Comparing Dose Levels to Placebo using a Continuous Outcome in a Small n, Sequential, Multiple Assignment, Randomized trial (snSMART)

ABSTRACT Identifying optimal treatments for patients living with rare diseases is challenging due to the small numbers of individuals affected. One design used to address this challenge is known as the small n, sequential, multiple assignment, randomized trial (snSMART). To investigate the efficacy of an active drug measured by a continuous outcome tested at a low and high dose compared to placebo, we propose a new two-stage snSMART design. In stage 1, patients are randomized to an initial treatment. In stage 2, patients are re-randomized, depending on their stage 1 outcome, to either the same or a different dose of treatment. Data from both stages are used to determine the marginal efficacy of the dose levels of active treatment. We propose a Bayesian approach for borrowing information across stage 1 and stage 2 data. We compare the proposed approach to standard methods using only stage 1 data. We observe that the joint stage Bayesian method has smaller root-mean-square-error and 95% Bayesian credible interval widths than standard methods in several tested settings. We conclude that our approach using data from both stages is advantageous for efficacy inference and the proposed snSMART design is useful for the design of registration trials in rare diseases.


Introduction
In the United States, there are approximately 7000 rare diseases, each of which is defined as rare because it has an incidence of fewer than 200,000 people (107th Congress 2002). Although each rare disease may occur only in a small number of people, collectively rare diseases are experienced by over 30 million people in the United States (Griggs et al. 2009). Unfortunately, treatments approved by the US Food and Drug Administration (FDA) exist for only 4% of rare diseases, while the vast majority of rare diseases exist with few treatment options available to patients (FDA 2015).
The dearth of available treatments suggests that more clinical studies of rare diseases are needed (FDA 2015). Although natural history and registry studies are important and can provide critical information guiding treatment development, randomized clinical trials (RCTs) are generally regarded as providing the strongest scientific evidence for treatment efficacy (Grimes and Schulz 2002). However, rare disease trials are more likely than non-rare disease trials to be single arm (63.0% vs. 29.6%) and non-randomized (64.5% vs. 36.1%), and studies of rare diseases often have reduced power relative to studies of non-rare diseases (Bell and Smith 2014). This differential occurs for a variety of reasons, including the lack of sufficient numbers of individuals required for a RCT, as well as participant reluctance to be part of RCTs, especially those with a placebo arm. It is therefore critical to develop novel clinical trial designs and analyses that can maximize information from these small trials.
There have been multiple calls for innovative trial design and efficient analysis to study effective treatments in small samples (Gupta et al. 2011), and several approaches toward this goal exist. Randomized discontinuation trials have been proposed in oncology as an alternative to Phase II study designs (Rosner, Stadler, and Ratain 2002), in which patients are all treated with an investigational drug for a period of time, then randomly assigned to receive either the same treatment or placebo (Amery and Dony 1975). These designs have been modified recently to incorporate a sequential, multiple assignment, randomized trial (SMART) design to gather information about individualized sequences of clinical decisions (Almirall et al. 2012). Makubate and Senn (2010) promoted the use of crossover trials studying infertility treatments, viewing crossover trials essentially as parallel group trials that generated extra information, and they implemented flexible analysis approaches. Nason and Follmann (2010) proposed a combination of a crossover design and a parallel group design in the context of absorbing binary endpoints such as death or HIV infection, while Honkanen et al. (2001) advocated a three-stage trial design consisting of an initial randomized placebo-controlled stage, a randomized withdrawal stage for participants who achieved a clinical response, and a third randomized stage for participants who were assigned to placebo, did not achieve a clinical response, and subsequently responded to treatment.
A more recent study design is the small n, sequential, multiple assignment, randomized trial (snSMART) (Tamura et al. 2016). As a variant of a SMART design (Murphy 2005) that relies upon larger sample sizes, asymptotic results and interest in tailored sequences of treatments, an snSMART design is instead intended for small samples to estimate first stage treatment effects. An snSMART design is applicable for diseases for which patients' response to a given treatment remains stable over time. Furthermore, an snSMART design may improve recruitment of participants because the same treatment is continued for participants who respond, while participants who do not respond to their assigned treatment are able to remain in the study and receive an alternative treatment. This design characteristic may be more favorable for participants than a crossover design that requires all patients, regardless of response status, to switch treatment.
An snSMART design has been previously proposed to compare the efficacy of three unique, potentially active treatments for a rare disease (Tamura et al. 2016;Wei et al. 2018), and we later extended it to studies in which one of the arms was placebo rather than an active agent (Fang et al. 2021). In these approaches, efficiency gains were demonstrated over a single-stage design in which each participant is randomized only once to a treatment, while also maintaining very little bias for the treatment effect estimates. However, these methods assumed that patient outcomes were binary, while registration trials of new drugs often collect a continuous measure of response, which can provide more statistical power than the dichotomized binary outcomes (Donner and Eliasziw 1994;Bhandari, Lochner, and Tornetta 2002). Thus, in this manuscript, we present an snSMART design that incorporates comparison of two dose levels of a drug to placebo when the primary outcome is continuous. The methods required for analysis of an snSMART with continuous outcomes are not simple extensions of the methods developed to analyze an snSMART with binary outcomes. Instead, the new design incorporates new features that require the development of different models and prior distribution considerations.
Our design and methods are motivated by examples in lymphangioleiomyomatosis (LAM), which is a progressive, cystic, rare lung disease in women. Although no curative treatment exists, sirolimus at 2 mg/day has been shown to be effective in preventing loss of forced expiratory volume (FEV 1 ) in women who have already demonstrated a loss of FEV 1 (McCormack et al. 2011). Currently, a placebo controlled trial of sirolimus at a lower dose of 1 mg/day is being conducted in women with early stage LAM and normal FEV 1 (MILED trial: ClinicalTrials.gov Identifier NCT03150914). The prototype snSMART design proposed in this research would be an excellent candidate design to simultaneously evaluate both a low and high dose for sirolimus or any other investigational drug in early stage LAM.
In Section 2, we conceptualize the snSMART design and develop a Bayesian approach that borrows information across both stages for the primary analysis of comparing the mean outcome of dose levels versus placebo. In Section 3, we conduct simulations to assess the bias and efficiency of our approach in a variety of settings and compare our proposed method to a similar method using only stage 1 data. We present concluding thoughts in Section 4. Figure 1 conceptualizes the proposed snSMART design comparing dose levels to placebo. The specific goal of this design is to estimate the differences in the first stage mean outcome between low dose and placebo and between high dose and placebo. Patients are equally randomized to placebo, low dose or high dose in stage 1 as the initial treatment and then are rerandomized in stage 2 conditional on the stage 1 treatment and a dichotomized response variable collected at the end of stage 1. This response variable can be a dichotomized version of the continuous stage 1 outcome, or a variable that differs altogether from the stage 1 outcome. An important feature of our design is that placebo is only a treatment option in stage 1. By doing so, every patient enrolled in the trial will be treated with a dose level of treatment by the end of stage 2, even when initially assigned to receive placebo in stage 1. This re-randomization scheme is also advantageous for participants receiving low dose in stage 1 because they are equally likely to receive a higher dose of the drug that is effective for them at a lower dose or to remain at the low dose. Receiving low dose in both stages may be advantageous because participants receive two administrations of a dose that could be effective for them, and the additional data helps us collect more information about the efficacy of low dose. Non-responders to high dose in stage 1 receive high dose again in stage 2, while patients who responded to high dose are re-randomized to either continue receiving high dose or receive low dose. This design allows high-dose responders to receive a lower dose later in stage 2 because a lower dose may still be efficacious and less toxic.

Design
Using the setting of LAM as an example, women with normal lung function, defined as greater than or equal 70% predicted FEV 1 , are enrolled and randomized at baseline to either placebo, 1 mg/day, or 2 mg/day of sirolimus. The primary endpoint is defined as change in FEV 1 from baseline, with increasingly negative changes indicating worsening lung function. After one year of follow-up for the primary endpoint, women are randomized to either 1 mg/day or 2 mg/day of sirolimus and are followed for an additional year. With regard to the response variable used to determine second stage treatment randomization, nonresponders are defined as those women whose FEV 1 declined by 10% or more in stage 1 (Taveira- DaSilva et al. 2004;McCormack et al. 2011). Non-responders to 2 mg/day of sirolimus are assigned to continue using the same dose level during stage 2, and all other participants are randomized between 1 mg/day and 2 mg/day.

Model
The trial will enroll a total of N subjects, each of whom will be observed for a continuous outcome at the end of each of two stages. For subject i = 1, . . . , N observed in stage j = 1, 2, we let T ij be the assigned treatment and Y ij denote the observed continuous outcome. A binary indicator (1=yes; 0=no) of response, Z i , is measured at the end of stage 1 and is used for re-randomization as illustrated in Figure 1. In stage 1, we adopt the conditional model where the three treatment arms are denoted by k ∈ {P, L, H}, and I(T i1 = k) is an indicator of patient i being assigned to treatment arm k in stage 1. In stage 2, we adopt the conditional model is an indicator of the patient receiving dose level k in stage 2 for k ∈ L, H. Thus, the conditional mean outcome after stage 2 for a treatment is the mean outcome that would have been observed for that treatment after stage 1, but augmented by a shift parameter α and a proportional individual residual response [Y i1 − μ i1 ] from stage 1. Here, α serves as a parameter that allows for increases or decreases in treatment response in stage 2 relative to stage 1. We refer to β as a linkage parameter because it links an individual's residual in stage 1 to their mean outcome in stage 2.

Prior Distributions of Parameters
We incorporate prior knowledge by first assuming that the placebo mean has a N(μ 0 , η 2 ) prior distribution, where the value of η quantifies how confident we are about the placebo having mean μ 0 . This information would likely be informed by natural history studies, drug registries or expert opinions. For the mean outcomes of participants assigned to low and high dose, we use normal prior distributions with prior means μ 0 + γ 1 and μ 0 + γ 2 , respectively, each with variance η 2 . In practice, one can assume different prior standard deviations for the mean outcomes of all three treatment arms. We also assume σ , the standard deviation of the stage 1 and 2 outcomes, has a Gamma(θ 1 , θ 2 ) prior distribution.
The elicitation of prior distributions from experts' opinions is not always straightforward due to the scarcity of historic information or may not be representative of current data. Thus, for the prior distributions for the mean outcomes, we also consider a mixture prior approach that mixes an informative prior with a non-informative one. Suppose we denote two proper probability densities of a parameter x as f 1 (x) and f 2 (x), then is the density of a mixture distribution that consists of the two component densities with weights w 1 and w 2 , respectively, given that w 1 + w 2 = 1. We assume such a mixture distribution for the prior distribution of each mean parameter of interest.

Computations of Posterior Distributions and Considerations
Based on the conditional joint stage model construction in Section 2.2, the observed outcomes from the two stages jointly follow a bivariate normal distribution as The marginal expected outcome observed at the end of stage 2 is the mean outcome of the treatment received at stage 2 as if it were received in stage 1, but adjusted by the shift parameter α. The marginal variance of samples collected in stage 2 is influenced by the linkage parameter and becomes (β 2 +1)σ 2 . Meanwhile, the linkage parameter induces a withinsubject correlation of β/ (1 + β 2 ) between Y i1 and Y i2 . Having the likelihood constructed based on the model assumption as above, the posterior distribution of all unknown parameters θ = (μ P , μ L , μ H , α, β) given the observed data can then be computed by incorporating the prior distributions as specified in Section 2.3. We draw samples from the posterior distribution generated via Monte Carlo Markov Chain algorithm and we take the posterior means of each parameter as their Bayesian estimators.
Including the shift parameter α in the proposed model adds in flexibility and allows researchers to account for potential resistance to the drug given historic knowledge of the drug. The linkage parameter results in more variability in stage 2 observations, but also helps in efficiency gains in estimating the mean outcomes of low dose and high dose by inducing withinpatient correlation. The estimation of placebo is impacted by stage 2 data and therefore likely to be slightly biased, but our simulations suggest that the contrast between drug levels and placebo remain essentially unbiased and less variable than stage 1 estimators.

Data Generation and Parameter Values
Via simulation, we examine the performance of our approach in three scenarios for a trial that will enroll a total of N participants. For each simulation, we assign N/3 participants equally to receive placebo, low and high doses of the study treatment in stage 1. The observed continuous outcomes collected after stage 1 are randomly drawn from a normal distribution with standard deviation σ = 25 and with means being drawn from the simulation scenarios to be specified later in this section. The response variable Z is set to 1 for any stage 1 outcome greater than or equal to 0 (e.g., No change or increase in FEV 1 from baseline). The participants who receive high dose in stage 1 with Z = 0 remain at the same dose level in stage 1, while the others are re-randomized with equal probabilities to receive low or high dose of the study treatment in stage 2. We set values of α and β for the conditional mean stage 2 outcomes as specified below. Finally, the continuous endpoints at the end of stage 2 are sampled from a normal distribution with the same standard deviation of σ = 25.
In terms of the parameter values for μ P , μ L , and μ H , we consider three scenarios. In Scenario 1, we simulate stage 1 outcomes under a "null" setting in which placebo, low and high doses all have the same mean outcome. We have selected μ P = μ L = μ H = −60, which is motivated by the results presented in McCormack et al. (2011). We then examine the performance of our approach in two alternative settings. In Scenario 2, we have a dose-response pattern among the three arms, with mean stage 1 outcomes increasing with the dose. Specifically, we have selected μ P = −75, μ L = 0, and μ H = 25. In Scenario 3, we examine a setting in which the low and high doses are equally effective, so that μ P = −75 and μ L = μ H = 0. All other parameter values used in these two scenarios are equal to those used in Scenario 1.
As the benchmark simulations, we implemented the three data generating scenarios described above with a total sample size of N = 60, α = 0 and β = 1 that yields a conditional correlation of 0.71 between the primary outcomes in the two stages. We repeated our simulations for these three scenarios by first using smaller sample sizes (N = 30 and N = 15) to assess if smaller numbers of participants could still lead to acceptable operating characteristics. We also conducted a set of simulations in which outcomes are no longer normally distributed by adding a skewed error to each individual mean. The skewed error is built by sampling values from a Gamma distribution with mean 2σ and standard deviation σ that are then shifted by 2σ so that the error terms are centered at 0 with a skewness of 0.28. To address the potential impact of discrepancy between our assumed prior means and true parameter values, we performed additional simulations in which α = −2 and β = 1 and in which α = 0 and β = 0.5. Because our model assumes values for α and β that are constant regardless of treatment received in stage 1, we performed additional simulations in which one of the two parameters, or both parameters, have values that are different across the three treatment arms.

Prior Distributions
In our Bayesian analysis, we examine two different sets of prior distributions. In the first set, we assume μ P ∼ N(−75, 25 2 ), μ L ∼ N(0, 25 2 ), and μ H ∼ N(25, 25 2 ), so that the means in the three prior distributions match the actual values used to simulate data in Scenario 2, that is, the mean responses in Stage 1 increase with dose. We refer to this as our "optimistic" set of priors. We also assume σ ∼ Gamma(25, 1), α ∼ N(0, 2), and β ∼ N(0, 1). In the second set of prior distributions, which we refer to as a mixture set of priors, we mix the "optimistic" prior of each treatment mean parameter with a noninformative prior with equal weights (w 1 = w 2 = 0.5). The noninformative prior for each mean parameter is selected as a normal distribution with a mean of zero and a variance of 1000. This mixture allows for a more flexible shape of the prior distributions and indicates less certainty in the treatment effect. The prior distributions for σ , α, and β remain the same.

Results
All simulations were done using R, version 4.0.3. Each scenario was simulated 2000 times and draws from the posterior distributions of all parameters were generated using Markov Chain Monte Carlo via the R library rjags. The posterior mean is used as a point estimate and we compute the highest posterior density (HPD) regions that include 95% of the posterior draws. Each scenario is summarized by the mean bias, root meansquare error (rMSE), and the coverage rate and width of the 95% credible intervals (CI) of the three stage 1 means, as well as the stage 1 mean differences between placebo and each of low and high doses. As a comparator, we also fit our models based solely on the data from the first stage. Results can be found in Tables 1-4. Simulation codes are available at https://github.com/sqrfang/ snSMART_PLH.
In Table 1, we present the simulation results under Scenarios 1-3 with the optimistic prior setting. Across all three scenarios, the joint stage model outperforms the first stage model with comparably lower rMSE and narrower 95% credible intervals in estimating the mean outcomes of each dose level and their Table 1. Bias, root mean-square error (rMSE), coverage rates (CR) and the width of 95% credible intervals for the posterior mean treatment effects under Scenarios 1-3 (see Section 3.2) with total sample size N = 60, using the optimistic prior setting. differences with placebo. In Scenario 1, μ L and μ H are overestimated in both the joint stage model and the first stage model, affecting the bias of their differences with μ P as well. In Scenario 2, both joint stage estimators and first stage estimators for each dose level have low bias because we used priors that are centered around the true parameter values. As for Scenario 3, the prior mean of μ H is far from the true value, while the prior means of μ P and μ L are correctly specified. We also see that the simulated coverage rates of the joint stage estimators for μ L and μ H are slightly below 95% under Scenario 1. However, the coverage rates for the difference in mean stage 1 outcomes are stable at around 95%, which is important because oftentimes decisions are made on the difference in means. Table 2 consists of the same scenarios as shown in Table 1, but using the mixture prior setting. In Scenario 1, we observe slightly less biased estimates of μ L and μ H as well as their differences between placebo, as compared to the same models in Table 1, and we observe similarly biased estimates of parameters for mean outcomes under Scenarios 2 and 3. The differences in the widths of the 95% HPD regions and rMSEs for the estimates between Tables 1 and 2 are negligible in Scenarios 2 and 3, while estimates in Table 2 have similar width and smaller rMSE because of less bias. Overall, we still see the efficiency gain in the estimates of all mean outcome parameters when using the joint stage estimators, which carries through to the differences between low dose versus placebo, and high dose versus placebo. The coverage rates of all parameters under all scenarios are around 95%.
We then repeated the simulations in Scenarios 1-3 using the two prior settings, but with total sample sizes of 30 and 15. The simulation results are presented in Table 3 for N = 30 and  Table 4 for N = 15. In Scenario 1, as the sample size decreases, we observe increases in bias and rMSE for all estimators and slightly lower coverage rates than expected. In Scenarios 2 and 3, the bias using optimistic priors with smaller total sample size is comparable to the bias with N = 60, but estimates from smaller sample size have greater rMSE and width of the 95% Table 2. Bias, root mean-square error (rMSE), coverage rates (CR) and the width of 95% credible intervals for the posterior mean treatment effects under Scenarios 1-3 (see Section 3.2) with total sample size N = 60, using the mixture prior setting.   Results for simulations with skewed outcomes can be found in supplementary Table S1, which demonstrate similar accuracy and efficiency compared to that produced from normally distributed outcomes. Supplementary Tables S2-S3 demonstrate that joint stage model results are impacted by the discrepancy between the true values of α and β and their respective prior distributions. Specifically, in supplementary Table S2, although deviation of α from its prior mean leads to more biased estimators for the mean response of all treatment arms, there is no substantial change in their efficiency. In Supplemental Table  S3, we see that the true value of β impacts the efficiency of our estimates by altering the within-subject correlations in the outcomes, such that there is greater rMSE when correlation is lower. Last, in supplementary Table S4, in which our assumption of constant values for α and β is violated, we see that there is increased bias for the treatment means and slightly lower coverage rates when β actually varies by treatment arm. Bias and efficiency differ from ideal settings when assumptions about α and β are violated, but bias remains low in general and using data from both stages in a joint stage model is more efficient than using data from only the first stage. Thus, our methods are relatively robust to the prior distributions chosen for α and β and using a parsimonious model even if there are treatmentspecific α and β values.

Discussion
In this article, we propose an snSMART design that compares dose levels to placebo when the outcome is continuous and describe how this model can be applied to a trial studying treatment for the rare disease LAM. We propose a Bayesian model to obtain the stage 1 mean outcomes of each dose level and test its performance across various assumptions via simulations. We conclude that the proposed model that incorporates data from both stages provides results with low bias and high efficiency compared to a similar model that uses only first stage data. As opposed to other designs for rare diseases, our design is advantageous in three aspects. First, our design allows for a comparison against placebo, which is necessary to demonstrate efficacy where there is no registered drug or reliable historical information for the chosen endpoint of the trial. A second advantage of the snSMART design is that it investigates more than one dose level of a drug and can examine a dose-response relationship. Sponsors often choose to test the high dose of the investigational drug, which could expose subjects to unnecessary toxicity. Last but not the least, placebo administration is restricted to stage 1. Thus, every participant has the ability to receive treatment. This attractive feature of the design may help participants enrollment in the trial.
The endpoint of interest at the end of stage 1 and 2 in the proposed snSMART design is continuous, but the design requires a binary outcome variable for re-randomization to second stage treatment. In our example and the simulations, we defined the response variable, Z, as the dichotomization of the primary continuous outcome collected at the end of stage 1. In reality, this response variable can actually be any binary outcome that is reasonable to investigators, having either a strong or weak correlation to the primary outcome. Allowing this variable to differentiate from the primary outcome is especially helpful when the measurement of the primary outcome is expensive or time-consuming and could hold up the second stage treatment assignment. The binary response variable is not directly used in our proposed model because it is less informative than the actual continuous outcome observed at the end of stage 1 which would be readily available at the end of the trial for analysis.
In the simulated trials with very small total sample sizes (< 30), we observe greater bias as the prior means deviate farther away from the actual values. We also observe slightly lower coverage rates for the credible intervals for low and high dose. However, well-specified prior distributions can substantially improve the accuracy and efficiency. Investigators should exercise extra caution in the choice of the prior distributions for the means when the total sample size is small (≤ 30).
Under all primary simulation scenarios, we tested two sets of prior distributions, including an optimistic one and one with a mixture prior, both assuming normal priors as the basic elements for all three parameters that represent the mean outcomes for three dose levels. The normal distribution is most intuitive since it is well-known among researchers and the parameters are easily elicited from experts. Morita, Thall, and Müller (2008) demonstrated that the effective sample size for a normal prior distribution is the ratio of the sampling variance to the normal prior variance when sampling variance is known. This helps in determining the values of the hyperparameters used in prior distributions. For the mixture prior distribution, we assumed equal weights for the informative and noninformative element distributions although we could consider unequal weights or even adaptively determining the weights. For example, researchers may consider incorporating ways such as an automatic prior elicitation method (Egidi, Pauli, and Torelli 2021) to choose the weight given the observed data. We also found that the estimates using the mixture priors are robust especially when the prior means misspecify the true mean outcomes. The mixture prior is associated with less bias and better coverage under the null scenario where the treatment groups are equivalent.
When this study design is used in practice, we note a few additional considerations. When describing our design, we assume equal rerandomization in stage 2 for all patients except for the nonresponders to high dose in stage 1. In our proposed design, questions might arise whether it is ethical to allow the low-dose responders to receive a higher dose level in stage 2. While toxicity may be a concern, a higher dose may result in increased efficacy; for patients with severe and fatal rare diseases such as certain types of cancers, the potential improvements in mitigation or curative effects from taking a higher dose level may outweigh the risks of the accompanied potential toxicity. However, in practice, researchers might consider reasonable unequal rerandomization adapting to response measured at the end of stage 1. For example, low dose responders may continue to receive low dose while all low dose nonresponders could be assigned to high dose. When using a dichotomous variable Z to restrict rerandomization for any group, we suggest this Z variable is a quickly accessible response variable measured at the end of stage 1. A washout period can be included in our design, similar to a standard crossover design if a large carryover effect is expected. Our method can allow for a carryover effect by assuming varied α parameters among different stage 1 treatments in the Bayesian model. However, the model and estimation are most appropriate when little to no carryover effect is expected.
Similarly, when analyzing the data from this design, we should note some additional considerations. When building the joint stage Bayesian model, we assume the same conditional variance for the observations from the two stages. In reality, this "equal variance" assumption can be relaxed as long as there is evidence to support other assumptions. In choosing the prior distributions for the parameters, our case simulations mainly focus on how to deal with the misspecification of the mean outcome parameters. In addition, for the shift parameter α, we always assume its mean to be around 0, implying little carryover effect nor stage effect exists. The prior variance of the α reflects our belief in the possible range of treatment effect shiftings in stage 2. Since β has the same sign as the correlation coefficient within a patient's observations, it is very likely to be positive. Having the prior distribution of β centered around 0 is to account for the situation when extremely weak correlation exists between observations across two stages. Moreover, although α and β might vary among different stage 1 treatments, our simulations show that our model was still quite robust to such circumstances (see supplemental tables).
One limitation of our Bayesian model is the potential model misspecification due to little prior information. For example, in Section 3.3, we detect non-negligible bias when using the optimistic priors (implying belief in strong treatment effects) to analyze data generated under Scenario 1 where none of the three treatments were efficacious. As an alternative, we apply the mixture prior setting in which we assume equal weights for the optimistic and noninformative element distributions to analyze the same data. We found that the estimates using the mixture priors have smaller bias and better coverage under Scenario 1 than the estimates using the optimistic priors. Under the other two scenarios, the mixture priors exhibit little bias while sacrificing a small amount of efficiency, as compared to the optimistic priors. Thus, we believe the use of a flexible type of prior distribution can help accommodate the lack or misspecification of prior information. Another limitation of our design is the potential loss to follow-up for some patients due to the longer duration of snSMART. As opposed to the benchmark one-stage parallel arm design, snSMARTs allow patients to receive more than one dose level or treatment throughout their follow-up and collect more observations, all of which require an extended study period. Potential compliance issues are inevitable in such studies. Nevertheless, we believe that restricting placebo to be a treatment option only for stage 1 may potentially improve patients' retention and compliance and thus may offset the loss due to the extension of the follow-up period. As a final limitation, we note the risk of very high or very low observed response rates to stage 1 treatments. For example, the stage 1 response rates are extremely low (less than 5%) for all patients under Scenario 1 where all three treatments have equal low mean outcome. Since the response rate only impacts the re-randomization of those patients who receive high dose in stage 1, only a small number of patients are impacted. Thus, an unequal allocation does not make a great impact to the analysis nor the decision making since our major objective in this study is to examine the efficacy of each dose level instead of identifying the best treatment regimen. However, if randomization is more restricted in the second stage (i.e., second stage treatment depends on response for more than those initially assigned to high dose), bias and efficiency may be detrimentally affected.
Our future work includes exploring methods that estimate and compare the mean outcome of the embedded treatment regimens in the proposed two-stage design and constructing a way to calculate the sample size required for this snSMART design with regards to our proposed model.