# Design Considerations for a Phase II platform trial in Major Depressive
Disorder

Michaela Maria Freitag  Charité – Universitätsmedizin Berlin, corporate member
of Freie Universität Berlin, Humboldt-Universität zu Berlin, and Berlin
Institute of Health, Institute of Biometry and Clinical Epidemiology, Berlin,
Germany Dario Zocholl  Charité – Universitätsmedizin Berlin, corporate member
of Freie Universität Berlin, Humboldt-Universität zu Berlin, and Berlin
Institute of Health, Institute of Biometry and Clinical Epidemiology, Berlin,
Germany Elias Laurin Meyer  Medical University of Vienna, Center for Medical
Data Science, Vienna, Austria  Berry Consultants, Vienna, Austria  Stefan M.
Gold  Charité – Universitätsmedizin Berlin, corporate member of Freie
Universität Berlin, Humboldt-Universität zu Berlin, and Berlin Institute of
Health, Department of Psychiatry and Psychotherapy, Berlin, Germany  Charité –
Universitätsmedizin Berlin, corporate member of Freie Universität Berlin,
Humboldt-Universität zu Berlin, and Berlin Institute of Health, Medical
Department, Section Psychosomatics, Berlin, Germany  DZPG, German Center for
Mental Health  Universitätsklinikum Hamburg-Eppendorf, INIMS, Hamburg, Germany
Marta Bofill Roig  Medical University of Vienna, Center for Medical Data
Science, Vienna, Austria  Heidi De Smedt  Janssen Research and Development,
Beerse, Belgium  Martin Posch  Medical University of Vienna, Center for
Medical Data Science, Vienna, Austria  Franz König Correspondence to
<EMAIL_ADDRESS>Medical University of Vienna, Center for Medical
Data Science, Vienna, Austria  on behalf of the EU-PEARL MDD Investigators
Membership of The EU-PEARL MDD Investigators is provided in the
Acknowledgments

##  1 Abstract

Major Depressive Disorder (MDD) is one of the most common causes of disability
worldwide. Unfortunately, about one-third of patients do not benefit
sufficiently from available treatments and not many new drugs have been
developed in this area in recent years. We thus need better and faster ways to
evaluate many different treatment options quickly. Platform trials are a
possible remedy - they facilitate the evaluation of more investigational
treatments in a shorter period of time by sharing controls, as well as
reducing clinical trial activation and recruitment times. We discuss design
considerations for a platform trial in MDD, taking into account the unique
disease characteristics, and present the results of extensive simulations to
investigate the operating characteristics under various realistic scenarios.
To allow the testing of more treatments, interim futility analyses should be
performed to eliminate treatments that have either no or negligible treatment
effect. Furthermore, we investigate different randomisation and allocation
strategies as well as the impact of the per-treatment arm sample size. We
compare the operating characteristics of such platform trials to those of
traditional randomised controlled trials and highlight the potential
advantages of platform trials.

##  2 Introduction

Major depressive disorder (MDD) is one of the leading causes of disability.
Studies based on clinical interviews indicate an estimated worldwide
prevalence of 5–6 % at any given time and a 1 in 6 lifetime prevalence [31].
Additionally, MDD is associated with a twofold increased risk to develop other
medical diseases and about 8-10 life years lost compared to the general
population [14]. While there are several different antidepressant treatments
available, about 50% of patients do not benefit sufficiently from the first
treatment (”Partially Responsive Depression”, PRD) and the majority of these
also do not benefit from second-line treatment (”Treatment-Resistant
Depression”, TRD) [42]. Up to one-third of MDD patients do not achieve full
symptomatic remission despite multiple medication attempts [39]. Moreover, in
recent years [29], comparatively few new drugs have been developed and
approved for psychiatric indications, including MDD, especially few with new
mechanisms of action. Faster and more efficient development procedures,
including novel trial designs, could thus contribute to facilitating drug
development, especially for early-phase studies in this field. Besides multi-
arm multi-stage trials and group sequential designs, one option to improve the
efficiency of study designs is the use of master protocols and platform trials
in particular. Such designs can a) accelerate the development and approval of
new treatments by enabling the investigation of multiple treatments in
parallel, sharing controls and reducing clinical trial activation times as
well as recruitment times and b) lead to lower costs and higher quality data
while being more patient-centric [8, 22]. Some successful adaptive platform
trials have already been implemented in the past, e.g. REMAP-CAP in Covid and
lung diseases [2] and I-SPY 2 in breast cancer [3, 1]. There are multiple
definitions of platform trials [17, 37, 22]. This article considers them as
clinical trials allowing for simultaneous and sequential evaluation of
multiple interventions in one indication against a common control possibly
taking into account specific disease sub-types. Their unique feature is the
possibility of treatments joining or leaving the trial over time [51, 22].
This definition is consistent with the one used in the FDA guidance document
on master protocols [15]. The IMI project EU-PEARL (EU Patient-cEntric
clinicAl tRial pLatforms) aims to promote the development of platform trials
by providing a generic framework to design and conduct integrated research
platforms[19, 34]. The project is motivated by use cases in four indications
still facing high unmet needs, one of them being MDD. The proposed platform
trial design in MDD was created in an iterative process involving different
stakeholders such as clinicians, statisticians, pharmacists, and experts by
experience. Additionally, a meeting with EMA representatives took place to
discuss several design elements under consideration. The goal was to develop
an efficient phase II trial design to screen novel treatments and repurposed
drugs for use in MDD. The two subpopulations of MDD to be investigated are
patients with PRD or TRD. Potential treatments may work in both groups but may
also differ with regard to their efficacy and safety between these groups.
With the caveat that TRD is a more severe subpopulation than PRD, and thus a
treatment that is effective for PRD may not have the same effectiveness in
TRD. For the purpose of this simulation, we have made the assumption that both
would show identical results.Therefore we focus on presenting EU-PEARL
considerations for designing and simulating platform trials in TRD. The
summaries of the platform design considerations for one of the other use
cases, Non-Alcoholic Steatohepatitis (NASH), have already been published [24,
25] alongside a general master protocol template [33].
For a platform trial, a number of trial characteristics need to be tailored to
the purpose of the trial, including choice of endpoint, sample size,
definition of control group (concurrent vs non-concurrent), allocation ratio,
etc. In the current paper, we explore the impact of these design choices on
trial performance and derive informed recommendations for a phase II platform
trial in TRD.
Platform trials increase efficiency due to e.g. shared controls and
infrastructure. The aim is to maintain some of the flexibility that is
available in separate trials also within the platform trial, but it will be
limited as e.g. endpoints should be the same in all arms. The gained
efficiency comes with statistical challenges and design challenges when
planning platform trials. Adaptations, design, and analysis elements have to
be carefully tailored specifically to the area of application. For example,
the sample size reduction realized by platform trials vs. running multiple
separate trials in parallel is mainly due to sharing of common control group
data. One important question is if only the concurrent control data should be
used for the analysis of an arm, i.e. only the data of control patients who
could have been randomised to the treatment arm in question, or if all control
data should be used, i.e. also non-concurrent controls. If all control data
was used, the power would be higher, but time trends could lead to distortions
especially if platform trials run for many years. Several methods have
recently been developed that include time as a covariate in the analysis to
address the time trend effects [5, 40].
Another statistical challenge is the implementation of adaptive interim
analyses during which possible adaptations can be made. One such adaptation is
the possibility of terminating treatment arms early and enabling faster
decisions. In a platform trial, it is critical to drop non-promising
treatments due to futility and continue with the promising ones. By dropping
one arm, resources become available to test another arm. This is especially
valuable in phase II settings when screening for potentially active treatments
is emphasized.
In this paper, we develop a phase II platform trial design in TRD and
investigate a broad range of design options including allocation strategies to
different arms and dropping treatment arms for futility. In section 2 we
define the hypotheses to be tested, the analysis methods, trial design
options, and the setup of the simulation study. In section 3 we report the
results of the simulation study for different design elements. We also compare
the performance of the proposed platform trial with traditional 2-arm trials,
illustrating the potential benefits of the platform trial approach. We close
with a discussion in section 4.

##  3 Methods

###  3.1 General Design Aspects

The target population for the platform trial are patients with Treatment-
resistant Depression (TRD). If patients are eligible for the trial, they are
invited to enrol and subsequently be randomised to either the control arm or a
treatment arm. The allocated treatment (or placebo) is administered in
addition to antidepressants and therapies the patients were receiving at the
time of inclusion in the trial. As the primary outcome measure, we evaluate
the change in Montgomery-Åsberg Depression Rating Scale (MADRS) score between
week 6 and the baseline value. Both the duration of 6 weeks for short-term
trials and the use of MADRS score are common standard elements in depression
trials [13]. For all analyses in the platform trial, we use a one-sided
significance level of 0.05 and only concurrent controls, i.e. only information
from patients in the control arm that could have been randomised to the
treatment arm in question. Figure 1 shows a schematic of the specific platform
trial design for TRD patients.

Figure 1: MDD platform trial design proposal. If patients are eligible for the
platform, they are randomised to either control or one of the treatment arms
within the platform. Different drugs can enter the trial at different time
points. The design might also allow for interim analyses to drop treatment
arms early. The time point of the interim analyses is indicated by a dotted
line.

Furthermore, the allocation ratio to control is dependent on the actual number
of enrolling treatment arms. We suggest a modified block randomisation. It is
discussed in detail in section 3.2.4. For the specific design elements of the
platform trial, we mainly focus on the selection of adequate allocation
ratios, the selection of futility boundaries and the handling of time trends.
We will also consider standard 2-arm trials and compare their performance
later on in the results section to the performance of platform trials. For
good comparability, we selected the same general design aspects for both types
of trials

###  3.2 Statistical Methods

####  3.2.1 Hypotheses

In a platform trial, several treatment arms may enter and leave the trial at
different time points. The goal of the design under consideration is to
compare the efficacy of each experimental treatment against a shared control.
The arms are therefore tested individually without comparing the effect of one
experimental treatment to that of another. The platform trial also does not
investigate a global hypothesis.
Consider a platform trial where investigational treatments $j$,
$j\in\\{1,...,J\\}$ are compared to a common control $c$. The objective of
this platform trial is to find any efficacious treatment, i.e. any treatment
that lowers the MADRS score at week 6 compared to a control treatment. The
corresponding baseline value of the MADRS score will be measured at the time
point patients are being randomized into either treatment arm $j$ or control
arm $c$. To demonstrate the efficacy of an experimental treatment $j$ against
the control group $c$, an elementary null hypothesis $H^{0}_{j}$ is tested at
a one-sided significance level $\alpha$. For any such test, control data that
is concurrently collected will be used, thereby defining a different set
$c_{j}$ of control data for every treatment $j$. Let $\mu_{j}^{6w}$ and
$\mu_{j}^{baseline}$ be the true means of the MADRS score of treatment $j$ at
week 6 and baseline, respectively and $\mu_{c_{j}}^{6w}$ and
$\mu_{c_{j}}^{baseline}$ the same values for the concurrent control group.
Then the one-sided null hypotheses are given by $H^{0}_{j}$:
$\mu_{c_{j}}^{6w}-\mu_{j}^{6w}\leq 0$ vs the alternative $H_{j}^{A}$:
$\mu_{c_{j}}^{6w}-\mu_{j}^{6w}>0$ controlling for the baseline values.
Alternatively, one could also express the null and alternative hypotheses for
the change in MADRS score between week 6 and baseline with
$\Delta_{j}=\mu_{j}^{baseline}-\mu_{j}^{6w}$ and
$\Delta_{c_{j}}=\mu_{c_{j}}^{baseline}-\mu_{c_{j}}^{6w}$ for the experimental
treatment $j$ and the concurrent control arm, respectively. Then the
elementary null and alternative hypotheses being tested can be given as

$H^{0}_{j}:\Delta_{j}-\Delta_{c_{j}}\leq 0\text{ vs
}H_{j}^{A}:\Delta_{j}-\Delta_{c_{j}}>0$

####  3.2.2 Analysis Method

For the analysis of the primary endpoint, i.e. the MADRS score at week 6
controlled for the baseline value, an analysis of covariance (ANCOVA) is
conducted using the factor treatment and adjusting for the baseline MADRS
score as a covariate. ANCOVA assumes linearity of the covariate effect and
absence of covariate-by-group interaction. Adjusting for the baseline value
has the advantage that the estimate and test of the treatment effect are
equivalent when using the value at week 6 or the change between baseline and
week 6 as the dependent variable in the ANCOVA model [41, 12]. The idea of the
ANCOVA is to use regression to control (i.e. adjust) for additional covariates
such as the baseline value so one can study the post-treatment measure free of
the proportion of variance linearly associated with the baseline. The ANCOVA
is also the preferred analysis method for randomised clinical trials with a
pre- and post-treatment measurement in case of continuous endpoints and
homogeneous covariance matrices [50, 52, 7].
As mentioned before we test the different null hypotheses $H^{0}_{j}$
separately for every treatment $j$, $j\in\\{1,...,J\\}$. We therefore fit
different models for every treatment arm $j$ using the data of treatment arm
$j$ and the corresponding concurrent control data $c_{j}$ only. The formal
models $M^{j}$, $j\in\\{1,...,J\\}$ can be written as

$M^{j}:Y_{ih_{j}}=\alpha_{j}+\beta_{j}G_{ih_{j}}+\gamma_{j}X_{ih_{j}}+e_{ih_{j}},$
(1)

whereby $Y_{ih_{j}}$ is the post-treatment MADRS score of person $i$ in group
$h_{j}$ and $X_{ih_{j}}$ the corresponding baseline value. In every model, the
index $h_{j}$ only takes two different values, $j$ for the treatment arm in
question and $c_{j}$ for the concurrent control group. For each ANOCOVA model
$M^{j}$ the corresponding intercept is denoted by $\alpha_{j}$. $G_{ih_{j}}$
is the treatment indicator for person $i$ (i.e. $G_{ih_{j}}=0$ for control and
$G_{ih_{j}}=1$ for treatment), $\beta_{j}$ quantifies the treatment effect and
$\gamma_{j}$ the baseline effect. Additionally a random term $e_{ih_{j}}$ is
added, which is normally distributed with zero mean and constant variance.
Practical use of ANCOVA requires estimation of $\gamma_{j}$, which is a
function of the within-group variances and correlation of the pre-treatment
and post-treatment scores. For the patients $i$ only the data of the $n_{j}$
subjects randomised to the experimental treatment arm $j$ of interest and the
corresponding concurrent control data of $n_{c_{j}}$ subjects in the control
group is used. Please note that the size $n_{c_{j}}$ of concurrent control
data might distinctly differ between experimental treatments $j$.
Additionally, the ANCOVA model can be expanded to adjust for further
variables. In the context of a platform trial, it is also reasonable to adjust
not only for the MADRS score at baseline but also for the factor time period
to avoid bias in the estimates due to time trends and to address the change in
allocation ratios due to entering or dropping of arms. We define the
categorical covariate time period as the time intervals where there are no
arms entering or leaving the trial. So the time period changes whenever a
treatment arm enters or leaves the platform trial. We explored a second ANCOVA
model with the factor time period. This modelling allows control of the type 1
error under certain assumptions if there were changes in the treatment effects
over time. We refer to Bofill et al. [5] for a formal definition of time
periods in the context of platform trials and for more detailed methods on how
to adjust for potential time trends.

####  3.2.3 Effect size definition

The effect sizes used in this paper are adjusted for the correlation between
the baseline value and the value at week 6. They follow a logic similar to the
calculation of Cohen’s d, see formula 2. $\Delta_{C}$ is the difference
between baseline and week 6 in the control group and $\Delta_{T}$ is the
corresponding value in the treatment group.

$\displaystyle
d=\frac{\Delta_{T}-\Delta_{C}}{\sqrt{\frac{\left(SD_{\Delta_{T}}^{2}+SD_{\Delta_{C}}^{2}\right)}{2}}}.$
(2)

For the simulation we assume $SD_{\Delta_{C}}$ and $SD_{\Delta_{T}}$ to be
equal. The value used in the simulation for the standard deviations is based
on a variance-covariance matrix from data of a placebo control arm in a past
phase II study in augmentation treatments in MDD. Based on the same data, it
is assumed that the MADRS score reduces from 32 points at baseline to 20 at
week 6 in the control group and that the correlation between baseline value
and week 6 is 0.214. According to equation 2 a value of $d=0.2$ corresponds to
an absolute reduction of 2.25 in the MADRS score compared to the control
group, $d=0.35$ corresponds to an absolute reduction of 4, and $d=0.5$ of 5.7.
We assume a standardized effect size $d=0.35$ to be the clinically relevant
effect for augmentation strategies in TRD. An effect of 0.5 is regarded as
rather big.

####  3.2.4 Allocation ratios and randomisation methods

There are many different options to define allocation rates to different
treatment arms and the control arm in multi-arm trials like the platform
trial. Common ones are a 1:1:…:1 allocation where every treatment arm and the
control arm are allocated the same proportion of patients and a 1:1:..:1:$x$
allocation where $x$ relates to the ratio in the control arm and all treatment
arms get the same number of patients but the control arm is allocated a
different fraction. The value $x$ can either be constant or dependent on the
number $k$ of treatment arms concurrently enrolling in the trial. For multi-
arm trials a square-root allocation, i.e. 1:1:…:1:$\sqrt{k}$, yields good
results [10]. It minimizes the standard error of treatment effect estimates
for normally distributed endpoints with equal variances across groups.
However, the adding and terminating of treatment arms during the course of a
platform trial impacts the performance of allocation rules and other rules
than the one for normal multi-arm trials may offer the best results [6]. The
allocation rate to control is not fixed upfront, but varies over time,
depending on the number of treatments concurrently under evaluation, and the
timing of entry and departure of interventions. It is to be noted that the
(placebo) response in patients with MDD strongly depends on factors like the
expectancy to receive placebo, i.e. it depends on the number of treatment arms
that are recruiting at the same time [32]. In order to avoid large variations
in the treatment effect over time, the allocation rate to control needs to be
controlled. Therefore, it can be reasonable to consider a cap for minimal
allocation to the control arm. Throughout the project, this cap was discussed
multiple times with clinical experts and finally it was recommended that about
one-third of patients should be randomised to the control arm. For the
simulations presented in the results section, we used a cap of 35%. Other
values for the cap were also investigated and are presented in the online
supplement.
All considered allocation ratios can be easily achieved by using simple
randomisation for any $x$ by modifying the randomisation probabilities
accordingly. In order to limit the variability introduced by simple
randomisation, we also implemented a modified version of block randomisation.
A performance comparison of simple and block randomisation is provided in the
online supplement.
For the modified block randomisation we were aiming to get blocks of minimal
size to reach the targeted allocation ratio of 1:1:…:1:$x$, where x
corresponds to the ratio of the control arm. For the 1:1:…:1 allocation, basic
permuted blocks are created with the number of open treatment arms (including
control) as the length of the block to be permuted, i.e. number of currently
enrolling treatment arms (=$k$) + 1. For example, aiming at an allocation
ratio of 1:1:1:1 a block with the spots $T_{1}T_{2}T_{3}C$ is permuted.
For the other allocation methods aiming at a 1:1:..:1:$x$ ratio, additional
control spots have to be added to the block with length $k+1$ to reach the
desired ratio. Here $x$ denotes the control ratio. The length of the control
blocks is equivalent to the number of patients still needed in the control
group. If $x$ is an integer, then the final block length is simply $k+x$, with
$x$ spots for the control in a permuted block. For example for the allocation
ratio of 1:1:1:3 a block with the spots $T_{1}T_{2}T_{3}CCC$ is permuted. If
$x$ is not an integer, we combine block randomisation with some random
elements on how many spots should eventually be added. So the basic block has
$k$ spots for experimental treatments and $y$ spots for the control arm, with
$y=\lfloor x\rfloor$. Furthermore, for each spot, it is decided whether to add
an additional spot for the control arm with a probability of $Frac(x)$ or not.
For example for 1:1:1:$\sqrt{3}$ allocation with $x=\sqrt{3}=1.73$, this
method results in a minimal block length of 4. With a probability of
$1-0.73=0.27$ such a permuted block $T_{1}T_{2}T_{3}C$ with length 4 is taken
or with probability $0.73$ a block $T_{1}T_{2}T_{3}CC$ with length 5 is taken
adding an additional spot for control. By applying this principle to randomly
add an additional spot for control the targeted allocation ratio is
approximately reached implementing a minimal block length in the randomisation
procedure. This modified procedure combines elements from traditional block
randomisation and random elements like in simple randomisation.

###  3.3 Simulations

During the design stage and simulation of any randomised controlled trial,
several design specifications and assumptions are needed to understand the
behaviour and operating characteristics of the trial. Design choices are
aspects that can be controlled by the decision maker and assumptions refer to
unknown quantities that have to be estimated from preexisting data [4, 16].
For a trial with continuous pre-treatment and post-treatment values analyzed
by an ANCOVA, the sample size per group, the expected (or clinically relevant)
effect, the assumed correlation between pre-treatment and post-treatment
values, and the significance level are needed to calculate the power. In this
simple case, the sample size and significance level are design choices and the
rest are assumptions about the true nature of the treatment effect, while the
only operating characteristic we are interested in is the power. For designs
with adaptive elements such as group sequential and platform trial designs,
typically many more design choices and assumptions need to be made, while at
the same time evaluating additional operating characteristics. As an example,
in the case of a group sequential design with one interim analysis and the
option to stop for futility, additionally, the time point of the interim
analysis and the futility stopping boundary are needed as design parameters,
the accrual rate is needed as an additional assumption and another operating
characteristic we might evaluate is the average duration of the trial and the
probability to stop at interim. Due to their flexibility with respect to
incorporating adaptive design features, platform trials require even more
design choices and assumptions for the simulation setup, and many more
operating characteristics are evaluated.
In this subsection, we will first give a description of the general simulation
settings with the design choices and assumptions considered. Then we specify
operating characteristics of interest. R version 4.2.1 was used for the
simulation and the code is publicly available on Github [27].
The main objective of the simulations was to investigate whether a platform
trial offers more efficiency in terms of sample size or time compared to
separate 2-arm trials in the context of phase II MDD trials. Such a sequence
of 2-arm trials will therefore act as a reference for the platform trial.

####  3.3.1 Simulated trial designs

For the simulations we consider a base design with some fixed parameters and
some that vary over a range of options. All parameters that are varied are
described in Table 1.

Table 1: Parameters required to be specified for the simulation study. They are classified as either design choices or assumptions made regarding the platform trajectory or treatment effects. Some values are fixed and some varied for different simulation scenarios. Values marked by ∗ are presented in the online supplement. Name |  Type |  Investigated Values |  Description
---|---|---|---
Randomisation |  Design choice |  Simple∗,
(Modified) Block |  For the simple randomisation the randomisation probabilities are set to achieve the targeted allocation ratios. A modified block randomisation was implemented which combines traditional block randomisation with random adding of controls to allow for minimal block length (details see 3.2.4)
Allocation ratio |  Design choice |  1:…:1
1:…:1:k
1:…:1:$\sqrt{k}$
1:…:1:$\sqrt{k}$ with minimum allocation cap to control ∗ |  Patients are randomised to one of the treatment arms or to the control arm with the given ratio. The variable $k$ denotes number of concurrently enrolling treatment arms.
∗ Different possible values for the cap on minimal allocation to control are
investigated in the online supplement. Here the results of the selected cap
35% are shown.
Analysis method |  Design choice |  one covariate
two covariates |  The analysis is based on an ANCOVA which either adjusts only for the covariate baseline value or additionally for the time period.
Timing of interim analyses |  Design choice |  no interim analysis,
50% |  Timing of the interim analysis of a single treatment arm as proportion of the planned sample size for this treatment arm (counting observed outcomes).
Futility stopping rule |  Design choice |  no futility stopping,
0.2, 0.25, 0.3, 0.35, 0.4, 0.45, 0.5 |  Treatment arms will be stopped for futility at the time point of the interim analysis if the one-sided interim p-value is above this threshold.
Total sample size per treatment |  Design choice |  variable options from 40 to 120 |  Number of patients after which the final analysis of one treatment arm is conducted.
Initial treatments |  Assumption |  3,
6 |  Number of treatments available at the beginning of the platform trial
Timing of new treatments |  Assumption |  20%,
100% |  Every month a new treatment can enter the platform with a given probability if the maximum number of concurrently enrolling treatment arms is not yet reached.
Standardized effect size |  Assumption |  0,
0.2,
0.35,
0.5 |  Every treatment that enters the platform trial is randomly assigned one of these standardized effect sizes $d$ with predefined probability $\theta_{d}$, with $\theta_{0}+\theta_{0.2}+\theta_{0.35}+\theta_{0.5}=1$. The effect sizes are expressed in standardized mean difference between baseline and 6-week MADRS score. A variance-covariance matrix based on data from past studies is used for standardization.
Effect size
distribution |  Assumption |  equal,
pessimistic |  Different scenarios for the probabilities of the effect sizes are investigated. The equal scenario sets $\theta_{0}=\theta_{0.2}=\theta_{0.35}=\theta_{0.5}=0.25$ and the pessimistic scenario $\theta_{0}=0.5$, $\theta_{0.2}=0.3$, $\theta_{0.35}=0.1$, and $\theta_{0.5}=0.1$.
Time trend |  Assumption |  0%,
10% |  The assumed drift over time is modelled by a step function with steps at the beginning of every time period. The step width is given as a percentage in terms of the 6-week MADRS variance.

As the base design, we used a platform trial with 6 concurrently running
treatment arms and a common control group. The targeted sample size per
treatment arm $j$ is $n_{j}=80$ patients and for the treatment arms, each of
the four standardized effect sizes $d=0$, $d=0.2$, $d=0.35$, and $d=0.5$ are
assumed as equally likely, i.e. the probability of each effect size is
$\theta_{0}=\theta_{0.2}=\theta_{0.35}=\theta_{0.5}=0.25$. Every week a mean
number of 7 patients is recruited with 7 being most likely (90%) and a slight
variability to 6 or 8 patients per week (both with probability 5%). Also every
week a final analysis can take place if enough patients are allocated to an
arm. In the simulations, we assume that the outcome is observed immediately
and analyses (and possible trial adaptations) are conducted as soon as a
target number of outcomes have been observed. Therefore, active arms and
enrolling arms are synonymous in the simulations. The decisions are based on
p-values using an ANCOVA adjusting for the baseline value and a nominal one-
sided significance level $\alpha=0.05$ was used.
For each combination of simulation parameters, 10000 simulation runs were
performed. 10000 replicates correspond to a simulation error for a rate of
0.05 (=significance level) of $\sqrt{0.05*(1-0.05)/10000}\approx 0.002$ and
the worst case simulation error for rates of $\sqrt{(0.5*0.5)/10000}=0.005$.
At the beginning of each month, if a treatment arm has been removed from the
platform, another treatment arm replaces it. For simulation purposes, we set
one month to 4 weeks. This scenario uses an optimistic assumption that there
are always treatments available to be entered into the platform trial and
shows the maximum benefit of a platform trial compared to multiple 2-arm
trials.
After 60 months, no more new treatment arms can be added and the platform ends
once all compounds have made a decision. In order to archive a more
homogeneous total sample size in the investigated platform trial designs, we
only allow treatments to enter if at least one-fifth of the targeted sample
size is expected to be recruited until month 60. The distribution of the
platform sample size in case this rule is not applied is provided in the
online supplement.
We also investigated another scenario that makes more pessimistic and maybe
more realistic assumptions about the availability of new treatment arms and
the effect size distribution. In this second scenario, the platform starts
with 3 arms and at the beginning of each month, a new arm enters the trial
with 20% probability if the maximum number of 6 concurrently enrolling
treatments in the platform is not yet reached. In the comparison section to
multiple 2-arm trials, results for this scenario are shown additionally to the
results of the platform running at maximum capacity. More results for this
setting are provided in the online supplement.
For the effect size distribution, we investigate a more pessimistic scenario
with probabilities of assignment $\theta_{0}=0.5$, $\theta_{0.2}=0.3$,
$\theta_{0.35}=0.1$, and $\theta_{0.5}=0.1$. Results for the pessimistic
scenario are shown in the futility section. Additional results for this
setting are provided in the online supplement.
Starting with this base design we investigate different design elements
separately. We first evaluate the impact of different allocation ratios to
control and select the most promising one which will be fixed for the
following simulations. Secondly, we show how the power is impacted when
adjusting for time periods in the final analysis to address potential changes
in the treatment effect due to adding and dropping of treatment arms. Thirdly,
an interim analysis is included in the platform trial after half of the
targeted patients per treatment arm are accrued. We only consider early
futility, which is triggered if the p-value is larger than a pre-defined
futility boundary (different values for this futility boundary are
investigated). In our design, we do not account for futility stopping in the
significance level of the final analysis, therefore the futility boundaries
can be considered non-binding. This offers more flexibility because they allow
for overruling the stopping decision at interim. However, in order to present
operating characteristics, predictability is needed. So in the visualization
of the simulation results, we treat the boundaries as binding. As a fourth
step, we analyse the impact of the targeted sample size per treatment arm on
the operating characteristics of the platform trial.
Additionally, in order to be able to compare the results of the platform trial
to a more traditional approach, we simulated standard parallel group designs
with 1:1 allocation between treatment and control both with and without an
interim analysis after half of the targeted per-arm sample size is accrued.
For comparability, we always use the same general assumptions (e.g. effect
size and per-arm sample size) as for the platform trial design.

####  3.3.2 Operating Characteristics

For the traditional parallel group design operating characteristics that are
often determined are the power and type I error per investigated treatment, as
well as the expected sample size. In the context of platform trials, many more
operating characteristics can be of interest depending on the objective of the
platform trial. In Table 2 we give an overview of operating characteristics we
considered important for the platform trial in MDD. As several treatments are
investigated within a platform, operating characteristics can be defined on
several levels, e.g. on the platform level or just for a subset of interest
like treatment arms or a certain effect size. For example, one could be
interested in the expected sample sizes both on the treatment and platform
level for budgeting reasons.

Table 2: Operating characteristics of interest in platform trials. This table gives names and descriptions of different operating characteristics that will be evaluated in the simulation section. It also states on which levels the characteristics are calculated, i.e. if they are characteristics of the overall platform, of arms in the platform or stratified by different effect sizes. Name |  Level |  Description
---|---|---
Rate of decisions made |  per effect size |  Decisions can be ”success”, ”failure” or ”stopped for futility”. The proportion of decisions made is evaluated depending on the assumed effect size. If the effect size is $d=0$ the success rate corresponds to the type I error. If the effect size is greater than $0$ the success rate corresponds to the power and the rates for failure and stopped for futility together give the type I error.
Absolute number of rejected null hypotheses |  platform,
per effect size |  Gives the absolute number of treatments for which the null hypothesis can be rejected either within the whole platform or stratified by effect sizes.
Sample size (median and interquartile range) |  platform,
treatment |  Gives the average number of patients in the whole platform trial, and the single treatments taking into account the potential interim analysis.
Size of control group for interim analyses and final analyses (median and interquartile range) |  platform,
treatment |  Only concurrent controls are used for the interim and final analyses of a specific treatment. Because the allocation to control is not fixed, this value can vary notably.
Number of treatment arms (median and interquartile range) |  platform |  Gives the average number of different treatments that can be investigated in the platform trial depending on the stopping criteria of the overall platform.
Standardized expected number of treatment arms |  platform |  Gives the average number of different treatments that can be investigated per 1000 patients in the platform trial.
Duration (median and interquartile range) |  treatment |  Gives the value of how long the platform will run and how long it takes on average for a treatment to finish within the platform trial.

##  4 Simulation Results

We will first present the results of the impact of different allocation ratios
to control. Secondly, we show how the power is influenced when adjusting for
time periods in the analyses. Thirdly, interim stopping rules are investigated
followed by an analysis of the targeted sample size per treatment arm.
Finally, a platform trial for the selected allocation strategy and an interim
analysis for futility is compared to a sequence of standalone 2-arm trials.
At the beginning of every subsection, we state the fixed parameters if they
differ between the subsections. In this main paper, we only present a limited
number of operating characteristics and simulation scenarios. We refer to the
online supplement for more details.

###  4.1 Comparison of allocation ratios

We simulated platform trials with different choices of allocation methods. The
targeted sample size per treatment arm was set to $N=80$ and no interim
analysis was conducted. The allocation methods considered are 1:1:…:1
randomisation (called balanced allocation), 1:1:…:$k$ randomisation (called
$k$ allocation), 1:1:…:$\sqrt{k}$ (called $\sqrt{k}$ allocation) and
1:1:…:$\sqrt{k}$ with a cap at 35% for control.

Figure 2: Treatment arms per 1000 patients in the platform, and rejection
rates for platforms running at maximum capacity, i.e. always investigating 6
arms in parallel. The targeted sample size per treatment arm was fixed at
$N=80$, and all effect sizes were assumed to be equally likely. The minimal
control cap for the $\sqrt{k}$ allocation was set to 35%. A) depicts the
number of arms that can be evaluated per 1000 patients in a corresponding
platform trial. In B the percentage of rejected null hypotheses is depicted.
It equals the type I error rate for $d=0$ and the power for the other values
of $d$. The type I error rate is always controlled at 5%. This value is
indicated by the lower dotted line. The higher dotted line highlights the 80%
mark.

The median number of experimental treatment arms per 1000 patients in the
platform trial is the highest for the balanced allocation with 10.5 arms. When
applying the k allocation substantially fewer arms (6.2) can be investigated
due to the higher proportion of controls. The $\sqrt{k}$ allocation and
$\sqrt{k}$ allocation with a minimum allocation to control of 35% are
somewhere in between with a median of 8.6 and 7.9 arms per platform, as seen
in Figure 2A. Directly correlated to the number of controls per comparison,
the duration of experimental treatment arms is the shortest for the balanced
1:…:1 randomisation and the longest for the $k$ allocation. The arms in the
scenario with $\sqrt{k}$ allocation take more time than the ones in the
balanced allocation scenario and when using a minimum cap for control at 35%
they again take a little longer.
Figure 2B shows the percentage of rejected null hypotheses in platform trials
using the different allocation methods stratified by the four different
standardized effect sizes $d=0$, $d=0.2$, $d=0.35$, and $d=0.5$. All effect
sizes are assumed to be equally likely, i.e.
$\theta_{0}=\theta_{0.2}=\theta_{0.35}=\theta_{0.5}=0.25$. For $d=0$ the
rejection rate equals the type one error rate, which is always controlled at
5%. In the other scenarios the power is always higher the higher the number of
control comparators per decision. So the $k$ allocation yields the highest
power followed by $\sqrt{k}$ allocation with a lower cap for control and
$\sqrt{k}$ allocation without a cap. The lowest power is achieved using
balanced allocation. It even yields under 80% power in the case of $d=0.35$
(the minimal clinically relevant effect size) where all other methods have
power clearly over 80% power.
Overall, even though the $k$ allocation method yields the highest power it
also has the lowest ratio of patients on treatment and by far the highest
duration per experimental treatment arm as well as the lowest (standardized)
number of arms which can be investigated in the platform. The balanced
allocation enables investigation of the most treatment arms per 1000 patients
and the lowest ratio of patients on control but the power is much smaller than
for the other allocation methods. As a trade-off between number of arms
investigated and power, we selected the $\sqrt{k}$ allocation method with a
minimum cap of 35% for control. It achieves the second highest power of all
investigated allocation methods and enables the investigation of more
treatment arms within the platform than the balanced allocation method.
Furthermore, this boundary was chosen based on clinical considerations: In
patients with MDD, the placebo response fluctuates greatly with personal
expectations of whether placebo is given or an investigational drug. The
expectation is that the lower the probability of being randomised to the
control arm, the greater the placebo response [32]. Therefore, clinicians
advise randomising at least one-third to the control arm. A more thorough
investigation of the impact of different values for the cap can be found in
the online supplement.

###  4.2 Comparison of ANCOVA models

An ANCOVA is used to test the null hypothesis of no treatment effect against
the one-sided alternative hypothesis. Potential covariates to include are the
baseline value and the time period. Time period refers to a section of time
during which no treatment leaves the trial and no new treatment enters. When
assuming no time trend, additionally including the time period in the analysis
leads to a very slight power loss, see Table 3. However, one can never be sure
if there really is no time trend in real-world settings. Table 3 illustrates
the possible difference between including and not including the time period
when a time trend is present.

Table 3: Power of ANCOVA models with and without adjustment for time periods as factor assuming no time trend and a time trend modeled by a step function assuming a step width of 10% of the 6-weeks MADRS score variance. The power is stratified by different effect sizes. | no time trend assumed | stepwise time trend assumed
---|---|---
Effect Size $d$ |  without time period |  with time period |  without time period |  with time period
0 |  4.97 |  4.95 |  4.99 |  4.98
0.2 |  48.3 |  47.9 |  46.2 |  48.1
0.35 |  87.9 |  87.7 |  86.7 |  88.2
0.5 |  99 |  98.9 |  98.8 |  99.1

The trend in this exemplary simulation is assumed to be a step function on the
6-week MADRS score with steps at time points where treatments enter or leave
the platform trial (i.e. at the beginning of every time period). The step
width is set to an increase of about 10% of the variance of the 6-week MADRS
score. This value and also the time trend model are exchangeable and only
serve the purpose of illustrating the improvement of power in settings with
time trends. As there is only a minimal loss in power when there is no time
trend at all and a noticeable increase in power depending on the actual time
trend, it is recommended to include the time period as a covariate in the
ANCOVA for real world applications. However, our further simulations do not
include assumptions on time trends and we therefore only used the baseline
value as a covariate in the ANCOVA.

###  4.3 Comparison of futility stopping rules

We simulated platform trials with different choices of futility boundaries. We
applied a $\sqrt{k}$ allocation with a minimal control cap at 35% and a
targeted sample size of 80 patients per experimental treatment arm. The
interim analysis was carried out after 40 patients were accrued in a treatment
arm. We present two different scenarios for the assignment probabilities of
the four considered standardized effect sizes, an equal scenario and a more
pessimistic one. In the equal scenario all effect sizes are assumed to be
equally likely, i.e.
$\theta_{0}=\theta_{0.2}=\theta_{0.35}=\theta_{0.5}=0.25$. For the more
pessimistic scenario these probabilities of assignment are $\theta_{0}=0.5$,
$\theta_{0.2}=0.3$, $\theta_{0.35}=0.1$, and $\theta_{0.5}=0.1$. In the online
supplement we additionally report the observed probabilities for stopping for
futility depending on the effect sizes.

Figure 3: Rejection rates and standardized number of arms when implementing
different futility rules. In the scenario on the left side (A and C) all
effect sizes are assumed to be equally likely, i.e.
$\theta_{0}=\theta_{0.2}=\theta_{0.35}=\theta_{0.5}=0.25$. On the right side
(B and D) we present results for a more pessimistic scenario with
probabilities of assignment $\theta_{0}=0.5$, $\theta_{0.2}=0.3$,
$\theta_{0.35}=0.1$, and $\theta_{0.5}=0.1$. A and B give the standardized
number of arms per 1000 patients in the platform trial. All arms are included
in this number regardless which of the four different investigated effect
sizes was allocated. In the more pessimistic scenario (B) more arms can be
investigated. The difference becomes more prominent the stricter the futility
boundary. In B and D the percentage of rejected null hypotheses is depicted.
It equals the type I error rate for $d=0$ and the power for the other values
of $d$. The type I error rate is always controlled at 5%. This value is
indicated by the lower dotted line. The higher dotted line highlights the 80%
mark. The power decreases with stricter futility boundaries. Overall C and D
are quite similar. So the effect size scenario does not have a big impact on
the rejection rates.

Overall the rejection rates, seen in Figure 3C and D are quite similar in both
scenarios. With a more strict stopping rule, the duration of the platform
decreases as is the median number of control comparators per decision. As a
trade-off for using non-binding futility boundaries, the power decreases with
stricter boundaries but also more arms can be tested. The number of arms that
can be tested per 1000 patients in the platform differs notably between the
scenarios, see Figure 3A and B. In the more pessimistic scenario more arms can
be investigated than in the equal scenario. This difference becomes more
prominent the stricter the applied futility boundary and goes as high as 1.45
arms per 1000 patients for a futility boundary of 0.2. Here we only present
the overall number of arms. In the equal scenario the same number of arms can
be investigated for each effect size. In the more pessimistic scenario the
most arms can be investigated for $d=0$ followed by $d=0.2$ and then tied for
the last place $d=0.35$ and $d=0.5$, corresponding to the probability of
occurrence of the individual effect sizes. Figure 3 shows that in both
scenarios the difference between not stopping at all and a very soft boundary
of 0.5 is relatively large for the standardized number of arms that can be
evaluated in the platform. The impact on the power, however, is very small.
The differences in these operating characteristics between the single steps
for the futility boundary are not very pronounced when comparing one step with
the next. However, the differences become clearly perceptible when values
further apart are compared, like the boundaries 0.5 and 0.25. Here, however,
not only does the number of arms that can be examined increase, but the power
also decreases notably. So one has to decide for the special use case how
aggressive the applied stopping rules should be. As this is a phase II study,
we recommend applying futility stopping with a boundary of at least 0.5. It is
also quite an intuitive boundary because it stops the investigation when the
treatment effect points in the opposite direction.

###  4.4 Analysis of per arm sample sizes

We simulated platform trials with different choices of the per treatment arm
sample size. The $\sqrt{k}$ allocation with a minimal control cap of 35% was
used and we investigated designs without the option to stop for futility and
with an interim analysis after 50% of the targeted sample size and a futility
boundary of 0.5. The higher the targeted sample size per treatment arm the
longer the investigation of this treatment arm takes but the higher the power.
Figure 4B shows the power reached when targeting different per treatment arm
sample sizes spanning from $N=40$ to $N=120$ with a step width of 10. The
standardized number of arms that can be investigated is depicted in 4A.

Figure 4: Rejection rates and standardized number of arms for different per-
arm sample sizes. All effect sizes are assumed to be equally likely, i.e.
$\theta_{0}=\theta_{0.2}=\theta_{0.35}=\theta_{0.5}=0.25$. The circles give
the values without the implementation of an interim analysis and the triangles
the corresponding values when a futility boundary of 0.5 is applied. The
sample size depicted on the x-axis was examined in steps of 10. The small
variation in x direction is based on jittering for better readability. Figure
A) shows the median number of arms per 1000 patients and the interquartile
range. In B) the rejection rates are depicted stratified by the four different
investigated effect sizes. The rejection rate equals the type I error rate for
$d=0$ and the power for the other values of $d$. The type I error rate is
always controlled at 5%. This value is indicated by the lower dotted line. The
higher dotted line highlights the 80% mark. The power is higher the higher the
targeted sample size but fewer arms can be investigated. When futility
stopping is implemented generally more arms can be investigated and the power
is lower.

The values with inclusion of the interim analysis are depicted by triangles
and the values without the option to stop for futility are depicted by
circles. Applying the specified interim analysis, for the minimal clinical
relevant effect size $d=0.35$ a sample size of $N=60$ gives a power of 78.2%.
It therefore falls a little short when wanting to reach 80%. When the futility
boundary 0.5 is used $N=70$ is the smallest investigated sample size with
power above 80% and $N=100$ the smallest with power above 90%. It is most
cost-efficient to use the smallest sufficient sample size for the desired
power. But the problem with a smaller sample size is that it introduces higher
variability and it becomes more likely to stop for futility. In the next
subsection, we therefore use the sample sizes between 60 and 90 for the
comparison between platform trials and traditional randomised controlled
trials, again with a step-width of 10.

###  4.5 Comparison to Traditional Parallel Group Design

The classical approach for evaluating multiple treatments in the context of
one disease, especially if more than one company is involved, is using
multiple randomised controlled trial designs with one treatment arm and one
control arm and 1:1 allocation between treatment and control. We simulated a
series of such traditional trials in order to compare the operating
characteristics to those of the designed platform trial. For the 2-arm trials
we make the same assumptions regarding sample size per treatment arm, assumed
effect sizes (and their distribution), and analysis method as in the platform
design. We also included the option to stop for futility at an interim
analysis after half of the total sample size is accrued. Figure 5 shows the
results of the comparison between sequential 2-arm trials and platform trials.
The circles give the values for designs without interim analysis for futility
and the triangles the values with a futility analysis after 50% of the sample
size was reached and with a futility boundary of 0.5.

Figure 5: Comparison of operating characteristics in different trial types.
All effect sizes are assumed to be equally likely, i.e.
$\theta_{0}=\theta_{0.2}=\theta_{0.35}=\theta_{0.5}=0.25$. The circles give
the values without the implementation of an interim analysis and the triangles
the corresponding values when a futility boundary of 0.5 is applied. The
sample size depicted on the x-axis was examined in steps of 10. The small
variation in x direction is based on jittering for better readability. Figure
A) shows the median number of arms per 1000 patients and the interquartile
range for the three different trial types platform trial with maximum capacity
utilization, platform trial with expected load in the MDD case, and the
traditional approach with a series of individual 2-arm randomised controlled
trials. B) gives the power for the same type of trials. A series of
traditional 2-arm trials reaches the lowest power and the fewest arms can be
investigated per 1000 patients. Incorporation of the possibility to stop for
futility always results in evaluation of more arms and a slightly smaller
power.

Besides the platform trial running at maximum capacity, i.e. always running 6
treatment arms in parallel, we also included a more realistic scenario in the
comparison. This is important as a platform running at maximum capacity shows
the maximum benefit reached when using a platform trial but this maximum
benefit is often not achieved in practice. The more realistic scenario
considers the platform to start with three treatment arms in parallel and at
the beginning of every month the probability of a new treatment arm to enter
the platform is 20%. Figure 5A shows the number of arms that can be
investigated per 1000 patients. The inclusion of a futility analysis leads in
all cases to a larger number of arms that can be investigated per 1000
patients. The platform trial running at maximum capacity enables evaluation of
the most arms. However, the difference to the more realistic platform setting
diminishes with bigger targeted sample sizes per treatment arm. This is due to
the treatment arms staying longer in the platform if more patients are needed
and therefore often more arms run in parallel. An important benefit of using
platform trials is generated by investigation of multiple treatment arms in
parallel. By sharing of the control group fewer patients per treatment arm are
needed in the control group and the number of control comparators increases
and therefore also the power. This, however, only holds true for some
allocation methods like the $\sqrt{k}$ allocation method with a minimum cap
for control used here. If a 1:1:…:1 allocation was to be applied in the
platform the power would not increase as much and one could just use a
traditional 2-arm trial with 1:1 allocation. With the platform design options
used in the simulations we always get higher power than for a series of 2-arm
trials even when the platform does not run at full capacity, see Figure 5B.
The figure only shows the power for the minimal clinically relevant effect
size $d=0.35$ because this effect is the most relevant when deciding about the
sample size and design of a trial. When using 2-arm trials, only with a per-
arm sample size of 100 we reach a power of over 80% for this minimal
clinically relevant effect size. In a platform running at maximum capacity a
per-arm sample size of 70 suffices and in the more realistic workload setting
a per-arm sample size of 80 would be needed. In a real world setting we cannot
be sure about the actual workload the platform trial will have. Hence, the
decision about the targeted per-arm sample size should not be made solely
based on the power reached in a platform trial running at maximum capacity.
For our specific use-case we would instead recommend a targeted per-arm sample
size of 80 when a power of 80% is desired.

###  4.6 Summary and recommendations

Based on our simulations we recommend the use of $\sqrt{k}$ allocation with a
minimal cap for control at 35%, inclusion of time period as a factor (even
though we do not include it in further simulations) and futility stopping with
at least a boundary of 0.5, or even stricter like e.g. 0.25 if the platform is
used for screening purposes. Like the futility boundary the sample size also
depends on the specific use case. It is especially influenced by the desired
power. Note that the power reached is also dependent on the available
concurrent treatment arms, as we show in section 4.5. One should therefore
select a sample size that is a little higher than the minimum needed for the
desired power.
Overall, the implementation of a platform trial provides both a higher power
and a larger number of arms that can be tested with the same amount of
patients. It should therefore be preferred in settings when it is anticipated
that multiple treatments would participate. If one is unsure about the
potential of the availability of new treatments to be investigated in the
specific disease context and only very few are anticipated, the traditional
2-arm trial approach should be preferred. The organizational effort involved
in launching a platform would then simply not be justified by the gain.

##  5 Discussion

This paper summarizes the design considerations made by an EU-PEARL working
group for a phase II platform trial in MDD [35], including EMA consultation at
an ITF meeting. The simulations were conducted to evaluate if running a
platform trial would be feasible especially compared to separate 2-arm trials.
The simulations were also needed to fine-tune the design elements, such as
decision rules, analysis strategy, randomisation method, and sample size. Due
to the many random influences inherent in platform studies, it is not possible
to calculate the operating characteristics deterministically.
The use of platform trials allows great flexibility and individual design
elements such as futility bounds can be individually selected to best suit the
specific application. For reproducibility, we made our extensive simulation
code available on Github [27]. An overview of different available simulation
software for platform trials can be found in Meyer et al. [21]. However, the
code for the simulation studies is very individual, as are the platform
studies themselves. Often it is hard to generalize code and large parts have
to be rewritten. Recently, more generally applicable simulation and
visualisation tools for platform trials have been proposed [26, 23].
Platform trials allow for great flexibility and many additional design
elements might be included. For example, by using group sequential boundaries
stopping for efficacy could be incorporated. Also, the platform might allow
different arms to target different sample sizes per experimental treatment
arm. This could, for example, allow arms of sponsors targeting 80% power and
arms of those targeting 90% power to be accommodated in the same platform
trial. However, the specific implications of this would need to be explored
separately. Assumptions about frequency distributions of the different
targeted per-arm sample sizes at different time points in the platform would
have to be made in order to investigate how this changes the respective
concurrent control arms and thus also the power.
Since most available treatments are administered orally, we focus the
investigation on this way of administration although we discussed platform
designs for MDD including multiple ways of administration in the process.
Allowing different ways of administration (e.g. intravenous or intranasal)
would require having multiple control arms because otherwise appropriate
blinding could not be ensured. Having more control arms would however result
in smaller allocation rates for individual treatment arms and thus also longer
durations per investigation. Overall the benefit of using a platform trial
would be split between the different ways of allocation. Because non-oral
treatments are rather rare we therefore recommend investigating treatments
with different ways of administration in separate trials.
Additionally, in the context of MDD patients with treatment resistant
depression (TRD) one could consider the possibility of allowing patients who
had no treatment benefit to re-enter the platform trial after participation.
In case of allowing different routes of administration, re-entry could be
restricted to another way of administration. However, the statistical
implications would need to be further investigated.
In this article, we have focused on an adaptive allocation method with the
allocation ratio to control depending on the actual number of open treatment
arms. More controversially discussed are adaptive allocation methods also
utilizing information on the observed treatment effect, such as response
adaptive randomisation [43, 49, 36, 47, 38]. Challenges arise if considering
response adaptive randomisation in the presence of time trends, as response
adaptive randomisation could lead to biased estimates if the analyses used are
not appropriate for this situation. The current literature reflects
considerations in more traditional 2-arm [20] and multi-arm designs [46], but
not in (perpetual) platform trials, where more information for estimation of
potential time trends is available and/or the goal of response adaptive
randomisation might only be to accelerate evaluation of beneficial arms, while
all arms reach their targeted sample size eventually. Investigation of how
response adaptive randomisation would affect the efficiency of platform trials
and the performance of their analyses remains open for future work.
There has been some debate about whether multiplicity adjustment is required
when comparing multiple treatment arms with a common control in a platform
trial without a consensus being reached [28, 30]. Guidance documents of EU-
and US-authorities do not give a clear answer on when or how adjustment for
multiplicity should be included in platform trials [11, 44, 45]. If separate
trials were run no adjustment for multiplicity would be required and e.g. in
platform trials with individual control arms, the correlation of test
statistics leads to the family-wise error rate being lower compared to running
individual trials with individual controls [30]. Therefore on the one hand, it
could be argued that no adjustment for multiplicity should be required in a
platform trial setting. On the other hand, the dependency in the test
statistics impacts the decisions made and should be considered especially in
confirmatory settings [9]. Another point of discussion is the interdependence
of the individual hypotheses. At the moment the general approach is that no
adjustment for multiplicity has to take place when the hypotheses are fairly
unrelated, e.g. the treatments come from different sponsors and use different
mechanisms of action. However, when the hypotheses are related, e.g. when
several doses of one drug are tested, adjustment should take place [48, 18].
In our platform trial we will not adjust for multiplicity as we design an
exploratory phase II trial and the hypotheses tested can be considered
inferentially independent.
Overall, based on our simulations we recommend a phase II platform trial in
MDD using $\sqrt{k}$ allocation with a minimal control cap of 35%, futility
analyses after 50% of the targeted per treatment arm sample size with futility
boundary 0.5, inclusion of time period as a covariate in the ANCOVA analysis
and a targeted per treatment arm sample size of 80 patients. However, one
should carefully investigate the different design choices for the specific
use-case as they impact the performance characteristics greatly.
We have shown that a platform trial offers a more efficient way to test more
treatments compared to a sequence of separate 2-arm trials each with its own
control arm and they also achieve greater power in the evaluation of
individual arms. The benefit depends on how many treatments are actually
enrolling concurrently. The more enrolling treatments, the greater the benefit
as less control data is required compared to the traditional approach. To
allow the testing of more treatments, interim futility analyses should be
performed to eliminate treatments that have either no or negligible treatment
effects.

## Funding

EU-PEARL (EU Patient-cEntric clinicAl tRial pLatforms) project has received
funding from the Innovative Medicines Initiative (IMI) 2 Joint Undertaking
(JU) under grant agreement No 853966. This Joint Undertaking receives support
from the European Union’s Horizon 2020 research and innovation programme and
EFPIA and Children’s Tumor Foundation, Global Alliance for TB Drug Development
non-profit organisation, Springworks Therapeutics Inc. This publication
reflects the authors’ views. Neither IMI nor the European Union, EFPIA, or any
Associated Partners are responsible for any use that may be made of the
information contained herein.
MMF additionally received funding from the German Research Foundation (Project
number RA 2347/11-1).

## Acknowledgements

The authors are grateful to the EU-PEARL investigators who contributed to the
development of the MDD master protocol. The EU-PEARL MDD investigators are:
Jelena Brasanac, Woo Ri Chae, Michaela Maria Freitag, Stefan Gold, Eugenia
Kulakova, Christian Otte, Dario Zocholl (Charité - Universitätsmedizin
Berlin), Marta Bofill-Roig, Elias Laurin Meyer, Franz König, Martin Posch
(Medizinische Universität Wien), Heidi de Smedt, Yanina Flossbach (Janssen
Pharmaceutica NV), Melissa Kose, Giulia Lombardi, Carmine Pariante, Luca
Sforzini, Courtney Worrell (King’s College London), Tasneem Arsiwala,
Alexandra Bobirca (Novartis Pharma AG), Fernanda Baroso de Sousa, Pol Ibanez-
Jimenez, Gabriela Perez-Fuentes, Toni Ramos-Quiroga (Fundació Hospital
Universitari Vall d´Hebron – Institut de Recerca), Witte Hoogendijk (Erasmus
Universitair Medisch Centrum Rotterdam), Francesco Benedetti (Universita Vita-
Salute San Raffaele), Fanni Laura Mäntylä (GAMIAN-Europe)

## Author contributions

Conceptualization: MMF, DZ, SMG, MP, FK
Methodology: MMF, DZ, MP, FK
Software: MMF, DZ, ELM
Conduct of simulation study: MMF
Supervision: SG, MP, FK
Validation: FK
Visualization: MMF
Writing – original draft: MMF, FK
Writing – review & editing: MMF, DZ, ELM, SMG, MBR, HDS, MP, FK

## Conflict of interest

ELM is a salaried employee of Berry Consultants. SMG reports honoraria from
Hexal and Streamed-up. All other authors did not report any conflict of
interest.

## Data availability statement

The R code is made publicly available on Github [27].

## ORCID

Michaela Maria Freitag https://orcid.org/0009-0009-0924-1277
Dario Zocholl https://orcid.org/0000-0002-9218-6919
Elias Laurin Meyer https://orcid.org/0000-0001-5398-6334
Stefan M. Gold https://orcid.org/0000-0001-5188-4799
Marta Bofill Roig https://orcid.org/0000-0002-4400-7541
Martin Posch https://orcid.org/0000-0001-8499-8573
Franz König https://orcid.org/0000-0002-6893-3304

##  6 Bibliography

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