A conventional trial fixes everything in advance: the sample size, the doses, the population, and a single analysis at the end. An adaptive design allows pre-planned changes during the trial based on accumulating data, without undermining its validity. Used well, it can stop a trial early when the answer is already clear, rescue a trial whose assumptions were too optimistic, and spend fewer patients on doses that do not work.
This article explains the main types of adaptive design, what regulators expect, and the statistics that keep the type I error under control. It then works through a complete example in SAS: a group sequential design with an interim analysis, conditional power, sample size re-estimation and a simulation of the operating characteristics.
Types of adaptive design
| Adaptation | What can change | Typical use |
|---|---|---|
| Group sequential | The trial can stop early for efficacy or futility at pre-planned interim analyses | Confirmatory trials with a long recruitment period |
| Sample size re-estimation | The final sample size is revised using interim data, blinded (variance only) or unblinded (treatment effect) | Trials with uncertain variability or effect size |
| Adaptive dose selection | Doses are dropped or added; often a seamless Phase 2/3 design | Programmes that would otherwise need separate dose-finding and confirmatory trials |
| Adaptive enrichment | Enrolment is restricted to a subgroup that appears to benefit | Targeted therapies with a candidate biomarker |
| Response-adaptive randomisation | Allocation ratios shift toward better-performing arms | Multi-arm exploratory and platform trials |
| Platform and master protocols | Arms enter and leave under a common protocol and shared control | Diseases with many candidate treatments |
What regulators expect
The FDA guidance on adaptive designs (2019) and the ICH E20 guideline (issued as a draft for consultation in 2025; the final version is still pending) rest on the same principles:
- Pre-specification. The adaptations, their timing and the decision rules are written into the protocol before any unblinded data are seen.
- Control of the type I error. The chance of a false positive conclusion must stay at the nominal level (usually one-sided 2.5%) despite the interim looks and adaptations.
- Reliable estimation. The treatment effect estimate and confidence interval should account for the adaptive design, because naive estimates can be biased.
- Trial integrity. Unblinded interim results are seen only by an independent data monitoring committee and an independent statistician, so that knowledge of the results cannot influence trial conduct.
- Evidence of operating characteristics. For anything beyond a standard group sequential design, simulations are expected to show the type I error, power and expected sample size across plausible scenarios.
Statistical concepts behind adaptive designs
1. Why repeated looks inflate the type I error
If a trial is tested at the full 2.5% level every time the data are examined, the chance of at least one false positive grows with each look. Two looks give about 4.2% instead of 2.5%; five looks give about 7%. Every adaptive method is, at its core, a way of spending the allowed error across the looks.
2. Information fraction
The timing of an interim analysis is expressed as the fraction of the total statistical information available. For a continuous endpoint this is the proportion of patients with data; for a time-to-event endpoint it is the proportion of the planned events.
3. Alpha spending functions
An alpha spending function specifies how much of the total alpha has been used by each information fraction. The Lan-DeMets approach allows the number and timing of looks to change without invalidating the design. Two shapes are common. The O'Brien-Fleming type spends very little alpha early, so early stopping needs overwhelming evidence and the final analysis is almost unaffected. The Pocock type spends alpha evenly, making early stopping easier but the final test noticeably stricter.
4. Stopping boundaries
The spending function is converted into critical values for the test statistic at each look. Calculating them requires the joint distribution of the statistics across looks, which are correlated because later analyses include the earlier data.
5. Conditional power
Conditional power is the probability that the final analysis will be significant, given the interim data and an assumption about the true effect for the remainder of the trial. It is usually calculated under the observed trend and under the originally assumed effect. Low conditional power supports stopping for futility; intermediate values may justify increasing the sample size.
6. Binding and non-binding futility rules
A non-binding futility rule can be overruled by the monitoring committee without inflating the type I error, because the efficacy boundaries are calculated as if no futility stopping occurs. Regulators generally prefer non-binding rules.
7. Blinded and unblinded sample size re-estimation
Blinded re-estimation uses only the pooled variance and has a negligible effect on the type I error. Unblinded re-estimation uses the interim treatment effect. If the sample size is increased because the interim result looks promising and the data are then analysed as if the size had been fixed, the type I error is inflated.
8. Combination tests
The standard solution is to analyse the two stages separately and combine them with weights fixed in advance. In the Cui-Hung-Wang (CHW) method the final statistic is Z = w1Z1 + w2Z2, where the weights are based on the planned stage sizes and the squared weights sum to 1. Because the weights do not depend on the interim result, Z keeps its standard normal distribution under the null hypothesis however the second-stage sample size is chosen, and the type I error is preserved.
9. The promising zone
A common rule increases the sample size only when the interim conditional power falls in a pre-defined "promising" range: high enough that the treatment plausibly works, but too low for comfort. Trials with unfavourable or already favourable results continue as planned.
10. Simulation
Once several rules interact (efficacy stopping, futility stopping, sample size increase with a cap), closed-form calculations are no longer practical. The design is evaluated by simulating many thousands of trials under different true effects and counting how often each outcome occurs.
The worked example: design
A randomised, double-blind, two-arm trial compares an active treatment with placebo on a continuous endpoint. The planning assumptions and adaptive rules are:
| Design element | Specification |
|---|---|
| Expected treatment difference | 5 units |
| Standard deviation | 15 units |
| Type I error | One-sided 2.5% |
| Power | 90% |
| Interim analysis | One, at 50% of the planned information |
| Efficacy stopping | O'Brien-Fleming type alpha spending (Lan-DeMets) |
| Futility stopping (non-binding) | Conditional power under the observed trend below 10% |
| Sample size re-estimation | If conditional power is 30% or more but below 90%, increase the second stage to target 90% conditional power, up to a maximum of twice the planned second stage |
| Final analysis | CHW combination test with equal weights (√0.5 for each stage) |
SAS code, step by step
Step 1: Group sequential design and boundaries
PROC SEQDESIGN calculates the stopping boundaries and the required sample size. METHOD=ERRFUNCOBF requests the Lan-DeMets O'Brien-Fleming-type spending function, and BOUNDARYSCALE=STDZ reports boundaries on the Z scale.
proc seqdesign altref=5 boundaryscale=stdz errspend;
OBF_2stage: design nstages=2
info=equal
alt=upper
stop=reject
method=errfuncobf
alpha=0.025
beta=0.10;
samplesize model=twosamplemean(stddev=15);
run;
Step 2: Interim analysis and conditional power
At the interim, 95 patients per arm have data. The observed difference is 3.6 units with a pooled standard deviation of 15.4. The data step calculates the interim Z statistic and the conditional power under three assumptions about the true effect.
data interim;
/* Design constants from Step 1 */
c1 = 2.9626; /* interim efficacy boundary (Z scale) */
c2 = 1.9686; /* final boundary (Z scale) */
t = 0.5; /* information fraction at interim */
drift = 3.2471; /* expected final Z under the design */
/* Interim data */
n1 = 95; /* patients per arm */
diff1 = 3.6; /* observed difference */
sd1 = 15.4; /* pooled standard deviation */
se1 = sd1 * sqrt(2 / n1);
z1 = diff1 / se1;
/* Conditional power for an assumed drift theta */
theta_trend = z1 / sqrt(t); /* observed trend */
cp_trend = 1 - probnorm((c2 - z1*sqrt(t) - theta_trend*(1 - t)) / sqrt(1 - t));
cp_design = 1 - probnorm((c2 - z1*sqrt(t) - drift*(1 - t)) / sqrt(1 - t));
cp_null = 1 - probnorm((c2 - z1*sqrt(t)) / sqrt(1 - t));
length decision $40;
if z1 ge c1 then decision = 'Stop for efficacy';
else if cp_trend lt 0.10 then decision = 'Consider stopping for futility';
else if 0.30 le cp_trend lt 0.90 then decision = 'Promising: re-estimate sample size';
else decision = 'Continue as planned';
run;
proc print data=interim noobs;
var z1 c1 cp_trend cp_design cp_null decision;
format z1 c1 8.4 cp_trend cp_design cp_null percent8.1;
run;
Step 3: Sample size re-estimation
With the CHW test, the second-stage statistic Z2 must exceed b = (c2 − w1Z1) / w2 for the trial to succeed. The second-stage sample size is chosen so that the probability of this, assuming the observed effect continues, is 90%, subject to the pre-specified cap.
data ssr;
set interim;
w1 = sqrt(0.5); /* pre-specified weights */
w2 = sqrt(0.5);
n2_planned = 95; /* planned stage 2 size per arm */
n2_max = 2 * n2_planned; /* pre-specified cap */
b = (c2 - w1*z1) / w2; /* hurdle for the stage 2 Z */
/* Stage 2 size per arm for 90% conditional power */
n2_needed = 2 * ((b + probit(0.90)) * sd1 / diff1)**2;
n2_new = min(max(ceil(n2_needed), n2_planned), n2_max);
/* Conditional power with the planned and the new stage 2 size */
cp_planned = probnorm(diff1 * sqrt(n2_planned/2) / sd1 - b);
cp_new = probnorm(diff1 * sqrt(n2_new/2) / sd1 - b);
n_total_new = n1 + n2_new;
run;
proc print data=ssr noobs;
var b n2_needed n2_new n_total_new cp_planned cp_new;
format b n2_needed 8.2 cp_planned cp_new percent8.1;
run;
Step 4: Final analysis with the combination test
The second stage enrols 190 patients per arm. Its data, analysed alone, give a difference of 4.4 units with a standard deviation of 14.8. The two stage statistics are combined with the pre-specified weights.
data final;
set ssr;
diff2 = 4.4; /* stage 2 only: difference */
sd2 = 14.8; /* stage 2 only: pooled SD */
z2 = diff2 / (sd2 * sqrt(2 / n2_new));
z_chw = w1*z1 + w2*z2; /* CHW combination statistic */
p_chw = 1 - probnorm(z_chw); /* one-sided p-value */
length result $24;
if z_chw ge c2 then result = 'Significant';
else result = 'Not significant';
run;
proc print data=final noobs;
var z1 z2 z_chw c2 p_chw result;
format z1 z2 z_chw c2 8.4 p_chw pvalue6.4;
run;
Step 5: Simulate the operating characteristics
The simulation generates 400,000 trials for each of three true treatment differences and applies every design rule: efficacy stopping, futility stopping, sample size re-estimation with the cap, and the CHW final test.
%let c1 = 2.9626;
%let c2 = 1.9686;
%let n1 = 95;
%let sd = 15;
data sim;
call streaminit(12345);
w = sqrt(0.5);
do delta = 0, 3.6, 5; /* true treatment difference */
do rep = 1 to 400000;
reject = 0; stop_eff = 0; stop_fut = 0; promising = 0; n2 = 0;
/* Stage 1 */
z1 = rand('normal', delta*sqrt(&n1/2)/&sd, 1);
if z1 ge &c1 then do; /* efficacy stop */
reject = 1; stop_eff = 1;
end;
else do;
cp = 1 - probnorm((&c2 - z1*sqrt(0.5) - (z1/sqrt(0.5))*0.5) / sqrt(0.5));
if cp lt 0.10 then stop_fut = 1; /* futility stop */
else do;
n2 = &n1;
if 0.30 le cp lt 0.90 then do; /* promising zone */
promising = 1;
dhat = z1 * &sd * sqrt(2/&n1);
b = (&c2 - w*z1) / w;
need = 2 * ((b + probit(0.90)) * &sd / dhat)**2;
n2 = min(max(ceil(need), &n1), 2*&n1);
end;
/* Stage 2 and CHW test */
z2 = rand('normal', delta*sqrt(n2/2)/&sd, 1);
if w*z1 + w*z2 ge &c2 then reject = 1;
end;
end;
n_arm = &n1 + n2;
output;
end;
end;
keep delta reject stop_eff stop_fut promising n_arm;
run;
proc means data=sim mean maxdec=4;
class delta;
var reject stop_eff stop_fut promising n_arm;
run;
Output
Design (Step 1)
| Analysis | Information fraction | Patients per arm | Efficacy boundary (Z) | Cumulative alpha spent |
|---|---|---|---|---|
| Interim | 0.50 | 95 | 2.9626 | 0.00153 |
| Final | 1.00 | 190 | 1.9686 | 0.02500 |
A fixed design with the same assumptions needs 189.1 patients per arm; the group sequential design needs a maximum of 189.8, an inflation of 0.3%. Both round up to 190 per arm. Under the planning assumptions, the probability of stopping for efficacy at the interim is 25.3%.
Interim analysis (Step 2)
| Quantity | Value |
|---|---|
| Observed difference (standard error) | 3.6 (2.234) |
| Interim Z statistic | 1.6111 |
| Efficacy boundary | 2.9626 |
| Conditional power, observed trend | 66.9% |
| Conditional power, design assumption | 86.9% |
| Conditional power, no further effect | 12.0% |
| Decision | Promising: re-estimate sample size |
Sample size re-estimation (Step 3)
| Quantity | Value |
|---|---|
| Hurdle for the stage 2 statistic (b) | 1.17 |
| Stage 2 size needed for 90% conditional power | 220.5 per arm |
| Pre-specified maximum for stage 2 | 190 per arm |
| Stage 2 size adopted | 190 per arm |
| New total sample size | 285 per arm (planned: 190) |
| Conditional power with planned stage 2 (95 per arm) | 66.9% |
| Conditional power with new stage 2 (190 per arm) | 86.6% |
Final analysis (Step 4)
| Quantity | Value |
|---|---|
| Stage 1 statistic (Z1) | 1.6111 |
| Stage 2 statistic (Z2) | 2.8977 |
| CHW combination statistic | 3.1882 |
| Final boundary | 1.9686 |
| One-sided p-value | 0.0007 |
| Result | Significant |
Simulated operating characteristics (Step 5)
| True difference | Probability of success | Stopped early for efficacy | Stopped for futility | Sample size increased | Average patients per arm |
|---|---|---|---|---|---|
| 0 (no effect) | 2.2% | 0.1% | 77.5% | 10.8% | 125 |
| 3.6 (smaller than planned) | 66.8% | 9.5% | 18.3% | 34.7% | 189 |
| 5 (as planned) | 90.0% | 25.3% | 6.1% | 27.4% | 179 |
Simulation results vary slightly with the random seed. The figures above are from 400,000 simulated trials per scenario.
Interpretation
- The design costs almost nothing. Adding an interim look with O'Brien-Fleming-type spending raises the maximum sample size by only 0.3%, and the final test uses a boundary of 1.9686 instead of 1.96. In return there is a 25% chance of stopping early if the treatment works as planned.
- The interim result is not enough to stop. The interim Z of 1.61 corresponds to a one-sided p-value of about 0.054, far from the boundary of 2.96. Early stopping would have required an extreme result.
- The trial is in the promising zone. The observed difference of 3.6 is smaller than the 5 units assumed. If that trend continues, the trial has only a 66.9% chance of success at the planned size. This is neither hopeless nor safe, which is exactly the situation sample size re-estimation is designed for.
- The cap matters. Reaching 90% conditional power would need 220.5 patients per arm in the second stage, but the protocol allows at most 190. With the capped increase, conditional power rises to 86.6% and the total sample size grows from 190 to 285 per arm.
- The final test is valid. The combination statistic of 3.19 exceeds the boundary of 1.9686 (p = 0.0007). Because the weights were fixed in advance, this conclusion holds at the one-sided 2.5% level even though the sample size was increased after seeing the interim effect.
- The simulation confirms the error control. When there is no true effect, the trial succeeds in 2.2% of simulations, below the 2.5% limit. The shortfall arises because the futility rule stops some trials that would otherwise have crossed the boundary by chance; with a non-binding rule the limit of 2.5% is guaranteed either way.
- The design is efficient across scenarios. If the treatment does not work, the trial usually stops at the interim and uses 125 patients per arm on average instead of 190. If it works as planned, power is 90% with an average of 179 per arm.
What sample size re-estimation does and does not do. When the true difference is 3.6 rather than 5, the adaptive design reaches 66.8% power with an average of 189 patients per arm, similar to a fixed design of 190 per arm (about 65%). The adaptive design does not create power from nothing. Its value is in where the patients are spent: it stops quickly when the treatment is failing and invests more only when the interim data suggest the investment is likely to pay off. A sponsor who wants high power for the smaller effect must raise the cap or plan a larger trial from the start.
A caution on the estimate. The combination test gives a valid p-value, but the simple pooled difference across both stages (4.1 units here) is not an unbiased estimate after an adaptive increase. The method for the final estimate and confidence interval should be pre-specified along with the test.
Practical points
- Independent monitoring. The interim analysis is run by an independent statistician and reviewed by a data monitoring committee under a written charter. The sponsor's trial team stays blinded.
- Protecting the interim result. A sample size increase can reveal that the result was promising. Limit who knows the rule and the size of the increase, and consider reporting only "continue" or "continue with the revised size".
- Timing of the interim. Too early, and the estimate is too unstable to act on; too late, and little can be saved. Between 40% and 60% of information is typical. Fast recruitment relative to the endpoint follow-up reduces the benefit, because most patients are enrolled before the interim data mature.
- Simulation report. For regulatory submission, document the simulation scenarios, software, code and number of replicates, and include scenarios that stress the assumptions, such as a different variance or delayed effect.
- Operational readiness. Drug supply, randomisation systems and site contracts must be able to handle both early stopping and a larger trial.
- Keep it simple. Each additional adaptation adds complexity to interpretation and regulatory review. Use the adaptations that address a real uncertainty in the programme.
References
- US FDA. Adaptive Designs for Clinical Trials of Drugs and Biologics, Guidance for Industry. 2019.
- ICH E20. Adaptive Designs for Clinical Trials, draft guideline for consultation. 2025.
- O'Brien PC, Fleming TR. A multiple testing procedure for clinical trials. Biometrics. 1979;35(3):549–556.
- Lan KKG, DeMets DL. Discrete sequential boundaries for clinical trials. Biometrika. 1983;70(3):659–663.
- Cui L, Hung HMJ, Wang SJ. Modification of sample size in group sequential clinical trials. Biometrics. 1999;55(3):853–857.
- Mehta CR, Pocock SJ. Adaptive increase in sample size when interim results are promising: a practical guide with examples. Statistics in Medicine. 2011;30(28):3267–3284.
The data in this article are simulated and are provided for training purposes only.




