Blinded and unblinded sample size re-estimation in crossover trials balanced for period
Michael Grayling Adrian Mander James Wason





Blinded and unblinded sample size re-estimation in crossover trials balanced for period
    M. J. Grayling1, A. P. Mander1, J. M. S. Wason1,2

1. Hub for Trials Methodology Research, MRC Biostatistics Unit, Cambridge, UK, 
 2. Institute of Health and Society, Newcastle University, Newcastle, UK.
    
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Corresponding Author: M. J. Grayling, MRC Biostatistics Unit, Forvie Site, Robinson Way, Cambridge CB2 0SR, UK; Tel: +44-(0)1223-330300; E-mail: mjg211@cam.ac.uk.


Abstract: The determination of the sample size required by a crossover trial typically depends on the specification of one or more variance components. Uncertainty about the value of these parameters at the design stage means that there is often a risk a trial may be under- or over-powered. For many study designs, this problem has been addressed by considering adaptive design methodology that allows for the re-estimation of the required sample size during a trial. Here, we propose and compare several approaches for this in multi-treatment crossover trials. Specifically, regulators favour re-estimation procedures to maintain the blinding of the treatment allocations. We therefore develop blinded estimators for the within and between person variances, following simple or block randomisation. We demonstrate that, provided an equal number of patients are allocated to sequences that are balanced for period, the proposed estimators following block randomisation are unbiased. We further provide a formula for the bias of the estimators following simple randomisation. The performance of these procedures, along with that of an unblinded approach, is then examined utilising three motivating examples, including one based on a recently completed four-treatment four-period crossover trial. Simulation results show that the performance of the proposed blinded procedures is in many cases similar to that of the unblinded approach, and thus they are an attractive alternative.



Keywords: Blinded; Crossover trial; Internal pilot study; Sample size re-estimation.





§ INTRODUCTION


Crossover trials, in which participants are randomly allocated to receive a sequence of treatments across a series of time periods, are an extremely useful tool in clinical research. Their nature permits each patient to act as their own control, exploiting the fact that in most instances the variability of measurements on different subjects in a study will be far greater than that on the same subject. In this way, crossover trials are often more efficient than parallel group trials. Like most experimental designs, the determination of the sample size required by a crossover trial, to achieve a certain power for a particular treatment effect, depends on the significance level, and at least one factor which accounts for the participant's variance in response to treatment. Whilst the former are designated quantities, the variance factors will usually be subject to substantial uncertainty at the design stage. Their value will often be greatly affected by components of the current trial, such as inclusion/exclusion criteria for example, that renders estimates obtained from previous trials biased. This is troubling since sample size calculation is of paramount importance in study design. Planning a trial that is too large results in an unnecessary number of patients being made susceptible to interventions that may be harmful. It also needlessly wastes valuable resources in terms of time, money, and available trial participants. In contrast, too small a sample size confers little chance of success for a trial. The consequences of this could be far reaching: a wrong decision may lead to the halting of the development of a therapy, which could deprive future patients of a valuable treatment option.

To address this problem in a parallel group setting with normally distributed outcome variables, <cit.>, building upon previous work by <cit.>, proposed the internal pilot study design. In their approach, at an interim time period the accrued data is unblinded, the within-group variance computed, and the trial's required sample size adjusted if necessary. However, unblinding an ongoing trial can reduce its integrity and introduce bias <cit.>. Consequently, <cit.> explored several approaches for re-estimating the required sample size in a blinded manner. Since then, a number of papers have advocated for re-estimation in a parallel group setting to be based upon a crude one-sample estimate of the variance, and methodology has also been proposed which allows the type-I error-rate to be more accurately controlled <cit.>. More recently, much work has been conducted on similar methods for an array of possible trial designs and types of outcome variable (see, e.g., <cit.> and <cit.>), with these methods also gaining regulatory acceptance <cit.>.

Thus, today, sample size re-estimation procedures have established themselves for parallel group trials as an advantageous method to employ when there is pre-trial uncertainty over the appropriate sample size. In contrast, there has been little exploration of such methodology within the context of multi-treatment crossover trials. <cit.> recently explored a blinded sample size re-estimation procedure for establishing bioequivalence in a trial utilising an AB/BA crossover design. <cit.> discussed how the results of <cit.> could be rephrased for an AB/BA crossover trial testing for superiority. In addition, several unblinded re-estimation procedures for AB/BA bioequivalence trials have been proposed <cit.>, the performance of which has recently been extensively compared <cit.>. The work of <cit.> and <cit.> on sample size re-estimation in cluster randomised trials has some parallels with the methodology required for crossover trials, because of the necessitated mixed model for data analysis. Likewise, this is true of the methodology presented by <cit.> on re-estimation procedures for longitudinal trials. However, we are unaware of any article that explicitly discusses re-estimation in crossover trials with more than two-treatments. There are many examples of such trials in the literature, whilst they also remain the focus of much research (see, e.g., <cit.> and, <cit.>).

In this article, we consider several possible approaches to the interim re-assessment of the sample size required by a multi-treatment crossover trial. We assume a normally distributed outcome variable, and that a commonly utilised linear mixed model will be employed for data analysis. We focus primarily on a setting in which the final analysis is based on many-to-one comparisons for one-sided null hypotheses, but provide additional guidance for other possibilities in the Appendix. Blinded procedures for estimating the between and within person variance in response are proposed, following either simple or block randomisation to sequences that are balanced for period. The performance of these estimators is contrasted to that of an unblinded procedure via a simulation study motivated by a real four-treatment four-period crossover trial. Additionally, in the Appendix we provide results for two additional examples. We now proceed by specifying the notation used in the re-estimation procedures. Our findings are then summarised in Section 3, before we conclude in Section 4 with a discussion.



§ METHODS




 §.§ Hypotheses, notation, and analysis


We consider a crossover trial with D treatments, indexed d=0,…,D-1. Treatments d=1,...,D-1 are considered experimental, and are to be compared to the common control d=0. We suppose that K sequences, indexed k=1,…,K, are utilised for treatment allocation, and denote by n_k the number of patients allocated to sequence k. The number of periods in the trial, which is equal to the length of each of the sequences, is denoted by P.

We restrict our focus to trials with normally distributed outcome data, to be analysed using the following linear mixed model

    y_ijk = μ_0 + π_j + τ_d(j,k) + s_ik + ϵ_ijk,     i=1,…,n_k, j=1,…,P, k=1,…,K.

Here

	
  * y_ijk is the response for individual i, in period j, on sequence k;
	
  * μ_0 is an intercept term; the mean response on treatment 0 in period 1;
	
  * π_j is a fixed effect for period j, with the identifiability constraint π_1=0;
	
  * τ_d(j,k) is a fixed direct treatment effect for the treatment administered to an individual in period j, on sequence k, with the identifiability constraint τ_0=0. Thus d(j,k)=0,…,D-1;
	
  * s_ik∼ N(0,σ_b^2) is a random effect for individual i on sequence k;
	
  * ϵ_ijk∼ N(0,σ_e^2) is the residual for the response from individual i, in period j, on sequence k.

This model, and its implied covariance structure, is the standard for a crossover trial that ignores the possible effects of carryover. Thus we are implicitly heeding the advice of <cit.>, and others, that a crossover trial should not be conducted when carryover is likely to be an issue. Furthermore, note that by the above, two observations y_i_1j_1k_1 and y_i_2j_2k_2 are independent unless i_1=i_2 and k_1=k_2.

We assume that the following hypotheses are to be tested, to attempt to establish the superiority of each experimental intervention versus the control

    H_0d : τ_d ≤ 0,      H_1d : τ_d > 0,      d=1,…,D-1.

Note though that for Examples 1 and 3, slightly different hypotheses are assessed, as negative effects imply efficacy. Additionally, in the Appendix we detail how one can handle alternate hypotheses of interest.

We suppose that it is desired to strongly control the FWER, the maximal probability of one or more incorrect rejections amongst the family of null hypotheses for all possible treatment effects, to some specified level α∈(0,1). There are several possible ways to define power in a multi-treatment setting. Throughout, we assume that pairwise power of at least 1-β∈(0,1) to reject, without loss of generality, H_01 is required when τ_1=δ>0 for designated type-II error-rate β and clinically relevant difference δ. Thus, from here, when referring to power we mean the probability that H_01 is rejected. However, in the Appendix we describe how a desired familywise power could be achieved.

To test the hypotheses, we assume that N patients in total will be recruited to the trial, with each randomised to one of the K sequences, and that the the linear mixed model (<ref>) will be fitted to the accumulated data. Note that in fitting this model, a choice must be made over whether to utilise maximum likelihood, or restricted error maximum likelihood (REML), estimation. Given the bias of the maximum likelihood estimator of the variance components of a linear mixed model in finite samples, and that crossover trials are often conducted with relatively small sample sizes, here we always take the latter approach. Note though that this would have little effect for larger sample sizes. For further details on these considerations, we refer the reader to, for example, <cit.>. In brief, the REML estimation procedure, for a linear mixed model of the form y=Xβ+Zb+ϵ with b∼ N(0,G) and ϵ∼ N(0,R), iteratively optimizes the parameter estimates for the effects in the model. The following modified log-likelihood is maximised to provide an estimate, Σ̂, for Σ=ZGZ^⊤+R, using an estimate, β̂, for β
	
    -1/2log|Σ|-1/2(y-Xβ̂)^⊤Σ^-1(y-Xβ̂)-1/2log|X^⊤Σ^-1X|.

	Then, β̂ is updated to
	
    β̂ = (X^⊤Σ̂^-1X)^-1X^⊤Σ̂^-1y,

	and the process repeated. Given the final solutions β̂ and Σ̂, we take Var(β̂)=(X^⊤Σ̂^-1X)^-1.
	
	In our case, β=(μ_0,π_2,…,π_P,τ_1,…,τ_D-1)^⊤, and the following D-1 Wald test statistics are formed
	
    T_d = τ̂_d/√(Var(τ̂_d)),      d=1,…,D-1,

	where τ̂_d and Var(τ̂_d) are extracted from β̂ and Var(β̂) respectively.
	
	Next, we reject H_0d if T_d>e, with e chosen to control the FWER. Explicitly, using a Dunnett test <cit.>, we take e as the solution to
	
    1 - α = Ψ_D-1{(e,…,e)^T,Var(T),ν_N},

	where Ψ_M{x,Λ,ν} is the M-dimensional cumulative distribution function of a central multivariate t-distribution with covariance matrix Λ and ν degrees of freedom. We take the degrees of freedom here, for sample size N, to be ν_N=(N-1)(P-1)-(D-1), which arises from that associated with an analogous multi-level ANOVA design. Moreover, Var(T) is the covariance matrix of T=(T_1,…,T_D-1)^⊤, which can be calculated using Var(β̂).
	
	Now, in this case, if σ_e^2 and σ_b^2 were known, and we assumed that n_1=…=n_K, we could derive a simple formula for the total number of patients, N, required to achieve the desired power for the trial. Here, we denote this formula using the function N(σ_e^2,σ_b^2), explicitly stating it's dependence upon the within and between person variances. In the Appendix, we elaborate on how this formula can be derived.
	
	Our problem, as discussed, is that in practice σ_e^2 and σ_b^2 are rarely known accurately at the design stage. Therefore, we propose to re-estimate the required sample size at an interim analysis timed after n_int∈ℕ patients. That is, we consider several methods to construct estimates, σ̂_e^2 and σ̂_b^2, for σ_e^2 and σ_b^2 respectively, based on the data accrued up to the interim analysis. Then, the final sample size for the trial is taken as
	
	
    N̂ = {[                                 n_int          if N(σ̂_e^2,σ̂_b^2) ≤ n_int,;                   ⌈N(σ̂_e^2,σ̂_b^2) ⌉ if  n_int < N(σ̂_e^2,σ̂_b^2) < n_max,;                                 n_max          if N(σ̂_e^2,σ̂_b^2) ≥ n_max, ].


where ⌈ x ⌉ denotes the nearest integer greater than or equal to x and n_max∈ℕ is a specified maximal allowed sample size. It could be based, for example, on the cost restrictions or feasible recruitment rate of a trial. Of course, if N̂ = n_max then the trial will be expected to be under-powered. Thus, if necessary, additional patients are recruited and a final analysis conducted as above based on the calculated values of the test statistics T_d, and the critical value e as defined in Equation (<ref>).

Throughout, to give our function N(·) a simple form, we consider values of n_int that imply an equal number of patients could be allocated to each of the K sequences, and assume randomisation schemes that ensures this is the case. Moreover, for reasons to be elucidated shortly, we consider from here only settings where the K sequences are balanced for period. That is, across the chosen sequences, each treatment appears an equal number of times in each period. We now proceed by detailing each of our explored methods for estimating σ_e^2 and σ_b^2 based on the internal pilot data.



 §.§ Unblinded estimator


The first of the methods we consider is an unblinded procedure. As noted, such an approach is typically less well favoured by regulatory agencies. However, though this may not always actually prove to be the case (see, e.g., <cit.>), one may anticipate its performance in terms of estimating the key variance components and provided desired operating characteristics to be preferable to that of the blinded procedures. This method therefore serves as a standard against which to assess the blinded estimators. Explicitly, this approach breaks the randomisation code and fits the linear mixed model (<ref>) to the accrued data using REML estimation. With the REML estimates of σ_e^2 and σ_b^2 obtained, they are utilised in the re-estimation procedure as described above.



 §.§ Adjusted blinded estimator


<cit.> considered a blinded estimator for two-arm parallel trial designs based on an adjustment to the one-sample variance. <cit.> considered a similar unadjusted procedure for two-arm bioequivalence trials. Here, we consider a similar approach for multi-treatment crossover trials. Specifically, the following blinded estimators of the within and between person variances are used
	
	
    σ̂_e^2    = 1/2(P - 1)(n_int - 1)∑_j=2^P∑_k=1^K∑_i=1^n_int/K(p_ijk - p̅_j)^2 
            -n_int/2K(P-1)(n_int - 1)∑_j=2^P∑_k=1^K(τ_d(j,k)^* - τ_d(j-1,k)^*)^2,
    	
    σ̂_b^2    = 1/2{1/2(P - 1)(n_int - 1)∑_j=2^P∑_k=1^K∑_i=1^n_int/K(q_ijk - q̅_j)^2 - σ̂_e^2 .
               .- n_int/2K(P-1)(n_int - 1)∑_j=2^P∑_k=1^K(τ_d(j,k)^* + τ_d(j-1,k)^*)^2 . 
                   .+ 2n_int/D^2(n_int-1)( ∑_k=1^Kτ_d(1,k))^2},

	for specified τ_d^*, d=0,…,D-1, with τ_0^*=0, where
	
	
    p_ijk   = y_ijk - y_ij-1k,
    
    	q_ijk   = y_ijk + y_ij-1k,
    p̅_j   = 1/n_int∑_k=1^K∑_i=1^n_int/Kp_ijk,
    q̅_j   = 1/n_int∑_k=1^K∑_i=1^n_int/Kq_ijk.

	
	In the Appendix, we show that if τ_d^*=τ_d for d=1,…,D-1 then E(σ̂_e^2) = σ_e^2 and E(σ̂_b^2) = σ_b^2, and thus σ̂_e^2 and σ̂_b^2 are unbiased estimators for σ_e^2 and σ_b^2 respectively. This is the reason for our restrictions on the employed randomisation scheme (which assumes n_1=…=n_K=n_int/K at the interim reassessment), and the employed sequences (which are assumed to be balanced for period). The above estimator could be used when there is imbalance in the number of patients allocated to each sequence, or without making this restriction on the sequences, but results on the expected values of the variance components would have a more complex form. It is therefore advantageous to ensure an equal number of patients are allocated to each sequence, and also logical to utilise period balanced sequences. We also view is as sensible therefore to explore the performance of the estimators in this case.

It is also important to assess the sensitivity of the performance of these estimators to the choice of the τ_d^*, hoping for it to have negligible impact as in analogous procedures for other trial settings <cit.>. Adapting previous works (see, e.g., <cit.>), we assess this procedure for τ_d^*=0, and τ_d^*=δ, d=1,…,D-1, and refer to these henceforth as the null adjusted and alternative adjusted re-estimation procedures respectively. 

Note that one limitation of this approach in practice is that there is no guarantee that the above value for σ̂_b^2 will be positive. Therefore, we actually re-evaluate the required sample size as N{σ̂_e^2,max(0,σ̂_b^2)}. For the examples provided in the Appendix, we demonstrate that the above procedure still performs well despite this inconvenience. Moreover, in certain routinely faced scenarios, as will be discussed shortly, the value of σ_b^2 is inconsequential and this issue therefore no longer exists. However, in general this must be kept in mind when considering using this procedure for sample size re-estimation.



 §.§ Blinded estimator following block randomisation


The above re-estimation procedures are explored within the context of a simple randomisation scheme that only ensures an equal number of patients are allocated to each sequence prior to the interim re-assessment. In contrast, the final blinded estimator we consider exploits the advantages block randomisation can bring, extending the methodology presented in <cit.> for parallel arm trials to crossover studies.

We suppose that patients are allocated to sequences in B blocks, each of length n_B (with these values chosen such that Bn_B = n_int). We recategorise our data as y_ijb, the response from patient i=1,…,n_B, in period j, in block b. Then, the following blinded estimators are used to recalculate the required sample size
	
    σ̂_e^2    = 1/2(P - 1)(n_int - B)∑_j=2^P∑_b=1^B∑_i=1^n_B(p_ijb - p̅_jb)^2,
    σ̂_b^2    = 1/2{1/2(P - 1)(n_int - B)∑_j=2^P∑_b=1^B∑_i=1^n_B(q_ijb - q̅_jb)^2 - σ̂_e^2 },

	where
	
    p_ijb   =y_ijb-y_ij-1b,
    
    	q_ijb   = y_ijb + y_ij-1b,
    p̅_jb   = 1/n_B∑_i=1^n_Bp_ijb,
    q̅_jb   = ∑_i=1^n_B∑_i=1^n_Bq_ijb.

	
	In the Appendix, provided that an equal number of patients are allocated to each of a set of period balanced sequences, these are also shown to be unbiased estimators for σ_e^2 and σ_b^2. Note though that as above, we must actually re-estimate N using N{σ̂_e^2,max(0,σ̂_b^2)}. Additionally, when using block randomisation, the actual sample size used by a trial may differ from N̂, if it is not divisible by the block length n_B.



§ SIMULATION STUDY


	

 §.§ Motivating examples

	
	We present results for three motivating examples based on real crossover trials. Example 1 is described in Section 3.2, with Examples 2 and 3 discussed in the Appendix, where their associated results are also presented. Among the three examples we consider settings with a range of required sample sizes, utilising complete block, incomplete block, and extra-period designs. This allows us to provide a thorough depiction of the performance of the various estimators in a wide range of realistic trial design settings.



 §.§ Example 1: TOMADO


First, we assess the performance of the various re-estimation procedures using the TOMADO trial as motivation. TOMADO compared the clinical effectiveness of a range of mandibular devices for the treatment of obstructive sleep-apnea hypopnea. Precise details can be found in <cit.>. Briefly, TOMADO was a four-treatment four-period crossover trial, with patients allocated treatment sequences using two Williams squares. The data for the outcome Epworth Sleepiness Scale was to be analysed using linear mixed model (<ref>), with the following hypotheses tested

    H_0d : τ_d ≥ 0,      H_1d : τ_d < 0,      d=1,…,D-1,

since a reduction in the Epworth Sleepiness Scale score is indicative of an efficacious treatment. Consequently, the null hypotheses were to be rejected if T_d<-e, using the value of e determined as above.

Following the methodology described in the Appendix, we can demonstrate that when complete-block period-balanced sequences are used for treatment allocation, that the required sample size has no dependence upon the between person variance σ_b^2. Explicitly, we have
	
    N(σ_e^2,σ_b^2)≡N(σ_e^2) = 2σ_e^2(z_1-α_* + z_1-β)^2/δ^2,

	where α_* is defined in the Appendix. See <cit.>, for an alternative derivation of this formula. This substantially simplifies the re-estimation procedure, as we only need to provide a value for σ_e^2, and do not require use of the estimators for σ_b^2.

TOMADOs complete case analysis estimated the following values for the various components of the linear mixed model (1)

    μ̂_0 = 10.65,  π̂_2 = -0.77,  π̂_3 = -0.96,  π̂_4 = -0.55,


    τ̂_1 = -1.51,  τ̂_2 = -2.15,  τ̂_3 = -2.37,  σ̂_e^2 = 6.51, σ̂_b^2 = 10.12.

Therefore, for σ_e^2=σ̂_e^2, the trials planned recruitment of 72 patients would have conferred power of 0.8 at a significance level of 0.05 for δ=-1.24. Consequently, we set β=0.2 and α=0.05 throughout. In the main manuscript, we additionally take δ=-1.24 and σ_b^2=10.12 always. The effect of other underlying values for δ and σ_b^2 is considered in the Appendix. In contrast, whilst we focus here on the case with σ_e^2=6.51, we also consider the influence of alternative values for this parameter. When simulating data we take μ_0 = 10.65, π_2 = -0.77, π_3 = -0.96, and π_4 = -0.55. However, the effect of other period effects is discussed in Section <ref> and in the Appendix.

We explore the performance of the procedures under the global null hypothesis (τ_1=τ_2=τ_3=0), when only treatment one is effective (τ_1=δ,τ_2=τ_3=0), when treatments one and two are effective (τ_1=τ_2=δ,τ_3=0), under the global alternative hypothesis (τ_1=τ_2=τ_3=δ), and under what we refer to henceforth as the observed treatment effects (τ_1=-1.51, τ_2=-2.15, τ_3=-2.37). For simplicity, we assume a single Latin square was used for treatment allocation, and set n_max=1000 so that there is no practical upper limit on the allowed sample size. In all cases, the average result for a particular design and analysis scenario was determined using 100,000 trial simulations.



 §.§ Distributions of σ̂_e^2 and N̂


First, the performance of the re-estimation procedures was explored for the parameters listed in Section <ref>, with σ_e^2=6.51, and n_int∈{8, 16, 24, 32, 40}. The resulting distributions of σ̂_e^2, the interim estimate of σ_e^2, are shown in Figure 1 via the median, lower and upper quartiles in each instance. Additionally, Figure 2 depicts the equivalent results for the distribution of N̂, the interim re-estimated value for N. The results are grouped according to the timing of the re-estimation and by the true value of the treatment effects. Note that n_B=4 is only considered for values of n_int which allows an equal number of patients to be allocated to each sequence by the interim analysis.

The median value of σ̂_e^2 for the unblinded procedure is always close to, but typically slightly less than, the true value σ_e^2. The same statement holds for the block randomisation procedure with n_B=2 or 4. However, whilst this is true for the adjusted procedures under the global null hypothesis, it is not otherwise always the case. In particular, both perform poorly for the observed treatment effects.
	
	As would be anticipated, the alternative adjusted procedure has lower median values for σ̂_e^2 than the null adjusted procedure. Moreover, using the block randomised re-estimation procedure with n_B=4 seems to improve performance over n_B=2, both in terms of the median value of σ̂_e^2, and by imparting a smaller interquartile range for σ̂_e^2.

The results for N̂ mirror those for σ̂_e^2. Thus N̂ is larger for the adjusted estimators under the observed treatment effects, but otherwise the distributions are comparable.

Increasing the value of n_int reduces the interquartile range for σ̂_e^2 and N̂ for each procedure, and results in median values closer to the truth, as would be expected. Finally, we observe that the interquartile range for the unblinded procedure is often smaller than that of its adjusted or block randomisation counterparts.



 §.§ Familywise error-rate and power


For the scenarios from Section 3.3 that were not conducted under the observed treatment effects, the estimated FWER and power were also recorded. The results are displayed in Table 1.

The FWER for each of the procedures is usually close to the nominal level, with a maximal value of 0.052 for the unblinded procedure with n_int=32. The adjusted procedures arguably have the smallest inflation across the considered values of n_int.

In most cases the re-estimation procedures attain a power close to the desired level. Of the adjusted procedures, the null adjusted has a larger power, as would be anticipated given our observations on σ̂_e^2 and N̂ above. In fact, the null adjusted method conveys the highest power for each value of n_int. The power of the block randomised procedures is typically similar to that of the alternative adjusted method. In addition, whether only treatment one, treatments one and two, or all three treatments are effective has little effect on the power.

There is no clear to trend as to the effect of increasing n_int on the FWER, however it leads in almost all instances to an improvement in power. Finally, increasing the value for n_B in the block randomisation procedure increases power as would be predicted.



 §.§ Influence of σ_e^2

	
	In this section, we consider the influence of the value of σ_e^2 on the performance of our re-estimation procedures. Specifically, whilst we know that increasing σ_e^2 will increase the required sample size, we would like to assess the effect this has upon the ability of the methods to control the FWER and attain the desired power.
	
	Figures 3 and 4 respectively present our results on the FWER and power of the various re-estimation procedures when n_int∈{16,32} for several values of σ_e^2∈[0.25(6.51),4(6.51)], under the global null and alternative hypotheses respectively.
	
	Arguably, we observe that the FWER is more variable for smaller values of σ_e^2, with it changing little for several of the procedures when σ_e^2>10. There is additionally some evidence to suggest that increasing the value of n_int reduces the overall effect σ_e^2 has on the FWER.
	
	For the power, as would be anticipated, the re-estimation procedures are over-powered when n_int=32 and σ_e^2 is small. Moreover, increasing the value of n_int universally increases the power. Finally, as σ_e^2 increases beyond approximately σ_e^2=5, for both considered values of n_int, there is little change in power.



 §.§ Sample size inflation factor


Whilst the above suggests the overall performance of the re-estimation is good, there are several simple refinements that can be implemented to improve the observed results.

One such refinement, to help ensure the power provided by the re-estimation procedures is at least the desired 1-β, is to utilise a sample size inflation factor as originally proposed by <cit.>. With it, the value of N̂ as determined using the arguments above, is enlarged by the following factor


    (t_1-α,ν_n_int + t_1-β,ν_n_int/z_1-α + z_1-β)^2.


Of course, one must be careful that the new implied sample size does not exceed any specified value of n_max. However, this factor has then been shown to improve the performance of re-estimation procedures in both superiority <cit.>, non-inferiority <cit.>, and two-treatment bioequivalence trials <cit.>.

Figure 5 displays its effect in the context of our multi-treatment crossover trials. Explicitly, the power of the various re-estimation procedures under the global alternative hypothesis, for n_int∈{8,16,24,32,40} and σ_e^2=6.51, is shown with and without the use of the inflation factor. For the unblinded, null adjusted, and block randomised method with n_B=4, the inflation factor increases power to above the desired level in every instance. Consequently, this simple inflation factor appears once more to be an effective adjustment to the basic procedures.



§ DISCUSSION


In this article, we have developed and explored several methods for the interim re-assessment of the sample size required by a multi-treatment crossover trial. Our methodology is applicable to any trial analysed using the linear mixed model (<ref>), when there is equal participant allocation to a set of period balanced sequences. Thus whilst adapting the work of <cit.> would be advisable in the case of an AB/BA superiority trial, given that it does not require the use of simulation, our methods are pertinent to a broader set of crossover designs. Indeed, they are as readily applicable to multi-treatment superiority trials as they are ones for establishing bioequivalence.

We explored performance via three motivating examples, allowing consideration of settings with different types of sequences and a range of required sample sizes. Overall, the results presented here for the TOMADO trial are similar to those provided in the Appendix for Examples 2 and 3. However, larger inflation to the FWER was observed in Example 2, most likely as a consequence of its associated smaller sample sizes. Nonetheless, the methods were found to provide desirable power characteristics with negligible inflation to the FWER in many settings. In particular, the blinded procedures provided comparable operating characteristics to the unblinded procedure, and thus can be considered viable alternatives. Following results for parallel arm trials <cit.>, the null adjusted blinded estimator arguably performed better than the other estimators in that its typical over-estimation of the variance at interim led to the desired power being achieved more often. We may therefore tentatively suggest the null adjusted blinded estimator to be the preferred approach in this setting.

Our findings indicate that for each of the re-estimation procedures, the choice of δ and the underlying values of σ_e^2 and σ_b^2 often have little effect upon the FWER and power. We may be reassured therefore that the performance of the procedures should often be relatively insensitive to the design parameters. On a similar note, it is important to recognise that one cannot be certain when utilising these methods that the value of the period effects will not influence the performance of the re-estimation procedures. Whilst the final analysis should be asymptotically invariant to period effects, in finite samples it may influence the results of the hypothesis tests. Intuitively though one would not anticipate this effect to be large, nor would one routinely expect large period effects in many settings. In the Appendix, simulations to explore this are presented for the TOMADO example. The results indicate that there is little evidence to suggest the value of the period effects influences the performance of the re-estimation procedures. Trialists must be mindful however that this cannot be guaranteed, and should therefore be investigated.

We also considered the utility of a simple sample size inflation factor in ensuring the power reaches the desired level. Ultimately, we demonstrated that this was an effective extension to the basic re-estimation procedures. Though the observed inflation to the FWER of our procedures was often small, if more strict control is desired, a crude α-level adjustment procedure can also be utilised. For a particular re-estimation scenario, the values of σ_e^2 and σ_b^2, σ_e,max^2 and σ_b,max^2 say, which maximise the inflation to the FWER under the global null hypothesis can be determined via a two dimensional search. Then, the significance level used in the analysis of the trial can be adjusted to the α_adj that confers a FWER of α for this σ_e,max^2, σ_b,max^2 pair, according to further simulations. This may be useful in practice if the inflation is large for a particular trial design scenario of interest.

It is important to note the seemingly inherent advantages and disadvantages of the various re-estimation procedures. The adjusted estimator is perhaps the most constrained of those considered; requiring an equal number of patients to be allocated to each sequence for any non-zero adjustment to be reasonable. This is particularly troubling because of the possibility of patient drop-out. 

The estimator following block randomisation does not necessitate equal allocation to sequences (though its performance was considered here only when this was the case), but could also fall foul of patient drop-out that would prevent the estimation of the within person variance for each block. It also requires block randomisation, and could not be used with a more simple randomisation scheme if this was desired. The unblinded estimator of course suffers from none of these problems, but as discussed may be looked upon less favourably by regulators.

Finally, note that in conducting our work we also considered the performance of two re-estimation procedures based on methodology for the clustering of longitudinal data <cit.>. The motivation for this came from the Expectation-Maximisation algorithm approaches of <cit.> for parallel two-arm, and <cit.> for parallel multi-arm, studies. These methods may seem appealing, as they are blinded, under certain assumptions can produce unbiased estimates of the variance parameters, do not require specification of any adjustment, and in theory should be able to more readily handle small amounts of missing data. However, we found that they routinely vastly under-estimated the size of within person variance, resulting in substantially lower power than that attained by the other re-estimation procedures. Accordingly, especially given the associated concerns about the appropriateness of an Expectation-Maximisation algorithm for blinded sample size re-estimation <cit.>, we would not recommend re-estimation be performed based on a clustering based approach.

In conclusion, following findings for other trial design settings, blinded estimators can be used for sample size re-estimation in multi-treatment crossover trials. The operating characteristics of any chosen procedure should of course be assessed pre-trial through a comprehensive simulation study. But, often, investigators can hope to find that the likelihood of correctly powering their study when there is pre-trial uncertainty over the within and between person variances can be enhanced.



§ ACKNOWLEDGEMENTS

The authors would like to thank the two anonymous reviewers whose comments helped to substantially improve the quality of this article. This work was supported by the Medical Research Council [grant number MC_UU_00002/3 to M.J.G. and A.P.M., and grant number MC_UU_00002/6 to J.M.S.W.].

















§ DERIVING N(Σ_E^2,Σ_B^2)

	
	In this section, we elaborate on how a formulae for the sample size required by a trial, N(σ_e^2,σ_b^2), can be specified when σ_e^2 and σ_b^2 are known, a set of K sequences have been chosen, and n_1=…=n_K. First, we focus on the set up from Section 2.1, before briefly describing adjustments for other testing scenarios.
	
	We begin by denoting the linear mixed model for our vector of observations y by y=Xβ+Zb+ϵ. Here, it is important to note that the particular form of the matrices X and Z is dependent on the sample size and the chosen sequences. Then, the generalised least squares estimate for β, β̂, is given by
	
    β̂ = (X^⊤Σ^-1X)^-1X^⊤Σ^-1y,

	where Σ=ZGZ^⊤+R is known. Precisely, by our choice of covariance structure implied by linear mixed model (1), Σ will be an NP× NP block diagonal matrix, consisting of P× P blocks given by σ_e^2I_P + σ_b^2J_P. In addition, Var(β̂)=(X^⊤Σ^-1X)^-1, will also be known. Finally, β̂ is an unbiased estimate of β. Thus the vector of test statistics Q=(Q_1,…,Q_D-1)^⊤, where
	
    Q_d = τ̂_d/{Var(τ̂_d)}^1/2,     d=1,…,D-1,

	has the following multivariate normal distribution
	
    Q∼ N{τ∘I^1/2, Diag(I^1/2)Var(τ̂)Diag(I^1/2)}.

	Here, τ=(τ_1,…,τ_D-1)^⊤, and I=(I_1,…,I_D-1)^⊤ with I_d={Var(τ̂_d)}^-1. Furthermore, Diag(v) is the matrix formed by placing the elements of the vector v along the leading diagonal, and we take the convention that {(v_1,…,v_m)^⊤}^1/2=(v_1^1/2,…,v_m^1/2)^⊤.
	
	Using the distribution of Q, we can control the FWER to a desired level α for our hypotheses of interest by rejecting H_0d if Q_d>e, for the e which is the solution of
	
    1 - α = Φ_D-1{(e,…,e)^⊤,Var(Q)},

	where Φ_M{x,Λ} is the M-dimensional cumulative distribution function of a central multivariate normal distribution with covariance matrix Λ.
	The power to reject H_01 when τ_1=δ is then
	
    Φ_1{δ I_1^1/2-Φ^-1_1(1-α_*,1),1},

	for α_*=1-Φ_1(e,1). Consequently, to have power of 1-β we must have
	
    Φ_1{δ I_1^1/2-Φ^-1_1(1-α_*,1),1} = 1-β.

	By deriving the explicit form of I_1 we can determine its dependence upon the sample size N, which allows the above to be arranged and our final formula N(σ_e^2,σ_b^2) specified.
	
	For example, as discussed in Section 3.2, in the case where complete block sequences that are balanced for period are utilised, it is well known that I_1=N/(2σ_e^2) (Jones and Kenward, 2014). Thus, we can rearrange the above to acquire our previously specified formula
	
    N(σ_e^2,σ_b^2)≡N(σ_e^2)= 2σ_e^2{Φ^-1_1(1-α_*,1) + Φ^-1_1(1-β,1)}^2/δ^2≡2σ_e^2(z_1-α_* + z_1-β)^2/δ^2.

	In the case where alternative hypotheses are to be assessed (e.g., a global test that foregoes many-to-one comparisons), provided testing is performed using effects from β̂, the above can easily be adapted to designate an appropriate sample size formula. In each instance, one specifies a vector of test statistics, the distribution of which can be derived using that of β̂. This allows an appropriate formulae for controlling the FWER to be provided. For example, in the case where
	
    H_0d : τ_d = 0,     H_1d : τ_d≠0,     d=1,…,D-1,

	we still utilise Q as defined above, but now reject H_0d if |Q_d|>e, where e is the solution of
	
    1 - α/2 = Φ_D-1{(e,…,e)^⊤,Var(Q)}.

	Then, a formulae for the power of interest can similarly be designated, which allows N to either be specified explicitly, or permits an iterative search to be performed to determine its required value.
	
	For example, for the design scenario of Section 2.1, if we instead desire a familywise power of at least 1-β when τ=(δ,…,δ)^⊤ (that is, power to reject at least one of H_01,…,H_0D-1), our formula for the power becomes
	
    1 - Φ_D-1{(e-δ I_1^1/2,…,e-δ I_D-1^1/2)^⊤,Var(Q)}.

	Having derived I and Var(Q) for any N, a one-dimensional search can then be performed to acquire the minimal N such that the above is at least 1-β.



§ ADJUSTED BLINDED ESTIMATOR


In this section, we find the expected value of the adjusted blinded estimators of the within and between person variances discussed in the main paper.

First, note that for any K sequences which are balanced for period
	
    ∑_k=1^K (τ_d(j,k) - τ_d(j-1,k)) = 0,

	for j=2,…,P, and
	
    ∑_k=1^Kτ_d(1,k) = … = ∑_k=1^Kτ_d(P,k).

Now note that for the linear mixed model (1) that

    E(p_ijk) = π_j - π_j-1 + τ_d(j,k) - τ_d(j-1,k).

In addition, observe that Cov(p_i_1j_1k_1,p_i_2j_2k_2)=0 unless i_1=i_2 and k_1=k_2. Furthermore

    Var(p_ijk)    = Cov(y_ijk-y_ij-1k,y_ijk-y_ij-1k),
       = Cov(y_ijk,y_ijk)-Cov(y_ijk,y_ij-1k)
            -Cov(y_ij-1k,y_ijk)+Cov(y_ij-1k,y_ij-1k),
       = (σ_e^2+σ_b^2) - σ_b^2 - σ_b^2 + (σ_e^2+σ_b^2),
       = 2σ_e^2.

Consequently

    E( p̅_j )    = E( 1/n_int∑_k=1^K∑_i=1^n_int/K p_ijk),
       = 1/n_int∑_k=1^K∑_i=1^n_int/KE(p_ijk),
       = 1/n_int∑_k=1^K∑_i=1^n_int/K (π_j - π_j-1 + τ_d(j,k) - τ_d(j-1,k)),
       = 1/n_int n_int(π_j - π_j-1),
       = π_j - π_j-1,

where we have used Equation (3). Additionally

    Var( p̅_j )    = Var( 1/n_int∑_k=1^K∑_i=1^n_int/K p_ijk),
       = 1/n_int^2Var( ∑_k=1^K∑_i=1^n_int/K p_ijk),
       = 1/n_int^2{∑_k=1^K∑_i=1^n_int/KVar(p_ijk) + ∑_k_1≠ k_2∑_i_1 ≠ i_2Cov(p_i_1jk_1,p_i_2jk_2) },
       = 1/n_int^2{∑_k=1^K∑_i=1^n_int/KVar(p_ijk) },
       = 1/n_int^2 (2σ_e^2n_int),
       = 2σ_e^2/n_int.

Next, consider the following, which we call σ^2_within

    σ^2_within   = 1/2(P - 1)(n_int - 1)∑_j=2^P∑_k=1^K∑_i=1^n_int/K(p_ijk - p̅_j)^2,
       = 1/2(P - 1)(n_int - 1)∑_j=2^P(∑_k=1^K∑_i=1^n_int/Kp_ijk^2 - n_intp̅_j^2).

Taking expectations we have

    2(P - 1)(n_int - 1)E(σ^2_within)    = ∑_j=2^P{∑_k=1^K∑_i=1^n_int/KE(p_ijk^2) - n_intE(p̅_j^2)},
       = ∑_j=2^P[∑_k=1^K∑_i=1^n_int/K{Var(p_ijk) + E(p_ijk)^2 }.
               . ∑_j=2^P -n_int{Var(p̅_j) + E(p̅_j)^2 }],
       = ∑_j=2^P[∑_k=1^K∑_i=1^n_int/K{ 2σ_e^2 + (π_j - π_j-1 + τ_d(j,k) - τ_d(j-1,k))^2}.
               . - n_int{2σ_e^2/n_int + (π_j - π_j-1)^2 }],
       = ∑_j=2^P{ 2(n_int - 1)σ_e^2 + ∑_k=1^K∑_i=1^n_int/K(π_j - π_j-1 + τ_d(j,k) - τ_d(j-1,k))^2 .
               . ∑_j=2^P - n_int(π_j - π_j-1)^2 },
       = 2(P - 1)(n_int - 1)σ_e^2
            + ∑_j=2^P{∑_k=1^K∑_i=1^n_int/K(π_j - π_j-1)^2 + ∑_k=1^K∑_i=1^n_int/K (τ_d(j,k) - τ_d(j-1,k))^2 .
               . ∑_j=2^P + 2(π_j - π_j-1)∑_k=1^K∑_i=1^n_int/K (τ_d(j,k) - τ_d(j-1,k)) .
               . ∑_j=2^P -  n_int(π_j - π_j-1)^2 },
       = 2(P - 1)(n_int - 1)σ_e^2
            + ∑_j=2^P{ n_int(π_j - π_j-1)^2 + ∑_k=1^K∑_i=1^n_int/K (τ_d(j,k) - τ_d(j-1,k))^2 .
               . ∑_j=2^P -  n_int(π_j - π_j-1)^2 },
       = 2(P - 1)(n_int - 1)σ_e^2 + ∑_j=2^P∑_k=1^K∑_i=1^n_int/K (τ_d(j,k) - τ_d(j-1,k))^2,
       = 2(P - 1)(n_int - 1)σ_e^2 + n_int/K∑_j=2^P∑_k=1^K (τ_d(j,k) - τ_d(j-1,k))^2.

Thus we have that

    E(σ^2_within) = σ_e^2 + n_int/2K(P-1)(n_int-1)∑_j=2^P∑_k=1^K(τ_d(j,k) - τ_d(j-1,k))^2,

and for our adjusted blinded estimator

    σ̂_e^2 = σ^2_within - n_int/2K(P-1)(n_int-1)∑_j=2^P∑_k=1^K(τ_d(j,k)^* - τ_d(j-1,k)^*)^2,

it is clear that if τ_d^*=τ_d for d=1,…,D-1 then E(σ̂_e^2) = σ_e^2, and σ̂_e^2 is an unbiased estimator for σ_e^2 as claimed.

For the case where the sequences utilised for treatment allocation are additionally complete-block, the above estimator for σ_e^2 is all that is required by the adjusted blinded re-estimation procedures. When this is not the case however, we further require a blinded estimate of the between person variance σ_b^2. For this, define 
	
    q_ijk   =y_ij-1k+y_ijk,
    q̅_j   =1/n_int∑_k=1^K∑_i=1^n_int/Kq_ijk.

	Then, by a direct adaptation of the arguments above, and by using Equation (4), we can show that
	
    E(q_ijk)    = π_j-1+π_j + τ_d(j-1,k) + τ_d(j,k),
    Var(q_ijk)    = 2(σ_e^2+2σ_b^2),
    E(q̅_j)    = π_j-1+π_j + 2/D∑_k=1^Kτ_d(1,k),
    Var(q̅_j)    = 2(σ_e^2+2σ_b^2)/n_int.

	Now define
	
    σ_between^2=1/2(P-1)(n_int-1)∑_j=2^P∑_k=1^K∑_i=1^n_int/K(q_ijk-q̅_j)^2.

	Modifying the derivations for σ^2_within, we have that
	
    E(σ_between^2)   =σ_e^2 + 2σ_b^2 + n_int/2K(P-1)(n_int-1)∑_j=2^P∑_k=1^K(τ_d(j-1,k) + τ_d(j,k))^2
            +2n_int/D^2(n_int-1)( ∑_k=1^Kτ_d(1,k))^2.

	We can thus then take our blinded estimate for σ_b^2, σ̂_b^2, as
	
    σ̂_b^2    = 1/2{σ_between^2 - σ̂_e^2 - n_int/2K(P-1)(n_int-1)∑_j=2^P∑_k=1^K(τ_d(j-1,k)^* + τ_d(j,k)^*)^2 . 
               . - 2n_int/D^2(n_int-1)( ∑_k=1^Kτ_d(1,k)^* )^2 }.

	Again, in the case that τ_d^*=τ_d for d=1,…,D-1, this is an unbiased estimator for σ_b^2.



§ BLINDED ESTIMATOR FOLLOWING BLOCK RANDOMISATION


Here, we first demonstrate the forwarded blinded estimator for σ_e^2 following block randomisation is also unbiased. Throughout, the index k above is essentially replaced by the index b. To begin, observe that

    E(p_ijb) = π_j - π_j-1 + τ_d_B(j,b) - τ_d_B(j-1,b),

where d_B(j,b) is the index of the treatment given to a patient in block b in period j. As above, Cov(p_i_1j_1b_1,p_i_2j_2b_2)=0 unless i_1=i_2 and b_1=b_2, and Cov(p_ijb,p_ijb) = 2σ_e^2. Consequently


    E( p̅_jb)    = E( 1/n_B∑_i=1^n_B p_ijb),
       = 1/n_B∑_i=1^n_BE(p_ijb),
       = 1/n_B∑_i=1^n_B (π_j - π_j-1 + τ_d_B(j,b) - τ_d_B(j-1,b)),
       = 1/n_B n_B(π_j - π_j-1 + τ_d_B(j,b) - τ_d_B(j-1,b)),
       = π_j - π_j-1+ τ_d_B(j,b) - τ_d_B(j-1,b),
    Var( p̅_jb)    = Var( 1/n_B∑_i=1^n_B p_ijb),
       = 1/n_B^2Var( ∑_i=1^n_B p_ijb),
       = 1/n_B^2{∑_i=1^n_BVar(p_ijb) + ∑_i_1 ≠ i_2Cov(p_i_1jb,p_i_2jb) },
       = 1/n_B^2{∑_i=1^n_BVar(p_ijb) },
       = 1/n_B^2 (2σ_e^2n_B),
       = 2σ_e^2/n_B.


Next consider the proposed blinded estimator


    σ̂_e^2    = 1/2(P - 1)(n_int - B)∑_j=2^P∑_b=1^B∑_i=1^n_B(p_ijb - p̅_jb)^2,
       = 1/2(P - 1)(n_int - B)∑_j=2^P[∑_b=1^B(∑_i=1^n_Bp_ijb^2 - n_Bp̅_jb^2)].


We have


    2(P - 1)(n_int - B)E(σ̂_e^2)    = ∑_j=2^P{∑_b=1^B∑_i=1^n_BE(p_ijb^2) - n_B∑_b=1^BE(p̅_jb^2)},
       = ∑_j=2^P[∑_b=1^B∑_i=1^n_B{Var(p_ijb) + E(p_ijb)^2 }.
               . ∑_j=2^P -n_B∑_b=1^B{Var(p̅_jb) + E(p̅_jb)^2 }],
       = ∑_j=2^P[∑_b=1^B∑_i=1^n_B{ 2σ_e^2 + (π_j - π_j-1 + τ_d_B(j,b) - τ_d_B(j-1,b))^2}.
               . - n_B∑_b=1^B{2σ_e^2/n_B + (π_j - π_j-1 + τ_d_B(j,b) - τ_d_B(j-1,b))^2 }],
       = ∑_j=2^P[ 2(n_int - B)σ_e^2 + ∑_b=1^B∑_i=1^n_B(π_j - π_j-1 + τ_d_B(j,b) - τ_d_B(j-1,b))^2 .
               . ∑_j=2^D - n_B∑_b=1^B(π_j - π_j-1 + τ_d_B(j,b) - τ_d_B(j-1,b))^2],
       = ∑_j=2^P[2(n_int - B)σ_e^2],
       = 2(P - 1)(n_int - B)σ_e^2.

Thus E(σ̂_e^2) = σ_e^2, and the estimator is unbiased.

For non-complete-block treatment allocation, we can in this case take
	
    σ̂_b^2 = 1/2{1/2(P - 1)(n_int - B)∑_j=2^P∑_b=1^B∑_i=1^n_B(q_ijb - q̅_jb)^2 - σ̂_e^2 }.

	To show this is unbiased, again without loss of generality consider the case where μ_0=0. Then
	
    E(q_ijb)    = π_j + π_j-1+τ_d_B(j,b)+τ_d_B(j-1,b),
    Var(q_ijb)    = 2(σ_e^2+2σ_b^2),
    E(q̅_jb)    = π_j + π_j-1+τ_d_B(j,b)+τ_d_B(j-1,b),
    Var(q̅_jb)    = 2(σ_e^2+2σ_b^2)/n_B.

	Using these results, a direct modification of the derivation for σ̂_e^2 gives E(σ̂_b^2)=σ_b^2.
	
	

§ EXAMPLE 1: TOMADO

	
	

 §.§ Introduction

	
	In this section, we expand on our results from Section 3 on Example 1; the TOMADO trial. Throughout, we set
	
    μ_0 = 10.65,  σ_e^2=6.51,  α = 0.05,  β = 0.2.

	However, we now consider, in turn, the effect of altering the values of σ_b^2, δ, and the π_j, from those used in Section 3.
	
	

 §.§ Influence of σ_b^2

	
	First, we examine, in the case where π_2 = -0.77, π_3 = -0.96, π_4 = -0.55, and δ=-1.24, the influence of the value of σ_b^2 on the performance of the re-estimation procedures. As in Section 3.5, we would like to ascertain the effect changing σ_b^2 has upon the FWER and power.
	
	Figures 6 and 7 respectively present our results on the FWER and power of the various re-estimation procedures when n_int∈{16,32} for several values of σ_b^2∈[0.25(10.12),4(10.12)], under the global null and alternative hypotheses respectively.
	
	As would be anticipated, the value of σ_b^2 appears to have extremely little effect upon the performance of each of the re-estimation procedures. Recall that this is a consequence of the fact that the complete block sequences utilised in Example 1 render the requisite sample size independent of the between person variance.
	
	
	
	
	
	

 §.§ Influence of δ

	
	Here, we consider the case where π_2 = -0.77, π_3 = -0.96, π_4 = -0.55, and σ_b^2=10.12, focusing on the influence δ has upon the procedures FWER and power. Precisely, Figures 8 and 9 respectively present our findings for the FWER and power of the various re-estimation procedures when n_int∈{16,32} for several values of δ∈[2(-1.24),0.5(-1.24)], under the global null and alternative hypotheses respectively.
	
	In Figure 8 we can see that there is no clear pattern to the effect on the FWER of changing δ, with the fluctuations for several of the estimators relatively small. However, there is some evidence to suggest that increasing the value of δ (that is, making it closer to zero) reduces the FWER, as may be expected as this implies a larger requisite sample size.
	
	Similar statements are true for the power when examining Figure 9. Analogous to our discussions around Figure 4, the re-estimation procedures are over-powered when n_int=32 and δ is large in magnitude. Furthermore, increasing the value of n_int once more universally increases the power, whilst there appears to be a point beyond which the power remains relatively constant.
	
	
	
	
	
	

 §.§ Influence of period effects

	
	In Section 4, we discussed how the influence of the period effects should be examined using simulation. Again, though the final analysis on the trials data is asymptotically invariant to the true value of the period effects, their value may influence the ability of the various re-estimation procedures to accurately estimate the variance parameters at the interim reassessment. In this section, we assess the influence of the value of the period effects on each of the re-estimation procedures. Explicitly, we consider the case with n_int=16 and σ_e^2=6.51, under the global null hypothesis. All others parameters are left as specified in Section 3.2, except for the π_j for j=2,3,4. For these, in each replicate simulation we take
	
    π_j ∼ N(π̂_j,σ_π^2),      j=2,3,4.

	
	That is, a value for each π_j is drawn from a normal distribution with mean π̂_j, and specified variance σ_π^2. We then assess the effect of the size of σ_π^2 upon the trials FWER and values for σ̂_e^2. Figures 10 and 11 display our findings. From them, it does appear that at least for this design scenario and associated parameter set, the value of the period effects tends to have little influence on the interim estimation of the within person variance, or on the trials FWER.
	
	
	
	
	
	

§ EXAMPLE 2: FORMOTEROL

		
		

 §.§ Introduction

		
		Senn (2002) reported the results of a double-blind placebo controlled cross-over trial to assess the performance of two doses of formoterol solution aerosol (D=3). Denoting the treatments by d=0,1,2, with d=0 the placebo and d=1,2 corresponding to the two doses of formoterol, patients were allocated to one of the following six incomplete block sequences
		
    01, 10, 02, 20, 12, 21.

		We assume that the primary FEV1 (forced expiratory volume in 1 second) outcome data was to be analysed with the linear mixed model (1), in order to test the following hypotheses
		
    H_0d : τ_d ≤ 0,     H_1d : τ_d > 0,     d=1,2.

		A complete case analysis of the data presented by Senn (2002) gives the following estimates for the parameters in the model
		
    μ̂_0 = 1.51,  π̂_2 = 0.03,  τ̂_1 = 0.50,  τ̂_2 = 0.52,  σ̂_e^2 = 0.053,  σ̂_b^2 = 0.49.

		Consequently, for α=0.1 and β=0.2, a sample size of 30 patients would be powered to detect a clinically relevant difference of δ=0.2.
		
		Accordingly, in this section we investigate the performance of the re-estimation procedures with the various design parameters motivated by those obtained from the results of this formoterol trial. In particular, this allows us to consider performance in a more challenging small sample setting. In all of what follows we set μ_0=1.51, π_2=0.03, α=0.1 and β=0.2, and we suppose that patients are allocated treatments via one of the six sequences listed above (P=2). We then consider in turn the effect of varying one of the parameters σ_e^2, σ_b^2, and δ. As for Example 1, we will consider performance under the global null hypothesis (τ_1=τ_2=0), when only treatment one is effective (τ_1=δ,τ_2=0), under the global alternative hypothesis (τ_1=τ_2=δ), and under the observed treatment effects (τ_1=0.50, τ_2=0.52). Moreover, we again take n_max=1000, and estimate the average performance of each design and analysis procedure using 100,000 trial simulations.
		
		

 §.§ Distributions of σ̂_e^2, σ̂_b^2 and N̂

		
		We first examine the performance of the re-estimation procedures when σ_e^2=0.053, σ_b^2=0.49, and δ=0.2, for n_int=18. The resulting distributions of σ̂_e^2, σ̂_b^2, and N̂, are shown in Figures 12-14, via their median, lower and upper quartiles across the simulations. The results are grouped according to the true value of the treatment effects.
		
		Following our findings for Example 1, the median values of σ̂_e^2, σ̂_b^2, and N̂ for the unblinded and block randomised procedures are always close to their respective true values. However, this is not always the case for the adjusted estimators. In particular, the null adjusted estimator over-estimates the value of σ_e^2 when τ_1=δ, and the alternative adjusted procedure under estimates σ_e^2 when τ_1=τ_2=0. Both adjusted estimators perform extremely badly at re-estimating σ_e^2 under the observed treatment effects.
		
		In terms of σ̂_b^2, the performance of the re-estimation procedures is more comparable, though the adjusted procedures fair worse under the observed treatment effects.
		
		As expected, the results for N̂ once again mirror those for σ̂_e^2. This means, in particular, that the median value of N̂ is substantially larger for the adjusted estimators under the observed treatment effects, and is slightly larger for the null adjusted procedure when τ_1=δ.
		
		Increasing the value of n_int reduces the interquartile range for σ̂_e^2 and N̂ for each procedure, and results in median values closer to the truth, as would be expected. Finally, we observe that the interquartile range for the unblinded procedure is often smaller than that of its adjusted or block randomisation counterparts.
		
		
		
		
		
		
		
		

 §.§ Familywise error-rate, power, and sample size inflation factor

		
		For the scenarios from Section S.M.5.2 that were not conducted under the observed treatment effects, the estimated FWER and power were also recorded. Additional simulations were also performed to ascertain the power of the procedures under the global alternative hypothesis when the sample size inflation factor introduced in Section 3.6 was utilised. The results are displayed in Table 2.
		
		We can see that the unblinded and block randomised procedures experience similar and substantial inflation to the FWER. In contrast the adjusted procedures have an equal FWER with much smaller inflation above the nominal level. Thus for this example, the small requisite sample size appears to have inhibited the ability of the re-estimation procedures to retain a FWER close to α.
		
		Each of the procedures attain the desired power apart from that utilising the alternative adjusted estimator. The null adjusted estimator provides the largest power. These findings are not surprising in light of the distributions of σ̂_e^2 observed in Figure 12. Therefore in this instance the inflation factor appears to only be of use to the alternative adjusted procedure.
		
		

 §.§ Influence of σ_e^2

		
		We now consider cases where σ_b^2=0.49 and δ=0.2, but σ_e^2≠0.053. Specifically, in Figures 15 and 16 we respectively examine the FWER and power of the re-estimation procedures under the global null and alternative hypotheses when σ_e^2∈[0.25(0.053),4(0.053)].
		
		Figure 16 implies that the results for Example 2 are similar to those observed for Example 1. Explicitly, when σ_e^2 is very small the procedures are each over-powered, and as σ_e^2 increases there appears to be less of an effect upon the power.
		
		In contrast, the results on the FWER displayed in Figure 15 depict a distinctive pattern for each of the re-estimation procedures. Most likely, the observed peaks reflect a point at which the designs begin to switch from terminating the trial at the interim reassessment, to continuing to the end of the second stage. Overall, it is clear that the adjusted procedures typically have similar values of the FWER, with the same true of the unblinded and block randomised procedures. Moreover, whilst all of the estimators experience notable inflation to the FWER, it is smaller for the adjusted estimators, particularly as σ_e^2 increases.
		
		
		
		
		
		

 §.§ Influence of σ_b^2

		
		Next, we examine scenarios where σ_e^2=0.053 and δ=0.2, but σ_b^2≠0.49: in Figures 17 and 18 we respectively examine the FWER and power of the re-estimation procedures under the global null and alternative hypotheses when σ_b^2∈[0.25(0.49),4(0.49)].
		
		Allowing for Monte Carlo error, it appears that the value of σ_b^2, as in Example 1, has negligible effect upon the FWER and power of each of the the re-estimation procedures. This may seem surprising as we specifically noted that a value for σ_b^2 would be required to estimate the required sample size of a trial using the incomplete block sequences specified in Section S.M.5.1. However, this result reflects two factors. The first is that, as evidenced by Figure 13, the re-estimation procedures are very effective at estimating the value of σ_b^2. More importantly, though, is that whilst the sample size required by the formoterol trial will be dependent upon σ_b^2, it will still be principally driven by the value of σ_e^2. Therefore, the main driver of the utility of the re-estimation procedures in this setting remains their ability to re-estimate the within person variance.
		
		
		
		
		
		

 §.§ Influence of δ

		
		In our final investigations for Example 2 we consider scenarios in which σ_e^2=0.053 and σ_b^2=0.49, but δ≠0.2. Precisely, in Figures 19 and 20 we respectively examine the FWER and power of the re-estimation procedures under the global null and alternative hypotheses when δ∈[0.5(0.2),2(0.2)].
		
		Examining Figure 19, the FWER for the unblinded and block randomised procedures display the same rising and falling shape as observed in Figure 15. In contrast, the FWER for the adjusted procedures appears only to rise with in δ. This should not be surprising as larger values of δ imply smaller requisite sample sizes, leaving the procedures prone to small sample size issues.
		
		From Figure 20, as we would anticipate, for the larger considered values of δ the re-estimation procedures are substantially over-powered. All but the alternative adjusted procedure still perform well though when δ=0.1.
		
		
		
		
		
		

§ EXAMPLE 3: HYPERTENSION

		
		

 §.§ Introduction

		
		Ebbutt (1984) presented an analysis of data from a two-treatment (D=2) three-period (P=3) crossover hypertension trial. Denoting the treatments by d=0,1, patients were assigned to one of the following four sequence groups
		
    011, 100, 010, 101.

		Whilst Ebbutt (1984) assessed the data from only ten subjects on each sequence, Jones and Kenward (2014) discussed the data from all patients who completed the trial. Here, we suppose that the data Jones and Kenward (2014) presented on the outcome systolic blood pressure were to be analysed using the linear mixed model (1) in order to test the following hypotheses
		
    H_01 : τ_1 ≥ 0,     H_11 : τ_1 < 0.

		Thus, as in Example 1, a negative treatment effect implies efficacy.
		
		In analysing the data from this trial using linear mixed model (1) we find
		
    μ̂_0 = 156.77,  π̂_2 = -2.13,  π̂_3=-4.90,  τ̂_1 = -7.55,  σ̂_e^2 = 169.8,  σ̂_b^2 = 255.0.

		Therefore, for α=0.025, the trial's sample size of 90 patients would provide power for a clinically relevant difference of δ=-5.39 when β=0.1.
		
		In this section, we explore the performance of the re-estimation procedures with the parameters motivated by the results of this hypertension trial. Thus, having considered complete block sequences in Example 1, and incomplete block sequences in Example 2, we now consider a design utilising extra-period sequences.
		
		Following the same path as in Example 2, throughout what follows we set μ_0=156.77, π_2=-2.13, π_3=-4.90, α=0.025 and β=0.1, supposing that patients are allocated treatments based upon one of the four sequences given above. We then again consider the effect of varying the parameters σ_e^2, σ_b^2, and δ. We examine performance under the null hypothesis (τ_1=0), the alternative hypothesis (τ_1=δ), and under the observed treatment effect (τ_1=-7.55). Finally, once more, we take n_max=1000, and estimate the average performance of each design and analysis procedure using 100,000 trial simulations.
		
		

 §.§ Distributions of σ̂_e^2, σ̂_b^2 and N̂

		
		We first examine the performance of the re-estimation procedures when σ_e^2=169.8, σ_b^2=255.0, and δ=-5.39, for n_int∈{16,32,48}. The resulting distributions of σ̂_e^2, σ̂_b^2, and N̂, are shown in Figures 21-23, via their median, lower and upper quartiles across the simulations. The results are grouped according to the timing of the re-estimation and by the true value of the treatment effects.
		
		Overall, the results are very similar to those of Examples 1 and 2. In particular, the unblinded and block randomised procedures typically perform well in terms of re-estimating σ_e^2, whilst the adjusted estimators performance is highly dependent on the value of τ_1.
		
		As in Example 1, increasing the value of n_B for the block randomised procedure appears advantageous. Moreover, as expected, increasing the value of n_int reduces the distance between the median values of σ̂_e^2, σ̂_b^2, and N̂ and their respective true values, whilst also reducing the interquartile range.
		
		In this case, the distributions of the σ̂_b^2 are comparable across the procedures, regardless of the value of n_int or τ_1.
		
		Once more, the results for N̂ largely reflect those for σ̂_e^2. However, the median values for N̂ are larger when using the block randomised procedure with n_B=8. This is a consequence of the fact that by our assumptions an entire additional block of patients will be recruited even when a smaller number of patients are required to attain the requisite sample size.
		
		
		
		
		
		
		
		

 §.§ Familywise error-rate and power

		
		For the scenarios from Section S.M.6.2 that were not conducted under the observed treatment effect, the estimated FWER and power were also recorded. The results are displayed in Table 3.
		
		In this instance, we observe that the FWER is in many instances slightly below the nominal level, with a maximal value of only 0.0252 for the block randomised procedure with n_B=4 when n_int∈{16,48}. This is likely a result of the fact that the number of observations accrued in each of the designs is, for a crossover trial at least, large relative to the number of hypotheses that are to be tested.
		
		Most of the re-estimation procedures attain a power close to the nominal level. However, the alternative adjusted estimator again leads to lower levels of power. Finally, as would be anticipated, increasing the value of n_int improves the power of the re-estimation procedures. However, it has no clear effect upon the FWER.
		
		

 §.§ Influence of σ_e^2

		
		We now consider cases where σ_b^2=255.0, and δ=-5.39, but σ_e^2≠169.8. Specifically, in Figures 24 and 25 we respectively examine the FWER and power of the re-estimation procedures under the null and alternative hypotheses when σ_e^2∈[0.25(169.8),4(169.8)].
		
		Here, there appears to be some evidence that the smallest considered values of σ_e^2 result in lower values of the FWER. This may once more reflect a change between terminating the trial at the interim reassessment and continuing to the end of the second stage. Nonetheless, is it clear that in this case the procedures control the FWER well regardless of the value of the within person variance.
		
		Similarly, whilst the smallest values of σ_e^2 lead to the designs being substantially over-powered, it is evident that when σ_e^2 is increased they are still able to provide approximately the desired power.
		
		
		
		
		
		

 §.§ Influence of σ_b^2

		
		Next, we examine scenarios in which σ_e^2=169.8, and δ=-5.39, but σ_b^2≠255.0: in Figures 26 and 27 we respectively examine the FWER and power of the re-estimation procedures under the null and alternative hypotheses when σ_b^2∈[0.25(255.0),4(255.0)].
		
		Similar to both Examples 1 and 2, allowing for Monte Carlo error, the value of σ_b^2 seems to have little effect upon the ability of the re-estimation procedures to control the FWER to 0.025, and to provide power at level 0.9. We therefore have further evidence that we do not need to be concerned about the underlying between patient variance when considering the appropriate use of the proposed methods.
		
		
		
		
		
		

 §.§ Influence of δ

		
		We now investigate settings in which σ_e^2=169.8 and σ_b^2=255.0, but δ≠-5.39. Precisely, in Figures 28 and 29 we respectively examine the FWER and power of the re-estimation procedures under the null and alternative hypotheses when δ∈[2(-5.39),0.5(-5.39)].
		
		Our results indicate that in this case, the smallest considered values of δ appear to result in reduced values of the FWER. However, regardless of the value of δ, each of the procedures is generally able to control the FWER to approximately the nominal level.
		
		From Figure 29, we once more observe that when the magnitude of δ is large, the designs are over-powered, but outside of this region the specified clinically relevant difference appears to have little effect upon the power.
		
		
		
		
		
		

 §.§ Sample size inflation factor

		
		Our final consideration is to once more examine the utility of the sample size inflation factor introduced in Section 3.6. In Figure 30 we present the power of the re-estimation procedures under the alternative hypothesis, when n_int∈{16,32,48}, with and without the use of the inflation factor.
		
		As was observed for Example 1, the inflation factor leads to a notable boost in power, helping several of the estimators achieve the desired performance. Therefore, when there are concerns around attaining the desired power, we may again recommend that investigators consider utilising this simple adjustment.
		
		

10
	
	
	
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