8  Clinical Trial Design

8.1 Learning objectives

By the end of this chapter you should be able to:

  • Distinguish trial phases (I, II, III, IV) and identify the design questions specific to each.
  • Choose between simple, stratified, block, and covariate-adaptive randomisation, and recognise the consequences of each for analysis.
  • Conduct a sample-size calculation for a two-arm trial with a continuous, binary, or time-to-event endpoint, including non-inferiority designs.
  • Apply the ICH E9 R1 estimand framework to a proposed trial protocol and identify the primary estimand attributes.
  • Recognise when an adaptive, group-sequential, or pragmatic design is the right choice and articulate the trade-offs.

8.2 Orientation

Clinical trial design is where the biostatistician makes some of the most consequential decisions in the project: the primary endpoint, the sample size, the randomisation procedure, the stopping rules, the estimand. Each decision constrains the trial’s ability to answer its question; collectively they determine whether the trial succeeds or produces ambiguous data.

This chapter covers design; Chapter 9 covers analysis and reporting. The split mirrors the temporal flow of trial work: design happens before any patient is enrolled and is documented in the protocol; analysis happens after enrolment is complete and is documented in the SAP. Design decisions cannot be undone after the trial starts.

The chapter is organised in three threads. Design fundamentals: phases, randomisation, blinding, sample size. The estimand framework (continuing from Ch 1): how to specify what the trial estimates. Modern designs: adaptive, group-sequential, pragmatic, platform.

8.3 The statistician’s contribution

Three judgements are not delegable.

(Judgement 1.) The primary endpoint defines the trial. Everything else — sample size, analysis, stopping rules — flows from it. The biostatistician chooses the primary endpoint by considering three things: clinical relevance (does it inform a decision), measurability (can it be reliably ascertained in this trial), and statistical efficiency (how much information does it contain per patient). A composite primary endpoint is sometimes the right answer, but introduces interpretation complexity; a continuous endpoint is sometimes the right answer, but may not match the regulatory question.

(Judgement 2.) Sample size is a contract with the data. The sample size is computed from the primary analysis’s effect size, variability, type I error, and power. The biostatistician’s role is to defend each input, not to engineer the calculation to produce a feasible \(n\). An optimistic effect-size assumption produces a trial powered to detect an effect that does not exist; a pessimistic one produces a trial too large to enrol.

(Judgement 3.) Estimands precede randomisation. The estimand framework (Ch 1) applies in trials with particular force because intercurrent events (treatment discontinuation, switching, death) are known in advance to occur. The biostatistician specifies the primary estimand and the intercurrent-event strategy in the protocol, before any data is collected. ITT is a treatment-policy strategy; it is one estimand among several, not the default for every trial.

These judgements are what distinguish a trial that informs a regulatory or clinical decision from a trial that produces ambiguous data.

8.4 Phases of clinical development

Phase I: first-in-human, dose-finding. Small (often 20-80 patients), often healthy volunteers (oncology exception). Primary endpoint typically safety, pharmacokinetics. Designs: 3+3, model-based (CRM, EWOC, BOIN), Bayesian-adaptive.

Phase II: efficacy signal in patient population. Single-arm or small randomised, 50-200 patients. Primary endpoint often a surrogate (response rate, biomarker change, PFS) rather than a hard endpoint. Designs: Simon’s two-stage, Bayesian-adaptive.

Phase III: definitive efficacy. Large randomised (hundreds to thousands), powered for hard clinical endpoints. The phase that supports regulatory approval. Standard designs: parallel-group, two-arm; sometimes multi-arm or factorial.

Phase IV: post-approval surveillance and real-world effectiveness. Pragmatic designs, often embedded in routine care. Outcomes include long-term safety, real-world effectiveness, comparative effectiveness.

The chapter focuses on Phase III conventions, since those are most fully developed and most commonly encountered in MS-level biostatistical work. Phase I designs require a separate methodology (the ‘A Practical Guide to Biostatistics’ literature) beyond the scope here.

8.5 Randomisation

The point of randomisation: balance unmeasured confounders in expectation, eliminate selection bias by the investigator, create a reference distribution for the test statistic.

Simple randomisation: each patient assigned independently with probability 0.5 (for a 1:1 trial). Easy; can produce imbalance in small trials.

Block randomisation: assign in blocks of size 2, 4, or 6 (or vary the block size). Guarantees balance at the end of each block; reduces imbalance from chance. Standard for most trials.

Stratified randomisation: block randomisation within strata defined by one or more baseline variables (e.g., centre, disease stage). Guarantees balance within strata. Use when the strata are strongly prognostic and the trial is small enough that imbalance within a stratum could matter.

Covariate-adaptive randomisation (e.g., minimisation): assigns each new patient based on the current imbalance across multiple baseline variables. Achieves better balance than stratified randomisation but introduces a degree of predictability that some regulatory bodies discourage. The literature is mixed (Taves, 2010); check current FDA / EMA guidance.

Implementation: most trials use a centralised randomisation system (web or IVRS) that handles the mechanics. The biostatistician specifies the procedure in the protocol; an unblinded statistician (separate from the analysis team) sometimes implements and monitors.

The analysis must respect the randomisation procedure. A stratified randomisation requires stratified analysis; ignoring the stratification inflates the type I error.

8.6 Blinding

Blinding addresses bias from differential treatment or assessment of outcomes:

  • Single-blind: the patient does not know their assignment.
  • Double-blind: neither patient nor investigator knows.
  • Triple-blind: patient, investigator, and analysis team are blinded.

Blinding is rarely fully achievable for invasive treatments (surgery, devices) and is sometimes infeasible for behavioural interventions. When blinding fails, the analysis should examine investigator effects and consider sensitivity analyses.

The unblinding procedure is specified in advance: typically after the database lock, after the analysis of the primary endpoint by the unblinded statistician, or after the last patient’s last visit.

8.7 Sample size

The two-arm continuous-outcome calculation: \[ n_{\text{per arm}} = \frac{2 \sigma^2 (z_{1-\alpha/2} + z_{1-\beta})^2}{\delta^2} \] where \(\sigma\) is the within-arm SD, \(\delta\) is the target effect size (mean difference), and \(z\) are standard normal quantiles. For two-sided 5% type I error and 80% power, \(z_{1-\alpha/2} + z_{1-\beta} = 1.96 + 0.84 = 2.80\), and: \[ n_{\text{per arm}} \approx 2 \cdot 7.85 \cdot (\sigma/\delta)^2. \]

Concrete: with \(\sigma = 10\) mmHg and \(\delta = 5\) mmHg, \(n \approx 63\) per arm.

The binary-outcome calculation: \[ n_{\text{per arm}} = \frac{(z_{1-\alpha/2} + z_{1-\beta})^2 (p_1(1-p_1) + p_2(1-p_2))} {(p_1 - p_2)^2}. \]

The time-to-event calculation depends on the expected number of events, not the number of patients: \[ \text{events} = \frac{4 (z_{1-\alpha/2} + z_{1-\beta})^2} {\log(\text{HR})^2}. \]

The R packages pwr, clinfun, gsDesign, and pwrss implement these formulas plus more elaborate ones. The Hmisc::cpower() and the dedicated trial- design package rpact are alternatives.

library(pwr)

# two-sample t-test
pwr.t.test(d = 5/10, sig.level = 0.05, power = 0.8,
           type = "two.sample")
#> n = 63.8 per arm

# proportions
pwr.2p.test(h = ES.h(0.30, 0.20),
            sig.level = 0.05, power = 0.8)
#> n = 313.5 per arm

The biostatistician’s task: defend each input. Where does \(\sigma\) come from (a prior trial? the literature? expert opinion)? Where does \(\delta\) come from (clinically meaningful difference? smallest worth detecting?)? Why this \(\alpha\) (one-sided vs. two-sided?), this power (80%? 90%?). The protocol should answer each.

8.8 Non-inferiority and equivalence

A standard trial tests whether treatment X is better than control at a pre-specified \(\alpha\). Sometimes the question is whether X is not worse by more than a pre-specified margin. The non-inferiority margin \(\Delta\) is the largest acceptable difference in the wrong direction.

The hypothesis: \[ H_0: \mu_X - \mu_C \le -\Delta \text{ vs. } H_1: \mu_X - \mu_C > -\Delta \] (for outcomes where higher is better).

Sample size for non-inferiority is generally larger than for superiority because the margin is smaller than the typical effect size. The power calculation uses the formula above with \(\delta\) replaced by the effect on the non-inferiority margin (zero if the new treatment is assumed identical, the actual expected effect minus the margin if some superiority is expected).

The non-inferiority margin is a substantive choice: the largest difference that would still be clinically acceptable. It should be defended on clinical grounds and is typically a fraction (often 50%) of the historical effect size of the active control over placebo, to preserve at least half of the historical benefit. The biostatistician proposes; the clinical team decides.

Question. A new oral anticoagulant is proposed as a more convenient alternative to warfarin (which requires INR monitoring). The new drug is expected to have similar efficacy. Should the trial be designed as superiority, non-inferiority, or equivalence?

Answer.

Non-inferiority is the right design. The clinical question is ‘is the new drug at least as good as warfarin in terms of efficacy, given its convenience advantage?’ Superiority would require demonstrating that the new drug is better, which is unlikely (and not necessary for the clinical use case). Equivalence would require demonstrating the new drug is neither better nor worse, which is rarely needed; for a ‘similar efficacy, better convenience’ positioning, the asymmetric non-inferiority test is sufficient and better-powered. The non-inferiority margin would be a fraction (typically 50%) of the warfarin-vs-no- anticoagulant effect on the primary endpoint (stroke), to preserve at least half of warfarin’s historical benefit.

8.9 Estimand framework for trials

The ICH E9 R1 estimand framework (Ch 1) applies to trials with particular force. The five attributes (population, treatment, comparator, outcome, summary) plus the intercurrent-event strategy must be specified in the protocol.

Common intercurrent events in trials:

  • Treatment discontinuation (patients stop taking the treatment)
  • Treatment switching (patients switch to the other arm or to a third treatment)
  • Death (when not the primary outcome)
  • Use of rescue medication
  • Loss to follow-up

For each, the protocol specifies one of the five strategies (treatment policy, composite, hypothetical, principal stratum, while-on-treatment).

The default for many regulatory trials is treatment-policy for treatment discontinuation (estimating the effect of being assigned to a treatment strategy regardless of adherence). This is ITT. Per-protocol or hypothetical analyses are secondary or sensitivity. The protocol must name the primary estimand explicitly.

For a non-inferiority trial, ITT may be the wrong primary because it biases toward no difference (any ‘noise’ from non-adherence makes the new treatment look more like the control). Per-protocol or hypothetical strategies are sometimes the primary in non-inferiority trials.

8.10 Adaptive and group-sequential designs

A group-sequential design analyses the data at pre-specified interim time points and may stop the trial early for efficacy or futility. The standard spending functions (O’Brien-Fleming, Pocock, Lan-DeMets) control the overall type I error across multiple looks.

The gsDesign R package implements these:

library(gsDesign)

design <- gsDesign(k = 4,                # 4 looks
                   test.type = 4,         # 2-sided
                   alpha = 0.025, beta = 0.1,
                   sfu = sfLDOF,         # O'Brien-Fleming spending
                   sfl = sfLDPocock)     # Pocock for futility
summary(design)

The output: the cumulative information times at each look, the boundary values (in standard units), expected sample size under the null and alternative.

An adaptive design changes some aspect of the trial based on accumulated data: sample size, allocation ratio, the primary endpoint, the patient population. Adaptive designs are increasingly common in oncology (basket and umbrella trials, platform trials) but require careful pre-specification to maintain the overall type I error.

The FDA’s guidance on adaptive designs (U.S. Food and Drug Administration, 2019) is the authoritative reference; the methodological literature is rich and evolving.

8.11 Pragmatic and platform trials

Pragmatic trials answer real-world effectiveness questions: enroll broad populations, deliver treatment in routine care, measure outcomes from existing data sources. Trade efficiency for generalisability. The PRECIS-2 framework (Loudon et al., 2015) is the design tool.

Platform trials test multiple interventions simultaneously against a shared control, with the ability to drop arms for futility and add new arms mid-trial. STAMPEDE in prostate cancer and the RECOVERY trial in COVID-19 are canonical examples. Platform trials require sophisticated statistical methods (master protocols, Bayesian decision rules) and substantial operational infrastructure.

For an MS-level biostatistician, knowing the names and the structural ideas of pragmatic and platform trials is enough; implementing one requires specialist methodological involvement.

8.12 Worked example: designing a Phase III trial

A new drug for moderate-to-severe COPD is ready for Phase III. Active control is salmeterol/fluticasone. Primary endpoint: change in FEV1 from baseline to week 24.

Step 1. Estimand. - Population: adults 40+ with moderate-to-severe COPD. - Treatment: new drug (specific dose). - Comparator: salmeterol/fluticasone. - Outcome: change in trough FEV1 from baseline to week 24 (mL). - Population summary: mean difference between arms. - Intercurrent events: - Treatment discontinuation: treatment policy (analyse as randomised). - Use of rescue medication: while-on-treatment (analyses based on FEV1 measurements during on-treatment period).

Step 2. Sample size. Prior trials show within-arm SD of 200 mL and a clinically meaningful difference of 50 mL. With \(\alpha = 0.05\) two-sided and 90% power: \[ n_{\text{per arm}} = \frac{2 \cdot 200^2 \cdot (1.96 + 1.28)^2} {50^2} \approx 339. \] Add 15% for dropout: 390 per arm. Total enrolment: 780.

Step 3. Randomisation. Stratified by baseline disease severity (moderate vs. severe) and current ICS use (yes/no). Block size 4. Centralised IVRS.

Step 4. Blinding. Double-blind, double-dummy. Both arms receive an identical-looking inhaler.

Step 5. Interim analysis. Single interim at 50% of events, with O’Brien-Fleming boundary for early efficacy stopping. Sample-size re-estimation based on the observed within-arm SD (without unblinding the treatment effect).

Step 6. Analysis. Mixed model for repeated measures (MMRM), with fixed effects for treatment, visit, treatment-by-visit, baseline FEV1, baseline severity, ICS use; unstructured covariance for repeated visits within patient. Handle missing data under MAR (the MMRM assumption); sensitivity analyses for MNAR (Ch 10).

The protocol now contains everything the trial needs. Six months in, when the DSMB asks ‘what was the sample-size justification?’, the protocol is the answer.

8.13 Collaborating with an LLM on clinical trial design

Three patterns.

Prompt 1: ‘Compute the sample size for this trial.’ Provide effect size, variability, alpha, power.

What to watch for. The LLM produces a calculation using pwr or gsDesign. It often defaults to two-sided \(\alpha\) when one-sided is appropriate (or vice versa) and over-simplifies the assumptions. Push for explicit defence of each input.

Verification. Recompute by formula or with a second package. The arithmetic is elementary and worth double-checking.

Prompt 2: ‘Write the estimand for this trial.’ Provide the trial protocol summary.

What to watch for. The LLM produces all five attributes. It commonly under-specifies the intercurrent-event strategies. Push for explicit naming of each strategy.

Verification. Read against ICH E9 R1.

Prompt 3: ‘Should this trial use a group-sequential design?’ Provide the trial details.

What to watch for. The LLM gives a competent discussion. It tends to recommend group-sequential designs more often than warranted (the operational cost is real). Push for the trade-offs.

Verification. The decision should consider the cost of an interim (operational, regulatory submissions, DSMB), not just the statistical efficiency.

The meta-pattern: LLMs are good at the syntactic mechanics (writing the formula, drafting the protocol section) and weak at the substantive choices (which estimand, which interim strategy, which margin in non-inferiority). Use them for code and drafts; bring substantive judgement yourself.

8.14 Principle in use

Three habits.

  1. Estimand before sample size. The sample size is computed for a specific estimand and a specific estimator. Specifying the estimand first prevents the calculation from being detached from the primary analysis.

  2. Defend each sample-size input. Effect size, variability, alpha, power, dropout rate. Each number in the calculation has a source; the protocol cites it.

  3. Document intercurrent-event strategies in the protocol. ITT is one strategy among several; the choice should be explicit.

8.15 Exercises

  1. For a hypothetical trial in your area, write the primary estimand using all six ICH E9 R1 attributes. Identify the intercurrent-event strategies for at least two intercurrent events.

  2. Compute the sample size for a two-arm continuous-outcome trial with \(\sigma = 15\), \(\delta = 5\), \(\alpha = 0.05\) two-sided, power = 80%. Verify by formula.

  3. For a published Phase III trial, find the sample- size justification in the protocol or supplement. Identify the inputs (effect size, variability, etc.) and assess whether each is defended.

  4. Design a non-inferiority trial. Choose a margin \(\Delta\) and defend it on clinical grounds. Compute the sample size required.

  5. Use gsDesign to design a 4-look group-sequential trial with O’Brien-Fleming efficacy boundary. Report the boundaries at each look and the expected sample size under the null.

8.16 Further reading

  • International Council for Harmonisation (2019), ICH E9(R1) Addendum on Estimands and Sensitivity Analysis. The regulatory text.
  • Piantadosi (2017), Clinical Trials: A Methodologic Perspective (3rd edition). The reference textbook.
  • Friedman et al. (2015), Fundamentals of Clinical Trials (5th edition). The classical applied reference.
  • Jennison & Turnbull (2000), Group Sequential Methods with Applications to Clinical Trials. The reference for group-sequential design.
  • The gsDesign, rpact, pwr, and clinfun package documentation.