EMA CHMP方法学工作组发布确证性平台试验方法学反思文件草案（EMA/217509/2026）并公开征求意见
Reflection paper on methodological aspects in confirmatory platform trials
EMA CHMP方法学工作组发布《确证性平台试验方法学反思文件》草案（EMA/217509/2026），于2026年10月19日启动公开征求意见，截止2027年1月31日。草案聚焦对照选择、随机化、盲法与适应性设计等平台试验特有要素，讨论其对偏倚、I类错误及内外部有效性的影响，旨在补充而非替代现有多重性与适应性设计指南。
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1 05 October 2026
2 EMA/217509/2026
3 Committee for Medicinal products for Human Use (CHMP)/Methodology Working Party
4 Reflection paper on methodological aspects in
5 confirmatory platform trials
6 Draft
Draft agreed by Methodology Working Party 20 August 2026
Adopted by CHMP for release for consultation 5 October 2026
Start of public consultation 19 October 2026
End of consultation (deadline for comments) 31 January 2027
7
Comments should be provided using this EUSurvey form. For any technical issues, please contact
the EUSurvey Support
8
Keywords Platform trials, multiplicity, non-concurrent controls, adaptive
design, randomisation
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11 Reflection paper on methodological aspects in
12 confirmatory platform trials
13 Table of contents
14 Purpose and Scope ............................................................................................................. 3
15 Relevant guidelines ............................................................................................................ 4
16 Key methodological topics in platform trials .......................................................... 4
17 Pre-specification .............................................................................................................................................. 4
18 Randomisation ................................................................................................................................................. 5
19 3.2.1. Allocation ratios and probabilities ........................................................................................................... 5
20 3.2.2. Multi-stage randomisation ......................................................................................................................... 6
21 3.2.3. Re-randomisation of participants ............................................................................................................ 6
22 Controls .............................................................................................................................................................. 7
23 3.3.1. Common controls .......................................................................................................................................... 7
24 3.3.2. Concurrent versus non-concurrent controls........................................................................................ 8
25 3.3.3. Change in control treatment ..................................................................................................................... 8
26 Blinding .............................................................................................................................................................. 9
27 3.4.1. Unblinding during study conduct ........................................................................................................... 10
28 Type I error control ..................................................................................................................................... 10
29 3.5.1. Requirements for strong FWER control ............................................................................................... 11
30 3.5.2. Risk of multiple false-positive decisions ............................................................................................. 11
31 3.5.3. When confirmatory hypotheses can be separated into unrelated families ........................... 11
32 3.5.4. Pre-specification of testing strategy and objectives ...................................................................... 12
33 Trial operating characteristics ................................................................................................................. 12
34 3.6.1. Power and sample size .............................................................................................................................. 12
35 3.6.2. Further operating characteristics .......................................................................................................... 12
36 Estimands ........................................................................................................................................................ 13
37 Complexity from Multiple Features ........................................................................... 13
38
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39 Purpose and Scope
40 Platform trials have become more common over recent years and are likely to play an increasingly
41 important role in marketing authorisation applications. Design elements, which frequently occur in
42 platform trials, such as adaptive designs and common controls increase the complexity in planning,
43 conduct and reporting of clinical trials. This makes dedicated guidance necessary to enable adequate
44 planning and assessment of platform trials such that they can be used as confirmatory trials. In this
45 reflection paper aspects specific to or highly prevalent in platform trials are highlighted. Their impact
46 on the reliability of the results in terms of bias, type I error, and internal, as well as external, validity is
47 discussed. These aspects include the choice and definition of controls, randomisation, blinding and
48 adaptive design elements. The aim of this reflection paper is to complement existing guidance
49 documents, e.g. on multiplicity and adaptive designs, not to replace or revise them.
50 For the purpose of this reflection paper, we define “platform trial” as the generic term for a multi-arm
51 clinical trial, which is executed as a single clinical trial but may address more than one primary
52 objective with the following key elements:
53 Multiple treatments are investigated within one trial in separate experimental arms in a
54 single target population.
55 Randomisation is used for treatment allocation. Randomisation probabilities may change over
56 time, e.g. due to a changing number of experimental arms.
57 Treatments are compared to a control. This may be implemented through either a comparison
58 to a common, shared control arm or to separate control arms for each treatment.
59 Arms may be added or terminated at different times, and there can be multiple analysis
60 time points. A multi-arm trial with all arms starting and ending at the same time can be
61 considered a platform trial as well.
62 In a platform trial, all objectives are preferably specified under a single protocol, which may sometimes
63 be referred to as a master protocol. However, the definition of a master protocol is wider than that of
64 platform trial in this reflection paper. It may encompass multiple protocols, each corresponding to a
65 sub-study, which are grouped under a single protocol for administrative and/or logistical purposes, that
66 could potentially stand alone as separate studies. In this reflection paper the term protocol will be used
67 throughout the document regardless of how the protocol is structured (i.e., if it is specified in one or
68 multiple documents). For these reasons, the term master protocol with the more general definition is
69 not used in this reflection paper. These operational aspects and aspects related to clinical trial
70 applications are not of relevance for the methodological considerations but are discussed elsewhere
71 (see Section 2. ).
72 The aim of this reflection paper is to describe under which concrete circumstances and methodological
73 constraints platform trials can provide reliable evidence for regulatory decision-making. The primary
74 focus of this reflection paper is on confirmatory trials, i.e., trials that are designed to provide pivotal
75 evidence for regulatory decision making. Other trials with similar design features and exploratory
76 platform trials are not explicitly in scope, although they may share the same key characteristics and
77 hence benefit from these considerations as well. Key methodological topics and design features of
78 relevance in platform trials to guide study planning, protocol development, conduct of study and
79 analyses of results are discussed, with the aim to obtain reliable results to support regulatory decision
80 making.
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81 Relevant guidelines
82 All general guiding principles for clinical trials naturally apply to platform trials as well, and should be
83 considered during planning, conduct and analysis of clinical trials. More specifically, this reflection
84 paper needs to be read in conjunction with the following methodological regulatory guidelines:
85 • ICH E9: Statistical principles for clinical trials (CPMP/ICH/363/96)
86 • ICH E10: Choice of Control Group in Clinical Trials (CPMP/ICH/364/96)
87 • ICH E20: Adaptive designs for clinical trials (EMA/CHMP/ICH/206586/2025)
88 • Reflection paper on methodological issues in confirmatory clinical trials planned with an
89 adaptive design (CHMP/EWP/2459/02)
90 • Multiplicity issues in clinical trials (EMA/CHMP/44762/2017)
91 • Guideline on data monitoring committees (EMEA/CHMP/EWP/5872/03 Corr)
92 • Questions and answers on data monitoring committees’ issues (EMA/CHMP/470185/2020)
93 Operational or clinical trial application aspects will not be covered in this reflection paper. Please refer
94 to the Complex clinical trials Q&A (EMA/298712/2022) and the following guidance:
95 • Recommendation Paper on the Initiation and Conduct of Complex Clinical Trials (hma.eu)
96 • Frequently asked questions on Complex Clinical Trials and CTIS (hma.eu)
97 Key methodological topics in platform trials
98 Pre-specification
99 Since platform trials are complex to design and conduct, additional efforts are required at the planning
100 stage to consider all relevant aspects. It is crucial that the objectives, estimands and the overarching
101 testing strategy in the platform trial are thoroughly documented at the start of the study as far as
102 possible. This documentation is essential to confirm that the design corresponds to the objectives and
103 to determine over which hypotheses the type I error has to be controlled. If new arms with potentially
104 new estimands, new specific analyses strategies or new objectives are foreseen to enter a platform
105 trial over time, these should be described and justified as early and as thoroughly as possible.
106 Adherence to these pre-specifications is of particular importance in a highly complex and adaptive trial
107 design. Modifications at a later point in time might potentially be data-driven. It usually is very hard or
108 even impossible to prove the opposite. Lack of pre-specification could render a confirmatory platform
109 trial as exploratory only.
110 Examples of aspects that are specific to platform trials, and require clarity and justification, include:
111 • The definition of all primary objectives and primary estimands;
112 • The subset of the total study data that will be utilized to inform each objective;
113 • The strategy for adapting the trial design based on emerging data, including criteria for adding
114 or removing arms;
115 • The approach to handling the multiple primary objectives and controlling type I error rates in
116 the platform trial;
117 • The timing of analyses (interim and primary analyses) for all objectives.
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118 Randomisation is a key element of statistical methods in clinical trials. It facilitates valid causal
119 inference and indirectly accounts for known and unknown prognostic factors. Together with blinding it
120 helps to conceal treatment allocation. Hence, randomisation is vital to avoid or reduce bias and forms a
121 basis for valid statistical inference and confirmatory analyses (see ICH E9, ICH E10). ICH E9 states
122 that the unique pre-planned assignment of treatment, or treatment sequence, to subject should be
123 clear, and that the randomisation schedule should be reproducible. In platform trials, some aspects of
124 randomisation are more complex, e.g., due to potential changes in the number of experimental arms.
125 Hence, it may not be possible to fully pre-specify the randomisation plan in advance. Nevertheless, the
126 principles of the randomisation procedure should be specified before study start and all details carefully
127 documented during study conduct. The high-level principles essential for understanding the approach
128 should be included in the protocol and the specific details documented in a “randomisation plan” or
129 equivalent. In general, circumstances under which the clinical trial is conducted evolve over time. This
130 potentially affects e.g. the clinical experience with a specific treatment, and the population enrolled to
131 a clinical trial. This is true for any trial, but particularly relevant in a platform trial context which
132 typically has an increased duration. The trial itself can also be altered, e.g., through a change of the
133 enrolling experimental arms during the trial, changing allocation ratios or even changing the control
134 arm, which may complicate the interpretation.
135 The population enrolled in the trial might be impacted by a participant’s willingness to participate
136 depending on changes in allocation probabilities, such as an increased likelihood of being randomised
137 to active treatment, or on changes in available treatments, for instance by the introduction of a
138 particularly promising treatment or a medicinal product with an expected high risk of side effects.
139 Thus, selection bias may be induced and may change over time. Randomisation may help to overcome
140 the induced issues of these fluctuations to some extent if only concurrently generated groups of
141 participants are compared (see Section 3.3.2. ). This is also pointed out in ICH E10 in general, and the
142 Complex clinical trials Q&A (EMA/298712/2022) in specific, “randomised controlled clinical trials with
143 an internal concurrent control arm are considered the standard in trial design where appropriate and
144 feasible". While randomisation addresses the issue of causal interpretation and isolation of a treatment
145 effect, it is worth noting that changes in circumstances within a clinical trial over time may complicate
146 and even compromise the interpretability of the treatment effect.
147 Randomisation
148 3.2.1. Allocation ratios and probabilities
149 Changes in allocation probabilities can occur for several reasons but in platform trials this issue arises
150 specifically due to the addition and removal of arms. In a platform trial, the relevant comparison is
151 typically between an experimental arm and a control arm within the trial. Thus, the allocation ratio
152 between these arms within the trial is central to the inference. Allocation ratios should ideally be
153 held constant for all comparisons of interest, even when the allocation probabilities are changed by
154 adding or dropping experimental arms. If the allocation ratio is constant for a comparison of interest,
155 standard inference applies. Equal allocation to all arms, i.e., 1: . .. ∶ 1 allocation, is a common choice to
156 achieve this. Complexity is added if the study design causes the allocation ratios to change over time.
157 The choice of allocation ratio may also depend on other factors, such as the need for sufficient safety
158 data for the medicinal products under investigation. Depending on the trial design and purpose, more
159 efficient allocation ratios than equal allocation exist. The square root allocation first introduced by
160 Dunnett is one example of an allocation rule for multiple comparisons to a single control. It is given by
161 allocating subjects with a ratio of 1: √𝑘𝑘 to each experimental arm and the control arm, where k is the
162 number of experimental arms, resulting in an allocation of 1: . .. ∶ 1: √𝑘𝑘). This reduces the correlation of
163 test statistics and increases power. While this allocation rule might be beneficial in platform trials with
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164 a fixed number of arms and without any adaptations over time, this is not always the case in adaptive
165 platform trials, as it is desirable to keep allocation ratios constant over time for each comparison of
166 interest.
167 Not only the allocation ratio but also the choice of the adequate randomisation scheme requires special
168 attention in platform trials. For instance, block randomisation, which is the most common
169 randomisation method, might cause challenges. With multiple arms the block size may become
170 unpractically large, especially with a small number of participants. This means that the block
171 randomisation becomes a simple, unconstrained randomisation approach and the desired allocation
172 balance between arms might suffer to an unknown extent. Furthermore, when square root allocation is
173 used, standard block randomisation may not even be feasible. Another example is the use of dynamic
174 randomization methods such as minimisation. In this case, the addition or removal of arms adds
175 further complexity to an already complex method and may have consequences for statistical inference.
176 Hence, such approaches are usually discouraged in platform trials. Operational implementation of the
177 randomisation scheme must be thoroughly considered.
178 Changes in allocation ratios over time can in theory be addressed in the statistical analysis, for
179 example using an analysis stratified by time periods, which are defined by the different randomisation
180 ratios. However, some design features may add too much complexity, making it difficult or impossible
181 to properly adjust for changes in the allocation ratio in the analysis. For this reason, it is recommended
182 to keep the allocation ratios for each comparison of interest fixed. Consequently, (response) adaptive
183 randomisation (RAR) is not supported.
184 3.2.2. Multi-stage randomisation
185 Randomisation might also be conducted in two (or more) stages. In the first stage, participants are
186 randomised to a group of treatments, e.g. based on route of administration. In the second stage,
187 participants are randomised to either the treatment (or one of the treatments) or control in that group.
188 The rationale for multi-stage randomisation is of relevance to understand its implications to study
189 conduct and the statistical analysis and should be included in the protocol.
190 Where all participants are eligible for all treatments, and two-stage randomisation is applied solely for
191 operational purposes (e.g. to facilitate partial blinding), the resulting allocation process is otherwise
192 equivalent to a standard randomisation approach. In that case, concurrently enrolled controls might be
193 pooled, if all aspects of study conduct are identical for all participants, in aspects key to the objectives.
194 However, differences may occur even if the study conduct is the same. For example, the expectations
195 of participants may differ for different groups of treatments, thus, potentially leading to different
196 placebo effects or different dropout patterns. An upfront discussion of these aspects is needed together
197 with a plan to assess the similarity of randomisation groups if pooling across different groups is
198 planned. The latter might be difficult due to the small sample size in each of the control arms. If other
199 reasons apply, e.g. as inclusion or exclusion criteria differ for different treatment options, the control
200 arm of one treatment may not be representative in a comparison to another treatment and control
201 arms cannot be pooled in most scenarios. See further discussion below in Section 3.3.1. .
202 3.2.3. Re-randomisation of participants
203 Due to the possible longer duration, the multiple treatment options and the dynamic nature of a
204 platform trial, the possibility to re-randomise participants might be considered by the sponsor. Re-
205 randomisation adds further complexity to the trial. It usually changes the questions that can be
206 answered (and hence impacts the indication). It may lead to situations where the new target
207 population is difficult to define, as re-randomised participants had previously been treated with non-
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208 marketed, experimental treatments. It might further induce statistical dependency issues and bias in
209 the estimated treatment effect for the target population. Hence, it is usually discouraged in a
210 confirmatory setting, and if planned to be used, it should be well justified, also on methodological
211 grounds, before being implemented and would need to be pre-specified in the protocol before study
212 start. Furthermore, the process related to the re-randomisation in terms of conditions for when it
213 might be applicable as well as methodological considerations should be pre-specified and well
214 described in the protocol.
215 Controls
216 The choice of a control arm is of fundamental importance as it defines which questions can be
217 answered. Guidelines relevant to choice of control arm such as ICH E10 apply. A platform trial may
218 provide answers to multiple questions concerning different treatments and, hence, the definition of
219 controls is more complex in platform trials than in standard two-arm randomised controlled trials,
220 given that multiple experimental arms are included. This leads to different options to define the control
221 arm for a specific comparison:
222 1) use a separate, independent control arm for each of the experimental arms that address a specific
223 comparative objective,
224 2) use a common control arm for all experimental arms together, or
225 3) use combinations or variants of these two options.
226 Another distinct aspect in platform trials is that randomisation is typically open only to certain arms at
227 a given point in time. In particular, enrolment into a control arm may be open for longer than
228 enrolment into the respective experimental arm. Concurrent and non-concurrent controls are discussed
229 in Section 3.3.2. .
230 3.3.1. Common controls
231 One of the most relevant and typical features of platform trials is the use of a common control arm,
232 which is also referred to as a shared control arm. Rather than randomising subjects to either an active
233 treatment or a dedicated control treatment (or placebo) on a per treatment basis, one randomly
234 allocates subjects to any of the enrolling experimental arms or to the shared control arm. This may
235 allow to achieve the same power to detect a specific treatment effect (marginal power) with less
236 subjects overall compared to separate controls for each treatment (see Section 3.4. ) and to treat
237 fewer subjects with the control treatment. However, the use of a common control arm will also lead to
238 correlation between the test statistics of the different comparisons, which increases the probability of
239 drawing simultaneous multiple false conclusions, while leading to a lower probability of at least one
240 false-positive rejection within the trial. This is discussed in Section 3.5.2. .
241 A sometime proposed approach is to randomise to a matching control treatment per experimental arm
242 and to pool the control arms for the primary analyses. Independent controls may be justified through
243 operational aspects as discussed in Section 3.2.2. , and if they are planned to be pooled, it is
244 paramount to discuss potential differences induced by different control treatments already at the
245 planning stage. In general, any differences in study conduct, such as the schedule of assessments, are
246 usually issues that prevent pooling.
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247 3.3.2. Concurrent versus non-concurrent controls
248 Concurrent controls are here defined as subjects in the control arm who have a positive probability to
249 be randomised to the experimental arm of interest at the time of randomisation. In practice, this
250 means that participants were all randomised at the same time and were eligible to be randomised to
251 the arms with respect to inclusion/exclusion criteria and participants provided informed consent for all
252 arms. A strong preference is given to concurrent controls as this enables that a causal conclusion can
253 be achieved without additional assumptions. Another advantage is that it may reduce the correlation
254 between test statistics, as it limits the overlap of the respective participants in the control arm used to
255 calculate the test statistics. If the trial is blinded, it might additionally help to mitigate practical issues
256 with blinding as discussed in Section 3.4. .
257 It is acknowledged, though, that unique situations exist where it might be acceptable to increase the
258 power by using non-concurrent controls. This needs to be pre-planned and well justified in the trial
259 protocol. Methods to reduce the temporal bias should be pre-specified as early as possible (see Section
260 3.1) together with supplementary and sensitivity analyses to assess the impact of the underlying
261 assumptions. These additional analyses should include other adjustment methods, and analyses solely
262 based on concurrent controls. Given the strong reliance on untestable assumptions, non-concurrent
263 controls are usually not acceptable for the primary analysis of the primary endpoint and are more
264 suitable for supplementary analyses or potentially for secondary endpoints. This approach might be
265 especially relevant for trials with primary endpoints which can be shown with sufficient power based on
266 concurrent controls, but where important secondary endpoints exist that are rarely observed.
267 External controls, i.e. data from other sources than the platform trial, are not specifically discussed in
268 this reflection paper. While the most reliable approach is to use concurrent controls, internal, non-
269 concurrent controls in platform trials would be preferred compared to external controls. The reason is
270 that non-concurrent controls within a platform trial were enrolled under the same protocol and hence
271 share many commonalities. Hence, assumptions required to augment concurrent controls and to
272 enable valid inference may be more plausible when trial conditions are governed by a common
273 protocol, leading in general to less bias. Temporal drifts or time bias might exist but attempts to model
274 the temporal changes are possible using other experimental arms, if overlapping with both concurrent
275 and non-concurrent controls.
276 3.3.3. Change in control treatment
277 In platform trials it is sometimes planned to change a treatment which met its primary endpoint within
278 the platform trial to become the new control treatment. The presented rationale for this adaption is
279 that the standard of care and, hence the scientific question of interest, has changed. While this may in
280 principle be understandable, it comes with various issues.
281 First, the fact that efficacy was shown for a new treatment does not mean that a positive benefit-risk
282 profile of the new treatment has been established and that the product will eventually be authorised.
283 Benefit-risk decisions require a careful analysis and assessment process. Only after a treatment has
284 been authorised, one could consider it as the new control, in order to not expose the trial participants
285 to unnecessary risk, but also not to hamper the clinical interpretation of the results. Exceptions from
286 this rule may apply in exceptional circumstances.
287 Second, a change in control treatment introduces substantial statistical issues and might compromise
288 the interpretation of trial results. The primary analysis and related operating characteristics, including
289 the sample size, for all arms currently ongoing in the trial may require modification. Furthermore, it is
290 not evident whether the initial control arm would be combined with the new control arm, or whether
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291 they would be assessed separately. The former is methodologically difficult and hampers the
292 interpretability of the derived results, since the effect before and after the modification must be taken
293 into account. It is also very difficult to pre-specify such changes and to control the type I error. The
294 latter approach leads to power issues and may not be considered adequate as not all enrolled
295 participants are used (equally) to support the objectives and decision making.
296 Hence, the control arm should be changed only in very exceptional circumstances. This principle
297 applies universally to all changes to the control regardless of trial phase. In exploratory trials
298 methodological issues might be less critical. However, it is likely to be questionable whether an
299 unauthorized treatment is safe and efficacious when it only met the trial objectives in an exploratory
300 trial and whether it could hence serve as a new control treatment. Therefore, it may be even less
301 appropriate to promote an experimental treatment to become the new control treatment in exploratory
302 trials.
303 Hence, for all the aforementioned reasons, it is discouraged to change the control treatment for arms
304 that have already started enrolling. If it cannot be avoided to change the control arm, usually a new
305 trial would be the preferable option. However, it may be justified to define a different control arm from
306 what was initially planned in the protocol for newly planned experimental arms which have not yet
307 started, if the standard of care for that specific indication has changed during the ongoing clinical trial.
308 Blinding
309 If the trial includes multiple test groups that are to be compared to a common control group, and
310 blinding is to be achieved for all comparisons, this requires that the subjects are blinded with respect
311 to all the groups that they could have been randomised to. While this is in theory possible by
312 performing a multiple-dummy type of blinding procedure, where participants receive placebo treatment
313 for all experimental arms that they do not belong to, such a procedure may be too burdensome for the
314 participants.
315 If experimental arms start at different time points this adds additional complexity to the blinding
316 procedure. Since participants have the right to know the potential treatments they may be randomised
317 to, blinding is only possible against arms that the participant is eligible for at the time of
318 randomisation.
319 A compromise may be to partially blind the trial. For example, participants will know their allocation to
320 a specific route of administration or even a specific treatment/control comparison but remain blinded
321 regarding their allocation to treatment or the corresponding control. They will know, however, that
322 they were not allocated to another route of administration, or another treatment and the
323 corresponding control treatment. Operationally, this can be achieved with a 2-stage randomisation
324 process (see also Section 3.2.2. ). Pooling of concurrently enrolled control arms may then be possible
325 upon justification (see Section 3.3.1. ).
326 Open-label trials are prone to operational bias. Hence, if the trial is conducted open label, it is
327 important to ensure that the protocol is adhered to. As platform trials often include adaptive features
328 and go through design changes while the trial is ongoing, it is particularly important to ensure that
329 these are not motivated by information stemming from the open-label nature. Regardless of whether
330 participants and local investigators are blinded, measures to blind the central study team should be
331 pre-specified in the protocol and/or a dedicated blinding plan. Clear rules for data access and decision
332 making should be in place. An independent data monitoring committee (DMC) is generally
333 recommended but might not be sufficient to solve all issues.
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334 3.4.1. Unblinding during study conduct
335 In platform trials, the primary analyses for the various primary objectives may be conducted at
336 different points in time, which may introduce bias and compromise the integrity of the study. The
337 main reason for this is partial or full unblinding of the shared control arm results and potentially also of
338 the results of other experimental arms. If subsequent adaptations of the trial use this information,
339 either implicitly or explicitly, without adequate pre-specification, this could lead to a type I error
340 inflation and biased results. Hence, great care should be taken to maintain blinding as much and as
341 long as possible and to fully pre-specify the study conduct as far as possible.
342 When data is planned to be analysed at the participant level and on aggregated level during the trial, it
343 is recommended to plan the trial such that as many evaluations and decisions as possible remain
344 blinded to participants, site personnel and sponsor. It will usually be expected that an independent
345 DMC is implemented (see Guideline on data monitoring committees, EMEA/CHMP/EWP/5872/03 Corr,
346 and Questions and answers on data monitoring committees issues, EMA/CHMP/470185/2020), an
347 adequate firewall to shield the decision makers in the trial team is in place, and that maintaining full
348 blinding until all concurrently recruiting experimental arms are completed is considered. Having
349 different analysis teams or even different study teams for different interventions studied in the
350 platform trial might further help to limit data leakage possibilities. Importantly, it should be
351 acknowledged that maintaining the study integrity is not always possible. It is not a realistic
352 expectation that results are not known if parts of the trial are submitted for Marketing Authorisation or
353 published elsewhere when other parts are still ongoing. This may compromise robustness of the
354 results and impact their reliability for regulatory decision making.
355 Note that in platform trials with time-to-event endpoints and event-driven analyses additional care is
356 needed. In this case, even the availability of standard monitoring information such as the pooled
357 number of events for one specific intervention and its concurrent control might lead to unblinding and
358 data leakage, as events could be attributed to each arm if multiple arms run concurrently. In that case,
359 it might be preferable to blind the study teams to the accrual of events and only report the projected
360 analysis times to the teams, while tasking external parties with the actual monitoring of the event
361 accrual and updates of the projected analysis times.
362 The above-mentioned measures may help to avoid or at least reduce the leakage of data. If data
363 leakage cannot be fully excluded, further measures might be required to reduce the impact of data
364 leakage on the conduct of study and the robustness and credibility of results. For example, one could
365 consider requiring that analyses are conducted at the same time for all concurrently running arms,
366 which essentially means possibly postponing the analysis time point.
367 Furthermore, any protocol amendments, in particular after some results have already become
368 available, require a strong justification in order not to compromise the integrity of the ongoing parts of
369 the platform trial.
370 Some of these sources of bias and risks to study integrity cannot be fully mitigated, as they are
371 integral to the motivation to conduct a platform trial. Therefore, such designs may only be feasible in
372 settings where objective endpoints can be used, and good study conduct and participant adherence
373 can be ascertained.
374 Type I error control
375 This section aims to determine under which conditions Family-Wise Error Rate (FWER) control across
376 the hypotheses related to all primary objectives may or may not be necessary in platform trials to
377 support confirmatory claims. Additional points of attention with multi-arm trials performed to generate
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378 evidence in support of more than one regulatory decision, such as the increased risk of multiple false-
379 positive decisions, i.e., wrongly rejecting multiple null hypotheses, are also discussed.
380 3.5.1. Requirements for strong FWER control
381 The consequences of multiplicity in platform trials are determined by the overall question(s) the trial is
382 intended to answer and the (regulatory) decisions it may lead to and requires a prospective, multi-
383 disciplinary justification. In platform trials strong FWER control (see Guideline on multiplicity issues in
384 clinical trials; EMA/CHMP/44762/2017) is not required by default across all hypotheses. However,
385 strong FWER control is required across hypotheses that are related to the same overall question and
386 the corresponding conclusions contributing to a regulatory decision.
387 3.5.2. Risk of multiple false-positive decisions
388 In every instance where there is more than one comparison, one carries the risk of drawing multiple
389 erroneous decisions (simultaneously). It has been shown that trials comparing multiple treatments to a
390 common control reduces the risk of at least one erroneous conclusion, as measured by the FWER,
391 compared to a platform trial with individual control arms for each experimental arm (when in both
392 scenarios no multiplicity adjustment is used). The latter trial scenario has the same error distribution
393 as separate independent trials that compare each treatment to an individual control group. From the
394 perspective of FWER control, a platform trial with a common control arm hence seems preferable.
395 However, using a common control increases the probability of drawing multiple erroneous conclusions
396 at the same time, as measured by the k-FWER with k ≥ 2. This is due to the correlation between the
397 test statistics. The expected number of false conclusions per family remains the same.
398 Controlling this potential increase in the risk of multiple false-positive errors is technically possible by
399 imposing stricter limits on the individual significance level associated with each experimental arm.
400 However, doing so would require stringent thresholds which may be more conservative than a
401 Bonferroni correction. An alternative to reduce the risk of multiple false-positive errors is to increase
402 the sample size in the control arm. A second confirmatory trial in the same or a similar setting,
403 potentially with different objectives, will usually be the best option to counter the issue of (multiple)
404 false-positive errors and bias. Additionally, it improves the overall strength of evidence when the trials
405 relate to the same treatment.
406 3.5.3. When confirmatory hypotheses can be separated into unrelated
407 families
408 Two conclusions from comparative hypothesis tests contributing to regulatory decisions are here
409 considered unrelated if the outcome of one comparison should have no influence on the outcome of the
410 other; correspondingly, hypotheses are considered unrelated if the outcome of the statistical test
411 regarding one hypothesis has no impact on the evaluation, interpretation, or regulatory decision
412 associated with the other. In other words, knowledge of the outcome of one hypothesis test does not
413 directly influence the conclusion, and related regulatory decision of the other one.
414 The most straightforward examples are as follows:
415 • If the two experimental arms in a pivotal trial are different doses of the same medicine, with
416 the aim of choosing at least one dose to be included in the label, the hypotheses are related.
417 • If the two experimental arms are two new active substances compared against a control arm
418 and the decision to license one of them is made independent of the results of the other one,
419 the hypotheses concerning the efficacy of either active substance are unrelated.
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420 Unlike statistical independence, the relatedness of hypotheses is not a mathematical property.
421 Unrelatedness, therefore, is based on the clinical context and the overall rationale of the clinical trial,
422 which is reflected in the design, objectives and experimental arms and hypotheses of interest. The
423 relatedness of hypotheses essentially refers to the question of whether the hypotheses refer to a
424 common “overarching hypothesis” that is reflected in the corresponding regulatory decision. In most
425 scenarios, hypotheses concerning the same active substance are related, because in most situations
426 the relevant regulatory decision will be at the active substance level.
427 If the hypotheses tested in a trial can be separated into families of unrelated hypotheses, the control of
428 the type I error rate may not necessarily be required across families. Yet, for hypotheses within a
429 given family the usual criterion, i.e., the need for strong FWER control, applies.
430 3.5.4. Pre-specification of testing strategy and objectives
431 As discussed in Section Error! Reference source not found., the overarching objectives, overarching
432 testing strategy, and a plan for how the results will be used, need to be clearly pre-specified and
433 described in the protocol. This pre-specification is essential and must be justified in relation to the
434 corresponding regulatory decisions they intend to inform. If any such information is missing in the
435 protocol, it is usually not possible to determine if the hypotheses can be separated into distinct
436 ‘families’ of unrelated hypotheses. Generally, this omission implies that FWER control will be necessary.
437 Trial operating characteristics
438 3.6.1. Power and sample size
439 The significance level depends on the specifics of the platform trial and naturally impacts the power
440 and sample size. In addition to that, power and sample size require additional attention in a platform
441 trial as there is more than one type of power. The marginal power is the power to reject a specific
442 hypothesis test. This is the standard power definition as used in other trials as well. In addition, the
443 disjunctive power is defined as the probability to reject at least one false null hypothesis, and the
444 conjunctive power is defined as the probability to reject all false null hypotheses. The relevance of each
445 of these definitions depends on the objectives of the trial. Thus, power and sample size always need to
446 be justified based on the relevant power definition(s).
447 The use of common controls impacts the power and sample size beyond the impact of the significance
448 level. For a specific targeted conjunctive power usually a smaller overall sample size is needed in a
449 platform trial with shared controls than in a trial with independent controls (or in separate trials). The
450 same is true for the marginal power due to the common control. To reach a specific disjunctive power,
451 however, a platform trial with shared controls usually needs a larger sample size than with individual
452 controls. This needs to be considered at the design stage as well.
453 Hence, a sample size justification for a platform trial should explicitly define which power is targeted
454 and whether the correlation between the test statistics was considered. The overall power and sample
455 size justification should be aligned with the overall objectives and multiplicity strategy as discussed in
456 Section 3.5. .
457 3.6.2. Further operating characteristics
458 In addition to the type I error rate (Section 3.5. ) and the different possible definitions of power
459 (Section 3.6.1. ), further operating characteristics should be considered in a platform trial. These
460 include plausible platform trial trajectories, including arm entries and discontinuations, number of arm
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461 open for recruitment at any given time point, recruitment rates over time, the impact of shared
462 controls (Section 3.3.1. ), the expected sample size per arm, the expected overall sample size, the
463 expected duration of each arm, and the expected overall trial duration. It is important to fully
464 characterize the relevant operating characteristics in the protocol to allow for comprehensive
465 regulatory assessment. For this purpose, simulations may be required and should be included in the
466 protocol as appropriate.
467 Estimands
468 The concept of estimands, as formalised in the International Council for Harmonisation E9(R1)
469 guideline, is essential for ensuring clarity in the definition of treatment effects in clinical trials, including
470 complex designs such as platform trials. The estimand definition(s) should correspond to and be
471 consistent with the overarching study objectives and hypothesis testing strategy outlined in the
472 protocol. By explicitly specifying the population, treatment (at least, intervention and comparator),
473 variable, and handling of intercurrent events, the estimand framework provides a structured approach
474 to align trial objectives with the scientific questions of interest. This is particularly important in
475 platform trials, because there are multiple primary objectives and, hence multiple estimands, and it
476 may need to be carefully considered for each estimand if it can be appropriately assessed with a study
477 design where, e.g., experimental arms may be added or dropped, or the target population might
478 evolve. Within a platform trial, each experimental arm is typically associated with its own estimand,
479 reflecting a specific clinical objective; while these estimands may share common components, such as
480 the target population, they may differ in other attributes depending on the scientific question. There
481 may be differences in intercurrent events between the arms, for example due to fundamental
482 differences in treatment regimens. These require particularly careful description and justification.
483 Ensuring transparency across these related estimands is critical. Furthermore, in the rare exemptions
484 where the control arm changes over time (for example, due to the emergence of a new standard of
485 care), careful consideration is needed to preserve interpretability: estimands may need to be
486 prospectively defined in a way that is robust to such changes (e.g., referencing a class of control
487 treatments), or alternatively, new or revised estimands may be introduced to reflect the updated
488 comparison. In all cases, clear documentation of how estimands evolve alongside the trial is essential
489 to maintain the validity and interpretability of the trial results.
490 Complexity from Multiple Features
491 While platform trials may be suitable for regulatory decision making, it is important to ensure that their
492 results are sufficiently robust and can be unambiguously interpreted for the specific treatment that is
493 subject of decision making. Trials incorporating more complex design features and operational
494 requirements are inherently more challenging to assess.
495 Therefore, the assessment whether a platform trial provides confirmatory evidence is based on a
496 holistic evaluation of all the methodological and operational aspects and their interdependencies. In
497 other words, while design or operational features may be justifiable and acceptable in isolation, their
498 complex interplay contributes to increase uncertainty and is, hence, of relevance and requires specific
499 attention. For instance, design modifications while the trial is ongoing may make pre-specification of
500 the overall objective challenging and consequently, corresponding multiplicity and sample size
501 considerations difficult. Or as an alternative example, multiple primary analyses at different points in
502 time in an (open-label) platform trial may compromise the study integrity and introduce substantial
503 bias. Depending on the circumstances, the combination of the design elements may render a clinical
504 trial initially planned as confirmatory an exploratory trial. Simpler designs are preferred if no
505 substantial advantage can be expected with a complex design. Therefore, all relevant aspects should
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506 be discussed, addressed and justified at the planning stage to allow for a comprehensive regulatory
507 assessment.
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来源：EMA Scientific Guidelines · ema.europa.eu