratio-mapping approaches will depend on J, π₀, and π₁. For this reason we favor max-mapping, and is used for the proposed trial in Section 5.

One criticism of Bayesian adaptive designs is that they are unstable for small amounts of data. A heuristic solution is to delay AR until a fixed number of patients are enrolled, and Cheung et al. (2006) suggested waiting until at least 10 patients are observed for every group. However, for phase II trials with integral biomarkers, this will typically not be feasible. For instance, in the BATTLE trial AR did not begin until 97 of 255 patients were enrolled (Kim et al., 2011), due to the requirement that n_jk ≥ 1 ∀jk for the Gibbs sampler defined in Zhou et al. (2008). We note that even at the completion of the trial, n_jk < 10 in approximately half of the subgroups. For this reason, we advocate the use of a class of informative prior distributions, termed “balanced priors” : ${\phi }_{\mathit{\text{bal}}}=\{\alpha =\frac{f({\pi }_1)+f({\pi }_0)}{2},0<{\sigma }^{-2},0<{\tau }^{-2}\}$. By increasing τ ⁻², one stabilizes the model so that ER occurs until data is accumulated from enough patients showing a difference in response rates.

3.3. Interim Monitoring of Efficacy

During AR all active treatment arms are continuously monitored in order to update randomization ratios. Although biomarker subgroups will assign fewer patients to ineffective treatments as the trial proceeds, for administrative purposes it may be valuable to permanently suspend treatment arms once there is sufficient evidence of ineffectiveness. Under the Bayesian paradigm, one can compute posterior odds or Bayes factors for hypotheses of ineffectiveness. Alternatively, the frequentist approach can be mirrored by defining a threshold for futility, and use the prior distributions and all accumulated data to compute credible sets for efficacy.

Decisions based on Bayesian interval estimation were proposed in Zhou et al. (2008) and can be generalized to binary models with f⁻¹(μ_jk) as

$$F_{n,jk}=\{\begin{array}{cc}1& \text{if Pr}({\mu }_{jk}\ge f({\pi }_1)|y_n)\le {\delta }_L\\ 0& \text{otherwise}\end{array}$$

where (1 − δ_L) is the size of a one-sided credible set, and F_{n, jk} is an indicator of suspension of assignment to treatment j in biomarker group k after n patients are enrolled on the trial. We further denote $F_{jk}={\cup }_{n=1}^N{F}_{n,jk}$ as the cumulative event of suspension at any point in the trial. If all J treatments are suspended, then patients in marker group k are excluded from enrolling on the trial. In order to be conservative about suspension with small n, we advocate using informative “skeptical” priors (Spiegelhalter et al., 1994) which would be centered around π₁ :φ_skep = {α =f(π₁), 0 < σ⁻², 0 < τ⁻²}.

3.4. Final Determination of Efficacy

A final evaluation is performed for all nonsuspended treatments after reaching target accrual, N, and once complete clinical information is obtained. Again, models can be contrasted using Bayes factors, or a determination of efficacy can be defined under the hierarchical model when a (1 – δ_U) sized one-sided credible set to f⁻¹(μ_jk) excludes the unacceptable response rate,

$$S_{jk}=\{\begin{array}{cc}1& \text{Pr}({\mu }_{jk}\ge f({\pi }_0)|y_N)>{\delta }_U\\ 0& \text{otherwise}\end{array}.$$

For the final analysis, a noninformative prior where τ⁻² approaches zero allows for the data from the trial to drive all inferences.

Using these interim and final analysis plans, there is no early stopping for highly effective treatments, which is analogous to frequentist staged designs as developed by Simon (1989). We advocate this for phase II trials, because any treatments demonstrating benefit within (or across) marker subgroups will have greater numbers of patients assigned, and consequently, a more precise declaration of efficacy in the final analysis. This provides the optimal information to support the development of a phase III trial, whether it be in a general or selected patient population.

The main study characteristics of interest are common to noncomparative phase II designs: true positive and true negative findings of efficacy. Using the decision criteria noted above, the probabilities of making correct determinations of efficacy in each treatment and biomarker combination are

$$\begin{array}{c}\mathrm{P}{1}_{jk}=\text{Pr}(S_{jk}=1|{\mu }_{jk}=f({\pi }_1))\\ \mathrm{P}{2}_{jk}=\text{Pr}(S_{jk}=0|{\mu }_{jk}=f({\pi }_0)).\end{array}$$

The complementary probabilities are analogous to the frequentist definitions of Type I and II error.

We can also define probabilities that are complementary to family-wise error rates, which relate to the chance of making correct determinations of efficacy across all marker subgroups where a treatment is effective (P3), or not effective (P4). Likewise, the overall probability of having both true positive and negative findings is their union (P5):

$$\mathrm{P}{3}_j=\text{Pr}(\underset{k:{\mu }_{jk}=f({\pi }_1)}{\cup }{S}_{jk}=1)$$

$$\mathrm{P}{4}_j=\text{Pr}(\underset{k:{\mu }_{jk}=f({\pi }_0)}{\cup }{S}_{jk}=0)$$

$$P5=\text{Pr}(\underset{jk:{\mu }_{jk}=f({\pi }_1)}{\cup }{S}_{jk}=1\cdot \underset{jk:{\mu }_{jk}=f({\pi }_0)}{\cup }{S}_{jk}=1)$$

Operating characteristics and sample-size determinations for the proposed design can be determined by simulating a series of relevant scenarios to the trial design.

4. Simulation

The following are two simplified scenarios where J = K = 2 that are representative of the general research setting of predictive biomarkers in multiarm trials: (a) evaluating a novel targeted agent against standard-of-care with a single predictive biomarker; and (b) selecting among multiple targeted agents specific to complementary predictive biomarkers. A global null to each scenario would be no increased efficacy with either agent. To illustrate how simulation is used to tune model parameters and select sample-size, we will explore each scenario with true unacceptable and acceptable rates of response of (π₀ = 0.25, π₁ = 0.5), and (π₀ = 0.05, π₁ = 0.2).

Characteristics are drawn from B=1000 simulations, where marker status is first sampled from a multinomial distribution defined by marker prevalence, p, which is here set to be p = (0.5, 0.5). Treatment assignment is made under the randomization scheme, and the observed responses are sampled as independent Bernoulli variables with {π_jk}. Figure 2 displays the average randomization rates under the single-marker scenario for ratio- and max-mapping. Within each panel, trajectories are drawn for models using balanced priors: φ_bal = {α = (Φ⁻¹(π₁) + Φ⁻¹(π₀))/2, σ⁻² = 1, τ⁻² = 100}, or using noninformative priors with τ⁻¹ = 0.01. With balanced priors, there is attenuation in the rate at which randomization approaches the true treatment effect to each mapping. Importantly, in subgroups where there is no increased efficacy, randomization ratios remain centered around 0.5 throughout enrollment. With ratio-mapping and balanced priors, randomization rates to the effective treatment approach the true ratios of 0.67 and 0.8 for π₁ = 0.5 and π₁ = 0.2, whereas max-mapping approaches 1 in both cases. Lastly, Table 1 shows that with a strong balanced prior, randomization has minimal variation (IQR < 0.02) when the number of patients on study is very small (n = 5), but that an unacceptably large variation (IQR > 0.5) is seen early on with noninformative priors, which is only partially attenuated using a moderate prior with τ = 1.

Figure 2.

The average randomization ratio from N = 5 to N = 100 under the single marker scenario for the target subgroup (solid line) vs. nontarget subgroup (dotted-line). In each panel, trajectories are drawn for noninformative priors (τ⁻² = 0.01, red) and for balanced priors (τ⁻² = 100, green). Results are displayed for ratio-mapping (left panels) and max-mapping (right panels); and for true efficacy levels of π₀ = 0.25 and π₁ = 0.5 (top panels) and for π₀ = 0.05 and π₁ = 0.2 (bottom panels).

Table 1.

Characteristics of response-adaptive randomization within the single-marker scenario with (π₀ = 0.25, π₁ = 0.5) and (π₀ = 0.05, π₁ = 0.2). Medians and interquartile ranges from 1000 simulations are given under differing priors and treatment effect mapping for (a) randomization ratios at varying n, (b) final allocation to treatment arm, and (c) posterior means the response rate in each subgroup

	Balance τ−2 = 100	Max-mapping moderate τ−2 = 1	Noninform. τ−2 = 0.01	Balanced τ−2 = 100	Ratio-mapping moderate τ−2 = 1	Noninform. τ−2 = 0.01
	Non-target subgroup (π11 =π21 =0.25)
Rand, ratio
n = 5	0.50(0.49,0.51)	0.51 (0.36,0.65)	0.52 (0.24,0.95)	0.50(0.49,0.51)	0.50(0.39,0.62)	0.51 (0.35,0.93)
n = 20	0.50 (0.29,0.73)	0.60 (0.27,0.83)	0.77(0.15,0.97)	0.50(0.38,0.62)	0.55(0.39,0.73)	0.61 (0.31,0.94)
n= 100	0.51 (0.22,0.78)	0.55 (0.22,0.87)	0.71 (0.21,0.98)	0.50(0.42,0.58)	0.51(0.42,0.60)	0.54(0.42,0.78)
Post, mean
π̂11,100	0.24(0.17,0.29)	0.24(0.14,0.29)	0.19(0.02,0.28)	0.25(0.19,0.30)	0.24(0.18,0.30)	0.22 (0.08,0.29)
π̂21,100	0.22(0.13,0.30)	0.21 (0.13,0.29)	0.18(0.02,0.28)	0.24(0.17,0.32)	0.23(0.16,0.30)	0.21 (0.07,0.29)
Allocation to Trt 2	0.51 (0.30,0.71)	0.54 (0.30,0.79)	0.68 (0.28,0.94)	0.50(0.40,0.59)	0.53(0.42,0.65)	0.57(0.39,0.86)
	Target subgroup (π21 =π22 =0.5)
Rand, ratio
n = 5	0.50 (0.49,0.83)	0.51 (0.48,0.88)	0.55 (0.35,0.98)	0.50(0.50,0.69)	0.51(0.48,0.72)	0.54(0.40,0.95)
n = 20	0.77 (0.54,0.90)	0.82(0.51,0.93)	0.91 (0.30,0.99)	0.61(0.51,0.72)	0.66(0.52,0.80)	0.71 (0.46,0.96)
n= 100	0.94 (0.86,0.98)	0.95 (0.87,0.98)	0.97 (0.84,0.99)	0.66(0.60,0.73)	0.67 (0.60,0.76)	0.69(0.60,0.88)
Post, mean
π̂12,100	0.25(0.18,0.30)	0.25(0.20,0.31)	0.24(0.17,0.30)	0.25(0.20,0.31)	0.25(0.20,0.31)	0.25(0.19,0.30)
π̂22,100	0.49 (0.43,0.54)	0.49 (0.42,0.54)	0.48 (0.40,0.54)	0.49(0.43,0.55)	0.49(0.42,0.54)	0.49(0.42,0.55)
Allocation to Trt 2	0.83(0.70,0.89)	0.84(0.71,0.92)	0.88(0.61,0.96)	0.63(0.55,0.71)	0.66(0.55,0.77)	0.69(0.53,0.90)
	Non-target subgroup (π11 =π21 =0.05)
Rand, ratio
n = 5	0.50(0.49,0.51)	0.50 (0.49,0.52)	0.52 (0.43,0.64)	0.50(0.49,0.51)	0.50(0.49,0.52)	0.52(0.41,0.67)
n = 20	0.50 (0.43,0.58)	0.60(0.41,0.75)	0.91 (0.24,0.97)	0.50(0.42,0.58)	0.58(0.41,0.73)	0.86(0.29,0.95)
n= 100	0.50 (0.25,0.77)	0.79 (0.28,0.92)	0.96 (0.22,0.99)	0.51 (0.35,0.67)	0.64(0.38,0.85)	0.92(0.39,0.98)
Post, mean
π̂11,100	0.04 (0.00,0.07)	0.02 (0.00,0.06)	0.01 (0.00,0.05)	0.04(0.01,0.07)	0.03 (0.00,0.07)	0.00 (0.00,0.05)
π̂21,100	0.04 (0.00,0.06)	0.03 (0.00,0.06)	0.01 (0.00,0.05)	0.04 (0.02,0.07)	0.03 (0.00,0.06)	0.00 (0.00,0.04)
Allocation to Trt 2	0.51 (0.35,0.67)	0.68(0.37,0.81)	0.88(0.32,0.93)	0.51 (0.40,0.60)	0.61(0.43,0.75)	0.84(0.41,0.90)
	Target subgroup (π21 = π22 =0.2)
Rand, ratio
n = 5	0.50(0.49,0.51)	0.50 (0.49,0.52)	0.52 (0.43,0.66)	0.50(0.50,0.51)	0.50(0.49,0.52)	0.52(0.41,0.67)
n = 20	0.68 (0.50,0.84)	0.79 (0.47,0.92)	0.96(0.31,0.99)	0.64 (0.50,0.75)	0.73(0.48,0.85)	0.94(0.31,0.98)
n= 100	0.94 (0.86,0.97)	0.97 (0.89,0.99)	0.99 (0.85,1.00)	0.80(0.68,0.86)	0.87(0.73,0.95)	0.97(0.76,0.99)
Post, mean
π̂12,100	0.05 (0.03,0.08)	0.05 (0.03,0.08)	0.05(0.01,0.07)	0.05(0.03,0.08)	0.05(0.03,0.08)	0.05 (0.02,0.07)
π̂22,100	0.19(0.14,0.24)	0.19(0.14,0.23)	0.18(0.11,0.23)	0.19(0.14,0.24)	0.19(0.14,0.23)	0.18(0.13,0.23)
Allocation to Trt 2	0.80 (0.69,0.86)	0.85(0.69,0.91)	0.91 (0.66,0.96)	0.70 (0.60,0.77)	0.79(0.64,0.86)	0.89(0.63,0.94)

Next, we evaluated the probabilities of truly and falsely determining efficacy (P1 and 1 – P2) when using the monitoring plans outlined above. Simulations focused on designs using balanced priors and max-mapping for randomization. By plotting P1 and 1 – P2 over a range of target sample sizes, one can use simulation to select the desired operating characteristics to a trial. For the target rates π₁ = 0.5 and π₀ = 0.25 we found that assessing futility with a threshold of δ_L = 0.025 and a skeptical prior: φ_skep = {α = (Φ⁻¹(π₁), σ² = 1, τ⁻² = 100} and making a final determination of efficacy using noninformative hyperprior φ_non = {α = (Φ⁻¹(π₀), σ² = 1, τ⁻² = 0.01} and δ_U = 0.9 provided a good balance between controlling for false positive and negative results. In particular, P1 ≥ 80% and 1 – P2 ≤ 10% is achieved with N = 55 in the single marker scenario and with N = 59 patients in the complementary marker scenario. By simulating under a null of no efficacy, we note the probability of early stoppage before N = 55 or N = 59 is 47% and 55%, such that the average sample size would be 48.4 and 50.3, respectively.

We next compare our method to independent Simon “optimal” two-stage tests performed within a randomized-block design, as an efficient nonadaptive approach to minimize sample-size when treatments are ineffective. Under a null, H₀ : π_jk = 0.25, and powered on the alternative H₁ : π_jk = 0.5, this requires 8 subjects in the first stage and 21 subjects total per arm (target N = 84) in order to control Type I and II errors at 10% and 20%, respectively. Under the respective alternative hypotheses to the single and complementary marker scenarios, the expected sample sizes to the two-staged design are 57.1 and 65.4, respectively, and 48.7 when there is truly no efficacy with either agent. Thus, marginal improvements in efficiency are seen with our adaptive approach. As advantages, resources would need not be budgeted for the larger target sample size, and more importantly, considerably less variation is seen under our simulations than the actual sample sizes that can occur with 4 independent two-stage tests (Fig. 3).

Figure 3.

Operating characteristics of Bayesian adaptive vs. fixed staged designs. The probabilities of determining efficacy are shown for target samples sizes ranging from N = 5 to 100. In both, the single marker (left panels) and complementary marker (right panels) scenarios, effective treatment-marker combinations are shown in green, vs. ineffective combinations in red. Vertical lines show the target and expected sample sizes (dark and light gray) that give 80% power and control Type I error at 10% in four parallel Simon two-stage tests. Lower panels display the cumulative distribution function (CDF) of sample sizes for the parallel Simon design (gray) under each scenario, vs. sample sizes seen under simulation for adaptive designs (blue) with target N = 55 and 59, respectively.

Simulations under other true effective response rates show a slight attenuation in power when compared to the larger staged-tests: under π₁ = 0.45, P1 ranged from 0.64 to 0.67 vs. power of 0.69 with the Simon design. With a larger true effect size (π₁ = 0.55), P1 ranged from 0.86 to 0.88 vs. power of 0.89 with a Simon design. The small differences may be due to P2 being slightly lower than the Type I error to the Simon design, or may be reflective of tuning the parameters and size of the adaptive design to optimize characteristics against the target response rates.

For target response rates of π₀ = 0.05 and π₁ = 0.2, simulations were repeated to parameterize the model and select samples sizes. Figure 2 and Table 2 show that informative balanced priors are needed to stabilize {r_jk,n} early in the trial and remain 1:1 on average in the nontarget subgroup, and we focus on max-mapping to increase allocation to optimal therapy. Despite the lower event rates, similar gains in efficiency can be seen in the adaptive design when allowing for a higher false positive rate. Using thresholds of δ_L = 0.025 and δ_U = 0.8, we find that N = 74 and 71 control P1 ≥ 80% and 1 – P2 ≤ 15% for the two scenarios. In comparison, Simon two-stages tests would require a target N = 108 (E[N] = 70.2 and 82.8, for the two scenarios) to control Type I and II errors at this level.

Table 2.

Hypothetical relationships between intrinsic subtype, PI3K mutation status, and efficacy of the inhibitor (π _XP,k below). Subgroups with clinical benefit over capecitabine alone (π _X,k = 0.25 in all subgroups) are highlighted in gray. The joint prevalence was reported by TheCancer Genome Atlas Network (2012), and accounts for inclusion into the luminal B* subgroup basal and Her2-enriched subtypes which are seen more rarely in ER+/Her2– disease by IHC

	Luminal B*		Luminal A
Prevalence	PI3K mut. 16.1%	PI3K wt. 39.3%	PI3K mut. 20.0%	PI3K wt. 24.4%
Global Null	0.25	0.25	0.25	0.25
No Biomarker	0.50	0.50	0.50	0.50
Single Biomarker
Luminal B only	0.50	0.50	0.25	0.25
PI3K mut. only	0.50	0.25	0.50	0.25
Joint Biomarker
Either marker	0.50	0.50	0.50	0.25
Both markers	0.50	0.25	0.25	0.25

Lastly, when using noninformative priors for determinations of efficacy, the posterior means for the response rate are biased slightly downward for J = K = 2, as is known to occur with AR (Rosenberger and Lachin, 2002). At n = 100, median relative risks of 0.976 and 0.959 are seen to π₁ = 0.5 and π₁ = 0.2, respectively, after randomizing patients under max-mapping and balanced priors (Table 2). The extent of bias must be carefully considered if one reports Bayesian point-estimates from the hierarchical model at the completion of the study.

5. Example

Increasingly, both clinicians and laboratory scientists have recognized that breast cancer is a heterogeneous disease, which poses a challenge to the development of new therapies and to the appropriate application of existing treatments to individual patients. Using DNA microarray technology, Sorlie et al. (2001) identified five major subtypes of breast tumors, including basal-like, Her2 over expressing, luminal-like (including luminal A and B), and normal breast tissue-like. It was later shown that luminal B subtype tumors have a poor prognosis relative to other ER+/Her2– breast cancers, and represent a population that may derive benefit from novel treatments in the locally advanced setting (Bild et al., 2009).

Phosphatidylinositol 3-kinases (PI3Ks) have come to attention as both a marker of prognosis and a potential target for therapy in a variety of human cancers (Vanhaesebroeck et al., 2010). Once activated, these kinases phosphorylate membrane lipids which in turn trigger a complex signaling cascade leading to cell cycle entry, growth, and survival. Mutations leading to constitutive activation of the pathway have been observed, with early studies reporting a 40% rate of somatic mutations in the gene in breast cancer, especially hormone receptor-positive breast cancer (Campbell et al., 2004). Multiple inhibitors of the PI3K pathway are in development that demonstrate anti-tumor activity in pre-clinical and clinical studies (Markman et al., 2010; Baselga et al., 2011). Among the most interesting targeted strategies for PI3K inhibition is the luminal B subtype of breast cancer. Although typically hormone receptor-positive, this subtype is more chemosensitive than luminal A breast cancer (Fan et al., 2006), and recent studies implicate PI3K pathway signaling in proliferation and cell survival in this subtype (Bild et al., 2009). However, aberrations of PI3K pathway signaling are common across breast cancer subtypes, and a selection strategy for identifying those most likely to respond to inhibition of the PI3K pathway has not yet been defined.

We propose a randomized phase II to evaluate a PI3K inhibitor in advanced hormone refractory breast cancer patients. Activity of the agent will be assessed in combination with standard capecitabine in ER+/Her2– breast cancer defined by standard histological methods. Integral biomarkers will be used to evaluate whether increased efficacy is seen in molecular subgroups of greatest potential to provide a selection strategy. This includes intrinsic subtypes by mRNA expression and PI3K DNA sequencing, with the scientific hypothesis that greater efficacy is seen with either PI3K mutations over wild-type, or with luminal B and other subtypes relative to luminal A tumors.

The primary clinical endpoint for evaluating patient response to capecitabine alone (X) and capecitabine plus PI3K inhibitor (XP) will be objective response. Based on prior knowledge of the efficacy of capecitabine, we will consider a response rate of θ₀ = 0.25 as unacceptable, and θ₁ = 0.5 as a target level of efficacy for treatments within all marker subgroups.

5.1. Design and Operating Characteristics

In the Bayesian AR design, we set a threshold probability of δ_L = 0.01 for the futility monitoring, and δ_U = 0.9 for the threshold for concluding efficacy. The balanced, skeptical, and noninformative priors described above are used for randomization, interim monitoring, and final analysis, respectively.

One heuristic rule is applied over the AR scheme to further control enrollment to the trial. Since there are no interim rules for stopping for superiority, the total number of patients enrolled into a single treatment by subgroup will be capped at 35 to avoid oversam-pling. This threshold was selected under a reduced Bayesian model for a single treatment and single biomarker subgroup, as providing greater than 95% posterior probability of concluding efficacy when θ = Φ⁻¹(π₁).

Simulations were run to select a maximum target sample size based on the probabilities of truly and falsely concluding efficacy. Specifically, six scenarios define different relationships between clinical benefit of XP and the two integral biomarkers, as enumerated in Table 2. Based on anticipated accrual, and the length of follow-up needed to observe objective response, a lag of 10 patients is included into the simulation for randomization and interim monitoring of futility.

Table 3 shows that with a target sample size of N = 168, in all scenarios probabilities of falsely concluding efficacy in each ineffective treatment is less than 10%, while probabilities of concluding success in each effective treatment ranges from 82.1% to 92.8% varying largely by the marker prevalence. Across simulations, effective combinations were stopped at rates between 3.7% and 6.4% while ineffective treatments were stopped at some point during the AR phase 17.8% to 87.3% of the time. In comparison, parallel Simon two-stage designs require greater maximum target sample sizes, needing to allocate 24 × 8 = 192 patients to control Type I and II errors at 0.1 and 0.15 in every group. An even greater number of patients is needed to match the exact operating characteristics to each scenario that is given in Table 3, although the discrete binomial distribution prevents a direct comparison.

Table 3. Probabilities of concluding efficacy by treatment and biomarker subgroup under the six scenarios defined in Table 2. All effective treatments by subgroups per scenario are shaded in gray.

	Luminal B*		Luminal A
	PI3K mut.	PI3K wt.	PI3K mut.	PI3K wt.
Global Null
XP	0.058	0.073	0.072	0.066
X	0.071	0.069	0.076	0.063
No Biomarker
XP	0.821	0.928	0.892	0.899
X	0.057	0.085	0.053	0.06
Luminal B only
XP	0.856	0.928	0.094	0.094
X	0.064	0.066	0.061	0.059
PI3K mt only
XP	0.870	0.085	0.909	0.069
X	0.074	0.059	0.07	0.055
Either marker
XP	0.847	0.923	0.884	0.085
X	0.061	0.074	0.068	0.072
Both markers
XP	0.874	0.075	0.067	0.074
X	0.076	0.066	0.057	0.072

Finally, there is a distinctive advantage of using all available data across biomarker subgroups when making inferences under the hierarchical model (Table 4). For each scenario, the joint probabilities of correctly identifying all subgroups where XP is effective (P3), and where XP or X are ineffective (P4). Results are superior to independent analysis with the larger Simon two-stage designs. The largest improvements are see when multiple biomarker groups demonstrate increased efficacy. For instance, if intrinsic subtype and PI3K mutation are equally predictive (Scenario 5), the probability of identifying all three subgroups increases from 0.618 to 0.694, while under a global null (Scenario 1), the chance of a false discovery decreases from 54.4% down to 42.5%.

Table 4. Family-wise operating characteristics of the AR design vs. parallel Simon two-stage designs.

	P3	P4x	P4xp	P5
Global Null
AR	−NA−	0.748	0.760	0.575
Simon	−NA−	0.676	0.676	0.456
No Biomarker
AR	0.625	0.771	−NA−	0.497
Simon	0.527	0.676	−NA−	0.356
Luminal B only
AR	0.798	0.786	0.820	0.536
Simon	0.726	0.676	0.822	0.403
PI3K mt only
AR	0.789	0.766	0.855	0.521
Simon	0.726	0.676	0.822	0.403
Either marker
AR	0.694	0.750	0.915	0.485
Simon	0.618	0.676	0.907	0.379
Both markers
AR	0.874	0.763	0.802	0.526
Simon	0.852	0.676	0.745	0.429

6. Discussion

We have presented a novel approach to studying the efficacy of treatments in the context of integral biomarkers. By adopting a Bayesian response adaptive model, flexibility in the trial design allows for a seamless transition from investigating agents in a general population toward a marker-directed strategy where patients are randomized with greater probability to their optimal therapy. To meet the requirements of randomized phase II studies, the model incorporates a continuous monitoring for futility and a final analysis of efficacy that are conditioned on the integral biomarkers. Simulations demonstrate the properties of the model, and its advantages over using parallel and independent staged designs.

Adaptive trial designs give a framework whereby the mathematical models account for flexibility required in phase II screening trials, and with modern computational resources the numerical routines can be implemented as easily as exact binomial tests. Adaptive trials do require a larger informatics structure to continuously monitor enrolled patients in order to maximize gains in efficiency. However, adaptive approaches can be seamless and do not require suspension of enrollment until complete outcome information is obtained and evaluated, thus removing a large operational barrier to the study team and common hindrance to study accrual with staged phase II trials.

We have shown under simulation that adapting with a Bayesian hierarchal model lowers the total target sample sizes over traditional designs. Further, in staged designs, interim looks that occur early in the trial to optimize the characteristics can cause wide variations in final sample sizes. Flexibility and robust performance of our Bayesian AR model is demonstrated by the consistent operating characteristics seen across a variety of relationships between treatment efficacy and biomarker subgroups. Conversely, it may not be feasible to use parallel multistage tests for biomarker groups with unequal prevalence. We also propose that adaptive designs will be more robust to marker misspecification than a randomized-block design, based on the flexibility and gains in power from the hierarchical model. Future simulation studies are planned to demonstrate and quantify this assertion using the biomarker prevalences reported by Kim et al. (2011). All these points allow for such trials to be planned and budgeted for more easily using Bayesian hierarchical models and response-AR.

The greatest benefit of our approach is that by jointly modeling efficacy of treatments in the Bayesian hierarchical model, improved statistical inferences can be made about the predictive or prognostic value of biomarkers over designs that focus on efficacy within or across patient subgroups. This will be critical for clinical contexts where integral biomarkers can be used to identify the proper study population for definitive phase III studies of efficacy. Finally, we note that as a conservative element to the adaptive approach, if the clinical data are missing or delayed (completely at random to treatment assignment), the AR will transition more slowly from ER.

Future efforts are to apply the Bayesian hierarchical structure to statistical models for other clinical endpoints that are continuous and right-censored. However, the advantages of adaptive design are maximized when endpoints can be assessed early. With the expansion of rationally identified therapeutic targets, the simultaneous identification of rational biomarkers naturally follows. Indeed, the FDA has released a draft guidance document “In Vitro Companion Diagnostic Devices” to encourage development of biomarkers (molecular or otherwise) as diagnostics for guiding treatment decisions and patient selection. The flexibility and efficiency of adaptive clinical trial designs provide important advances for guiding and accelerating this complex co-development process.

Figure 4.

Schema for the adaptive randomized phase II to evaluate capecitabine (X) with and without a PI3K inhibitor across four biomarker-defined subgroups of ER+/Her2– breast cancer.

Appendix: Sample R Code

####################

## Dependent function for simulation in R

####################

MCMCfun <- function(n_i, y, group2, theta.0, theta.1, phi) {

  require (msm)

  alpha <- phi[1]; sigma2 <- phi[2]; tau2 <- phi[3]

  mu <- pr.eff <- pr.stop <- pihat <- rmax <- rep(0, J* K)

  psi <- rep (0, J)

  n.jk <- table (group2)

  n.j < - tapply (n.jk, rep(1:J, each=K), sum)

  sd.mu <- (n.jk + 1/sigma2) ˆ (-.5)

  sd.phi <- (n.j + 1/tau2) ˆ (-.5)

  for (b in 1:(n.burn+ (skip + 1) * n.iter)) {

    z <- rtnorm(n_i, mu[group2], lower = c(-Inf, 0) [1+y], upper = c(0, Inf) [1+y])

   mu <- rnorm(J* K, mean = (sigma2 * tapply(z,group2,sum) + rep(psi,each=K) ) /

                               (sigma2 * n.jk + 1),sd=sd.mu)

   psi <- rnorm(J,mean = (tau2 * tapply(mu* n.jk,rep(1:J, each=K),sum) + alpha ) /

                               (tau2 * n.j + 1),sd= sd.phi)

   if(b > n.burn & trunc((b-n.burn)/(skip+1)) == (b-n.burn)/ (skip + 1)){

     pr.eff <- pr.eff + (mu > qnorm(theta.0))/n.iter

     pr.stop <- pr.stop + (mu > qnorm(theta.1))/n.iter

     pihat <- pihat + pnorm(mu) / n.iter

     rmax <- rmax + (mu == rep(tapply(mu,rep(1:K,J),max), J)) / n.iter

     }

  }

return(list(pr.eff = pr.eff, pr.stop = pr.stop, pihat = pihat, rmax = rmax))

}

####################

## Simultations for Figures 2 and 3, and Table 1

##    (parameterized for left-most column

####################

## Parameters

Nmax = 100

J = 2; K = 2;                                  ## Indexes for groups

prob.K = c(0.5,0.5)                            ## Proportion of genotype groups (length K)

p0 = 0.25; p1 = 0.2                            ## Target response rates

off =0                                         ## Offset between target and true rate.

pi = c(p1 + off, p0,                           ## True response rates

       p0 , p1+off)                            ## ordered as trt(group)

phi.r = c(alpha = (qnorm(p0)+qnorm(p1))/2,

          sigma2 = 1, tau2 = 0.01)             ## Hyperparameters for randomization

r.method =2                                     ## Mapping (1=ratio, 2=max)

phi.f = c(alpha = qnorm(p1),

          sigma2 = 1, tau2 = 0.01)             ## Hyperparameters for futility

phi.e = c(alpha = qnorm(p0),

          sigma2 = 1, tau2 = 0.01)              ## Hyperparameters for efficacy

delta.U = 0.9                                   ## Decision rule [efficacy]

delta.L = 0.025                                 ## Decision rule [stop]

n.burn = n.iter = 5000; skip =0                 ## MCMC parameters

#### Simulation

set.seed(seed)

group <- assign <- group2 <- y <- rep(NA,Nmax)

stop1 <- rep(0,J* K); fail1 <- 0

theta.0 = rep(p0,J* K); theta.1 = rep(p1,J* K)

group[1:(J* K)] <- rep(1:K,J)

assign[1:(J* K)] <- rep(1:J,each=K)

group2[1:(J* K)] <- group[1:(J* K)] + K * (assign[1:(J* K)]-1)

y[1:(J* K)] <-        runif(J* K) < pi[group2[1:(J* K)]]

## Adaptive Randomization

i <- J* K

while((i < Nmax) & (fail1==0)){

  post.f <- MCMCfun(i,y[1:i], group2[1:i],theta.0, theta.1,phi.f)                                          ## 1. Run MCMC for futility

  stop1[stop1==0] <- (post.f [[2]] [stop1==0] < delta.L) * i                                                        ## 2. Check futility in active arms

  drop <- tapply(stop1,rep(1:K,J),prod)                                            ## 3. Drop groups with stopped arms

  if(prod(drop)) {fail1 <- 1} else {                                                   ## 4. If all arms not dropped

     if(sum(!drop)>1){                                                           ## 4a. Draw new patients group

      group[i + 1] <- sample((1:K)[!drop], 1,prob=prob.K[!drop])

     } else group[i+1] <- (1:K)[!drop]

     post.r <- MCMCfun(i,y[1:i], group2[1:i],theta.0,theta.1,phi.r)                              ## 4b. Run MCMC for randomization

     if(r.method == 1){

        rand <- post.r[[3]]

     } else if(r.method == 2) rand <- post.r[[4]]

     rand[stop1>0] <- 0

     assign[i + 1] <- sample(1:J,1, prob=rand[rep(1:K,J) ==group[i + 1]])                              ## 4c. Assign treatment

  group2[i + 1] <- group[i + 1] + K* (assign[i + 1]-1)

    y[1+i] <- runif(1) < pi[group2[1+i]]                                                                  ## 4d. Simulate outcome

    post.e <- MCMCfun(i + 1,y[1:(i + 1)], group2[1:(i + 1)],theta.0,theta.1,phi.e)

    write(paste(c(i + 1,                       ## 4e. Output:

               table(group2[1:(1+i)]),                                   #Sizes

               (post.e[[1]] > delta.U)* (stop1==0), # Dec of Eff

               (stop1>0),                          # Dec of Fut

               post.e[[3]],                        # PostMean of Eff

               rand),                              # Rand weights

            collapse=” “),outfile, append=T)

  print(paste(”   “, i + 1, “patients analyzed”))

    }

    i <- i + 1

}

####################

## Simulation of PI3K trial design: Scenario #3: LumB ONLY

####################

## Parameters

Nmax = 200                              ## Maximum possible total sample size

J = 2; K = 4                            ## Indexes for groups

prob.K = c(0.161,0.393,0.200,0.244)     ## Proportion of biomarker subgroups

pi     = c(0.25,0.25,0.25,0.25,         ## True response rates (length J * K)

           0.50,0.50,0.25,0.25)         ## ordered as trt(group) -

r.method =2                             ## Treatment effect mapping

phi.r = c(alpha = (qnorm(0.25)+qnorm(0.5))/2,

         sigma2 = 1,tau2 = 0.01)        ## Hyperparameters for rand

phi.f = c(alpha = qnorm(0.5),

         sigma2 = 1,tau2 = 0.01)        ## Hyperparameters for fut

phi.e = c(alpha = qnorm(0.25),

         sigma2 = 1,tau2 = 100)         ## Hyperparameters for eff

delta.U <- 0.90                         ## Decision rule [success]

delta.L <- 0.02                         ## Decision rule [stop]

lag   <- 10                             ## Lag - estimated accrual before ORR

Imin  <- 0                              ## Minimum number of patients before AR

cap   <- 35                             ## Maximum number of patients per arm

n.burn = n.iter = 5000;  skip =0        ## MCMC parameters

#### Simulation

set.seed(seed)

theta.0 <- rep(0.25,J * K); theta.1 <- rep(0.5,J * K)

group   <- sample(1:K,Nmax,replace=T,prob=prob.K)

stop1   <- stop2 <- rep(0,J * K); screen <- fail1 <- 0

assign  <- y <- rep(NA,Nmax)

## Phase 1) ER phase until rule for interim monitoring triggered

   group2 <- factor(assign,levels=1:(J * K))

   i < - 0;

   while(i < (Nmax-lag-1) & (sum(table(group2)==0) | i < (Imin))){

     i <- i + 1

     assign[i] <- sample(1:J,1)

     group2[i] <- group[i] + K * (assign[i]-1)

     y[i] <- runif(1) < pi[group2[i]]

   }

   start <- (i + lag)

   print(paste(“ “, start, “patients in ER phase”))

   assign[i+ (1:lag)] <- sample(1:J,lag,replace=T)

   group2[i+ (1:lag)] <- group[i+ (1:lag)] + K * (assign[i+ (1:lag)]-1)

   y[i+ (1:lag)]      <- runif(lag) < pi[group2[i+ (1:lag)]]

## Phase 2) AR phase, arms are dropped by futility analysis

   while((i < (Nmax-lag)) & (!fail1)){

     post.f <- MCMCfun(i,y[1:i],group2[1:i],theta.0,theta.1, phi.f)

     stop1[stop1==0] <- (post.f[[2]][stop1==0] < delta.L) * i

     stop2 <- table(group2[1:(i + lag)]) >= cap

     drop <- tapply(stop1 + stop2,rep(1:K,J),prod)

     if(prod(drop)){ fail1 <- i } else {

       j <- i + 1 + lag

       if(drop[group[j]]){

         screen <- screen + 1

         c <- 1; while(c){

           group[j] <- sample((1:K),1,prob=prob.K)

         if(drop[group[j]]) screen <- screen + 1 else c <- 0

       }

     }

   post.r <- MCMCfun(i,y[1:i],group2[1:i],theta.0, theta.1,phi.r)

   if(r.method == 1){

     rand <- post.r[[3]]

   } else if(r.method == 2) rand <- post.r[[4]]

   rand[(stop1>0) |stop2] <- 0

   assign[j] <- sample(1:J,1,prob=rand[rep(1:K,J) ==group [j]])

   group2[j] <- group[j] + K * (assign[j]-1)

   y[j] <- runif(1) < pi[group2[j]]

   post.e <- MCMCfun(j,y[1:j],group2[1:j],theta.0,theta.1, phi.e)

   print(paste(“    ”, j, “patients analyzed”))

   write(paste(c(j,screen, table(group2[1:j]),            ## Total, screened and subgroup sizes

                 (post.e[[1]] > delta.U)  * (stop1==0),   ## Decision of efficacy

                 (stop1>0),                               ## Decision of futility

                 rand),                                   ## Randomiztion ratios

                 collapse=“\t”),outfile, append=T)

   }

   i <- i + 1

}