# Biomarker-Guided Non-Adaptive Trial Designs in Phase II and Phase III: A Methodological Review

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## Abstract

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## 1. Introduction

## 2. Methods and Findings

#### 2.1. Single Arm Designs

**Design:**In this design all patients are prescribed the experimental treatment and there is no comparison with a control treatment. These trial designs aid in the identification of association between biomarker status and the efficacy or safety of the experimental treatment. An illustration of this approach is shown in Figure 2.

**Utility:**These designs can be useful for the initial identification and/or validation of a biomarker and their aim is not to estimate the treatment effect in a definitive way but to identify whether the biomarker is sufficiently promising to proceed to a definitive Phase III biomarker-guided randomized controlled trial.

**Methodology:**In single arm designs first we assess the biomarker status of patients and then as all patients will be treated the same way we could compare the outcome of the biomarker-positive subgroup with the outcome of biomarker-negative subgroup. According to Tajik et al., 2012 [117], in terms of the required sample size, a standard formula can be used, however one should take into consideration the multiple testing issue that arise due to the exploration of several prognostic biomarkers (e.g., Bonferroni adjustment or normal exact method to protect against type I error $a$ for multiple tests are often considered [118]). Further information can be found in the paper of Zaslavasky and Scott, 2012 [118] who studied the sample size estimation in single arm clinical trials with multiple testing under frequentist and Bayesian framework.

**Statistical considerations:**The single arm approach can be considered as a simple statistical design as there is no need for randomization. However one limitation of this strategy is that there is no distinction between prognostic and predictive biomarkers i.e., as patients are not randomized to experimental and control treatment groups, it is not possible to determine whether an observed effect is attributable to the natural disease progression or to the treatment. Consequently, this study designs are unable to show the benefit of a biomarker with regard to the best choice of treatment.

#### 2.2. Enrichment Designs

**Design:**Figure 3 graphically represents the trial design. First, the entire population is screened in order to identify the biomarker status of each patient. Next, the random assignment of individuals to different treatment arms is restricted only to the biomarker-positive subgroup. More precisely, biomarker-negative patients are excluded from the study and consequently, the assessment of the effectiveness of the experimental treatment is limited to the biomarker-positive subgroup. Thus, other patients apart from the biomarker-positive subpopulation can receive only the standard treatment (i.e., control treatment), but they are not included in the investigation during the trial design. The biomarker in this design is referred to as either the ‘selection’ or ‘enrichment’ biomarker.

**Utility:**Enrichment designs are useful for clinical trials aiming to test the treatment effect in a specific biomarker-defined subpopulation where there is evidence to suggest that effectiveness is limited to those within that subgroup, but the candidate biomarker still requires prospective validation. This design is recommended when both the cut-off point for determination of biomarker status of patients and the analytical validity of the biomarker have been well established. A rapid turnaround time for assessing the biomarker status of a patient is also needed to avoid any delay in treatment initiation. This strategy is particularly useful where it is unethical to randomize the biomarker-negative population into different treatment arms, for example where there is prior evidence that the experimental treatment is not beneficial for biomarker-negative individuals, or is likely to cause them harm. However, when it remains unclear whether or not biomarker-negative individuals will benefit from the novel treatment, the enrichment design is not appropriate and alternative designs, which also assess effectiveness in the biomarker-negative individuals, should be considered (e.g., randomize-all designs).

**Methodology:**An online tool has been developed by Zhao and Simon [19,28,53,57,60] that allows sample size planning for the enrichment design both for binary and time-to-event (survival) outcomes, and is available at http://brb.nci.nih.gov/brb/samplesize/td.html [113]. For the purpose of estimating the sample size in the case of a survival outcome, data are simulated based on a marker stratified design (see next section for further information) in which both biomarker-positive and biomarker-negative subgroups are investigated in the study and formulae for the enrichment design described in the paper of Rubinstein et al., 1981 [110] are used. Furthermore, an exponential distribution of survival for the experimental and control treatment groups within both the biomarker-positive and biomarker-negative subpopulations is assumed. More precisely, Rubinstein et al.provide the formula of the expected number of events per treatment group allowing to include exponential loss to follow-up given the following assumptions: (i) patients enter the trial according to a Poisson process and patient entry times will be independent and identically distributed uniformly over $\left[0,T\right]$ where $T$ denotes the accrual time. Consequently, given the total number of patients $N$, the times from entry to the end of the trial will be independent and identically distributed uniformly over $\left[\tau ,T+\tau \right]$, where $\tau $ denotes the follow-up time and $T+\tau $ the total duration of the study and (ii) 1:1 randomization between experimental and control treatment group is considered. The expected number of events per treatment arm according to Rubinstein et al. is given by

**Statistical considerations:**Simon and Maitournam [65,111,112] undertook a simulation study, assuming a binary outcome, to compare power of the enrichment design with an untargeted design (i.e., marker stratified design, see next section for further information) in which all patients are randomized without measuring the biomarker. They concluded that the efficiency of the enrichment design relies both on the prevalence of the biomarker-positive patients and on the accuracy of the assay. Whilst in the situation where the assay cut-off point is not well established, there is a risk of severely compromising the power of the trial when using an enrichment design, if fewer than half of the entire study population are biomarker-positive and there is robust evidence that the experimental treatment does not benefit the biomarker-negative patients, the required number of randomized patients to allow sufficient power to detect a significant treatment effect is much smaller in the enrichment design than in the untargeted trial design. However, in the latter situation a greater number of individuals would need to be screened when using the enrichment design, and accruing the required number of biomarker positive patients could take a longer period of time. More precisely, Simon and Maitournam showed that an approximation of the ratio of the required number of patients to be randomized for the untargeted trial design as compared with the required number of patients randomized in the enrichment design when using binary outcome can be given by the following equation

#### 2.3. Randomize-All Designs

#### 2.3.1. Marker Stratified Designs

**Design:**An illustration of the design is shown in Figure 4. Individuals are stratified into biomarker-positive and biomarker-negative subgroups according to the results of the biomarker assessment and then they are randomized either to the experimental or to the control treatment group. The biomarker status in the Marker-Stratified design acts as a stratification factor where stratification is used to ensure balance across treatment groups with regard to biomarkers. Only individuals with valid biomarker results enter the trial. Consequently, we have four treatment groups, i.e., biomarker-positive patients assigned to either the experimental treatment arm or the control treatment arm and biomarker-negative patients assigned to either the experimental treatment arm or the control treatment arm. Thus, we can assess the relationship between treatment effect and biomarker status.

**Utility:**When there is enough evidence that the experimental treatment is more effective in the positive biomarker-defined subgroup than in the negative biomarker-defined subgroup but there is no sufficient compelling data that the experimental treatment is of no benefit in biomarker-negative individuals, the marker stratified design can be used.

**Methodology:**Biomarker status is used to stratify the randomization, rather than to restrict eligibility. Marker-stratified designs can be conducted using two different testing plans; the so-called marker-by-treatment interaction with separate tests and marker-by-treatment interaction with interaction test. Both of these approaches involve conducting two independent clinical trials.

**Statistical considerations:**Despite the fact that the marker stratified designs allow testing the treatment effect not only in the entire population but also in each biomarker-defined subpopulation, they might not be feasible when the prevalence of biomarker is low. Another limitation of such designs is that they might require a large sample size where several treatments and biomarkers are investigated in the study.

**Subgroup-Specific designs:**This strategy is an approach to analyze a biomarker-stratified trial. It is composed of two types; ‘Sequential Subgroup-Specific design’ and ‘Parallel Subgroup Specific design’. Both biomarker-positive and biomarker-negative subgroups can be tested in a sequential or in a parallel way. With the parallel way, we can assess simultaneously both biomarker-positive and biomarker-negative patients, whereas, with the sequential way we perform first the assessment of biomarker-positive patients and if the result is positive then we continue with the biomarker-negative patients.

**Sequential Subgroup-Specific design:**This approach was referred to in 11 papers (11%) of our review. Figure 5 graphically represents this approach.

**Design:**The sequential testing procedure uses the assumption that it is unlikely that the new treatment will be effective in the biomarker-negative patients unless it is effective in the biomarker-positive patients. First treatment effect is tested in the biomarker-positive subpopulation using the overall two-sided significance level $\alpha =0.05$ (Type I error); if this test is significant then treatment effect is tested in the biomarker-negative subgroup using the same level of significance $\alpha $.

**Utility:**Its use is recommended when there is compelling evidence that biomarker-positive individuals benefit more from the experimental treatment than the biomarker-negative patients. More precisely, it is appropriate when it is not expected for the novel treatment to be effective in biomarker-negative patients unless it is beneficial for the biomarker-positive patients.

**Methodology:**As this subgroup-specific design follows a sequential assessment and thus the design is composed of two stages, the sample size calculation is also staged. For binary outcome the required number of biomarker-positive patients is the same as for the enrichment design, i.e.,

**Statistical considerations:**This strategy preserves the overall type I error rate $a$ but requires a smaller number of positive patients as compared to the second type of subgroup-specific design, the so-called parallel subgroup-specific design (see below). Furthermore, it enables the identification of treatment efficacy in the biomarker-positive and biomarker-negative subpopulations separately. However, it yields low power when there is homogeneity of treatment effect across the different biomarker-defined subpopulations. Furthermore, in case that test for treatment effect among biomarker-negative patients is not statistically significant, an ‘exploratory’ analysis on the biomarker-negative subgroup might be considered.

**Parallel Subgroup-Specific design:**This design was identified in three papers (3%) of our review.

**Design:**Parallel subgroup-specific design (Phase III), also referred to as a Phase III Biomarker-Stratified design evaluates treatment effects separately in the positive biomarker-defined subgroup and in the negative biomarker-defined subgroup simultaneously. A graphical illustration of this strategy is given in Figure 6.

**Utility:**It is appropriate when the aim of the study is to give treatment recommendations for each biomarker-defined subgroup separately at the same time.

**Methodology:**In order to control the overall type I error rate of the design at the overall level of significance $\alpha $ (Type I error) it is required to allocate this overall $\alpha $ between the test for the biomarker-positive subgroup and the test for the biomarker-negative subgroup using the Bonferroni correction method [124] for multiple testing; e.g., if we choose the value of 0.025 for the global significance level $\alpha $, then we could choose the values of ${a}_{1}=0.010$ and ${a}_{2}=0.015$ for testing the biomarker-negative and biomarker-positive subgroups respectively. This trial design is powered in such a way so as to detect the treatment effect in each biomarker-defined subgroup separately. A higher portion of the type I error rate can be given for the test within the biomarker-positive subgroup in order to maximize the power of the trial to identify the treatment effect in this subpopulation. However, even if there is a slight increase in the type I error probability spent on the test of one of the biomarker-defined subgroups, the power would probably not change much.

**Statistical considerations:**With this approach, in case that the overall level of significance $a$ is equal in both subgroup-specific designs, it is more difficult to achieve statistical significance in the biomarker-positive subgroup as compared to the sequential subgroup-specific design due to the allocation of the overall significance level between the two biomarker-defined subgroup tests.

**Biomarker-positive and overall strategies:**This design provides an alternative strategy to analysing a biomarker-stratified design. It is an indirect way of evaluating both biomarker and treatment by testing the treatment effect in the entire study population and in the biomarker-positive subgroup separately. Three approaches are included in the biomarker-positive and overall strategies; the parallel assessment, the sequential assessment and the fall-back design (see below).

**Biomarker-positive and overall strategies with parallel assessment**: This approach was identified in eight papers (8%) of our review. Figure 7 graphically represents this strategy. In the parallel version, we test both the overall population and biomarker-positive subgroup simultaneously.

**Design:**In this approach the treatment effect is tested in both the entire study population and in the biomarker-positive patients while controlling the type I error by allocating the overall significance level $\alpha $ between the two tests. The significance level $a$ can be considered as one-sided or two-sided.

**Utility:**The parallel version is recommended when the aim of the study is to assess the treatment effect in both the overall study population and in the biomarker-positive subgroup but not in the biomarker-negative subgroup.

**Methodology:**If there is significant confidence that the biomarker is predictive, the sample size estimation is aimed at having a sufficient number of biomarker-positive individuals to enable the treatment effect in the biomarker positive subgroup to be detected. On the other hand, if there is no confidence in the predictive value of the biomarker, the sample size estimation is aimed at having a sufficient number of patients to detect a treatment effect in the overall study population [14].

**Statistical considerations:**This design has the ability to control the probability of rejecting the null hypothesis of no treatment effect either in the biomarker-positive population or in the biomarker-negative population under the global null hypothesis of no treatment effect in the entire population at the overall significance level $a$. However, it cannot control the probability of rejecting the null hypothesis of no treatment effect in the biomarker-negative subset when the treatment benefit is restricted to biomarker-positive patients. Consequently, there is high risk of inappropriately recommending the experimental treatment for biomarker-negative patients.

**Biomarker-positive and overall strategies with sequential assessment:**This approach was referred to in 11 papers (11%) of our review. A graphical illustration of this approach is shown in Figure 8.

**Design:**In this sequential version of the biomarker-positive and overall strategies, we first test the biomarker-positive subgroup using the significance level $\alpha $; if the test is significant, then we test the treatment effect in the overall population using the same $\alpha $ level. The significance levels $a$ can be considered as one-sided or two-sided significance levels.

**Utility:**The sequential version might be useful in cases where the experimental treatment is expected to be effective in the overall study population.

**Methodology:**As this design comprises two sequential stages, it follows that the sample size calculation should also be staged. At the first stage, the standard formula for a traditional randomized trial can be used for the biomarker-positive subgroup using the significance level $\alpha $ to estimate the treatment effect in that subset. More precisely, the formula used in the enrichment design for the required total number of events or the required number of patients can be used at the first stage of this design. At the second stage, the sample size must be adjusted in order to yield appropriate power for the entire population.

**Statistical considerations:**As in the parallel version of this designs, this strategy does not allow for identification of treatment efficacy in the biomarker-negative subgroup and despite the fact that it can control the overall type I error $\alpha $ it cannot control the probability of rejecting the null hypothesis of no treatment effect in the biomarker-negative subset when the treatment benefit is restricted to biomarker-positive patients. Consequently, for this design also there is high risk of inappropriately recommending the novel treatment for biomarker-negative patients.

**Biomarker-positive and overall strategies with fall-back analysis:**This strategy was identified in 15 papers (15%) of our review. It evaluates both the treatment effect in the overall study population and in the biomarker-positive subgroup sequentially. Figure 9 graphically represents this strategy.

**Design:**In the fall-back design, we first test the overall population using the reduced significance level ${a}_{1}$ and if the test is significant, we consider that the novel treatment is effective in the overall population; however, if the result is not significant then we test the treatment effect in the biomarker-positive subgroup using the level of significance ${a}_{2}=a-{a}_{1}$, where $a$ is the overall significance level (Type I error rate). The significance levels $a$ can be considered as one-sided or two-sided significance levels. The same analysis plan was used in the adaptive signature design which is further described in our methodological review regarding the biomarker-guided adaptive designs, Antoniou et al., 2016 [35]. More precisely, the difference between the adaptive signature design and the fall-back design is the following: in the adaptive signature design, in case that the first stage failures to show treatment effectiveness in the entire population, then the study population is divided in order to develop and validate a biomarker, using a split sample strategy, whereas in the biomarker-positive and overall strategies design with fall-back analysis the biomarker assessment is conducted at the beginning of the trial. However, both of the designs test at the first stage the entire population at the significance level ${a}_{1}$ and at the second stage the biomarker-positive patients at the significance level ${a}_{2}=a-{a}_{1}$.

**Utility:**This approach is recommended when there is insufficient confidence in the predictive value of the biomarker and that the novel treatment is believed to be effective in all individuals (i.e., the rationale for the biomarker is weak). This design can be used in order to avoid the possibility of missing an important treatment effect in the biomarker-positive patients (with insufficient benefit in the biomarker-negative subgroup).

**Methodology:**The sample size should be set in such a way so as to yield adequate power for the overall test at the reduced significance level ${a}_{1}$ and for the potential biomarker positive subgroup analysis at significance level $a-{a}_{1}$ [60]. The fall-back version is identical to the parallel version of biomarker-positive and overall strategies in terms of sample sizes and study outcomes, however the difference between these approaches is that the fall-back strategy is useful in settings where a biomarker will be assessed only if the overall population benefit is not promising [14]. This strategy can test the treatment effectiveness in biomarker-positive patients even if there is no detected benefit of the novel treatment in the overall population. However, it does not evaluate clearly the treatment benefit in the biomarker-negative subpopulation.

**Statistical considerations:**As the two aforementioned biomarker-positive and overall designs, this strategy can again control the overall type I error $\alpha $ but it cannot control the probability of rejecting the null hypothesis of no treatment effect in the biomarker-negative subgroup when the treatment benefit is restricted to biomarker-positive patients. Consequently, there is high risk of inappropriately recommending the novel treatment for biomarker-negative patients. Song et al., 2007 [129] and George, 2008 [1] have discussed refinement of the significance levels associated with this design, which takes into account the correlation between the test for overall treatment effect and the test for the biomarker-positive treatment effect [60]. Additionally, a recent paper by Choai et al., 2015 [97] proposes a bias-corrected estimation method for treatment effects for the all-comers randomized clinical trials with a predictive biomarker which incorporate the fall-back analysis. For Choai et al., 2015 [97] the terminology “all-comers randomized clinical trials” is referred to the “Biomarker-positive and overall strategies with fall-back analysis”. More precisely, as this study design has an adaptive nature and is composed of two stages, a bias is possible to arise in the treatment effect estimation in the biomarker-positive subset when the first stage of the trial yields an overall result which is not significant and thus fails to demonstrate a treatment efficacy in the entire population. For this reason, Choai et al. ,2015 [97], formulate a bias function using polynomials in order to take into account the possibility of failing to demonstrate overall treatment efficacy during the first stage of the trial.

**Marker Sequential test design (MaST):**This design was identified in four papers (4%) of our review and while controlling the appropriate type I error rates, it evaluates not only the biomarker-positive and biomarker-negative subgroups but also the entire population sequentially to limit the assessment of treatment effect in the overall population when it seems that the biomarker-positive subgroup does not benefit from the novel treatment. A graphical illustration of this approach is given in Figure 10.

**Design:**In this design which owns an adaptive nature, first, the biomarker-positive subgroup is tested at a reduced level ${a}_{1}$ in $\left[0,a\right]$ and if the result is significant, then the biomarker-negative subgroup is tested at the global significance level $\alpha $. Otherwise, if the result is not significant, then the overall population is tested at level ${a}_{2}=a-{a}_{1\text{}}$ in order to make a treatment recommendation for the biomarker-negative patients.

**Utility:**It is generally recommended when robust evidence is available regarding a biomarker and there is prior evidence showing that the novel treatment is more beneficial for the biomarker-positive patients as compared to the biomarker-negative patients. Additionally, it is appropriate when we can assume that the treatment will not be beneficial for the biomarker-negative subgroup unless it is effective for the biomarker-positive subgroup. Additionally, the marker sequential test design is considered as an alternative to the sequential subgroup-specific design when the aim is to consider the treatment effect not only in biomarker-positive but also in the biomarker-negative patients.

**Methodology:**Freidlin et al., 2014 [69] recommended using the value of 0.022 for the reduced significance level ${a}_{1}$ in order to control the type I error rate for biomarker-negative patients at the global significance level $\alpha =0.025$ and the value of 0.04 for the reduced significance level ${a}_{1}$ in order to control the type I error rate for biomarker-negative patients at the global significance level $\alpha =0.05$.

**Statistical consideration:**Freidlin et al., 2014 [69] performed a comparison between the MaST and the sequential subgroup-specific design through a simulation study and concluded that the marker sequential design yields higher power in cases where the treatment effect is homogeneous across biomarker-defined subgroups. Additionally, with this approach, the power is preserved in situations where the experimental treatment is effective only for the biomarker-positive patients. Furthermore, in situations where biomarker status is not available for a portion of patients included in the trial, the marker sequential test design can either exclude these patients or include them in the global test, whereas, the proposed subgroup-specific designs do not consider inclusion of these patients in the analyses. If researchers decide to exclude patients with unavailable biomarker status from the study when using a MaST design, no statistical adjustment is required. On the other hand, if the inclusion of this study population is chosen, then this can result in inflation of the type I error rate for the biomarker-negative subpopulation above the global significance level $\alpha $ due to the modification of correlation structure between the biomarker-defined subgroup tests and global test. In addition, while both MaST and subgroup-specific designs have the ability to control the probability of incorrectly rejecting the null hypothesis of no treatment effect in the biomarker-negative patients at the significance level $\alpha $ when the experimental treatment does not work in either biomarker-defined subgroup, the sequential subgroup-specific approach typically has a smaller probability of incorrectly rejecting the null hypothesis of no treatment effect in the biomarker-negative subset (when the null hypothesis is true) as compared to the MaST design, especially under the global null hypothesis of no treatment effect in the entire population; the probability of incorrectly rejecting the null hypothesis of no treatment effect in the biomarker-negative patients depends on the choice of ${a}_{1}$. This conservativeness of sequential subgroup-specific design, which is due to its sequential nature, makes the MaST design advantageous [69].

#### 2.3.2. Hybrid Designs

**Design:**In this approach, only the biomarker-positive patients are randomly assigned to either the experimental treatment group or to the control treatment group whereas the biomarker-negative patients receive the control treatment. These designs were first defined by Mandrekar and Sargent [30,31]. The difference compared with the enrichment designs is that the biomarker-negative patients are not excluded from the study.

**Utility:**Hybrid designs can be used when there is compelling prior evidence which shows detrimental effect of the experimental treatment for a specific biomarker-defined subgroup (i.e., biomarker-negative subgroup) or some indication of its possible excessive toxicity in that subgroup, thus making it unethical to randomize the patients within this population to the experimental treatment.

**Methodology:**Similar to the enrichment design, hybrid designs are powered to identify treatment effect only in the biomarker-defined subgroup which is randomly assigned to the experimental or control treatment groups. Consequently, the same formula used for the required number of patients or events for the enrichment designs can be used for hybrid designs. This design is a combination of an enrichment design where we randomize patients to either the experimental or the control treatment group and a single-arm design in biomarker-negative patients.

**Statistical considerations:**The strength of the hybrid design is that apart from the evaluation of the predictive ability of a biomarker, the feasibility of a prognostic biomarker can also be tested. It can be considered as an advantageous design of the enrichment designs when there is prior evidence showing not only that the control treatment works well for the biomarker-negative population but also a detrimental effect of the experimental treatment for that subgroup or possible excessive toxicity as we do not exclude these patients from the trial as it happens in the enrichment designs.

#### 2.4. Biomarker-Strategy Designs

#### 2.4.1. Biomarker-Strategy Design with Biomarker Assessment in the Control Arm

**Design:**First, the study population enrolled in the trial is tested for its marker status. Next, patients irrespective of their biomarker status are randomized either to the biomarker-based strategy arm (also referred to as personalized arm) or to the non-biomarker-based strategy arm. In the biomarker-based strategy arm, biomarker-positive patients receive the experimental treatment, whereas, biomarker-negative patients receive the control treatment. Patients who are randomized to the non-biomarker-based strategy arm receive the control treatment irrespective of their biomarker status. A graphical illustration of this design is given in Figure 12. This biomarker-strategy design can be extended to more than one experimental treatment. More precisely, this extension is referred to as Individual profile design in literature and was identified in two papers [36,72] (2%) of our review. This design includes different individual status, e.g., instead of biomarker-positive and biomarker-negative subgroups we can have patients who are positive for biomarker 1, biomarker 2, biomarker n, leading to the selection of personalized treatments, (patients who are positive for biomarker 1 are treated with the corresponding experimental treatment 1, etc.).

**Utility:**This approach is useful when we want to test the hypothesis that the treatment effect based on the biomarker-based strategy approach is superior to that of the standard of care.

**Methodology:**The clinical utility of a biomarker can be evaluated by comparing the two strategy groups. The predictive utility of the marker-based treatment strategy could be assessed by comparing the outcome of all patients in the biomarker-based strategy arm to all patients in the non-biomarker-based strategy arm. Patients in the marker-based strategy arm do not need to be limited to two treatments; in principle, a marker-based strategy involving many biomarkers and many possible treatments could be compared to standard of care treatment.

**Statistical considerations:**This type of designs is able to inform researchers whether the biomarker is prognostic, since both biomarker positive and negative patients are exposed to the control treatment, but it cannot answer the question of whether the biomarker is predictive since only biomarker positive patients are exposed to the experimental treatment. Additionally, these designs have been criticized by many authors as less efficient than the marker-stratified designs since it is possible for some patients in both the biomarker-based strategy arm and non-biomarker-based strategy arm to be assigned to the same treatment (due to the existence of biomarker-negative patients in both strategy arms the treatment effect can be diluted) and they require a large sample size to detect an overall difference in outcomes between arms. Furthermore, these designs cannot compare experimental treatment to control treatment directly as they are designed to compare not the treatments but the biomarker-strategies. Another limitation of these designs is the uncertainty about whether the results which indicate efficacy of the biomarker-directed approach to treatment are caused due to a true effect of the biomarker or due to a treatment effect irrespective of the biomarker status.

#### 2.4.2. Biomarker-Strategy Design without Biomarker Assessment in the Control Arm

**Design:**In this approach, patients are again randomized between testing strategies (i.e., biomarker-based strategy and non-biomarker-based strategy) but it differs in terms of the timing of biomarker evaluation. More precisely, first, patients are randomized to either the biomarker-based strategy or to the non-biomarker-based strategy. Next, this design evaluates the biomarkers only in patients who are assigned to the biomarker-based strategy. Patients who are found to be biomarker-positive will receive the experimental treatment and patients who are biomarker-negative will receive the control treatment. On the other hand, the population which is randomized to the non-biomarker-based strategy will receive the control treatment. A graphical illustration of this design is given in Figure 13.

**Utility:**This design is useful in situations where it is either not feasible or ethical to test the biomarker in the entire population due to several logistical (e.g., specimens not submitted), technical (e.g., assay failure) or clinical reasons (e.g., tumor inaccessible); thus the biomarker status is obtained only in patients who are tailored to the biomarker-based strategy arm.

**Methodology:**The same mathematical formula for sample size calculation assuming a continuous clinical outcome proposed by Young et al. (2010) [26] and the formula assuming binary outcome proposed by Eng, 2014 [92] for the biomarker-strategy design with biomarker assessment in the control arm could be applied. Further, in terms of survival outcome, the same formula provided for the required number of events in the first version of biomarker-strategy designs (i.e., biomarker-strategy design with biomarker assessment in the control arm) could be considered.

**Statistical considerations:**These designs have the same advantages and limitations as the previously discussed biomarker-strategy design with biomarker assessment in the control arm, e.g., they have been criticized for their lack of efficiency due to the fact that biomarker negative patients are exposed to the control treatment in both arms of the trial. An additional limitation is that the biomarker-positive and biomarker-negative subpopulations might be more imbalanced as compared with the first type of biomarker-strategy design due to the fact that the randomization is performed before the evaluation of biomarker (balancing the randomization is useful to ensure that all randomized patients have tissue available).

#### 2.4.3. Biomarker-Strategy Design with Treatment Randomization in the Control Arm

**Design:**A graphical illustration of this approach is given in Figure 14. The two previously described biomarker-strategy designs can answer the question about whether the biomarker-based strategy is more effective than standard treatment, irrespective of the biomarker status of the study population, whereas the biomarker-strategy design with treatment randomization in the control treatment is able to inform us about whether the biomarker-based strategy is better than not only the standard treatment but also better than the experimental treatment in the overall population. This is achieved by using a second randomization the ratio of which should be informed by the prevalence of the biomarker in question in the population as a whole to ensure balance between the study arms. Patients are first randomly assigned to either the biomarker-based strategy arm or to the non-biomarker-based strategy arm. Next, patients who are allocated to the non-biomarker-based strategy are again randomized either to the experimental treatment arm or to the standard treatment arm irrespective of their biomarker status. Patients who are allocated to the biomarker-based strategy and who are biomarker-positive are given the experimental treatment and patients who are biomarker-negative are given the control treatment. The clinical utility of the biomarker is evaluated by comparing treatment effect between the biomarker-based strategy arm and non-biomarker-based strategy arm. Such an approach can also identify whether a novel treatment is more effective in the entire population or in a biomarker-defined subgroup only, since both biomarker subgroups are exposed to both treatments.

**Utility:**These designs are preferable as compared to the two previously discussed biomarker-strategy designs in cases where there is interest in whether the biomarker is not only prognostic but also predictive.

**Methodology:**Mandrekar and Sargent, 2009 [31] calculated the total required sample size in terms of number of events for the comparison of a survival outcome in the biomarker-based strategy versus the non-biomarker-based strategy. According to them, the required total number of events when using 1:1 randomization to treatment arms is given by

**Statistical considerations:**Similar to both aforementioned biomarker-strategy designs, the biomarker-strategy design with treatment randomization in the control arm will need larger sample size as compared to the marker-stratified designs. However, one strength is that they allow clarification of whether the results which indicate efficacy of the biomarker-directed approach to treatment are caused due to a true effect of the biomarker or due to a treatment effect irrespective of the biomarker status which does not happen in the first two types of biomarker-strategy designs.

#### 2.4.4. Reverse Marker-Based Strategy Design

**Design:**A graphical illustration of this approach is given in Figure 15. In this design patients are randomized either to the biomarker-based strategy arm or the reverse biomarker-based strategy arm. As in the previous three biomarker-strategy subtype designs, patients who are allocated to the biomarker-strategy arm receive the experimental treatment if they are biomarker-positive whereas biomarker-negative patients receive the control treatment. By contrast, patients who are randomly assigned to the reverse biomarker-based strategy arm receive control treatment if they are biomarker-positive, whereas biomarker-negative patients receive experimental treatment.

**Utility:**Reverse marker-based strategy is a more efficient strategy as compared to the first and third biomarker-strategy subtype design for testing the interaction hypothesis of treatment and biomarker. This design should be used in cases where prior evidence indicates that both experimental and control treatment are effective in treating patients but the optimal strategy has not yet been identified.

**Methodology:**This subtype design is balanced (i.e., the randomization frequencies for each treatment are equal independent of the prevalence of the biomarker) and it is powered to evaluate the interaction between treatment and biomarker. For the case of binary outcomes, Eng, 2014 [92] provided the formula for the required sample size for each arm in a test of proportions between the two randomization arms (biomarker-based strategy arm and reverse biomarker-based strategy arm). This formula can be given by

**Statistical considerations:**This design enables the evaluation of the interaction between the biomarker and different treatments and can estimate directly the marker-strategy response rate. Additionally, this subtype design allows the estimation of the effect size of the experimental treatment compared to the control treatment for each biomarker-defined subgroup separately. Also, there is no chance that the same treatment will be tailored to biomarker-positive patients who are randomized either to the biomarker-based strategy arm or the reverse marker strategy (i.e., biomarker-positive patients in the biomarker-based strategy will be given only the experimental treatment and biomarker-positive patients in the reverse marker strategy arm will be given only the control treatment). Also, there is no possibility of the same treatment assignment to biomarker-negative patients who are randomly assigned to the two biomarker-based strategy arms (i.e., biomarker-negative patients in the marker-based strategy arm will be treated with the control treatment, whereas biomarker-negative patients in the reverse marker strategy arm will be treated with the experimental treatment). According to Eng, 2014 [92] who compared the reverse marker-based strategy design with the first (i.e., biomarker-strategy design with biomarker assessment in the control arm) and third (i.e., biomarker-strategy design with treatment randomization in the control arm) subtype of biomarker-strategy designs in the case of binary outcomes, the effect size in order to make a comparison of the different treatment strategy arms would be larger than in the first and third subtype designs. Furthermore, it has been shown by Eng, 2014 that in situations where a randomly chosen treatment has a better than 7% response rate, the reverse marker-based strategy design works better as compared to the third biomarker-strategy subtype (i.e., Biomarker-strategy design with treatment randomization in the control arm). It has also been demonstrated that this novel design is more than four times more efficient in order to test the interaction between treatment and biomarker compared to Biomarker-strategy design with biomarker assessment in the control arm, Biomarker-strategy design with randomization in the control arm and the marker stratified design. Eng, 2014 demonstrated the benefits of the Reverse Marker-Based strategy design with the aim to assess the interaction between treatment and biomarker. However, Baker, 2014 [93] stated that other designs than the Reverse Marker-Based strategy design would be more appropriate in order to investigate questions which include treatment effect of biomarker-defined subgroups and biomarker-based strategy arms.

#### 2.5. Other Designs

#### A Randomized Phase II Trial Design with Biomarker Proposed by Freidlin et al., 2012

**Design:**For this type of randomized Phase II trial, it is assumed that the experimental treatment will be more beneficial among biomarker-positive patients than biomarker-negative patients without ruling out the efficacy of the novel treatment in biomarker-negative patients. The intermediate endpoint of progression-free survival (PFS) is used which is able not only to give the results earlier but also to target larger treatment effects as compared to overall survival (OS) endpoint.

**Utility:**This design should be used when we want to conduct a Phase II randomized trial which allows decisions to be made about which type of Phase III biomarker-guided trial to proceed with. It is appropriate when there is prior evidence that the novel treatment benefits mostly the biomarker-positive patients without ruling out treatment effect in biomarker-negative patients.

**Methodology:**Freidlin et al., 2012 [71] have provided an online tool for calculating the sample size which can be found on the following website http://brb.nci.nih.gov/Data/FreidlinB/RP2BM [116]. In order for a sample size to be estimated, the following information is required: (i) the significance levels for testing the treatment effect in the biomarker-positive subgroup and in the entire population; (ii) cut-offs and confidence intervals for the hazard ratio in the biomarker-negative subgroup; (iii) the prevalence of biomarker-positive patients; (iv) the median progression-free survival in each treatment arm in each biomarker-defined subgroup and (v) the accrual parameters. Regarding the accrual parameters, the author specifies the minimum sample size for biomarker-positive patients for which the accrual continues until this number is reached, the maximum number of over-accrual in biomarker-positive subgroup for which the accrual to the entire population stops after this number is reached and the maximum accrual number in biomarker-negative patients for which the accrual to this biomarker-defined subgroup stops when this number is reached.

**Statistical considerations:**In real life, it might not be possible to obtain the biomarker status for the entire population. If the biomarker status is unknown for some patients, then these individuals could be included in the analysis of the overall population. More precisely, in case that the proportions of patients with unknown biomarker status is low, the randomization of them to either the experimental or the control treatment could be considered in the second stage of this Phase II trial where we test the treatment effectiveness in the entire population. Another statistical consideration is that researchers should take into account the adjustment for inflation in Phase III type I error as the chosen Phase III trial design depends on the performance of the aforementioned randomized Phase II trial. Additionally, the authors suggest generally that in cases where it seems that the control treatment has been shown more beneficial, an aggressive interim inefficacy/futility should be used, i.e., when the estimated hazard ratio of control treatment versus the experimental treatment is equal or less than one when half of the required number of events have been observed, then the accrual should stop to that biomarker-defined subgroup.

## 3. Discussion

## Supplementary Materials

## Acknowledgments

## Author Contributions

## Conflicts of Interest

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**Figure 1.**Flow diagram of the review process. From our search strategy a total number of 211 papers have been identified giving information regarding not only the biomarker-guided designs but also general information about personalized medicine and biomarkers. Before arriving at 211 papers, books, web pages for actual trials and papers published before 2005 were excluded. The 211 papers are split into two overlapping sets of 100 and 107 papers. The total of 207 is less than 211 due to overlap of papers, and also due to the fact that some articles referring to general information about personalized medicine and biomarkers and articles which do not provide further information on each broad of biomarker-guided designs were excluded. The 107 papers for biomarker-guided adaptive trial designs were reviewed in our published paper Antoniou et al. (2016) [35].

**Figure 5.**Sequential Subgroup-Specific design. “R” refers to randomization of patients. Uncolored boxes are referred to the first stage of the trial and colored boxes are referred to the second stage of the trial.

**Figure 7.**Biomarker-positive and overall strategies with parallel assessment. “R” refers to randomization of patients.

**Figure 8.**Biomarker-positive and overall strategies with sequential assessment. “R” refers to randomization of patients. Uncolored boxes are referred to the first stage of the trial and colored boxes are referred to the second stage of the trial.

**Figure 9.**Biomarker-positive and overall strategies with fall-back analysis. “R” refers to randomization of patients. Uncolored boxes are referred to the first stage of the trial and colored boxes are referred to the second stage of the trial.

**Figure 10.**Marker Sequential test design (MaST). “R” refers to randomization of patients. Uncolored boxes are referred to the first stage of the trial and colored boxes are referred to the second stage of the trial.

**Figure 12.**Biomarker-strategy design with biomarker assessment in the control arm. “R” refers to randomization of patients.

**Figure 13.**Biomarker-strategy design without biomarker assessment in the control arm. “R” refers to randomization of patients.

**Figure 14.**Biomarker-strategy design with treatment randomization in the control arm. “R” refers to randomization of patients.

**Figure 16.**Randomized Phase II trial design with biomarkers. “R” refers to randomization of patients. CI refers to the confidence interval. Uncolored boxes are referred to the first stage of the trial and colored boxes are referred to the second stage of the trial.

Types of Biomarker-Guided Non-Adaptive Trial Designs | Utility | Advantages | Limitations |
---|---|---|---|

Single arm designs (7 papers) [30,36,37,38,39,40,41] (see Figure 2) | Useful for initial identification and/or validation of a biomarker. | (A1) Considered as a simple statistical design as there is no need for randomization of patients. | (L1) There is no distinction between prognostic and predictive biomarker as patients are not randomized to experimental and control treatment arms. |

Also called: Nonrandomized clinical trial design, Uncontrolled Cohort Pharmacogenetic Study design | (A2) Simple logistics. | ||

Examples of actual trials: None identified ^{a} | (A3) Not complex statistical design | ||

(A4) In some cases, these designs may be viewed as ethical as all patients are given the opportunity to experience the experimental treatment. However, they may be viewed as unethical if the novel treatment does not benefit a subgroup of patients or causes adverse events. | |||

Enrichment designs (71 papers) [1,4,7,8,9,11,13,15,16,18,19,21,23,25,26,27,28,29,30,31,32,33,36,42,43,44,45,46,47,48,49,50,51,52,53,54,55,56,57,58,59,60,61,62,63,64,65,66,67,68,69,70,71,72,73,74,75,76,77,78,79,80,81,82,83,84,85,86] (see Figure 3) | Useful when we aim to test the treatment effect only in biomarker-positive subset for which there is prior evidence that the novel treatment is beneficial, but the candidate biomarker requires prospective validation. | (A5) Evaluates the effect of the experimental treatment in the biomarker-positive subgroup in a simple and efficient way. | (L2) Do not assess whether the experimental treatment benefits the biomarker-negative patients, thus we cannot obtain information about this subgroup. Also unable to demonstrate whether the targeted treatment is beneficial in the entire study population. |

Also called: Targeted design, Selection design, Efficient Targeted design, Biomarker-Enrichment design, Marker-enrichment design, Gene enrichment design, Enriched design, Clinically enriched Phase III study design, Clinically Enriched Trial design, Biomarker-Enriched design, Biomarker Enriched design, Biomarker Selected trial design, Screening enrichment design, Randomized Controlled Trial (RCT) of test positive design, Population enrichment design | Useful when it is not ethical to assign biomarker-negative patients to the novel treatment for which there is prior evidence that it will not be beneficial for this subpopulation, or that it will harm them. | (A6) Provides clear information about whether the novel treatment is effective for the biomarker-positive subgroup, thus these designs can identify the best treatment for these patients and confirm the usefulness of the biomarker. | (L3) Do not inform us directly about whether the biomarker is itself predictive because the relative treatment efficacy may be the same in the unevaluated biomarker-negative patients. Since these designs only enrol a subgroup of patients, they do not allow for full validation of the marker’s predictive ability. For full validation, a trial would need to randomize all patients in order to test for a treatment–biomarker interaction. |

Examples of actual trials: CRYSTAL [49], BRIM 3 [49,50,51], EURTAC [49], CLEOPATRA [49], PROFILE 1007 [49,50], LUX-Lung [49], NSABP B-31 and NCCTG N9831 [4,15,16,18,19,28,29,30,31,36,44,46,52,53,54,55,56,57,58,59,60], CALGB-10603 [61], CATNON [62], CODEL [62], Evaluation of epidermal growth factor receptor variant III (EGFRvIII) peptide vaccination [62], N0923 [7,21] , Flex study [64], TOGA trial [47], IPASS [33,43], N0147 [29], PetaCC-8 [29,47], C80405 [29], ECOG E5202 [29] | Recommended when both the cut-off point for determination of biomarker-status of patients and the analytical validity of a biomarker are well established. | (A7) Reduced sample size as the assessment of treatment effect is restricted only to biomarker-positive subgroup. Therefore, if the selected biomarker is “biologically correct” and reliably measured, the used enrichment strategy could result in a large saving of randomized patients. | (L4) Researchers should carefully decide whether or not to follow this strategy as it may be of limited value due to the exclusion of biomarker-negative patients. It may be that the entire population could benefit from the experimental treatment equally irrespective of biomarker status, in which case enrolling only the biomarker-positive patients will result in slow trial accrual, increase of expenses and unnecessary limitation of the size of the indicated patient population. |

(A8) Enables rapid accumulation of efficacy data. | (L5) Concern over an ethical problem as we cannot include individuals in a clinical trial if it is believed that the treatment is not effective for them, as raised by the US Food and Drug Administration (FDA) [50]. It was based on the facts that the experimental treatment can only be approved for a particular biomarker-defined subpopulation (i.e., biomarker-positive patients) if a companion diagnostic test is also approved, and how the test can be approved if the Phase III trial does not show that the novel treatment does not benefit the biomarker-negative patients. | ||

(A9) Allow us to avoid potential dilution of the results due to the absence of biomarker-negative patients. For example, if the design had included the biomarker-negative population and the biomarker positivity rate was low as compared to the biomarker negative rate, then the estimation of the overall treatment effectiveness could be diluted as it would be driven by the biomarker-negative subset. | (L6) The accuracy of diagnostic devices used to identify the biomarkers, e.g., biomarker assays, is not always correct [45]. This can result in incorrect selection of biomarker-positive patients and therefore these patients will erroneously be enrolled in a trial yielding biased treatment effect estimates. For example, even when the experimental treatment works well for a specific subgroup, if the biomarker assay is not able to identify this subgroup robustly then a promising treatment may be abandoned. | ||

(A10) Can be attractive in terms of speed and cost, meaning that patients are provided with tailored treatment sooner. | |||

Marker Stratified designs (45 papers) [4,10,12,13,15,16,17,18,19,21,25,26,27,30,31,33,44,45,46,49,50,51,53,58,61,62,66,68,71,72,73,74,79,80,81,84,85,86,87,88,89,90,91,92,93] (see Figure 4) | Useful when there is evidence that the novel treatment is more effective in the positive biomarker-defined subgroup than in the negative biomarker-defined subgroup but there is insufficient compelling data indicating that the experimental treatment does not benefit the biomarker-negative patients. | (A11) Ability to assess the treatment effect not only in the entire population but also in each biomarker-defined subgroup. Thus, this design can find the optimal treatment in the entire population and in each biomarker-defined subgroup. | (L7) In situations where there are several biomarkers and treatments this design may not be feasible as it involves randomization of patients between all possible treatment options and may require a large sample size. |

Also called: Marker-stratified design, Biomarker-stratified design, Stratified-Randomized design, Stratification design, Stratified design, Stratified Analysis design, Marker by treatment – interaction design, Marker-by-treatment interaction design, Treatment by marker interaction design, Treatment-by-marker interaction design, Marker × treatment interaction design, Treatment-marker interaction design, Biomarker-by-treatment interaction design, Non-targeted RCT (stratified by marker) design, Genomic Signature stratified designs, Signature-Stratified design, Randomization or analysis stratified by biomarker status design, marker-interaction design. | (A12) An ethical design even in situations where the biomarker is not useful as no treatment decisions are made based on biomarker status; all decisions are made randomly. Consequently, if the biomarker’s value is in doubt, this design may be preferred. | (L8) May not be feasible when the prevalence of the biomarker is low. | |

Examples of actual trials: MARVEL (N023) [4,16,30,31,33,44,61,89], GALGB-30506 [15,61], RTOG0825 [45], EORTC 10994 p53 [12,66], IBCSG trial IX [18], MINDACT [18] | (L9) Might be expensive to test the entire population for its biomarker status. | ||

(L10) Measuring the biomarker up front may be logistically difficult. | |||

(L11) There is no guarantee of balanced groups for analysis. | |||

Sequential Subgroup-Specific design (11 papers) [13,14,19,22,53,57,58,60,69,91,94] (see Figure 5) | Recommended when prior evidence indicates that the biomarker-positive subpopulation benefits more from the novel treatment as compared to the biomarker-negative subpopulation. | (A13) Allows for the estimation of treatment effect in biomarker-positive and biomarker-negative subgroups. | (L12) Has less power when there is homogeneity of treatment across the different biomarker defined subgroups as compared to the overall/biomarker-positive designs. |

Also called: sequential design, Fixed-sequence 2 design, hierarchical fixed sequence testing procedure | (A14) Preserves the overall type I error rates and allows for a smaller sample size than the parallel version mentioned below. | (L13) Need a much larger sample size than the overall/biomarker positive designs if we assume that the treatment effect is relatively homogeneous across the biomarker-defined subsets. | |

Examples of actual trials: PRIME [49], MARVEL [49] | (A15) Considered as the best direct evidence for clinical decision making as it tests the treatment effectiveness in both the biomarker-positive and biomarker-negative subset in a sequential way. | ||

(A16) Do not require larger sample size than the overall/biomarker-positive designs when the prevalence of the biomarker-positive patients is small. | |||

Parallel Subgroup-Specific design (3 papers) [14,49,69] (see Figure 6) | Appropriate when the aim of the study is to give treatment recommendations for each biomarker-defined subgroup separately at the same time. | (A17) Same as (A13), (A16) | (L14) Same as (L12) |

Also called: Phase III Biomarker-Stratified design | (L15) Allocates the overall level $a$ between the two biomarker-defined subgroup tests which means that it will be more difficult to achieve statistical significance in the biomarker-positive subgroup. | ||

Examples of actual trials: None identified ^{a} | |||

Biomarker-positive and overall strategies with parallel assessment (8 papers) [1,14,36,47,49,69,95,96] (see Figure 7) | Recommended when the aim of the study is to assess the treatment effect in both the entire population and in the biomarker-positive subset but not in the biomarker-negative population. | (A18) Can control the overall type I error $a$. | (L16) Can be overly conservative as in the SATURN trial because of the correlation between the test of treatment effect in the overall study population and in the biomarker subgroups. |

Also called: Overall/biomarker-positive design with parallel assessment, prospective subset design, hybrid design | (A19) Can require smaller sample size as compared to the subgroup-specific designs, especially when we assume that the novel treatment equally benefits both biomarker-defined subgroups. | (L17) Cannot control the probability of rejecting the null hypothesis of no treatment effect in the biomarker-negative subset when the treatment benefit is restricted to biomarker-positive patients. Consequently, there is a high risk of inappropriately recommending the novel treatment for biomarker-negative patients due to the large treatment effect in biomarker-positive subset. | |

Examples of actual trials: S0819 [14,49], SATURN [14,36,47,49,95,96], MONET1 [14,49], ARCHER [14,49], ZODIAC [49], MERiDiAN [49] | |||

Biomarker-positive and overall strategies with sequential assessment (11 papers) [13,14,30,44,49,69,80,84,85,88,94] (see Figure 8) | Might be useful in cases where the experimental treatment is expected to be effective in the overall population. | (A20) Same as (A18), (A19) | (L18) Can be problematic for determining whether the treatment is beneficial in the biomarker-negative subgroup. |

Also called: Overall/biomarker-positive design with sequential assessment, sequential design, Fixed-sequence 2 design, hierarchical fixed sequence testing procedure | (L19) Same as (L17) | ||

Examples of actual trials: Trial of letrozole plus lapatinib versus letrozole plus placebo in breast cancer, with the biomarker defined by human epidermal growth factor receptor 2 (HER2) [14], N0147 [30,49] | |||

Biomarker-positive and overall strategies with fall-back analysis (15 papers) [10,30,36,44,47,49,53,57,60,69,84,88,94,96,97] (see Figure 9) | Recommended when there is insufficient confidence in the predictive value of the biomarker and the novel treatment is assumed to probably benefit all patients. | (A21) Can assess the treatment effect in the biomarker-positive patients, if no benefit is detected in the overall population. | (L20) Same as (L17), (L18) |

Also called: Biomarker-stratified design with fall-back analysis, fall-back design, prospective subset design, sequential design, other analysis plan design, Fallback design | (A22) Same as (A18), (A19) | ||

Examples of actual trials: None identified ^{a} | |||

Marker Sequential test design (4 papers) [14,49,69,94] (see Figure 10) | Recommended when biomarkers with strong credentials are available and we have convincing evidence that the novel treatment is more effective in biomarker-positive than in biomarker-negative patients. | (A23) Can provide clear evidence of treatment benefit in the biomarker-positive subgroup and in the biomarker-negative subgroup. | (L21) In situations where biomarker status is not available for some of the patients included in the study, this design can either exclude these patients or include them in the global test, however, further statistical adjustments might be required in that case. |

Also called: MaST design, hybrid design | Appropriate when we can assume that the treatment will not be beneficial in the biomarker-negative subpopulation unless it is effective for the biomarker-positive subpopulation. | (A24) Enables sequential testing of the treatment effect in the entire study population and in the biomarker-defined subgroups to restrict testing of the treatment effect in the entire population when there is no significant result in the biomarker-positive subset, while controlling the appropriate type I error rates. | (L22) Does not decrease the sample size of the study as it was developed in order to increase the power compared to the sequential subgroup-specific design in situations where the novel treatment benefits equally both biomarker-negative and biomarker-positive patients. |

Examples of actual trials: ECOG E1910 [14,49] | (A25) Results in higher power as compared to the sequential subgroup-specific design in cases where the treatment effect is homogeneous across the biomarker-defined subgroups. | ||

(A26) Preserves the power in situations where the treatment effect is restricted only to the biomarker-positive patients and at the same time it controls the relevant type I error rates. | |||

(A27) Control the type I error rate for the biomarker-negative subgroup over all possible prevalence values. | |||

(A28) The probability of erroneously concluding that the novel treatment is beneficial for the entire population when the global effect is driven by the biomarker-positive patients is minimized since the design only tests the treatment effect in the entire population when no significant effect is detected in the biomarker-positive subgroup. | |||

Hybrid designs (14 papers) [1,13,15,29,30,31,36,46,48,55,66,84,88,98] (see Figure 11) | Can be used when there is prior evidence indicating that only a particular treatment is beneficial to a biomarker-defined subgroup which makes it unethical to randomize patients with that specific biomarker status to other treatment options. | (A29) The feasibility of a prognostic biomarker can be tested. | None found. |

Also called: Mixture design, Combination of trial designs, hybrid biomarker design | (A30) Allows for better risk assessment and improved individualized treatment since it assigns patients to treatments based on risk assessment scores instead of their biomarker status (biomarker-positive and biomarker-negative patients). | ||

Examples of actual trials: TAILORx [15,48,55,58,63,66], EORTC MINDACT [15,48,55,66], ECOG 5202 study [30,46] | |||

Biomarker-strategy designs with biomarker assessment in the control arm (21 papers) [15,25,26,32,33,36,45,61,62,64,79,82,85,86,92,93,99,100,101,102,103] (see Figure 12) | Useful when we want to test the hypothesis that the treatment effect based on the personalized approach is superior to that of the standard of care. | (A31) Biomarker can be validated without including all possible biomarker–treatment combinations [26] as in the non-biomarker-based arm all patients receive only the control treatment. | (L23) Unable to inform us whether the biomarker is predictive as these designs are able to answer the question about whether the biomarker-based strategy is more effective than standard treatment, irrespective of the biomarker status of the study population. |

Also called: Marker strategy design, Biomarker-strategy design, Strategy design, Marker-based strategy design, Marker-based design, Random disclosure design, Customized strategy design, Parallel controlled pharmacogenetic study design, Marker-based strategy design I, Biomarker-guided design, Biomarker-based assignment of specific drug therapy design, Marker-based strategy I design, Biomarker-strategy design with a standard control, Marker strategy design for prognostic biomarkers | (A32) Have the option of testing the biomarker status of patients in the non-biomarker-strategy arm which can aid secondary analyses [26]. | (L24) The evaluation of the true biomarker by treatment effect is not possible as the biomarker-positive patients receive only the experimental treatment and not the alternative treatment (control treatment). Consequently, this design cannot detect the case in which the control treatment might be more beneficial for the entire population. | |

Examples of actual trials: GILT docetaxel [15], Randomized phase III trial conducted in Spain, dedicated to patients with advanced Non-Small Cell Lung Cancer (NSCLC) candidates for first-line chemotherapy [32,64,100], Study the effect of Magnetic Resonance Imaging (MRI) in patients with low back pain on patient outcome and to evaluate Doppler US of the umbilical artery in the management of women with intrauterine growth retardation (IUGR), Randomized controlled trial in recurrent platinum-resistant ovarian carcinoma [101] | (A33) Able to inform us whether the biomarker is prognostic. | (L25) In case that the number of biomarker-positive patients is very small, then the treatment received will be similar in biomarker-strategy arm and non-biomarker strategy arm. Consequently, the trial might give little information regarding the efficacy of the experimental treatment or it might not be able to detect it. As a result, this type of design should be used when there is an adequate number of biomarker-positive and biomarker-negative patients. | |

(A34) Can be expanded to investigate several biomarkers and treatments [103]. Additionally, these designs can be attractive when evaluating multiple biomarkers or the predictive value of molecular profiling between several treatment options is to be assessed [45]. | (L26) Unable to compare directly experimental treatment to control treatment as the aim is to compare not the treatments but the biomarker-strategies. | ||

(A35) Might be used more frequently in the future due to the wide variety of molecular biomarkers, complexity of gene expression arrays, and several treatments directed at similar targets [103]. | (L27) Less efficient designs than biomarker-stratified designs [4,73] and a poor substitute for clinical trials which aim to compare the experimental treatment to control treatment, since it is possible for some patients in both the biomarker-based strategy arm and non-biomarker-based strategy arm to be assigned to the same treatment (due to the existence of biomarker-negative patients in both strategy arms the treatment effect can be diluted) [51]. Consequently, as a large overlap of patients receiving the same treatment might have occurred, the comparison of the two biomarker-strategy arms results in a hazard ratio which is forced towards unity, i.e., no treatment effect exists as the effect of experimental versus control treatment is diluted by the biomarker-based treatment selection. For this reason, a large sample size is needed to detect at least a small overall difference in outcomes between the two biomarker-strategy arms. | ||

(L28) Should be used only if you want to evaluate a complex biomarker-guided strategy with a variety of treatment options or biomarker categories [73]. | |||

Biomarker-strategy design without biomarker assessment in the control arm (14 papers) [9,13,17,18,20,25,36,38,61,74,101,104,105,106] (see Figure 13) | In situations where it is not feasible or unethical to test the biomarker in the entire population. | (A36) Galanis et al., 2011 [45] stated that these designs can be attractive when evaluating multiple biomarkers or the predictive value of molecular profiling between several treatment options is to be assessed. Also, Freidlin and Korn, 2010 [73] claimed that these biomarker-strategy designs should be used only if researchers want to evaluate a complex biomarker-guided strategy with a variety of treatment options or biomarker categories. | (L29) Criticized for their potential cost increase due to the fact that patients without predicted responsive biomarker are double enrolled in the trial (biomarker-negative patients receive control treatment in both strategy arms). |

Also called: Biomarker-strategy design with standard control, Direct-predictive biomarker-based, RCT of testing, Test-treatment, Parallel controlled pharmacogenetic diagnostic study, Marker strategy, Marker-based with no randomization in the non-marker-based arm, Classical, Marker-based strategy, Marker strategy design for prognostic biomarkers | (A37) Same as (A31), (A32), (A33) | (L30) Biomarker-positive and biomarker-negative subpopulations might be more imbalanced as compared with the first type of biomarker-strategy design due to the fact that the randomization to different treatment strategies is performed before the evaluation of the biomarker status (balancing the randomization is useful to ensure that all randomized patients have tissue available). This can happen especially when the number of patients is very small. | |

Examples of actual trials: A study, which evaluated the use of immediate computed tomography in patients with acute mild head injury [101,104]. | (L31) Same as (L23), (L24), (L25), (L26), (L27) | ||

Biomarker-strategy design with treatment randomization in the control arm (17 papers) [15,17,26,27,32,36,45,62,64,66,74,86,92,93,106,107,108] (see Figure 14) | In cases where we want to know whether the biomarker is not only prognostic but also predictive, these designs are preferable as compared to the two previously mentioned biomarker-strategy designs. | (A38) These designs have the ability to inform researchers about the potential superiority of the control treatment in the whole population or among a particular biomarker-defined subpopulation. | (L32) Generally require a larger sample size as compared to the marker-stratified designs. |

Also called: Biomarker-strategy design with a randomized control, Modified marker-based strategy design (for predictive biomarkers), Biomarker-strategy design with randomized control, Marker-based design with randomization in the non-marker-based arm, Marker-based strategy design II, Marker-strategy design, Augmented strategy design, Trial design allowing the evaluation of both the treatment and the marker effect | (A39) Able to inform us whether the biomarker is prognostic or predictive. | (L33) Same as (L27) | |

Examples of actual trials: None identified ^{a} | (A40) Allow clarification of whether the results which indicate efficacy of the biomarker-directed approach to treatment are caused due to a true effect of the biomarker status or to an improved treatment irrespective of the biomarker status. | ||

(A41) Same as (A36) | |||

Reverse marker-based strategy (4 papers) [86,92,93,109] (see Figure 15) | Enables testing the interaction hypothesis of treatment and biomarker in a more efficient way as compared to the first (i.e., Biomarker-strategy design with biomarker assessment in the control arm) and third biomarker-strategy subtype design (i.e., Biomarker-strategy design with randomization in the control arm and the marker stratified design) | (A42) Can estimate directly the marker-strategy response rate. | (L34) It has been claimed by Baker, 2014 [93] that other designs than the reverse marker-based strategy are more appropriate in order to investigate questions which include both treatment effect of biomarker-defined subgroups and the biomarker strategy treatment effect. These designs should allow the estimation of treatment effects within biomarker-defined subgroups as well as the estimation of the global treatment effect. |

Also called: None found | (A43) Allows the estimation of the effect size of the experimental treatment compared to the control treatment for each biomarker-defined subset separately. | ||

Examples of actual trials: None identified ^{a} | (A44) There is no chance that the same treatment will be tailored to biomarker-positive patients who are randomized either to the biomarker-based strategy arm or the reverse marker strategy. Also, there is no possibility of the same treatment assignment to biomarker-negative patients who are randomly assigned to the two biomarker-based strategy arms. | ||

(A45) It has been demonstrated by Eng, 2014 [92] that this new type of design is more than four times more efficient for testing the interaction between treatment and biomarker compared to Biomarker-strategy design with biomarker assessment in the control arm, Biomarker-strategy design with randomization in the control arm and the marker stratified design. | |||

A specific randomized phase II trial design that can be used to guide decision making for further development of an experimental therapy. (1 paper) [71] (see Figure 16) | Recommended when we want to conduct a Phase II randomized trial which allows decisions to be made about which type of Phase III biomarker-guided trial should be used. | (A46) Works well in providing recommendations for phase III trial design. | None found |

^{a}Although not found within the review, the design may be implemented in ongoing trials.

Types of Biomarker-Guided Non-Adaptive Trial Designs | Sample Size Formula | Definition |
---|---|---|

Single arm designs | Standard sample size formula can be used, more information can be found in the ‘methodology’ part of the ‘Single arm designs’ section in the main text. | |

Enrichment designs [55,61,65,110,111,112] | Online tool for sample size calculation when using either binary or time-to-event endpoints is available on the following website: http://brb.nci.nih.gov/brb/samplesize/td.html [113]. | |

$E\left({D}_{i,enrichment}\right)=\frac{nT{\lambda}_{i}}{2\left({\lambda}_{i}+{\phi}_{i}\right)}\left\{1-\frac{{e}^{-\left({\lambda}_{i}+{\phi}_{i}\right)\tau}}{\left({\lambda}_{i}+{\phi}_{i}\right)T}\left[1-{e}^{-\left({\lambda}_{i}+{\phi}_{i}\right)T}\right]\right\}$ | $E\left({D}_{i,enrichment}\right)$ is referred to the expected number of events per treatment arm (time-to-event outcome), $i$ corresponds to either the experimental or the control treatment group, $1:1$ ratio between the two treatment arms (experimental:control) is assumed, $\lambda $ corresponds to the event hazard rate, $\phi $ is the loss to follow-up rate, $T$ denotes the accrual time, patients enter the trial according to a Poisson process with rate $n$ per year over the accrual period of $T$ years, τ corresponds to the follow-up period. | |

${D}_{enrichment}=4{\left[\frac{\left({z}_{\alpha /2}+{z}_{\beta}\right)}{{\mathrm{log}\mathsf{\theta}}_{1}}\right]}^{2}$ | ${D}_{enrichment}$ is referred to the required total number of events (time-to-event outcome), $1:1$ ratio between the two treatment arms (experimental:control) is assumed, ${z}_{\alpha /2},\text{}{z}_{\beta}$ denote the upper $\alpha /2$- and upper $\beta $-points respectively of a standard normal distribution, $\alpha $ and $\beta $ denote the assumed type I error and type II error respectively, ${\mathsf{\theta}}_{1}$ denotes the assumed hazard ratio between the two treatment groups (control vs experimental) in the biomarker-positive subset. | |

${N}_{enrichment/arm}=2{\overline{p}}_{Q}\left(1-{\overline{p}}_{Q}\right){\left[\frac{\left({z}_{\alpha /2}+{z}_{\beta}\right)}{\left({p}_{A}^{Q}-{p}_{B}\right)}\right]}^{2}$ | ${N}_{enrichment/arm}$ is referred to the required number of patients per treatment arm (binary outcome), $1:1$ ratio between the two treatment arms (experimental:control) is assumed, ${p}_{A}^{Q}$ and ${p}_{B}$ are the response probabilities in the experimental and control groups respectively, ${\overline{p}}_{Q}=\left({p}_{A}^{Q}+{p}_{B}\right)/2$. | |

${N}_{enrichment/arm}=\frac{2{\sigma}^{2}{\left({z}_{\alpha /2}+{z}_{\beta}\right)}^{2}}{{\left({\mu}_{A+}-{\mu}_{B+}\right)}^{2}}$ | ${N}_{enrichment/arm}$ is referred to the required total number of patients per treatment arm (continuous response endpoints), $1:1$ ratio between the two treatment arms (experimental:control) is assumed, ${\sigma}^{2}$ denotes the anticipated common variance, ${\mu}_{A+}$ and ${\mu}_{B+}$ the mean responses for biomarker-positive patients in the experimental and control treatment arm respectively. | |

${N}_{enrichment/arm}=2{\sigma}^{2}{\left({z}_{\alpha /2}+{z}_{\beta}\right)}^{2}{\left\{{\lambda}_{1}\left[\left(1-\omega \right)\text{}\zeta +\omega \right]\right\}}^{-2}$ | ${N}_{enrichment/arm}$ is referred to the required total number of patients per treatment arm (continuous response endpoints when accounting for error in the assaying of the study population), $1:1$ ratio between the two treatment arms (experimental:control) is assumed, $\omega $ measures the accuracy of the assay and corresponds to the PPV (positive predictive value of the assay, i.e., the proportion of patients who are assigned biomarker positive status according to the assay who are truly biomarker positive), ${\lambda}_{1}$ is the treatment effect in the biomarker-positive patients and $\zeta ={\lambda}_{0}/{\lambda}_{1}$ (where ${\lambda}_{0}$ is the treatment effect in the biomarker-negative patients). | |

Marker Stratified designs [31,53,60,92,111,112,114] | Online tool for sample size calculation when using either binary or time-to-event endpoints is available on the following website: http://brb.nci.nih.gov/brb/samplesize/sdpap.html [115]. | |

${D}_{stratified}=4\frac{{\left({z}_{{a}_{1}}+{z}_{\beta}\right)}^{2}}{{\left[\mathrm{log}\left({\theta}_{1}\right)\right]}^{2}}+4\frac{{\left({z}_{{a}_{2}}+{z}_{\beta}\right)}^{2}}{{\left[\mathrm{log}\left({\theta}_{2}\right)\right]}^{2}}$ | ${D}_{stratified}$ is referred to the required total number of events for the achievement of sufficient power in each biomarker-defined subgroup separately (time-to-event endpoint), $1:1$ ratio between the two treatment arms (experimental:control) is assumed, ${\theta}_{2}$ corresponds to the hazard ratio of biomarker-negative subgroup, ${a}_{1}={a}_{2}=a/2$. | |

${D}_{stratified}=\frac{4{\left({z}_{a/2}+{z}_{\beta}\right)}^{2}}{{\left[k\mathrm{log}\left({\theta}_{1}\right)+\left(1-k\right)\mathrm{log}\left({\theta}_{2}\right)\right]}^{2}}$ | ${D}_{stratified}$ is referred to the required total number of events for the achievement of sufficient power in the overall population (time-to-event endpoint), $k$ is the proportion biomarker-positive patients, $1:1$ ratio between the two treatment arms (experimental:control) is assumed. | |

${N}_{stratified}=\frac{4{\left({z}_{a/2}+{z}_{\beta}\right)}^{2}}{{\left\{\left[kP{r}_{(+)}\left(event\right)\mathrm{log}\left({\theta}_{1}\right)+\left(1-k\right)P{r}_{(-)}\left(event\right)\mathrm{log}\left({\theta}_{2}\right)\right]/\sqrt{kP{r}_{(+)}\left(event\right)+\left(1-k\right)P{r}_{(-)}\left(event\right)}\right\}}^{2}}$ | ${N}_{stratified}$ is referred to the required total number of patients for the achievement of sufficient power in the overall population (time-to-event endpoint), $1:1$ ratio between the two treatment arms (experimental:control) is assumed, $P{r}_{(+)}\left(event\right)$, $P{r}_{(-)}\left(event\right)$ are the probabilities of an event in biomarker-positive subset and biomarker-negative subset respectively. | |

$\frac{{D}_{stratified}}{{D}_{enrichment}}=\frac{{\left[\mathrm{log}\left({\theta}_{1}\right)\right]}^{2}}{{\left[k\mathrm{log}\left({\theta}_{1}\right)+\left(1-k\right)\mathrm{log}\left({\theta}_{2}\right)\right]}^{2}}=\frac{1}{{\left[k+\left(1-k\right)\frac{\mathrm{log}\left({\theta}_{2}\right)}{\mathrm{log}\left({\theta}_{1}\right)}\right]}^{2}}$ | $\frac{{D}_{stratified}}{{D}_{enrichment}}$ is referred to the ratio of the required number of events between marker stratified and enrichment design (time-to-event endpoint). | |

$\frac{{N}_{stratified}}{{N}_{enrichment}}\approx \frac{1}{{\left[k+\left(1-k\right)\frac{{\delta}_{-}}{{\delta}_{+}}\right]}^{2}}$ | $\frac{{N}_{stratified}}{{N}_{enrichment}}$ is referred to the ratio of the required number of patients between marker stratified and enrichment design (binary outcome), ${\delta}_{-}$, ${\delta}_{+}$, correspond to the treatment effectiveness in biomarker-negative and biomarker-positive subgroup respectively. | |

${N}_{stratified}=2{\left({z}_{a}+{z}_{1-\beta}\right)}^{2}\left\{\frac{{r}_{A+}\left(1-{r}_{A+}\right)+{r}_{B+}\left(1-{r}_{B+}\right)}{{\left({\beta}_{A}+{\beta}_{I}\right)}^{2}}+\frac{{r}_{A-}\left(1-{r}_{A-}\right)+{r}_{B-}\left(1-{r}_{B-}\right)}{{\left({\beta}_{A}\right)}^{2}}\right\}$ | ${N}_{stratified}$ is referred to the required total number of patients (binary outcome), ${\beta}_{0}$ denotes a baseline effect, ${\beta}_{A}$ denotes the added effect of the experimental treatment, ${\beta}_{+}$ denotes the biomarker-positive effect and ${\beta}_{I}$ denotes the nonadditive effect, $\alpha $ corresponds to the target level, $1-\beta $ corresponds to the power, ${r}_{A+},\text{}{r}_{B+}$ are the assumed response rates of biomarker-positive patients receiving the experimental and the control treatment respectively, ${r}_{A-},\text{}{r}_{B-}$ are the assumed response rates of biomarker-negative patients receiving the experimental and the control treatment respectively. | |

Sequential Subgroup-Specific design [57] | ${N}_{sequential\text{}subgroup-specific}^{+}={N}_{enrichment}$ | ${N}_{sequential\text{}subgroup-specific}^{+}$ is referred to the required number of biomarker-positive patients (binary outcome), ${N}_{enrichment}$ is the required number of biomarker-positive patients (binary outcome) in the enrichment design. |

${N}_{sequential\text{}subgroup-specific}=\frac{{N}_{enrichment}}{k}$ | ${N}_{sequential\text{}subgroup-specific}$ is referred to the required total number of patients (binary outcome), ${N}_{enrichment}$ is the required number of biomarker-positive patients (binary outcome) in the enrichment design. | |

${N}_{sequential\text{}subgroup-specific}^{-}=\frac{\left(1-k\right){N}_{enrichment}}{k}$ | ${N}_{sequential\text{}subgroup-specific}^{-}$ is referred to the required number of biomarker-negative patients (binary outcome), ${N}_{enrichment}$ is the required number of biomarker-positive patients (binary outcome) in the enrichment design. | |

${D}_{sequential\text{}subgroup-specific}^{+}={D}_{enrichment}$ | ${D}_{sequential\text{}subgroup-specific}^{+}$ is referred to the required number of events for biomarker-positive patients (time-to-event outcome), ${D}_{enrichment}$ is the required number of events for biomarker-positive patients (time-to-event outcome). | |

${D}_{sequential\text{}subgroup-specific}^{-}={D}_{enrichment}\left(\frac{{\lambda}_{-}}{{\lambda}_{+}}\right)\left(\frac{1-k}{k}\right)$ | ${D}_{sequential\text{}subgroup-specific}^{-}$ is referred to the required number of events for biomarker-negative patients (time-to-event outcome), ${D}_{enrichment}$ is the required number of events for biomarker-positive patients (time-to-event outcome), ${\lambda}_{-}$, ${\lambda}_{+}$, are the event rates in biomarker-negative and biomarker-positive control subgroups. | |

Parallel Subgroup-Specific design | Same formula proposed for marker stratified designs could be considered to achieve sufficient power in each biomarker-defined subgroup simultaneously. However, in order to control the overall type I error rate of the design at the overall level of significance $\alpha $ it is required to allocate this overall $\alpha $ between the test for the biomarker-positive subgroup and the test for the biomarker-negative. Consequently, for biomarker-positive subgroup the reduced significance level ${a}_{1}=a-{a}_{2}$ can be used whereas the reduced significance level ${a}_{2}=a-{a}_{1}$ can be used for biomarker-negative subgroup. | |

Biomarker-positive and overall strategies with parallel assessment | If there is significant confidence that the biomarker is predictive, the sample size estimation is aimed at having a sufficient number of biomarker-positive individuals to enable the treatment effect in the biomarker positive subgroup to be detected. Standard formula for sample size calculation of biomarker-positive subgroup proposed for the enrichment designs could be considered by using the reduced significance level ${a}_{1}=a-{a}_{2}$. On the other hand, if there is no confidence in the predictive value of the biomarker, the sample size estimation is aimed at having a sufficient number of patients to detect a treatment effect in the overall study population; consequently, for the sample size calculation, the same formula proposed for marker stratified designs aiming to achieve sufficient power in the overall population could be applied by using the reduced significance level ${a}_{2}=a-{a}_{1}$. | |

Biomarker-positive and overall strategies with sequential assessment | At the first stage, the standard formula for a traditional randomized trial which is the same with the formula proposed for enrichment designs can be applied for the biomarker-positive subgroup. At the second stage, the sample size formula proposed for marker stratified designs aiming to yield appropriate power for the entire population could be considered. | |

Biomarker-positive and overall strategies with fall-back analysis | At the first stage, the sample size formula proposed for marker stratified designs aiming to yield appropriate power for the entire population could be considered by using the reduced significance level ${a}_{1}=a-{a}_{2}$. At the second stage, the formula proposed for enrichment designs could be applied for the biomarker-positive subgroup by using the reduced significance level ${a}_{2}=a-{a}_{1}$. | |

Marker Sequential test design (MaST) | A standard sample size calculation (i.e., the same sample size calculation as for the enrichment designs) can be applied for the biomarker-positive subpopulation. However, in order to have sufficient number of biomarker-positive patients to detect treatment effectiveness in that particular biomarker-defined subset and consequently to reach the desired power, the sample size should be calculated by using the reduced significance level ${a}_{1}$ $\left[0,a\right]$ instead of the global significance level $\alpha $ which is used in the sample size formulae of the enrichment designs. The same formula could be considered for the sample size calculation of the biomarker-negative subgroup; however, the corresponding hazard ratio of that subgroup and the global significance level $\alpha $ should be used. For the sample size calculation of the entire population, the same formula proposed for marker stratified designs aiming to achieve sufficient power in the overall population could be considered by using the reduced significance level ${a}_{2}=a-{a}_{1}$. | |

Biomarker-strategy, design with biomarker assessment in the control arm [26,61,92] | ${D}_{strategy\text{}I}=4{\left[\frac{\left({z}_{\alpha /2}+{z}_{\beta}\right)}{k{\mathrm{log}\mathsf{\theta}}_{1}}\right]}^{2}$ | ${D}_{strategy\text{}I}$ is referred to the required total number of events (time-to-event outcome), $1:1$ ratio between the two treatment arms (experimental:control) is assumed. |

${N}_{strategy\text{}I}=\frac{2{\left({z}_{1-\alpha /2}+{z}_{1-\beta}\right)}^{2}\left({\tau}_{m}^{2}+{\tau}_{n}^{2}\right)}{{\left({v}_{m}-{v}_{n}\right)}^{2}}$ | ${N}_{strategy\text{}I}$ is referred to the required total sample size (continuous clinical endpoints), $1:1$ ratio between the two treatment arms (experimental:control) is assumed, ${z}_{1-\alpha /2}$, ${z}_{1-\beta}$ denote the lower $1-\alpha /2$- and lower $1-\beta $-points respectively of a standard normal distribution, ${v}_{m}$ and ${v}_{n}$ denote the mean response from the biomarker-based strategy arm and the non-biomarker-based strategy arm respectively, and ${\tau}_{m}^{2},\text{}{\tau}_{n}^{2}$ denote the variance of response for the biomarker-based strategy arm and non-biomarker-based strategy arm respectively. | |

${N}_{strategy\text{}I/arm}=\frac{{\left({z}_{a}+{z}_{1-\beta}\right)}^{2}\left[{g}_{1}\left(1-{g}_{1}\right)+{g}_{2}\left(1-{g}_{2}\right)\right]}{{\Delta}_{2}^{2}}$ | ${N}_{strategy\text{}I/arm}$ is referred to the required total number of patients per arm (binary outcome), ${g}_{1}$ is the expected response rate in the biomarker-based strategy arm, ${g}_{2}$ is the expected response rate in the non biomarker-based strategy arm, ${\Delta}_{2}={g}_{1}-{g}_{2}$, ${g}_{1},{g}_{2}\text{}$can be found by calculating the formulae $k{r}_{A+}+\left(1-k\right){r}_{B-}$ and ${r}_{B}$ respectively, ${r}_{B}$ denotes the marginal effect of treatment B (control treatment). | |

Biomarker-strategy design without biomarker assessment in the control arm | Same formulae as for the ‘Biomarker-strategy design with biomarker assessment in the control arm’ can be considered. | |

Biomarker-strategy design with treatment randomization in the control arm [26,31,92] | ${D}_{strategy\text{}III}=\frac{4{\left({z}_{a/2}+{z}_{\beta}\right)}^{2}}{{\left\{\mathrm{log}\left[\frac{2k{m}_{B+}+2\left(1-k\right){m}_{A-}}{k\left({m}_{A+}+{m}_{B+}\right)+\left(1-k\right)\left({m}_{A-}+{m}_{B-}\right)}\right]\right\}}^{2}}$ | ${D}_{strategy\text{}III}$ is referred to the required total number of events (time-to-event outcome), $1:1$ ratio between the two treatment arms (experimental:control) is assumed, ${m}_{A+},{m}_{A-},\text{}{m}_{B+},{m}_{B-}$, denote the median survival for biomarker-positive and biomarker-negative patients receiving control and experimental treatments respectively. |

${N}_{strategy\text{}III}=\frac{2{\left({z}_{1-\alpha /2}+{z}_{1-\beta}\right)}^{2}\left({\tau}_{m}^{2}+{\tau}_{nr}^{2}\right)}{{\left({v}_{m}-{v}_{nr}\right)}^{2}}$ | ${N}_{strategy\text{}III}$ is referred to the required total sample size (continuous clinical endpoints), $1:1$ ratio between the two treatment arms (experimental:control) is assumed, ${v}_{nr}$ denotes the mean response from the non-biomarker-based strategy arm, ${\tau}_{nr}^{2}$ denotes the variance of response for the non-biomarker-based strategy arm respectively. | |

${N}_{strategy\text{}III/arm}=\frac{{\left({z}_{a}+{z}_{1-\beta}\right)}^{2}\left[{g}_{1}\left(1-{g}_{1}\right)+{g}_{3}\left(1-{g}_{3}\right)\right]}{{\Delta}_{3}^{2}}$ | ${N}_{strategy\text{}III/arm}$ is referred to the required total number of patients per arm (binary outcome), ${g}_{3}$ is the expected response rate in the non biomarker-based strategy arm and ${\Delta}_{3}={g}_{1}-{g}_{3}$, the expected response rate ${g}_{3}$ can be found by calculating the formula ${r}_{A}/2+{r}_{B}/2$, ${r}_{A}$ denotes the marginal effect of treatment A (experimental treatment). | |

Reverse marker-based strategy [92] | ${N}_{strategy\text{}IV/arm}=\frac{{\left({z}_{a}+{z}_{1-\beta}\right)}^{2}\left[{g}_{1}\left(1-{g}_{1}\right)+{g}_{4}\left(1-{g}_{4}\right)\right]}{{\Delta}_{4}^{2}}$ | ${N}_{strategy\text{}IV/arm}$ is referred to the required total number of patients per arm (binary outcome), ${g}_{4}$ is the expected response rate in the reverse biomarker-based strategy arm and ${\Delta}_{4}={g}_{1}-{g}_{4}$, the expected response rate ${g}_{4}$ can be found by calculating the formula $k{r}_{B+}+\left(1-k\right){r}_{A-}$, ${r}_{B+},\text{}{r}_{A-}$ are the assumed response rates of biomarker-positive patients receiving the control treatment and biomarker-negative patients receiving the experimental treatment. |

Randomized Phase II trial design with biomarkers [71] | Online tool for sample size calculation is available on the following website: http://brb.nci.nih.gov/Data/FreidlinB/RP2BM [116]. |

© 2017 by the authors. Licensee MDPI, Basel, Switzerland. This article is an open access article distributed under the terms and conditions of the Creative Commons Attribution (CC BY) license ( http://creativecommons.org/licenses/by/4.0/).

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**MDPI and ACS Style**

Antoniou, M.; Kolamunnage-Dona, R.; Jorgensen, A.L.
Biomarker-Guided Non-Adaptive Trial Designs in Phase II and Phase III: A Methodological Review. *J. Pers. Med.* **2017**, *7*, 1.
https://doi.org/10.3390/jpm7010001

**AMA Style**

Antoniou M, Kolamunnage-Dona R, Jorgensen AL.
Biomarker-Guided Non-Adaptive Trial Designs in Phase II and Phase III: A Methodological Review. *Journal of Personalized Medicine*. 2017; 7(1):1.
https://doi.org/10.3390/jpm7010001

**Chicago/Turabian Style**

Antoniou, Miranta, Ruwanthi Kolamunnage-Dona, and Andrea L. Jorgensen.
2017. "Biomarker-Guided Non-Adaptive Trial Designs in Phase II and Phase III: A Methodological Review" *Journal of Personalized Medicine* 7, no. 1: 1.
https://doi.org/10.3390/jpm7010001