A design is only as good as the document that fixes it. The earlier chapters argued that a trial is a decision, that a regulator approves on evidence meeting a legal standard, and that Bayesian adaptive designs reach that standard sooner by monitoring, by handling several arms together, and by using prior information, not by lowering the bar. All of that is worth nothing to a sponsor until it has been turned into sentences in a protocol, a statistical analysis plan, a simulation report and a data monitoring committee charter, and until a regulator has read those sentences and not objected.
The practical question is which sentences change. A sponsor who has written a dozen group sequential protocols knows what the document looks like. A Bayesian protocol shares most of its sections with that document and differs in a handful, and the handful is where reviewers will spend their time. The chapter walks through the protocol section by section, traditional version first, then the Bayesian version, with model sentences in “In the protocol” callouts that a sponsor can adapt. It then covers the statistical analysis plan and the simulation report, the structured protocol formats now in use, the data monitoring committee and its firewalls, the sequence of meetings with FDA and the parallel routes at EMA, the standard of substantial evidence and where Bayesian evidence fits in it, what the Bayesian design does not buy, and two checklists, one for sponsors and one for reviewers. Nothing here is new methodology. It assembles material from Chapter 3, Chapter 8, Chapter 11, Chapter 14, Chapter 15, Chapter 16, Chapter 19 and Chapter 20 into the form a submission takes.
FDA, Use of Bayesian Methodology in Clinical Trials of Drug and Biological Products (draft guidance, January 2026, U.S. Food and Drug Administration (2026d)). Not binding. Section VIII asks that the prior, the success criteria, the operating characteristics and the computational details be documented “as early as possible” in the protocol, the statistical analysis plan (SAP) and a simulation report, and that complex designs be compared with simpler alternatives and discussed with FDA before the trial starts. FDA’s draft recommends prespecifying and justifying the prior in the protocol; this book treats prespecification as essential design practice.
FDA, Adaptive Designs for Clinical Trials of Drugs and Biologics (final guidance, November 2019, U.S. Food and Drug Administration (2019)). Four principles: the chance of erroneous conclusions should be adequately controlled, estimation of treatment effects should be sufficiently reliable, details of the design should be completely prespecified, and trial integrity should be appropriately maintained. Simulations are the accepted route to operating characteristics for complex designs.
ICH E20, Adaptive Designs for Clinical Trials (Step 2 draft, endorsed June 2025, International Council for Harmonisation (2025a)). Adaptations are “prospectively planned” only if prespecified in the protocol before the trial starts, a “clear and compelling justification” is required, and Section 5 sets out what a simulation report should contain. Draft, not final.
ICH E9 (1998, International Council for Harmonisation (1998)) and E9(R1) (Step 4, November 2019, International Council for Harmonisation (2019)). Interim analyses must be planned in advance and described in the protocol. The estimand, the precise description of the treatment effect, must be defined before the trial.
FDA, Demonstrating Substantial Evidence of Effectiveness (revised draft guidance, June 2026, U.S. Food and Drug Administration (2026a)). When one adequate and well-controlled trial plus confirmatory evidence can carry an approval, and the advice to discuss the plan with FDA before the trial starts.
FDA, Formal Meetings Between FDA and Sponsors of PDUFA Products (guidance, August 2026, U.S. Food and Drug Administration (2026b)); FDA, Interacting with the FDA on Complex Innovative Trial Designs (final guidance, December 2020, U.S. Food and Drug Administration (2020)); ICH M11 structured protocol (Step 4, November 2025, International Council for Harmonisation (2025b)); SPIRIT 2025 (Chan et al. (2025)). How to ask, when, and in what format.
A traditional confirmatory protocol states a null hypothesis and a one-sided type I error of 0.025 (two-sided 0.05 divided by two, as everywhere in this book). It fixes a sample size, or for a time-to-event endpoint a number of events, from a power formula at a design alternative, and fixes the allocation, usually one to one. If there are interim analyses it schedules them, names the boundary family and the alpha spending function, and says that unscheduled looks are protocol deviations. It handles multiple comparisons by a stated procedure, Bonferroni, Holm, a gatekeeping sequence or a graphical scheme (Chapter 10). It lists safety stopping rules, often informally. It names the primary analysis population and, since E9(R1), the estimand. The final report carries a point estimate, a confidence interval and an adjusted \(p\)-value. Each of these has a regulatory basis: ICH E9 on prespecification of interim analyses and on multiplicity, E9(R1) on estimands, the 2019 adaptive designs guidance on anything that departs from a fixed design.
The Bayesian protocol keeps the skeleton and changes the parts that depend on how evidence is summarized and how the trial may change as data accumulate.
Table 23.1 sets the two designs side by side. It is a generalization of the table in the working paper that motivated this book (Polson and Sokolov 2026), which was written for one cardiovascular outcomes trial (the SELECT reconstruction of Chapter 21). The entries in the last column are written for any Bayesian confirmatory design, and the numbers in the traditional column are the ones that example used where a number helps.
| Protocol section | Traditional design | Bayesian design | What the reviewer will ask |
|---|---|---|---|
| Objective | Test \(H_0\) of no effect at one-sided 0.025. | Decide whether the evidence meets a prespecified criterion, for example \(\Pr(\delta > a \mid \text{data}) > c\); optionally, choose the action that maximizes expected utility. | Is the criterion the one that supports a labeling claim? |
| Estimand | Defined per E9(R1): population, treatment, variable, intercurrent event strategy, summary. | Identical. The estimand is not a statistical philosophy choice. | Does the posterior target the same estimand as the clinical question? |
| Prior | Not stated. The design alternative enters only the power calculation. | Stated in full, with its effective sample size (ESS), the source of any informative component, and a prespecified sensitivity analysis. | Why this prior? What happens under a skeptical or pessimistic one? What if the data conflict with it? |
| Sample size | Fixed (or number of events), from a power formula. | A maximum, with the distribution of the sample size at stopping reported from simulation. | What is the largest trial this protocol can produce, and is it feasible? |
| Interim looks | Prescheduled; alpha spending function; unscheduled looks are deviations. | Prescheduled in a confirmatory trial, with decision rules at each look. The posterior does not depend on when data were examined, but the operating characteristics do. | Is the schedule fixed before unblinding, and were the operating characteristics simulated on that schedule? |
| Stopping rules | Boundary on \(Z_n\) (for example O’Brien-Fleming: 4.05, 2.86, 2.34, 2.02 across four looks). | Posterior or predictive probability thresholds for efficacy, futility and safety, calibrated by simulation (the working paper’s SELECT example used 0.995 for efficacy). | How were \(a\) and \(c\) chosen, and is familywise type I error controlled at 0.025? |
| Multiple arms or endpoints | Bonferroni, closed testing, graphical procedures. | Hierarchical model across arms or subgroups when the effects are scientifically exchangeable, with the hypothesis family defined by the intended claims and the complete decision rule calibrated where strong familywise error control is needed; or the same traditional procedure applied to the posterior criterion. | Is familywise error still controlled where the guidance expects it? |
| Randomization | Fixed, usually 1:1. | May be response-adaptive, with a stated rule, floors on allocation, burn-in, and time-trend handling. | Is the rule prespecified, is bias from drift handled, and is the integrity risk managed? |
| Safety | Prespecified rules, often informal, outside the error budget. | A posterior statement, for example exclude an arm if \(\Pr(\text{toxicity} > \text{limit} \mid \text{data}) > 0.90\), with its false-stop rate simulated. | What is the probability of stopping a safe arm, and of missing a harmful one? |
| Operating characteristics | Type I error and power at the design alternative, analytically. | The full set by simulation over a grid of scenarios: error, power, expected sample size, bias, coverage, probability of correct decision. | Is the scenario set prespecified, comprehensive and plausible, and is the code provided? |
| Computation | Standard software, rarely discussed. | Model code, sampler settings, convergence diagnostics, seeds, software versions. | Can FDA reproduce the simulation and the analysis? |
| Final report | Estimate, confidence interval, adjusted \(p\)-value. | Posterior distribution of the effect, whether the criterion was met, sensitivity to the prior; a \(p\)-value and confidence interval alongside where FDA expects them. | Does the report show the effect of the prior? |
Four things stay the same. The estimand is the same, because it is a statement of the clinical question and E9(R1) applies to any statistical framework. The randomization is, in the default case, the same, and the reasons for randomizing do not depend on the inferential paradigm (Chapter 5). The default bar in this book is the same: calibration to a familywise type I error of 0.025 one-sided. For a trial with an overall frequentist statistical analysis plan the Bayesian draft says that success criteria are “almost always” chosen that way, and that \(a\) and \(c\) may be chosen so that the overall error is controlled at that level. The draft offers two other routes, direct interpretation of posterior probabilities and decision-theoretic criteria, and as a draft it recommends and does not require. Calibration is this book’s default for confirmatory adaptive designs without borrowing, not FDA’s universal requirement. And the need to prespecify is the same. What moves is where the numbers come from, and in each moved row the sponsor owes the reviewer a simulation rather than a formula.
Three rows carry most of the practical difference. The interim looks row is where the speed comes from, and the one a data monitoring committee cares about. The multiple arms row is where robustness comes from, and matters for platform trials in which the number of contrasts is not known when the protocol is written (Chapter 20). The operating characteristics row is where the burden falls. A Bayesian protocol must simulate, and the simulation is the deliverable that replaces the closed form power calculation.
Where the two designs agree numerically, say so in the protocol. With a flat prior, a normal approximation and a single look, the posterior probability that the effect is positive is one minus the one-sided \(p\)-value, so a criterion \(\Pr(\theta > 0 \mid \text{data}) > 0.975\) is the same test as one-sided \(\alpha = 0.025\) (Chapter 7).
The prior is the section with no traditional counterpart, and the one FDA’s draft recommends prespecifying and justifying in the protocol; this book treats prespecification as essential design practice. The Bayesian draft calls it “always critical” that a Bayesian analysis have a prespecified prior, asks that the full details be fixed and justified in the protocol, and, where the prior is informative or borrows external data, asks for strong justification, a description of each source including excluded ones, the discounting method, how prior-data conflict will be handled, and the ESS and other influence metrics (U.S. Food and Drug Administration 2026d). Chapter 8 and Chapter 19 give the methods. For the protocol, three habits matter. State the ESS, the number of patients the prior is worth, in the sense of Morita, Thall, and Müller (2008). A prior worth five patients in a trial of five hundred is a modeling choice, and one worth two hundred is an assumption that needs defending. Distinguish the analysis prior (used to compute the posterior that decides success) from design priors (used only in simulation to explore scenarios, including pessimistic ones). And plan a sensitivity analysis, naming the alternative priors in advance.
“The analysis prior for the negative log hazard ratio \(\theta = -\log\mathrm{HR}\) is \(N(0, \sigma_0^2)\) with \(\sigma_0 =\) [value], a skeptical prior centered at no effect. Its effective sample size is [value] events, which is [percentage] of the maximum [number] events. No external data are borrowed. The prior was chosen so that [justification, for example: a hazard ratio of [x] has prior probability [p]]. Prior sensitivity will be assessed by repeating the primary analysis with prior standard deviations of [values] and with a flat prior; the primary conclusion will be reported as robust only if the success criterion is met under [stated condition]. In simulation, design priors representing [pessimistic scenario] and [optimistic scenario] were used to assess performance when the analysis prior is wrong.”
The Bayesian draft describes the usual form of the criterion as based on the posterior probability that the true effect exceeds a threshold, \(\Pr(\delta > a \mid \text{data}) > c\), where \(a\) is the minimum benefit and \(c\) the minimum probability. It asks the sponsor to justify both \(a\) and \(c\), to give criteria for each primary and key secondary estimand, and, if the design is calibrated, to provide simulation evidence that the familywise error rate is controlled (U.S. Food and Drug Administration 2026d). The draft also recognizes that calibration to 0.025 “may not be applicable or appropriate” in some cases, for instance with borrowing, and describes two other routes, in which success rests on a direct interpretation of the posterior or on a decision-theoretic or benefit-risk criterion (Section IV.A.3) if sponsor and FDA agree in advance. A sponsor who wants that route has to ask for it, in a meeting, with a reason. The BNT162b2 statistical analysis plan is a worked example: posterior thresholds of 0.995 at the interim analyses and 0.986 at the final analysis, chosen so that the overall one-sided type I error is 2.5% (see “In practice” below).
“The trial will be declared successful for the primary estimand if, at the final analysis or at an interim analysis specified in Section [x], \(\Pr(\theta > a \mid \text{data}) > c\), with \(a =\) [value, with clinical rationale] and \(c =\) [value]. The threshold \(c\) at each analysis was calibrated by simulation so that the probability of declaring success under the null hypothesis \(\theta = 0\), across all analyses in the schedule and under the stated enrollment and dropout assumptions, does not exceed 0.025 one-sided. Simulation details are in the simulation report (version [x], dated [date]); the code and seeds are provided. If the number or timing of analyses departs from the schedule, the thresholds will be recomputed as described in Section [y] only if the change is demonstrably independent of comparative interim results, follows a prespecified rule whose timing mechanism was simulated, or is handled by a prespecified conditional-error method.”
E9 says that interim analyses “should be carefully planned in advance and described in the protocol”, and E20 repeats the point for adaptations in general. A Bayesian posterior is formally unaffected by how many times it is computed, and that is a property of the posterior, not of the decision rule. A rule that stops when a posterior probability crosses a threshold has operating characteristics that do depend on when and how often it is evaluated (Chapter 11). The protocol therefore does not say “continuous monitoring”. It says when looks occur, by information fraction or calendar rule, who sees them, what decisions are possible at each (stop for efficacy, stop for futility, continue, change allocation, drop an arm), and what happens if a look is missed or added. A look added after an external publication is a deviation from the simulated design, and the protocol should say what will be done about it, which is acceptable to handle by recalibration only if the change was demonstrably independent of comparative interim results, followed a prespecified rule whose timing mechanism was simulated, or is handled by a valid conditional-error approach; keeping the sponsor blinded does not by itself establish independence, and treating a schedule shaped by interim results as fixed ignores the selection mechanism (U.S. Food and Drug Administration 2019). Chapter 12 describes the alternative of an anytime-valid rule, whose guarantee holds at any stopping time but at the price discussed there. The DAWN stroke trial wrote its whole predictive-probability stopping schedule into the SAP (see “In practice” below).
“Interim analyses will take place when [number] participants (or events) have been observed on the primary endpoint, planned at [information fractions]. At each interim analysis the independent statistical center will compute (a) \(\Pr(\theta > a \mid \text{data})\) and (b) the predictive probability of success at the maximum sample size. The DMC will be informed of the following rules, and the sponsor will not see unblinded comparisons: stop for efficacy if (a) exceeds [\(c_k\)]; stop for futility if (b) is below [value]; otherwise continue. The DMC may recommend stopping for safety or any other reason at any time under the charter, independent of these rules. No unscheduled efficacy analysis will be used to support an efficacy claim without a protocol amendment and recalculation of the operating characteristics; safety review and DMC action under the charter are unaffected.”
If the design uses response-adaptive randomization, the rule belongs in the protocol, and so do its limits. Chapter 16 covers why a reviewer’s first questions concern time trends, bias in the estimate, and whether the control arm retains enough participants. EMA’s October 2026 draft reflection paper on confirmatory platform trials does not support response-adaptive randomization in that setting (European Medicines Agency 2026) (a draft, and its position on this point is a reason to ask EMA early). FDA’s Adaptive Designs guidance does not forbid it but asks that the chance of erroneous conclusions be controlled and the estimates be reliable. Adaptive randomization has a long Bayesian pedigree in dose finding and elsewhere (Thall et al. 2015). Many Bayesian protocols therefore use a restricted rule: a fixed burn-in at equal allocation, a floor on each arm’s probability, a cap on any change in allocation between updates, and analysis stratified by allocation period.
“After a burn-in of [number] participants randomized 1:1, allocation to each experimental arm will be updated every [number] participants in proportion to the posterior probability that the arm is best, raised to the power [value], subject to a minimum of [percentage] of participants per arm and a maximum change of [percentage points] between updates. The control arm will receive at least [percentage] of participants. The primary analysis will adjust for calendar period [method]. The operating characteristics of the rule, including bias of the effect estimate and the probability of allocating more than [x] participants to an inferior arm, are in Section [z] of the simulation report.”
Traditional protocols often leave safety stopping to the DMC’s judgment, with a guideline. A Bayesian protocol can state it as a posterior probability, which is more transparent and, more usefully, can be simulated: what is the probability that a safe arm is stopped, and that a harmful arm is not? The safety rule sits outside the efficacy error budget, so the protocol should say what its own false-stop rate is, and who may override it.
“An arm will be suspended and referred to the DMC if, at any safety review, \(\Pr(\text{[event rate]} > [\text{limit}] \mid \text{data}) > 0.90\) under the prior in Section [x]. Reviews take place after every [number] participants per arm. By simulation, the probability of suspending an arm whose true event rate equals [acceptable rate] is [value], and the probability of suspending an arm whose true rate equals [unacceptable rate] within [number] participants is [value]. The rule is a trigger for DMC review, not an automatic stopping rule.”
Nothing about the estimand is different in a Bayesian trial, and that is the point. E9(R1) defines an estimand as “a precise description of the treatment effect reflecting the clinical question posed by a given clinical trial objective” and requires that “the targets of estimation are to be defined in advance of a clinical trial” (International Council for Harmonisation 2019). It has five attributes: the treatment, the population, the variable, the strategy for each intercurrent event, and the population-level summary. The posterior is a summary of the data about a parameter, and the parameter is the estimand. The common error is to build a Bayesian model for a convenient analysis, a model on the observed outcome ignoring discontinuation, and then describe it afterwards in estimand language. The protocol should do it in the other order.
“The primary estimand is the [summary, for example hazard ratio] of [variable] at [time] for participants with [condition], comparing [treatment] with [control], under a treatment policy strategy for [intercurrent event 1] and a [hypothetical, composite, while on treatment] strategy for [intercurrent event 2]. The Bayesian model in Section [x] targets this estimand: the parameter \(\theta\) is [definition]; the likelihood handles [intercurrent event] by [method]. Sensitivity analyses address [list].”
The SAP is finalized before unblinding, and for a Bayesian design it carries the detail the protocol should not: the exact model, the likelihood, the parameterization of the prior, the computation (software, sampler, chains, burn-in, convergence diagnostics, seeds), the handling of missing data and intercurrent events in the model, the full set of success criteria at each analysis, and the plan for sensitivity analyses. The Bayesian draft asks for all of this “as early as possible” and says that FDA does not require any particular software (U.S. Food and Drug Administration 2026d). It asks that reproducibility be built in at the results stage as well: software versions, documented code and the seeds used to initialize chains. For the primary analysis it also fixes the baseline covariates for adjustment, the stratification factors that enter the model, the handling of missing covariate values and whether the estimand is conditional or marginal, as set out in Section 5.10.
The simulation report is a separate document, and for a Bayesian or complex adaptive design it is the central one. It is what replaces, for the reviewer, the closed form power calculation. Chapter 14 describes how to design the simulation and what to report; choosing a design by simulation has a longer history in Bayesian decision theory (Müller and Parmigiani 1995). For the protocol, what matters is the contents a regulator will look for, assembled from the Bayesian draft, the Adaptive Designs guidance and E20 Section 5:
The calibration that the SAP and the simulation report both reference can be a few lines of R. The chunk below simulates a binary-endpoint trial with four looks under the null (30% response in both arms), takes the success threshold \(c\) as the value for which the chance of crossing at any look is 2.5% in that calibration run, and then reports the operating characteristics at that threshold in a fresh null run with another seed and under a design alternative (30% against 45%). The report would give the same output for every scenario in the grid, with the seed and the package version.
sim0 <- oc_simulate(0.30, 0.30, looks = c(50, 100, 150, 200), nsim = 20000, seed = 2026)
c_star <- oc_calibrate(sim0, alpha = 0.025)
sim1 <- oc_simulate(0.30, 0.45, looks = c(50, 100, 150, 200), nsim = 20000, seed = 2027)
sim0v <- oc_simulate(0.30, 0.30, looks = c(50, 100, 150, 200), nsim = 20000, seed = 2028)
oc0 <- oc_summarize(sim0, c_star); oc0v <- oc_summarize(sim0v, c_star); oc1 <- oc_summarize(sim1, c_star)The calibrated threshold is \(c =\) 0.9904. The rejection proportion in the calibration run itself, 0.0249, is the calibration target and not an error assessment. On the fresh null run the type I error is 0.025 (Monte Carlo standard error 0.0011), and a protocol would repeat that validation across its prespecified nuisance grid (event rate, dropout, accrual). The power is 0.815, and the expected total sample size is 264 under the alternative against a maximum of 400. The same simulation gives the bias of the observed difference among trials that stop early for success, 0.062 under the alternative, which is the number the simulation report must show for the early-stopping reasons given in Chapter 21. The scenario grid, the futility rules (oc_with_futility) and the prior (the prior argument) are added the same way.
A sponsor that has done the calibration of Chapter 14 can write this report from its outputs. The report is versioned, and the protocol references a version by date, so that the design that was simulated is demonstrably the design that was run.
A final point about the SAP. The temptation in an adaptive design is to leave details to be fixed at an interim. E20 says the opposite: the number and complexity of adaptations in a confirmatory trial should generally be limited, and everything that drives a decision is prespecified. A Bayesian SAP that defers the prior or the success threshold to a later version has not prespecified the design.
Two standards shape the document itself, and neither is specific to Bayesian designs. ICH M11, the Clinical Electronic Structured Harmonised Protocol (CeSHarP), reached Step 4 in November 2025 and comes with a harmonized template and a technical specification, so that protocols present the same information in the same place and can be exchanged in a format acceptable to regulators (International Council for Harmonisation 2025b). SPIRIT 2025 is a checklist of minimum items a protocol of a randomized trial should address (Chan et al. 2025). The reporting counterpart for adaptive trials is the CONSORT 2010 adaptive-designs extension (ACE) (Dimairo et al. 2020).
The practical consequence is a mapping problem. M11 has sections where the design and statistics go, and a Bayesian design has components (prior, simulation-based calibration, predictive probability rules) that the template does not name. The sponsor should place them where a reviewer would look for the traditional counterpart: the prior with the statistical hypotheses and analysis methods, the decision rules with the interim analysis section, the operating characteristics with the sample size justification, and the detailed model and computation in the SAP, which the protocol references. The test of a good mapping is that a reviewer who has read only the protocol knows that the design is Bayesian, what the success criterion is, and where the simulation report is. A protocol that mentions “Bayesian methods” only in an appendix invites the first review question to be “where is the prior”.
Several reporting guidelines sit around the protocol, and none of them is a regulatory requirement for a Bayesian trial. SPIRIT 2013 (Chan et al. 2013) is the antecedent of SPIRIT 2025, CONSORT 2025 (Hopewell et al. 2025) is the reporting guideline for the results of a randomized trial, ACE, which extends CONSORT 2010 and predates CONSORT 2025, adds items on the pre-specified adaptations, and a guideline on the content of statistical analysis plans lists what the SAP should contain (Gamble et al. 2017). Only a few guidelines are written for Bayesian analyses, and they are author guidelines: the seven-item ROBUST checklist for reporting a Bayesian analysis of a clinical study (Sung et al. 2005), the Bayesian Analysis Reporting Guidelines (BARG) (Kruschke 2021), and a consensus checklist for clinicians who read a trial analyzed by Bayesian methods (Ferreira et al. 2020). The items a Bayesian trial adds to the generic lists are the same ones this chapter has put in the protocol: the prior and its source, the success criterion with its threshold and calibration, the interim schedule and the simulation report, the software and seeds, and the sensitivity analyses to the prior. A report that gives each of them where the generic checklist asks for its traditional counterpart satisfies the intent of all of these lists. ## The data monitoring committee, firewalls, and who sees what
Adaptive trials add a requirement that fixed trials mostly avoid: someone must see unblinded comparative data during the trial in order to apply the adaptation rules, and the sponsor must not. The Adaptive Designs guidance lists trial integrity as one of its four principles, and the integrity concern is that knowledge of interim results, or even of what decision was made, can change the behavior of investigators, patients and sponsor staff, and so bias the trial. The practice is by now standard, and the DMC guidance of 2006 (U.S. Food and Drug Administration 2006) remains the starting document (FDA issued a draft revision in February 2024). What a Bayesian adaptive design adds is that the DMC charter must spell out the rules in more detail, because more of the design is executed at interim.
A workable arrangement has four parties.
“An independent DMC, whose membership and charter are described in Appendix [x], will review unblinded data at each analysis in Section [y]. The independent statistical center will compute all decision quantities; no member of the sponsor’s study team, the investigators or the CRO’s blinded team will have access to unblinded comparative results or to the current allocation ratios, except [named roles and what they see]. Access to the unblinded system is logged. The DMC charter specifies the prespecified rules, the DMC’s authority to depart from them for safety or other reasons with documentation, the meeting schedule, the content of closed and open reports, and the communication path to the sponsor. A copy of the simulation report is available to the DMC.”
What does a Bayesian design change about who sees what? Two things. First, the DMC should receive the simulation report, or a summary, so that its members know what the rules were designed to do and how often they are expected to trigger. A DMC that is asked to apply a posterior probability rule it does not understand will either follow it blindly or ignore it, and neither is acceptable. Second, firewalls in a platform trial are more complex, since arms enter and leave, and a sponsor of one arm should not see data of competing arms. Chapter 20 describes the structure, and one independent statistical center with one DMC over all arms is a possible arrangement. FDA permits an independent external DMC or another appropriate independent entity, and the EMA reflection paper discusses separate analysis or study teams for different interventions, so the proposed structure has to protect independence and confidentiality across arms (U.S. Food and Drug Administration 2026c; European Medicines Agency 2026).
A regulator should never meet a Bayesian design for the first time in the submission. The Bayesian draft says that for complex designs the sponsor should request a meeting before the trial starts, and the substantial evidence draft says that a single-trial plan should be discussed with FDA before the single trial is started. The sequence below is the one a sponsor with a Bayesian confirmatory design should plan around. Meeting types and timelines are from the PDUFA formal meetings guidance of August 2026 (U.S. Food and Drug Administration 2026b); the program descriptions are from FDA’s program pages and the CID guidance (U.S. Food and Drug Administration 2020), which a sponsor should reread before applying, since program details change with each PDUFA cycle.
| Stage | Meeting or program | What a Bayesian sponsor brings |
|---|---|---|
| Early development | INTERACT (for novel products before first-in-human); Critical Path Innovation Meeting (CPIM) for a method not tied to a product | Questions about a general approach, for instance a dose-finding design (Chapter 17) or a borrowing method. |
| Pre-IND | Type B meeting | The development plan and, where a Bayesian phase 1 or 2 design is proposed, the design and the safety rules. |
| Phase 2 design | Type C or Type B; CID or MIDD paired meeting for a complex design | The proposed adaptive or Bayesian design, with a simulation report. |
| End of phase 2 | Type B (end of phase) | The phase 3 design: estimand, prior, success criterion and calibration, interim plan, evidence package. |
| Phase 3 protocol | Special Protocol Assessment (SPA) request; Type C | The final protocol and SAP; agreement on the design and analysis. |
| Before database lock | Type C | Changes to the SAP (but not the design, which cannot change after unblinding), and handling of deviations. |
| Pre-NDA or BLA | Type B | The planned submission, including the simulation report and the prior sensitivity analyses. |
Meeting types. Type A is for a stalled program or an important safety issue, Type B covers milestone meetings including pre-IND and end-of-phase meetings, Type C is any other meeting, Type D is a focused meeting on one or typically not more than two issues, and INTERACT is for novel products with unique early development challenges (U.S. Food and Drug Administration 2026b). In calendar days from receipt of the request, FDA’s response time is 14 for Type A, 21 for Type B, 14 for an end-of-phase Type B, 21 for Type C, 14 for Type D and 21 for INTERACT. Scheduling the meeting, or delivering a written response only (WRO), is 30 days for Type A, 60 for Type B, 70 for an end-of-phase meeting, 75 for Type C and 50 for Type D (Tables 1 and 2 of the guidance; the guidance says when the meeting is scheduled relative to the request, and the times in force should be checked against the guidance in effect). A sponsor planning a protocol should count backwards: an end-of-phase meeting requested in January is a spring meeting, and the simulation report has to be ready before the briefing package is due, which is earlier. The meeting is an opportunity to get written FDA feedback on the design, and the format of a written response only is often enough for a narrow question such as whether the proposed prior is acceptable.
The CID paired meeting program. FDA’s Complex Innovative Trial Design program was established under the PDUFA VI commitments, and continued under PDUFA VII, to give sponsors extra interaction on designs whose operating characteristics cannot be derived in closed form, which in practice means Bayesian designs and complex adaptive designs (U.S. Food and Drug Administration, n.d.c). The December 2020 guidance describes how to interact with FDA on such designs (U.S. Food and Drug Administration 2020). As the program page describes it, the program now runs under PDUFA VII for fiscal years 2023 to 2027 and is run by CDER and CBER. Requests are due on the last day of each quarter (31 March, 30 June, 30 September, 31 December), FDA notifies sponsors within 45 days, and it selects one or two proposals per quarter, up to eight a year. A granted request receives an initial meeting and a follow-up meeting on the same proposal, the second approximately 90 days after FDA receives the briefing materials, which is when the simulation work is done and a reviewer can say something concrete. The sponsor needs a pre-IND or IND number, the trial cannot be first in human, and there must be enough clinical information to inform the proposed design. Before the first meeting the sponsor and FDA agree which information FDA may publish in a public case study, which is how the January 2026 draft can name examples. To apply, a sponsor submits a request that describes the product and the development program, the proposed design and why it needs the program (what is complex about it), the planned use in an application, the simulation plan, and why the design is better for this product than a conventional alternative. A selection is not an agreement on the design, and the program is not a substitute for the regular Type B and C meetings.
MIDD paired meetings. The Model-Informed Drug Development Paired Meeting Program offers a similar structure for modeling and simulation in a specific program (U.S. Food and Drug Administration, n.d.e). A Bayesian design with a pharmacometric component, such as exposure-response modeling to support dose selection or a prior built from a model, may fit here as well as at CID. The ICH M15 guideline on model-informed drug development (Step 4 in January 2026, International Council for Harmonisation (2026)) frames the discussion in terms of question of interest, context of use, model influence, consequence of a wrong decision and model risk. A Bayesian trial whose prior or analysis depends on a model can use that vocabulary: the more the model decides, and the worse the consequences of a wrong decision, the more evaluation the regulator will want.
CPIM. Critical Path Innovation Meetings are nonbinding and not tied to a product, and are aimed at discussing emerging methods and technologies (U.S. Food and Drug Administration, n.d.d). A sponsor who has developed a method, for example a way to build a prior from historical data in a specific disease area, can seek FDA’s informal views before any product depends on it. FDA describes CPIM discussions as non-regulatory, product-independent and nonbinding on both FDA and the requester, and says they do not substitute for pre-IND, IND, NDA or BLA meetings.
Special Protocol Assessment. An SPA is a request for FDA’s written agreement on the design, endpoints and statistical analysis of certain trials, including trials intended to form the primary basis of an efficacy claim, whatever their phase (U.S. Food and Drug Administration 2018). The current guidance is the April 2018 revision. If FDA agrees, the agreement is documented, and FDA will not change its position on the agreed critical design elements unless a substantial scientific issue essential to determining safety or effectiveness is identified after the trial begins and the sponsor is notified (the statute also allows changes by agreement with the sponsor). An SPA resubmission after FDA comments is reviewed on a 45-day goal. It is worth considering for a Bayesian confirmatory trial, because it gets the prior, the criterion and the calibration agreed in writing before the data are seen. It is also demanding: FDA will not agree to what it has not seen, so the SAP and the simulation report must be complete, and the process will expose any design that cannot be defended. A sponsor should read the guidance on what happens if the sponsor changes the design afterwards. An SPA does not guarantee approval, or even that FDA will file the application: the agreement is about the design and not the result.
What to send. The Bayesian draft’s Section VIII is a ready list of what FDA wants in a pre-trial package: the prior and its justification; for informative priors the sources, including those excluded; the success criteria and the justification of \(a\) and \(c\); simulation evidence of familywise error control if calibrated, or Bayesian power and related metrics if not; the full simulation report with code; the computational details; and a comparison with simpler designs (U.S. Food and Drug Administration 2026d). A briefing package structured around that list makes the meeting short.
What to ask. Meetings are won by specific questions. “Is a Bayesian design acceptable?” gets a vague answer. “Does FDA agree that the success criterion \(\Pr(\theta > 0.1 \mid \text{data}) > 0.985\), calibrated to a one-sided familywise error of 0.025 under the scenarios in Table [x], is acceptable for the primary estimand?” gets a yes, a no with reasons, or a request for more simulation. Good questions name the prior, the criterion, the scenario grid, the interim schedule, the borrowing (if any) and the evidence package.
At EMA the corresponding route is scientific advice from the CHMP, with the Scientific Advice Working Party, and for novel methods a qualification procedure or the Innovation Task Force; in the EU the Complex Clinical Trials Q&A of the Commission, EMA and the Heads of Medicines Agencies discusses Bayesian methods and recommends early dialogue (European Commission and European Medicines Agency and Heads of Medicines Agencies 2022). The Q&A asks sponsors to justify the use of Bayesian methods and to document priors. The 2007 reflection paper on adaptive designs is more conservative than the FDA’s guidance; ICH E20 is a Step 2 draft, and until it is final the 2019 guidance is FDA’s current final guidance. The October 2026 draft reflection paper on confirmatory platform trials takes a cautious position on response-adaptive randomization and non-concurrent controls (European Medicines Agency 2026). The practical advice is that a global development should plan for both agencies, request advice from EMA in parallel, and raise the points where the agencies may differ (adaptive randomization, borrowing from non-concurrent controls) in both. Where agencies differ, the protocol follows the stricter reading unless advice says otherwise. The structured protocol format, ICH M11, is harmonized, which helps. Details of the programs, with their dates and links, are in Appendix B.
The legal standard is in FD&C Act section 505(d), and 21 CFR 314.126 defines the adequate and well-controlled investigation. The statute speaks of “adequate and well-controlled investigations”, and for decades the working interpretation was two trials, each significant at two-sided 0.05, which is one-sided 0.025 each. The book’s companion online lab (module 11, https://nytel.ai/testing/11-substantial-evidence.html) shows what that rule means arithmetically: a useless drug wins one trial in 40, and wins two independent trials about one time in 1,600 (one-sided 0.025 squared). Two trials are a strong filter, and a costly one.
FDA’s revised draft guidance of June 2026 describes when one adequate and well-controlled trial plus confirmatory evidence can satisfy the standard (U.S. Food and Drug Administration 2026a). A draft, not final, and not binding. It says that such an approach “will involve a highly persuasive trial or a source of strong confirmatory evidence” (Section IV.A). Among the factors it weighs: the seriousness of the disease and the unmet need, and “whether it is ethical and practicable to conduct more than one adequate and well-controlled trial”. Confirmatory evidence need not be another trial. The draft allows mechanistic evidence of the drug’s treatment effect in a particular disease as confirmatory evidence in appropriate cases. And it says that the plan “should be discussed with FDA prior to initiating the single trial”. The 2026 text revises the 2019 draft of the same name.
Where does Bayesian evidence fit? Three places, and they need to be kept apart.
First, a Bayesian trial can be one of the two trials, or the one trial. If its success criterion is calibrated to a familywise one-sided error of 0.025, it meets the default frequentist bar, and a reviewer treats it as a trial with a different analysis. This is the cleanest case, and nothing in the substantial evidence standard requires a \(p\)-value.
Second, a Bayesian analysis can combine the one trial with other evidence in a formal way. A prior built from earlier data, a borrowing model from an adult trial for a pediatric population, or a hierarchical model across related populations is a way to represent the confirmatory evidence. FDA’s Bayesian draft discusses borrowing, and the REBYOTA program, where a prior phase 2 trial informed the phase 3 analysis, is the example it gives (Chapter 19; the “In practice” section below shows how its two success thresholds map onto one trial and two trials). The draft warns that a prior that is too informative “risks overwhelming the data collected in the target population”, that dynamic discounting should borrow less when the data are less similar, and that type I error inflation is a poor measure of borrowing, so the sponsor must propose and justify other metrics such as the ESS. Here the Bayesian method does what the substantial evidence draft asks to be done informally. It does not remove the need for the persuasion: the judgment of whether the other evidence is relevant and strong remains with FDA.
Third, a Bayesian posterior probability can be offered as the measure of persuasiveness. A trial whose posterior probability of benefit is 0.9999 under a skeptical prior is “highly persuasive” in a way that a trial with \(p = 0.024\) is not. The draft does not say that a particular posterior probability makes a trial highly persuasive, and a sponsor should not claim so. The honest position is that the measure of how persuasive a single trial is can be stated on the posterior scale, as it can be stated on the \(p\)-value scale or as predictive probability of replication, and the reviewer decides. Module 11 of the companion lab makes this concrete: a trial that barely wins repeats only about half the time if its observed effect is the true effect, so a single marginal win is not persuasive on any scale. And the substantial evidence standard is not lowered by a fast review: expedited programs speed the review of serious conditions and do not lower the proof.
A final caution, from Chapter 21 and Chapter 7: among single trials that stop early for efficacy under a calibrated Bayesian rule, the observed effect estimate is biased away from the null on average, and the sponsor should show the bias in the simulation report and report estimates that account for it where possible. A highly persuasive single trial is persuasive about the existence of an effect, and its estimate may still need shrinkage.
Five documents show how sponsors wrote Bayesian rules into protocols and SAPs and what regulators did with them. Two are SAPs, one is an FDA briefing document, one an FDA case study, and one the FDA’s own January 2026 list of design examples.
The vaccine trial’s SAP wrote a beta-binomial success criterion with posterior thresholds of 0.995 at the interim analyses and 0.986 at the final analysis, calibrated so that the overall one-sided type I error was 2.5% (Pfizer Inc. 2022). The full case, with the prior, the arithmetic and the regulatory outcome, is in Section 21.5. FDA’s announcements contain no statement on the Bayesian criterion, so the lesson is about the sponsor’s side: a prior with its numbers stated, a calibrated threshold, a nonbinding futility rule and a changed look schedule (the first interim analysis was not performed) handled by saying what remained fixed. The binomial model assumes equal surveillance time in the two arms, an approximation that FDA’s briefing document adjusts with the surveillance-time ratio.
DAWN’s SAP is the most complete Bayesian adaptive design among this chapter’s sources: every threshold, every look, the enrichment rule and its irreversibility, and the predictive-probability stopping bounds were fixed before unblinding, with the type I error a simulation output (Stryker Neurovascular 2017; Jovin et al. 2017). The design is discussed in Chapter 15 and Chapter 14.
The protocol lesson is that success thresholds can be written in the language of the substantial evidence standard (analogues of a one-sided 0.025 for one trial and 0.00125 for a substitute for two), and that exchangeability is something the reviewer tests in the data alignment. The full case is in Section 19.17.1.
The protocol lesson is that when a borrowing weight cannot be justified in advance, a tipping-point table is a defensible fallback, and it is a post hoc one. FDA’s case study recommends early consultation, ideally at a pre-IND meeting, and discussion of the detailed analysis plan before the clinical investigation begins (U.S. Food and Drug Administration, Center for Drug Evaluation and Research 2026). The full case is in Section 19.17.2.
Two of the examples in FDA’s Bayesian draft come from the CID program, whose case studies are published (U.S. Food and Drug Administration 2026d). A pediatric multiple sclerosis study is a randomized, double-blind, Bayesian group sequential non-inferiority trial against an approved active control, with one interim analysis for efficacy, using a robust meta-analytic-predictive prior from a completed pediatric trial and several adult trials, and FDA lists the first use of an active-controlled non-inferiority design in this setting, the borrowing, and model-based extrapolation from adults as the innovative features (U.S. Food and Drug Administration, n.d.b). An epilepsy with myoclonic-atonic seizures (EMAS) study is a placebo-controlled trial that borrows from related epilepsy populations through a hierarchical model, with sample size updated at unblinded interim analyses by Goldilocks predictive probabilities (U.S. Food and Drug Administration, n.d.a). Both are proposals discussed in the program, not approvals, and the case studies say so by calling them proposed. The lesson for this chapter is what the CID route produced: a published description of a design FDA found worth discussing, which a sponsor can cite in its own briefing package.
A protocol chapter should say what the design cannot do, because sponsors who believe otherwise write the wrong protocol. There are four limits, taken from the working paper (Polson and Sokolov 2026) and stated plainly.
The saving is not against a single unadjusted analysis at a fixed level. The Bayes-factor bar is below the unadjusted \(z_\alpha^2\) only at small information: it exceeds it once \(I_n\tau^2\) passes about 41.6 for the exact normal-mixture boundary (for a unit-information prior, \(n > 41.6\); Chapter 11). In the SELECT reconstruction an unadjusted single look crosses at 309 events on the mean path, earlier than the calibrated Bayesian rule’s mean-path crossing near 600 events (conditional median stopping point 464). The unadjusted single look is not available to anyone who intends to look more than once, and the Bayesian gain is against the repeatedly monitored trial with the right error control, not against the fixed single look. Against a single analysis, the calibrated Bayesian bar is never lower unless an informative prior or borrowing is used.
The surcharge the Bayesian rule avoids buys a real guarantee. An e-value rule holds its level at every stopping time, including ones the protocol never contemplated: a look inserted after an external publication, an early stop ordered for reasons outside the trial, continuous unblinded inspection by a committee. A calibrated Bayesian rule holds 2.5 percent under the scheme to which it was calibrated, and under another scheme it holds something else. A sponsor who cannot commit to a monitoring plan should read Chapter 12 before choosing.
The calibration requires knowing the monitoring plan and the horizon. That is exactly the knowledge the anytime valid construction is built to do without. The two paradigms make different promises. In protocol terms: the Bayesian design is credible only if the schedule is fixed, the horizon is stated, and deviations trigger a recalibration that is independent of interim results.
The power ordering is not universal. In the SELECT reconstruction the calibrated Bayesian rule had higher power than the e-value rule, 94.7 against 83.1 percent. In a two arm binary endpoint design reported by Sokolova and Sokolov (2026) the order is reversed, 68.8 against 72.3 percent, with the Bayesian rule stopping slightly earlier. The comparison depends on prior scale, endpoint and monitoring grid. The robust finding concerns stopping time, not power, and the direction of the power difference should be checked by simulation for the design at hand.
Two further statements belong with these, from the case studies. The traditional scheduled design wins in some settings: the REWIND comparison in Chapter 21 is one, a single look with a sponsor that has no interest in early stopping. And no design, Bayesian or otherwise, removes the need for an adequate and well-controlled trial. A Bayesian design with a poor control, a bad endpoint or an unblinded outcome assessment is still a poor trial.
For the sponsor, before the end-of-phase 2 meeting and again before the protocol is final:
For the reviewer, reading a Bayesian submission:
Two pieces of advice are distinctive to this book and worth stating once. Clinicians and payers should ask what prior was used and how many patients it was worth, and should read a posterior probability as conditional on the model and the prior. Sponsors, regulators and statisticians should decide early whether the trial needs validity at stopping times the protocol cannot anticipate, and should report the realized type I error of whatever rule is used, with power beside it and stopping times as distributions. The key points below summarize the chapter.
Several questions remain open. The e-value price is exact for mixture e-values built on the same statistic as the Bayes factor, as an extra squared-standardized gap of \(2\log(1/\alpha)(1+1/q)\), whose constant large-information approximation is \(2\log(1/\alpha) = 7.38\) at \(\alpha = 0.025\) (Chapter 11). For betting e-processes with adaptively chosen bets the analogous quantity depends on the strategy and we have no general expression. The calibration of a posterior rule to a frequentist error under continuous monitoring, which this book did numerically, has no asymptotic characterization here. A posterior-probability cutoff cannot itself diverge, so any such result would concern a transformed boundary, such as the implied standardized boundary, over a stated monitoring horizon, and we do not state one. Finally, the utility-based designs of Thall and Cook (2004) and Houédé et al. (2010) have operating characteristics that have not been compared with the conventional apparatus on the deviation-scale ledger of Chapter 11, and doing so would show whether the phase 1 and 2 savings have the same source as the confirmatory ones.
Module 11, Substantial evidence (https://nytel.ai/testing/11-substantial-evidence.html): choose a first trial result and predict how often a second trial of the same drug would also win, then run it. Compare the answer for a marginal win with a very small \(p\)-value, and see why “highly persuasive” matters for the one-trial route.
Module 12, Decisions (https://nytel.ai/testing/12-decisions.html): move the type I error limit and watch what it costs in patients. Predict whether tightening or loosening the limit changes the false alarms or the missed drugs more, then check.
Module 13, Regulators’ map (https://nytel.ai/testing/13-regulators-map.html): open the meeting clocks and find the days FDA takes to reply to a Type B end-of-phase request and the days to the meeting. Count back from a planned protocol date to the date by which the request must be filed.
Module 14, Studio (https://nytel.ai/testing/14-studio.html): the full open simulator. Build the four-look design of the code chunk above, set the scenarios and read the operating characteristics table, the same table a simulation report carries. Predict first whether the calibrated threshold changes when the looks move, then check.