Show the R code
tab <- platform_shared_control_table(2:6, m = 80)
knitr::kable(tab, digits = 3, align = "rrrr",
col.names = c("Drugs tested", "Patients, separate trials", "Patients, shared control", "Fraction saved"))20 Master Protocols and Platform Trials
A conventional program builds a trial, answers one question, and takes the trial down. The site contracts, the database, the randomization system, the monitoring board and the regulatory file are all rebuilt for the next drug. A master protocol keeps that machinery standing and lets questions pass through it. The idea is not new, and it is not Bayesian. The UK prostate cancer platform STAMPEDE opened in 2005 with frequentist stopping rules and is still the clearest demonstration that a shared control arm and a standing infrastructure pay for themselves. What the Bayesian designs added is a different toolkit for the arms that nobody had planned yet: a decision rule per arm, calibrated by simulation, and hierarchical models that share information. Both frameworks can accommodate new arms and share information. They differ in their inferential machinery and decision rules, and both need a justified hypothesis family and demonstrated operating characteristics.
This chapter follows the order the rest of the book uses. It starts with the traditional answer to “we have five drugs to test”, which is five separate two-arm trials, and measures what is wasted. It then describes the frequentist multi-arm multi-stage platform (STAMPEDE), the shared-control arithmetic that all platforms inherit, the problem of non-concurrent controls and calendar drift, and the multiplicity rules that differ between FDA and EMA. Only then does it turn to the Bayesian platforms (I-SPY 2, GBM AGILE, REMAP-CAP and the COVID anticoagulation multiplatform), to governance, and to the one famous platform that never enrolled an arm.
ImportantRegulatory anchor
All documents below are described in Chapter 3. Status as of November 2026.
- FDA, Master Protocols for Drug and Biological Product Development, revised draft guidance (June 2026) (U.S. Food and Drug Administration 2026a). Revises the draft of December 2023. Defines master protocol, basket, umbrella and platform; recommends concurrent controls, a larger control allocation than any single arm, and generally no multiplicity adjustment across unrelated drugs; asks for amendments that substantively affect safety, quality or scope to be submitted at least 30 days before they start. A draft, so it recommends and does not bind.
- FDA, Master Protocols: Efficient Clinical Trial Design Strategies to Expedite Development of Oncology Drugs and Biologics, final guidance (March 2022) (U.S. Food and Drug Administration 2022). The final text for cancer drugs and biologics (docket FDA-2018-D-3292), and FDA’s final oncology-specific master protocol guidance: the 2026 revision above is a draft. For master protocols evaluating multiple drugs in one disease, FDA generally recommends comparisons with a common standard-of-care control. Experimental-arm comparisons may be proposed prospectively when the IND sponsor has the necessary right of reference. When changed standard of care makes the previous control unethical, FDA recommends suspending enrollment until the protocol and informed consent incorporate the new control, and updating the SAP before analysis. For adaptive and Bayesian master protocols it asks that the statistical analysis plan give the details of the method and the futility analyses. It recommends and does not bind.
- EMA, reflection paper on platform trials (draft, October 2026) (European Medicines Agency 2026). States a strong preference for concurrent controls, treats non-concurrent controls as generally unacceptable for the primary analysis of the primary endpoint, discusses control allocation (Dunnett’s square root rule) and the error rate across arms, and, for confirmatory platforms, does not support response-adaptive randomization (Section 3.2.1). A draft.
- EC, EMA and HMA, Complex clinical trials: Questions and answers (2022) (European Commission and European Medicines Agency and Heads of Medicines Agencies 2022). The operative EU document: definitions, the sub-protocol structure, substantial modifications when arms are added, and the roles of sponsor and investigators.
- FDA, Use of Bayesian Methodology in Clinical Trials of Drug and Biological Products, draft (January 2026) (U.S. Food and Drug Administration 2026b). Names the Bayesian “time machine” for non-concurrent controls in platforms (it cites GBM AGILE and Precision Promise) and asks that borrowing across substudies justify exchangeability and include known effect modifiers.
- ICH E20, Adaptive Designs for Clinical Trials, Step 2 draft (June 2025) (International Council for Harmonisation 2025). Pre-specification and simulation-based operating characteristics for adaptations such as dropping arms. See Chapter 14.
- FDA, Adaptive Designs for Clinical Trials of Drugs and Biologics, final (November 2019) (U.S. Food and Drug Administration 2019). The governing text for arm dropping, sample-size re-estimation and the control of type I error in adaptive designs.
20.1 Separate trials, and what they cost
Suppose a sponsor, or a network, has \(k\) experimental treatments for the same disease. The textbook plan runs \(k\) two-arm trials. Each has its own protocol and its own control group of \(m\) patients, so the program randomizes \(2km\) patients, half of them to a control arm that answers one question each. The plan is correct, easy to audit, and it is what regulators have approved drugs on for decades. Each trial has its own type I error rate and its own power, and nothing in one trial can contaminate another.
Its cost is the control arm. A trial of five drugs at 80 patients per arm randomizes 800 patients, 400 of them to the same standard of care measured five times. In the separate-trials plan, 400 participants receive standard of care, measured five times, so that five separate questions could each have an isolated comparison. The sponsor pays for it in time as well, since each trial must be started, sited and closed separately.
A platform answers the same \(k\) questions with one control group of size \(m\). Each drug-versus-control comparison has the same precision as before, because its variance depends only on the two arms it uses, and the program enrolls \((k+1)m\) patients rather than \(2km\). The saving is
which is 25% for two drugs, 37.5% for four and 40% for five, approaching one half as \(k\) grows (Polson and Sokolov 2026). Saville and Berry simulated whole development programs and found the same direction on a larger scale: platform designs found beneficial treatments with fewer patients, fewer patient failures, less time and a greater probability of success than a traditional two-arm strategy (Benjamin R. Saville and Berry 2016). These are simulations under stated assumptions, not trial results. The saving falls on control assignments. Whether that reduces exposure to an inferior treatment depends on the experimental treatments’ actual effects.
The five-drug row of Table 20.1 is the example of module 10 of the companion lab: 800 patients become 480. Two things in that arithmetic need care before it is believed. First, it assumes all \(k\) arms run at the same time and that each comparison is run on the same data as in a separate trial. Real platforms add arms later, which creates the control problem discussed below. Second, it treats the \(k\) questions as separate. Whether the \(k\) results then need a joint error rate is a regulatory question as much as a statistical one, and it is treated in the multiplicity section.
20.2 Definitions: master protocol, basket, umbrella, platform
The terms and the taxonomy were set out by Woodcock and LaVange (2017), and the platform trial was presented to clinicians in S. M. Berry, Connor, and Lewis (2015). FDA’s June 2026 draft defines the terms as follows. A master protocol is “a protocol designed with multiple substudies, which may have different objectives and involve coordinated efforts to evaluate one or more drugs” (Section I, printed pages 1 to 2). The three kinds it names are:
- Umbrella. “a trial designed to evaluate multiple drugs concurrently for a single disease or condition.”
- Basket. “a trial designed to evaluate a drug for multiple diseases, conditions, or disease subtypes.”
- Platform. “evaluate multiple drugs for one or more diseases, conditions, or disease subtypes in an ongoing manner, with drugs entering or leaving the platform.”
The three differ in what is held fixed. A basket fixes the drug and varies the population, as in the tissue-agnostic approvals built on a molecular marker. An umbrella fixes the disease and varies the drug, often assigning patients to arms by biomarker. A platform fixes the disease and the infrastructure and lets the drugs change over time. In practice the terms overlap: I-SPY 2 is a platform with biomarker-defined signatures, and many baskets are platforms for one drug family. The Adaptive Platform Trials Coalition uses adaptive platform trial for a platform whose adaptations (dropping or graduating arms, response-adaptive randomization, sample-size changes) follow decision rules fixed in advance (Coalition et al. 2019). The EC/EMA/HMA question-and-answer document defines a platform trial as a shared framework in which several investigational products enter and leave at different times under pre-specified decision rules, possibly in different diseases (European Commission and European Medicines Agency and Heads of Medicines Agencies 2022). Early reviews of how often the three designs were used, and with what mix of features, are J. J. H. Park et al. (2019) and Meyer et al. (2020). Basket designs and the borrowing that makes them efficient belong to Chapter 19 and are not treated further here.
The treatment-specific part of a platform sits in a module attached to the master protocol. It is called an intervention-specific appendix, sub-protocol, substudy appendix or, in REMAP-CAP, a domain-specific appendix. The master protocol holds what is common: eligibility, endpoints, schedule of assessments, the randomization system, the statistical framework and the governance. The module holds what is specific to one treatment: its dose, its safety monitoring, its exclusion criteria, and its decision thresholds (Woodcock and LaVange 2017).
20.3 The frequentist platform: multi-arm multi-stage designs
The platform with the longest record is frequentist. STAMPEDE (Systemic Therapy in Advancing or Metastatic Prostate Cancer: Evaluation of Drug Efficacy) was designed at the MRC Clinical Trials Unit at UCL as a multi-arm multi-stage (MAMS) trial. The first patient was randomized in October 2005 to one of six arms, a control on standard hormone therapy and five research arms, with allocation 2:1:1:1:1:1, so that the control received twice the share of each research arm (Mahesh K. B. Parmar et al. 2017). The MAMS design for time-to-event outcomes, with stopping for lack of benefit on an intermediate outcome, was introduced by Royston, Parmar, and Qian (2003), with stopping guidelines in Royston et al. (2011); Stallard and Todd (2003) gave a sequential treatment-selection design and Wason and Jaki (2012) optimal designs. The design follows the logic of a group sequential trial (Chapter 11) with one change: at each interim look every research arm is compared with the control, and arms that fail a pre-specified bar are dropped while the others continue (Sydes et al. 2009).
Three features of the design carry over to every platform.
Intermediate outcome first. The final outcome in STAMPEDE is overall survival, which takes years. The early stages use failure-free survival as an intermediate outcome, with a hazard-ratio cut-off at each stage that is lenient early and tighter later, so that arms with no sign of benefit leave the trial at a fraction of the cost. In STAMPEDE the early stages are therefore futility gates on an intermediate outcome, failure-free survival, ahead of the definitive outcome, overall survival. The intermediate outcome need not be a validated surrogate, and a MAMS design can instead use the same endpoint at successive stages (Sydes et al. 2009). General MAMS methods calibrate the stopping boundaries through the joint distribution of the test statistics across stages and arms, so as to control a chosen error rate such as the pairwise or familywise rate for the comparisons in a family (Magirr, Jaki, and Whitehead 2012). Which error family is required depends on the claims the trial intends to make. STAMPEDE’s own strategy was comparison-level testing: each research arm is compared with the control at its own level, and its investigators report a familywise error rate of 6.75% for the three original comparisons reaching their targets (Mahesh K. B. Parmar et al. 2017). These hazard-ratio cutoffs were derived under proportional hazards (Royston et al. 2011). For non-proportional hazards, define an appropriate summary measure (Section 18.5) and include delayed-effect scenarios in the design simulations.
Concurrent controls only. A new comparison added after the start is compared with controls randomized from the time it opened, using the same intermediate-outcome rules shifted in time. STAMPEDE kept its control arm in step with the standard of care: when the standard of care changed, the control regimen changed with it, and an arm opened after such a change would have a different control population from one opened before it (Nicholas D. James et al. 2016).
New arms by amendment. Over its life STAMPEDE added comparisons as earlier ones reported. New arms were substantial amendments, each requiring ethics and regulatory review before the arm could open. The abiraterone comparison joined later and, in men starting long-term hormone therapy, reduced the hazard of death (hazard ratio 0.63) (Nicholas D. James et al. 2016; Nicholas D. James et al. 2017). The project reports a correlation of 0.12 between the test statistic of the abiraterone comparison and those of the original arms (Mahesh K. B. Parmar et al. 2017).
STAMPEDE is a standing reminder that the Bayesian machinery is optional for a platform. A common control, pre-specified stopping rules, intermediate outcomes and a standing infrastructure were enough to answer several questions in the time that a sequence of separate trials would need (Mahesh K. B. Parmar, Carpenter, and Sydes 2014). Frequentist platforms can also let the set of arms grow: STAMPEDE itself added comparisons by amendment, an added arm can be treated as a new family with its own level (Mahesh K. B. Parmar et al. 2017), and online error-rate control methods exist for hypotheses that arrive over time (Robertson et al. 2023). What a MAMS error calculation for a fixed family assumes is that the family is known, so for added arms the choice of family has to be made and justified. The Bayesian platforms below start from a per-arm decision rule calibrated by simulation, with optional hierarchical sharing of information.
20.5 Concurrent and non-concurrent controls
A platform that runs for years faces a question that separate trials never face: which control patients may be compared with a given arm? Concurrent controls are those randomized while the arm was open. Non-concurrent controls were randomized before it opened. They are tempting because they are free patients, and they are dangerous because of drift. Over a platform’s life the standard of care, the mix of patients, the sites and the conduct of the trial change, so an arm that opens late is compared with controls treated under different conditions (Dodd, Freidlin, and Korn 2021).
Regulatory position
FDA’s June 2026 draft is the stricter of the two. It asks that the primary comparison for a drug use only concurrently eligible controls: those who met that drug’s eligibility criteria and could have been randomized to it but were randomized to control instead (PDF p. 11, “only concurrently eligible control participants”). Controls enrolled earlier, and controls enrolled at the same time who could not have received the drug (a kidney-toxic drug excludes some patients, or a site offers only some arms), are left out of the primary analysis. The draft says that using non-concurrent data can bias the estimate and change the type I and type II error probabilities even when the analysis tries to model a time trend, and that the shared control keeps most of its efficiency gain when only concurrent controls are used. A sponsor who wants to use non-concurrent data should justify this in advance, weigh the amount of data against the calendar gap, pre-specify the method, and run sensitivity analyses that give the non-concurrent data less weight or none (U.S. Food and Drug Administration 2026a).
The EMA draft reflection paper defines concurrent controls as those with a positive probability of being randomized to the arm of interest, states a strong preference for them, and says that non-concurrent controls are usually not acceptable for the primary analysis of the primary endpoint, though they may support supplementary analyses or rarely observed secondary endpoints (European Medicines Agency 2026). Both documents are drafts. They agree on the default and differ in how much room they leave for model-based exceptions.
How big is the bias? A simulation
Module 10 of the book’s companion online lab (https://nytel.ai/testing/10-platform-trials.html) draws a platform in which success on standard care rises 2 percentage points a year and shows a drug that does nothing and appears to help. The simulation below makes the arithmetic explicit. The platform runs for four years, enrolling 300 patients per year in equal proportions between control, arm A and (after two years have elapsed) arm B. Arm B has no effect in the first scenario, and in the second a true absolute improvement of 10 percentage points. Control success starts at 30% and rises by the drift. We analyze arm B three ways: against concurrent controls (those randomized in years 3 and 4), against all controls, and against all controls with a linear calendar-time term.
Show the R code
rows <- list("no drift, B null" = list(drift = 0, effect = 0),
"drift 2 pts/yr, B null" = list(drift = 0.02, effect = 0),
"drift 2 pts/yr, B +10 pts" = list(drift = 0.02, effect = 0.10))
tab <- do.call(rbind, lapply(names(rows), function(n)
cbind(scenario = n, do.call(platform_drift_simulation, c(rows[[n]], nsim = 4000, seed = 17)))))
tab$mean_estimate <- 100 * tab$mean_estimate; tab$rejection <- 100 * tab$rejection
drift_tab <- tab
dt <- function(s, m, col) drift_tab[[col]][drift_tab$scenario == s & drift_tab$method == m]
knitr::kable(tab, digits = 1, align = "llrr", row.names = FALSE,
col.names = c("Scenario", "Method", "Mean estimate (points)", "Rejection (%)"))| Scenario | Method | Mean estimate (points) | Rejection (%) |
|---|---|---|---|
| no drift, B null | concurrent | 0.1 | 2.5 |
| no drift, B null | all controls | 0.1 | 2.3 |
| no drift, B null | time-adjusted | 0.1 | 2.5 |
| drift 2 pts/yr, B null | concurrent | 0.0 | 2.9 |
| drift 2 pts/yr, B null | all controls | 2.4 | 8.1 |
| drift 2 pts/yr, B null | time-adjusted | 0.0 | 2.8 |
| drift 2 pts/yr, B +10 pts | concurrent | 10.1 | 53.0 |
| drift 2 pts/yr, B +10 pts | all controls | 12.4 | 85.8 |
| drift 2 pts/yr, B +10 pts | time-adjusted | 10.1 | 59.4 |
With no drift (Table 20.4), pooling all controls costs nothing and the three methods agree. With a 2-point-per-year drift and no true effect, the concurrent comparison is unbiased and rejects at about the nominal 2.5% (2.9% in 4,000 simulations), while pooling all controls produces a bias of 2.4 percentage points and a one-sided type I error of 8.1%, more than three times the nominal level. The platform’s own control arm turns into a source of false positives. When arm B has a true effect of 10 points, pooling “improves” power from 53% to 86%, and the improvement is partly spurious: the estimate is 12.4 points rather than 10.
The calendar-time adjustment does what it was designed to do under this smooth, linear drift: no bias, nominal type I error, and slightly higher power than the concurrent-only analysis (59% against 53%), because the non-concurrent controls are used to estimate the slope. That result depends on the model being right. FDA’s draft warns that modeling does not guarantee error control, and the time-machine simulation below shows a related failure when history breaks.
The Bayesian time machine
A less rigid alternative to a linear term lets the control rate drift as a random walk across calendar periods and estimates the control rate in the current period by borrowing from the neighboring periods, with a smoothing parameter \(\sigma_s\) that controls how fast the rate is allowed to change. This is the idea behind the time machine of Saville and colleagues, used in I-SPY 2, proposed for GBM AGILE and Precision Promise, and cited as such in FDA’s Bayesian draft (Benjamin R. Saville et al. 2022; U.S. Food and Drug Administration 2026b). Small \(\sigma_s\) pools almost everything, large \(\sigma_s\) is nearly the concurrent-only estimate. The code below is an illustrative first-order Gaussian smoother over period-level control rates, fitted from the simulated data only (the period variances are estimated from the observed rates, not taken from the truth). It is not the published second-order model, so its results illustrate the trade-off and do not establish the robustness of the published method. It is run two ways: with \(\sigma_s\) learned from the data by restricted maximum likelihood (REML), and with \(\sigma_s\) fixed at three values for illustration.
The simulation (Table 20.5) estimates the control success rate in the current period under three histories of the true rate: constant, linear drift of 2 points per period, and a step of 8 points in the last period (a change in standard of care). There are four periods, each with 100 control patients. We report bias and root mean squared error, and the mean smoothing parameter.
Show the R code
scen <- list(constant = c(0, 0, 0, 0), `linear drift` = c(0, .02, .04, .06), `step in last period` = c(0, 0, 0, .08))
tab <- do.call(rbind, lapply(names(scen), function(n) cbind(scenario = n, platform_time_machine(scen[[n]], seed = 17))))
tab$bias <- 100 * tab$bias; tab$rmse <- 100 * tab$rmse
tm <- function(h, m, col) with(tab, get(col)[startsWith(scenario, h) & startsWith(method, m)])
f1 <- function(x) sprintf("%.1f", x)
knitr::kable(tab, digits = c(0, 0, 1, 1, 3), align = "llrrr", row.names = FALSE,
col.names = c("History", "Method", "Bias (points)", "RMSE (points)", "Mean smoother scale"))| History | Method | Bias (points) | RMSE (points) | Mean smoother scale |
|---|---|---|---|---|
| constant | current only | 0.1 | 4.5 | NA |
| constant | pool all | 0.0 | 2.3 | NA |
| constant | learned smoothing (REML tau) | -0.1 | 3.0 | 0.015 |
| constant | fixed smoothing, tau=0.01 | -0.3 | 2.3 | 0.010 |
| constant | fixed smoothing, tau=0.03 | -0.2 | 2.7 | 0.030 |
| constant | fixed smoothing, tau=0.1 | 0.0 | 3.9 | 0.100 |
| linear drift | current only | 0.0 | 4.8 | NA |
| linear drift | pool all | -3.0 | 3.8 | NA |
| linear drift | learned smoothing (REML tau) | -1.7 | 3.9 | 0.026 |
| linear drift | fixed smoothing, tau=0.01 | -3.1 | 4.0 | 0.010 |
| linear drift | fixed smoothing, tau=0.03 | -2.0 | 3.4 | 0.030 |
| linear drift | fixed smoothing, tau=0.1 | -0.5 | 4.1 | 0.100 |
| step in last period | current only | 0.0 | 4.8 | NA |
| step in last period | pool all | -6.0 | 6.4 | NA |
| step in last period | learned smoothing (REML tau) | -3.3 | 5.4 | 0.037 |
| step in last period | fixed smoothing, tau=0.01 | -6.1 | 6.6 | 0.010 |
| step in last period | fixed smoothing, tau=0.03 | -4.5 | 5.3 | 0.030 |
| step in last period | fixed smoothing, tau=0.1 | -1.4 | 4.3 | 0.100 |
When nothing changes, borrowing is nearly free: pooling cuts the root mean squared error from 4.5 points (current period alone) to 2.3, the smoother with learned \(\sigma_s\) to 3.0 (mean estimated \(\sigma_s\) 0.015), and the smallest fixed \(\sigma_s\) to 2.3. Under linear drift, pooling is biased by 3.0 points and the error is 3.8. The learned smoother has bias 1.7 and error 3.9, against 4.8 for the current period alone; the fixed \(\sigma_s=0.03\) has the lowest rmse of the methods shown (3.4 points), and the loosest fixed smoothing, \(\sigma_s = 0.10\), has little bias (0.5 points). When the rate jumps at the end, pooling is biased by 6.0 points with an rmse of 6.4, worse than using the current period alone (4.8). The learned smoother, which has to infer the break from four periods of 100 patients, is also worse than the current period alone (bias 3.3, rmse 5.4), and only the loosest fixed smoothing improves on concurrent-only data, with an rmse of 4.3 and bias of 1.4 points. That value of \(\sigma_s\) was fixed with knowledge of the scenarios, which a real protocol does not have.
Two points follow for the protocol. First, a time machine involves a smoothing choice, and whether it is learned from a few periods or fixed in advance, it depends on how the standard of care can change, which is a clinical judgment to be made before the data. Second, in all three illustrated histories the loosest fixed smoother (\(\sigma_s = 0.10\)) has a lower rmse than the concurrent-only analysis (3.9, 4.1 and 4.3 against 4.5, 4.8 and 4.8 points). Three scenarios do not establish that it is better for other histories (an abrupt drift, for example), the value was fixed with knowledge of the scenarios, and smoothing introduces bias that has to be checked: borrowing gains precision when history is stable and gives it back when history breaks. The simulation report of Chapter 14 therefore has to include scenarios with a step change, which is what FDA means by asking that the method be pre-specified and accompanied by sensitivity analyses. The simulation studies and reviews of non-concurrent controls that examine this trade-off are Lee and Wason (2020), Roig et al. (2022), Roig et al. (2023) and Jiang et al. (2023), and the R package ncc implements the analyses (Krotka et al. 2023). FDA’s Bayesian draft adds that the relevance of borrowed data depends on recency and on changes in standard of care, which is the same point in different words (see Chapter 19 and Chapter 16).
20.6 Multiplicity across arms
A traditional trial with several treatment arms and one control usually controls the familywise error rate at 0.025, through Bonferroni, Holm, or Dunnett’s step-down procedure, because a regulator who approves a drug on one of several comparisons must know how many chances the sponsor had (Chapter 10). A platform raises the question of what the family is. Five unrelated drugs from five sponsors that happen to share a control group would never be put in a common family in separate trials, and their arrival in the same protocol does not change their clinical independence.
FDA
The FDA draft says so directly: FDA “generally does not recommend the use of multiplicity adjustments to strongly control the probability of making at least one type I error across the multiple comparisons of different drugs” (Section H, PDF pp. 18 to 19). The reason it gives is the one of the previous section: “the expected total number of type I errors is the same regardless of whether these comparisons are made in independent trials or in a single trial” (PDF p. 19). The unit of control is the drug, with its own level, not the platform. Collignon and colleagues similarly argue that sharing a control arm does not itself call for an additional multiplicity adjustment across substudies investigating different drugs, while recognizing the possibility of multiple false positive regulatory decisions (Collignon et al. 2020).
The draft keeps the adjustment where the comparisons answer one question: several doses or formulations of one drug, the components of a combination, or several endpoints for one drug. In those cases the sponsor should define the family arm by arm and defend the definition before the data are seen. Doses of one drug compared with a shared control, for example, are one family with \(d\) comparisons, and the usual tools of Chapter 10 apply: Bonferroni, Holm, a graphical procedure, or the Dunnett critical value, which uses the correlation of the shared-control statistics and is less conservative than Bonferroni.
EMA
The EMA draft is more cautious about the same fact. It notes that the shared control makes errors correlated, that the probability of at least one false positive may fall while the probability of several rises, and that tightening each arm’s level to hold down the chance of multiple false positives would require thresholds stricter than Bonferroni (European Medicines Agency 2026). It treats the choice of family as a design decision to be made in advance and argued, and it offers alternatives such as larger control groups. The comparison with FDA is subtle. Both reject a blanket adjustment across unrelated arms, and both want the sponsor to define the families. EMA’s draft puts more weight on the arms that share a regulatory submission or a sponsor, and on the distribution of the number of errors, which is the quantity the earlier simulation computed. For a program whose arms are all developed by one sponsor for one eventual label, a regulator in either jurisdiction may regard the arms as a single family; this needs a conversation, and Chapter 23 describes how to have it.
Bayesian error control across arms
A Bayesian platform does not remove the question, it moves it. Each arm has a success criterion of the form \(\Pr(\delta > a \mid \text{data}) > c\) (Chapter 7). For confirmatory adaptive comparisons without borrowing, this book uses simulation-calibrated criteria, and the same calibration can be extended to a familywise rate over a defined family if the regulator asks for one. FDA’s draft also discusses direct posterior interpretation and decision-theoretic or benefit-risk criteria; the proposed route should be discussed with FDA. FDA’s Bayesian draft specifies that the sponsor describe how the success criteria map to error control, and the simulation report shows it by arm and by family (U.S. Food and Drug Administration 2026b). The Bayesian framework also offers a natural route to sharing information across arms, shrinkage, which frequentist analyses can reach as well through hierarchical or empirical-Bayes estimation with its own calibration.
If arms in the same platform are modeled as exchangeable, with each arm’s effect drawn from a common distribution with between-arm variance \(\tau_b^2\) and sampling variance \(v\), each estimate keeps weight \(w = \tau_b^2/(\tau_b^2 + v)\) on its own data and is pulled toward the common mean with weight \(1-w\), and its posterior variance falls from \(v\) to \(v w\), an information multiple of \(1/w\) (Polson and Sokolov 2026). The reverse is also a cost: the multiple is an upper bound that treats the common mean as known, and an arm whose effect is far from its neighbors is shrunk toward them.
Show the R code
tau <- 0.264; v <- 0.09 # between-arm sd and sampling variance (log-odds scale, illustrative)
w <- tau^2 / (tau^2 + v)
knitr::kable(data.frame(quantity = c("Weight on own data", "Information multiple", "Posterior sd before", "Posterior sd after"),
value = c(w, 1 / w, sqrt(v), sqrt(v * w))), digits = 2, align = "lr", col.names = c("Quantity", "Value"))| Quantity | Value |
|---|---|
| Weight on own data | 0.44 |
| Information multiple | 2.29 |
| Posterior sd before | 0.30 |
| Posterior sd after | 0.20 |
With these values (Table 20.6; the between-arm spread from the ulcer example of Chapter 10) each arm’s posterior standard deviation falls from 0.30 to 0.20. That information is paid for by an assumption: that the arms are exchangeable. Between unrelated drugs that assumption is hard to defend, and FDA’s Bayesian draft asks that a model borrowing across substudies justify exchangeability and include known effect modifiers, such as biomarker status, as covariates rather than treating the groups as interchangeable (U.S. Food and Drug Administration 2026b). Shrinkage across arms is therefore most defensible for arms from one drug class, doses of one drug, or the same drug in related subgroups, which is the territory of Chapter 19. It is not a substitute for the multiplicity decision across unrelated drugs, and the protocol should not present it as one.
20.7 Bayesian platforms
The Bayesian platforms differ from STAMPEDE in what they do at each interim look and in how they treat information shared across arms.
I-SPY 2: graduation by predictive probability
I-SPY 2 is a platform for neoadjuvant breast cancer that has enrolled since 2010 and was later reconfigured as I-SPY 2.2 (J. W. Park et al. 2016; D. A. Berry 2025). The primary endpoint of each arm was pathologic complete response (pCR) at surgery, with tumor volume measured by MRI during treatment used to predict pCR for patients still in follow-up. Patients were classified into biomarker subtypes by hormone receptor status, HER2 status and a genomic profile, and each therapy was evaluated in each of up to ten signatures, the subtype combinations that might become a regulatory indication (Barker et al. 2009; Wang and Yee 2019).
An arm graduated in a signature when its Bayesian predictive probability of success in a hypothetical 300-patient, equally randomized phase 3 trial against the same control, with pCR as endpoint, reached 85%; it was dropped for futility if that probability fell below 10% in all ten signatures, and no arm took more than 120 patients (J. W. Park et al. 2016). The decision is made from phase 2 data, so it answers the question a sponsor asks at a go/no-go meeting. It differs from a posterior probability of benefit, which asks whether the effect is positive and says nothing about the size and power of the trial that would follow. The simulation below (Table 20.7) shows the difference with four phase 2 results, 50 patients per arm in the signature, and a phase 3 with 150 per arm tested at one-sided 0.025.
Show the R code
cases <- list("clear win, 24/50 vs 10/50" = c(24, 50, 10, 50), "good, 20/50 vs 10/50" = c(20, 50, 10, 50),
"modest, 18/50 vs 13/50" = c(18, 50, 13, 50), "none, 15/50 vs 15/50" = c(15, 50, 15, 50))
res <- t(sapply(cases, function(x) do.call(platform_predictive_graduation, c(as.list(x), seed = 5))))
tab <- data.frame(phase2 = names(cases), res, graduates = ifelse(res[, "pp"] >= 0.85, "yes", "no"))
knitr::kable(tab, digits = 3, align = "lrrc", row.names = FALSE,
col.names = c("Phase 2 result", "Predictive probability", "Posterior probability", "Graduates"))| Phase 2 result | Predictive probability | Posterior probability | Graduates |
|---|---|---|---|
| clear win, 24/50 vs 10/50 | 0.942 | 0.999 | yes |
| good, 20/50 vs 10/50 | 0.814 | 0.985 | no |
| modest, 18/50 vs 13/50 | 0.470 | 0.857 | no |
| none, 15/50 vs 15/50 | 0.161 | 0.499 | no |
The second row has a 98.5% posterior probability that the new arm beats the control, and a predictive probability of phase 3 success of 81.4%, below the threshold. The posterior probability is a statement about the present, and the predictive probability includes the chance that a true effect of ordinary size is missed by a finite phase 3. Setting the graduation threshold on the predictive scale therefore ties the platform’s decision to the confirmatory trial it feeds, and a sponsor can see at the start what phase 2 result would be enough. Predictive probabilities are developed in Chapter 15.
Three further features of I-SPY 2 are relevant. Randomization was response adaptive within a signature, with a fixed share held on control (20% (Nanda et al. 2020)), the remainder going to arms that looked better (J. W. Park et al. 2016). A control cohort for each signature accumulated over the years, with a time machine used to smooth the control response over time. And the platform also tested combination regimens as experimental arms against the shared control. The graduation results of the first two graduates, neratinib and pembrolizumab, and why their final predictive probabilities fell after all pathology was in, are told in Section 15.10. Because allocation adapts toward responsive subtypes, the raw difference should not be read as the treatment effect, and a design that allocates by subtype responsiveness needs a model that adjusts for it; Chapter 16 describes the mechanism and the critiques.
I-SPY 2 is a phase 2 screening platform. A graduation is a decision to run a phase 3, and it carries a false positive rate that was calibrated by simulation to be acceptable for a screening stage (Chapter 14). It does not replace a confirmatory trial, and a graduate is not an approval.
GBM AGILE: a registration platform
GBM AGILE (Adaptive Global Innovative Learning Environment, NCT03970447) is a Bayesian response-adaptive platform in glioblastoma designed with registration in mind, which I-SPY 2 was not (Alexander et al. 2018). An antecedent is the Bayesian adaptive randomized design for recurrent glioblastoma of Trippa et al. (2012). It uses a seamless phase 2/3 structure: in stage 1 each arm is randomized adaptively against a shared control (temozolomide in newly diagnosed disease, lomustine in recurrent), with allocation in proportion to the posterior probability of a hazard ratio below a benchmark and arms evaluated monthly; an arm that clears the stage 1 bar graduates to stage 2 with fixed randomization to confirm the finding for registration (Alexander et al. 2018). In the first completed arm, regorafenib, efficacy required a Bayesian probability of benefit (hazard ratio below 1) of at least 98%, and enrollment stopped for limited efficacy when the Bayesian predictive power fell below 25% in all signatures (Wen et al. 2026). The published report has since been corrected by an erratum (Wen, Berry, et al. 2026). Patients are classified into signatures based on newly diagnosed versus recurrent disease and MGMT methylation status, and 20% of each subtype’s patients are assigned to control (Alexander et al. 2018).
The 98% is the kind of number the FDA Bayesian draft discusses under calibration to type I error: the threshold is set by simulation so that the false positive rate over the design’s scenarios is acceptable, not by a view about the prior, and the simulation report is part of the submission (U.S. Food and Drug Administration 2026b). GBM AGILE is also the example FDA’s Bayesian draft names for the time machine: the shared control over the years has to be used carefully when standard of care changes. The platform’s own registry record lists 17 arm entries (ClinicalTrials.gov 2026), including regorafenib, paxalisib and VAL-083, with several arms (VT1021, troriluzole, ADI-PEG 20, tinostamustine) running dose-finding and enhanced safety management phases before the main arm. That reflects an amendment pattern worth copying: a safety lead-in as part of the arm’s appendix, with its own go/no-go rule, ahead of the efficacy comparison.
REMAP-CAP: domains, response-adaptive randomization, and an embedded design
REMAP-CAP (Randomized, Embedded, Multifactorial Adaptive Platform trial for Community-Acquired Pneumonia) is a platform designed before the pandemic it became known for (Angus et al. 2020). After the 2009 H1N1 pandemic, an EU-funded network built the infrastructure, which began enrolling in April 2016 according to its ClinicalTrials.gov record (NCT02735707) and carried a dormant pandemic stratum that was activated for COVID-19. Its design has four features that distinguish it from the oncology platforms.
Multifactorial. The platform is organized by domains, each a set of alternative interventions for one aspect of care: corticosteroids, antivirals, immune modulators, anticoagulation, antibiotic strategy, ventilation. A patient is randomized in every domain for which he or she is eligible, so a single patient can contribute to several comparisons, and the domains are analyzed together in a model that includes the interactions that were prespecified. Each domain has its own appendix and its own statistical analysis plan, which means the master protocol is stable while the domains come and go.
Embedded. The trial runs inside routine care and uses routinely collected data where it can, which keeps the burden per patient low enough for ICUs under pandemic load.
Ordinal primary endpoint. For the pandemic stratum the primary endpoint was organ-support-free days to day 21, an ordinal scale with death as the worst outcome, analyzed with a Bayesian proportional-odds model (REMAP-CAP Investigators, Gordon, et al. 2021).
Response-adaptive randomization and decision rules. Allocation within a domain is updated at pre-specified intervals to favor arms with a higher posterior probability of being best, and the domain stops when a pre-specified trigger is crossed. In the IL-6 domain the triggers were: superiority if the posterior probability of being best exceeded 99%; efficacy if the probability that the odds ratio against control exceeded 1 was above 99%; futility if the probability that the odds ratio exceeded 1.2 was below 5%; and equivalence of two non-control arms if the probability of an odds ratio between 0.83 and 1.2 exceeded 90% (REMAP-CAP Investigators, Gordon, et al. 2021; Angus et al. 2020). The platform declared that interleukin-6 receptor antagonists (tocilizumab and sarilumab) improved outcomes, including survival, in critically ill patients with COVID-19 (REMAP-CAP Investigators, Gordon, et al. 2021). Note that a platform with this structure can declare a domain complete and move on without waiting for the others, which is the property the sponsors of separate trials have to give up.
The domains share a hierarchical structure in one sense: the pandemic and non-pandemic strata, and subgroups within a domain, can be modeled with partial pooling. This is borrowing in the sense of Chapter 19, and the conditions under which it is acceptable are the same.
The COVID anticoagulation multiplatform
Three independently funded Bayesian platforms (REMAP-CAP, ATTACC in Canada, and ACTIV-4a in the United States) asked the same question early in the pandemic: therapeutic-dose against prophylactic-dose anticoagulation in COVID-19. Separate reports would have invited conflicting results and a post hoc meta-analysis. The three teams instead harmonized their protocols and statistical analysis plans before the data were in, and combined patient-level data in a Bayesian hierarchical model with dynamic borrowing across severity strata (ATTACC Investigators et al. 2021; REMAP-CAP Investigators, ACTIV-4a Investigators, et al. 2021). The stopping rule was superiority at a posterior probability above 99% or futility at above 95% for an odds ratio below 1.2, applied separately in each severity cohort. In critically ill patients enrollment stopped for futility (adjusted odds ratio 0.83, 95% CrI 0.67 to 1.03, futility probability 99.9%); in non-critically ill patients therapeutic dosing increased organ-support-free days (odds ratio 1.27, 95% CrI 1.03 to 1.58, probability of benefit 98.6%) (REMAP-CAP Investigators, ACTIV-4a Investigators, et al. 2021; ATTACC Investigators et al. 2021). The severity strata had been specified in advance, so the finding was not a post hoc subgroup.
The anticoagulation project is an unusual use of the platform idea. The shared object was a pre-agreed analysis, not a shared control group, and the platforms are the data sources for a single multi-site analysis. It shows what is possible when the sponsors agree on the estimand in advance, and it is the nearest thing the field has to a meta-analysis designed before the data exist.
Pragmatic pandemic platforms: RECOVERY and PANORAMIC
Not every pandemic platform was an elaborate Bayesian adaptive design. RECOVERY (Randomized Evaluation of COVID-19 Therapy) was a large, pragmatic and open-label platform in hospitalized patients, analyzed with frequentist methods, with deliberately little data collected beyond what the health service already records and 28-day mortality as the primary outcome. Its first major result was that dexamethasone reduced 28-day mortality overall (rate ratio 0.83, a reduction of about a sixth), by more among patients on invasive mechanical ventilation (0.64), and not at all among those who needed no oxygen (RECOVERY Collaborative Group et al. 2021). PANORAMIC took the pragmatic approach into UK primary care and analyzed its primary outcome with Bayesian logistic regression using weakly informative Cauchy priors. Its molnupiravir comparison randomized 25,783 participants between December 2021 and April 2022 to molnupiravir plus usual care or usual care alone (the platform’s total of 26,411 includes other comparisons), and hospitalization or death within 28 days in about 1% of each group (adjusted odds ratio 1.06), a clear negative result from a platform that could enroll that many community patients in under five months (Butler et al. 2023). The two trials show that simplicity and volume can do the work that a more elaborate adaptive design does elsewhere, and that a platform’s value comes first from its infrastructure and its speed.
Traditional against Bayesian platforms: what differs
Table 20.8 sets the frequentist MAMS and Bayesian platform side by side, as the book does for each design.
| Frequentist MAMS (STAMPEDE) | Bayesian platform (I-SPY 2, GBM AGILE, REMAP-CAP) | |
|---|---|---|
| Interim decision | hazard-ratio cut-off on an intermediate outcome, tightening by stage | posterior or predictive probability threshold, often monthly |
| Error control | error rates for the chosen comparisons, calibrated by the joint distribution of statistics (STAMPEDE: comparison-level testing, 6.75% familywise error reported for the three original comparisons) | per-arm or per-family type I error calibrated by simulation (Chapter 14) |
| Control allocation | fixed ratio (2:1:1:1:1:1 at the start), concurrent controls only | fixed control fraction, often response-adaptive for the rest (not supported for confirmatory platforms by the EMA draft), time machine optional |
| Arms nobody planned | added by amendment, as a new family with its own level or by online error allocation | added with a pre-specified decision rule; the family and its error rate still have to be defined |
| Information sharing | the shared control; hierarchical or empirical-Bayes estimation across arms is possible in principle | optional hierarchical borrowing across arms or strata with a justified exchangeability argument (Chapter 19) |
| What the regulator asks | the MAMS calculation and the stopping boundaries | the simulation report, prior and borrowing justification, time-trend handling |
| Where they agree | for a normal likelihood with known standard error, a flat prior and a single final look, the posterior probability of benefit equals one minus the one-sided p-value, and the corresponding thresholds agree | the same (for binary outcomes the correspondence is approximate) |
The traditional design is the better choice when the arms are known, the intermediate outcome is trusted, and the sponsor wants the simplest possible regulatory conversation. A Bayesian platform can earn its complexity when the outcome can be modeled longitudinally, or when information can be shared across strata with a defensible exchangeability argument. Frequentist platforms also accommodate added arms, and for confirmatory use the EMA draft does not support response-adaptive randomization, so the allocation rule is a point to settle with the regulator.
20.8 Governance, firewalls and the monitoring board
A platform survives its first arm only if the governance is built for arms that are not yet known. Typically a single data monitoring committee (DMC) oversees all arms, an independent statistical center runs the unblinded interim analyses and feeds the allocation algorithm, and a separate committee approves applications for new arms. The arrangement serves one aim: no sponsor sees how a competitor’s arm is performing. Under a Bayesian response-adaptive design, in which allocation probabilities depend on accumulating results, the allocation proportions themselves leak information, so the sponsor-facing report should show enrollment counts only when they cannot be inverted into outcomes. A burn-in period of equal allocation before adaptation begins, with the statistical center and not the sponsor holding the algorithm, is the usual safeguard (U.S. Food and Drug Administration 2026a; European Commission and European Medicines Agency and Heads of Medicines Agencies 2022).
Several other elements of governance have regulatory consequences.
Who is the sponsor. A master protocol needs a sponsor responsible for the platform (the “master protocol sponsor” of FDA’s draft) and, for each arm, an arm sponsor who owns the drug and its safety reporting. In the US, when all substudies sit under one master IND, FDA’s draft recommends that a new substudy be submitted at least 30 days before it begins and that the regulatory project manager is notified at least 48 hours before the amendment is submitted (U.S. Food and Drug Administration 2026a). In the EU, a new arm is a substantial modification of the authorization, and since a change to one sub-protocol can force changes to others, each sub-protocol states how far it depends on the rest (European Commission and European Medicines Agency and Heads of Medicines Agencies 2022). STAMPEDE’s experience was that each new comparison was a substantial amendment, and that drug supply could set the pace.
Simulating before opening. Analytical error-rate and power calculations are available for some platform designs with added arms. Platforms combining staggered entry, allocation changes and adaptive decisions generally need simulation to assess their full operating characteristics (Choodari-Oskooei et al. 2020; Meyer et al. 2025), and the simulation report of Chapter 14 is the vehicle. Meyer and colleagues draw lessons on why and how platform trials should be simulated from the EU-PEARL consortium.
What the firewall protects. The sponsor of one arm should not see another arm’s data, the control arm’s results, or the platform’s allocation algorithm in a way that would let it infer them. The DMC sees everything. The master protocol’s governance section should state who sees what, and the confidentiality agreements for arm sponsors should say so.
Rules fixed before data. The DMC charter should list the decision rules for each arm (stopping for efficacy, futility, graduation) and state that the DMC can override them for safety but not for convenience. The decision rules and the allocation algorithm are changed only by protocol amendment, with the simulation report updated accordingly. Operating characteristics must be re-established when anything that affects them changes (Chapter 14); a late-arriving arm changes the correlation structure and the allocation ratio, and the previous simulation may no longer apply.
TipIn the protocol
A master protocol should state, in the master document or an appendix: (1) the families of hypotheses, arm by arm, and the multiplicity method for each family; (2) the control allocation rule and when it changes as arms enter or leave; (3) the definition of a concurrent control, including eligibility; (4) the primary analysis population for each arm, and any use of non-concurrent data with its method, weight and sensitivity analyses; (5) the simulation report scenarios, including a step change in standard of care; (6) the decision rules and thresholds for each arm, and who may change them; (7) who sees which results, and the information given to arm sponsors; (8) the process and timing for adding an arm, with the 30-day regulatory submission that FDA’s draft recommends and the ethics review.
20.9 EPAD: a platform that never opened an arm
The European Prevention of Alzheimer’s Dementia program (EPAD) is the standard example of a platform that did not work. A 64-million-euro, five-year IMI-funded project, it built a 2,000-participant readiness cohort with detailed pre-characterization (amyloid status, cognitive baselines and longitudinal follow-up) to reduce the very high screen-failure rates of Alzheimer’s prevention trials (Ritchie et al. 2016; Saunders et al. 2022). It never enrolled a single treatment arm. In the project’s own post-mortem, two obstacles were decisive: owners of candidate interventions were reluctant to hand sponsorship of a critical asset to a university-run platform, and the stakeholders could not agree on a legal framework that suited every party (Saunders et al. 2022). When the five-year term ended in 2020, the treatment platform had never opened and the pandemic had made funding harder. The cohort data and biobank outlived the project.
The lesson is organizational, not statistical: nothing in EPAD’s statistical design was at fault, and the sample-size, borrowing and decision rules were never tested. Platforms need three things before a first arm. A legal framework that arm sponsors will sign, because they are handing control of an asset to a shared structure. A funding model that does not depend on the commercial pipeline the platform is meant to serve; the Healey ALS Platform Trial is the contrast (Quintana et al. 2023). And a governance structure that answers the question “who decides?” before the first arm’s sponsor asks it.
20.10 What changes in the protocol
A traditional two-arm trial and a platform differ less in the statistics of one comparison than in what surrounds it, as Table 20.9 shows.
| \(k\) separate two-arm trials | Platform with shared control | |
|---|---|---|
| Patients (\(k\) = 5, 80 per arm) | 800 | 480 |
| Control allocation | 1:1 in each trial | \(r > 1\) in favor of the control, often \(\sqrt{k}\) |
| Control data used | each trial’s own | concurrent only for primary; non-concurrent by pre-specified method |
| Multiplicity | none across trials | none across unrelated drugs (FDA); family defined per arm; distribution of the number of errors reported |
| New question | new trial, new submission | amendment; FDA draft recommends submission at least 30 days before |
| Simulation report | one design | all scenarios, including arms entering late and a step change in control |
| Consequences of failure | one trial | a comparison, or several comparisons if shared controls, analyses, or governance fail |
What stays the same: randomization within the platform defends each comparison against confounding exactly as in a two-arm trial, the estimand for each arm is still defined in the protocol table of Chapter 23, and the legal standard of substantial evidence of effectiveness is not lowered. A master protocol supports a marketing application for each drug on the evidence of that drug’s comparison. What the regulator will ask about is what is new: the controls, the multiplicity rule, the governance, and the simulation.
TipTry it in the lab
Open module 10 of the companion tutorial, https://nytel.ai/testing/10-platform-trials.html. Before you press the button, predict how many patients five separate trials need compared with one platform, then drop a drug into the platform in year 2 and check which control group the lab regards as fair when success on standard care is rising 2 points a year.
Key points
- A platform shares control patients: \(k\) comparisons need \((k+1)m\) patients rather than \(2km\), a saving of \((k-1)/(2k)\), with the same precision per comparison. Five drugs at 80 per arm need 480 patients, not 800.
- The best allocation puts \(\sqrt{k}\) patients on the control for each patient on an arm (Dunnett). FDA recommends more patients on the control than on any single arm, and the EMA draft cites the square-root rule.
- A shared control keeps the expected number of false positives at \(k\alpha\) but makes them correlated: in the four-arm illustration the chance of at least one falls and the chance of several rises. Report the distribution of the number of errors.
- Non-concurrent controls carry drift. In the simulation, pooling them under a 2-point-per-year drift raised the one-sided type I error from about 2.5% to 8.1%. FDA asks for concurrently eligible controls for the primary analysis, and EMA generally rejects non-concurrent controls for the primary endpoint.
- Time-trend models and time-machine smoothers recover power when history is stable and lose it, or bias, when it breaks. In our three illustrated histories the loosest fixed smoother had a lower rmse than the concurrent-only analysis, but three scenarios do not show it is better for other histories (an abrupt drift, for example), and the smoothing bias must be checked.
- FDA generally does not recommend multiplicity adjustment across unrelated drugs in a master protocol, and expects the sponsor to define families (doses, combinations, endpoints of one drug) in advance. Hierarchical shrinkage across arms needs a defensible exchangeability argument.
- STAMPEDE shows a frequentist MAMS platform works. I-SPY 2 graduates arms by predictive probability, GBM AGILE adds a seamless registration stage, and REMAP-CAP combines domains, ordinal outcomes and adaptive allocation. The anticoagulation multiplatform pre-agreed one analysis across three platforms. For confirmatory platforms the EMA draft does not support response-adaptive randomization.
- Governance decides whether a platform opens: EPAD had the cohort and the design and never enrolled an arm.
NoteDiscussion questions
- A sponsor has four drugs of its own for the same disease and proposes a platform with a shared control. Should the four comparisons share one familywise error rate under FDA’s draft, and what would change your answer if two of the drugs were doses of the same compound?
- In the drift simulation the time-adjusted analysis beat the concurrent analysis on power. Write the scenario in which it would not, and say what you would put in the simulation report to show it.
- An arm opens in year 4 of a platform in which the standard of care changed in year 3. What would you pre-specify about the use of controls from years 1 and 2?
- I-SPY 2 graduates an arm at a predictive probability of 85% for a later phase 3. A sponsor argues that the graduation should be at a posterior probability of 95%. What does each criterion say, and what trial does each assume?
- List what EPAD had and did not have that Healey ALS had, and say which of those a statistician could have fixed.