Missing Data and Intercurrent Events in Endpoint Power

Why Missingness and Intercurrent Events Belong in the Power Plan

A sample-size calculation is only as relevant as the endpoint it is designed to estimate. In a clinical trial, some participants may discontinue assigned treatment, receive rescue therapy, or miss one or more assessments. These events can change what outcome is being targeted, which observations contribute to its estimation, and how much uncertainty the estimate has. Treating every such event as “dropout” and applying one inflation factor can therefore produce a trial powered for the wrong question.

The introductory material on estimands establishes that the treatment effect must be defined for a specified population, treatment conditions, outcome, and summary measure, together with a strategy for handling intercurrent events. Here the emphasis is on consequences for endpoint assumptions and power. An intercurrent event is not itself missing data: a participant can discontinue treatment yet still provide the endpoint. Conversely, a participant can miss an assessment without experiencing any intercurrent event.

Definition: Missing outcome data are values of the endpoint that were not observed. An intercurrent event is an event after treatment initiation that affects the interpretation or existence of the outcome, such as treatment discontinuation or rescue medication. The estimand strategy specifies how such an event enters the treatment-effect question; a missing-data assumption specifies how unobserved endpoint values are related to observed information.

Missingness Assumptions and What They Permit

Let \(Y\) denote the endpoint that would be recorded at the planned assessment, and let \(R=1\) if it is observed and \(R=0\) if it is missing. The assumptions below concern the relationship between \(R\), observed information, and the unobserved value \(Y\). They are not interchangeable analysis methods, and no assumption can be verified fully from observed outcomes alone.

Missing completely at random (MCAR): the probability of missingness does not depend on observed or unobserved outcome information. In notation, \(P(R=1\mid Y,X)=P(R=1)\), where \(X\) denotes observed covariates or history.
Missing at random (MAR): conditional on the information observed in the analysis, missingness does not further depend on the unobserved outcome. Thus \(P(R=1\mid Y,X)=P(R=1\mid X)\). A likelihood-based longitudinal analysis can use observed outcomes under MAR when its outcome model is correctly specified.
Missing not at random (MNAR): even conditional on observed information, the chance of missingness depends on the unobserved outcome. For example, participants with worse unrecorded symptoms may be more likely to miss the assessment.

MCAR is a particularly strong condition. Under MCAR, an endpoint-only analysis of observed cases can estimate the randomized-group mean contrast without selection bias, though it loses precision. Under MAR, complete-case analysis can be biased if the observed cases differ in outcome prognosis, even when a correctly specified likelihood analysis using the available longitudinal data could be valid. Under MNAR, standard MAR-based analyses generally need sensitivity analysis; simply adding participants to the planned sample does not remove the potential bias.

Intermittent missingness means that a participant misses some scheduled assessments but contributes others. It differs from monotone dropout, where after a point the remaining assessments are all missing. A longitudinal model may extract information from available visits, but how much depends on the outcome model, correlation across visits, and the missingness pattern. An endpoint-only calculation should not assume that earlier observations fully replace a missing primary endpoint.

Connect the Event Strategy to the Target Effect

Common strategies include a treatment-policy strategy, which uses outcomes regardless of whether treatment was discontinued or rescue was used; a hypothetical strategy, which targets the outcome that would have occurred under a specified alternative event condition; a composite strategy, which incorporates the event into the endpoint; and a while-on-treatment strategy, which targets outcomes during treatment. These choices answer different questions. They can have different treatment effects, outcome variability, and data requirements, so they can imply different power.

A treatment-policy strategy requires continued outcome collection after discontinuation or rescue if those outcomes define the target. If those assessments are missing, there is also a missing-data problem. A hypothetical strategy may require modeling outcomes that were not observed after an event; its uncertainty depends on the assumptions used to extrapolate. A composite endpoint may avoid treating the post-event outcome as if it were observed on the original scale, but it changes the endpoint itself. The chosen strategy should therefore be stated before selecting an analysis and calculating sample size.

Deriving a Basic Attrition Adjustment

For a two-arm comparison of a continuous endpoint, suppose the endpoint is normally distributed in each arm with common standard deviation \(\sigma\), the target difference in means is \(\delta\), and the arms have equal sample size. With a two-sided test at level \(\alpha\), approximate power \(1-\beta\), independent participants, and complete endpoint data, the usual normal-approximation sample size per arm is:

n_{\text{eval}} = \frac{2\sigma^2\left(z_{1-\alpha/2}+z_{1-\beta}\right)^2}{\delta^2}.

Here \(z_q\) is the \(q\)-quantile of the standard normal distribution, and \(n_{\text{eval}}\) is the required number of evaluable participants per arm. If each randomized participant independently provides the endpoint with probability \(1-r\), and this probability is the same in both arms, the expected number with an observed endpoint from \(n_{\text{rand}}\) randomized participants is \(n_{\text{rand}}(1-r)\). Setting that expectation equal to \(n_{\text{eval}}\) gives:

n_{\text{rand}} = \left\lceil \frac{n_{\text{eval}}}{1-r}\right\rceil .

This derivation justifies a planning approximation, not a universal correction. It assumes that the target effect and endpoint variance apply to those who remain observed, that missingness does not create bias for the chosen analysis, and that the anticipated rate is credible in each arm. If missingness depends on prognosis, or if event-related outcomes change the estimand, the formula only increases the count; it does not repair a mismatch between the target and the analysis.

Worked Example: Inflating for Independent Dropout

Suppose a hypothetical two-arm trial targets a 5-point difference on a continuous endpoint. Assume a common standard deviation of 10 points, two-sided \(\alpha=0.05\), 90% power, and independent participants. Use \(z_{0.975}=1.960\) and \(z_{0.90}=1.282\).

The assumptions for the normal-approximation calculation are a prespecified mean contrast, equal allocation, common variance, and complete endpoint data for the initial calculation. The calculation gives:

n_{\text{eval}} = \frac{2(10^2)(1.960+1.282)^2}{5^2} = \frac{200(3.242)^2}{25} = 84.08.

Rounding up requires 85 evaluable participants per arm. If 20% are expected to have no endpoint and the independent, equal-rate attrition assumption is reasonable, then:

n_{\text{rand}} = \left\lceil\frac{85}{1-0.20}\right\rceil = \lceil106.25\rceil = 107 \quad\text{per arm}.

Thus 107 participants per arm are planned to obtain about 85 with observed endpoints on average. This calculation is not justified if discontinuation is followed by endpoint collection under a treatment-policy strategy: discontinuation alone is not endpoint loss. Nor does the inflation protect against bias if missingness depends on unobserved outcomes.

Intermittent Missingness Can Reduce Power

For an endpoint-only analysis, each participant without the primary endpoint contributes no direct observation to the arm mean, even if earlier visits are available. Consider a simple approximation in which the observed endpoint values are independent with common standard deviation \(\sigma\), and \(n_{\text{obs}}\) values are available per arm. The standard error of the difference in arm means is:

SE(\bar{Y}_1-\bar{Y}_0) = \sigma\sqrt{\frac{1}{n_{\text{obs},1}}+\frac{1}{n_{\text{obs},0}}}.

This formula assumes independent participants and equal endpoint variance. A longitudinal likelihood analysis using earlier observed visits may have a different standard error under its specified covariance and mean models; it should be calculated from that model or evaluated by simulation, rather than by assuming a fixed “credit” for each earlier measurement.

Worked Example: Intermittently Missing Primary Assessments

In a hypothetical study, 120 participants per arm are randomized. The primary endpoint is observed for 85% in each arm, while some participants with a missing primary visit have earlier measurements. For an endpoint-only comparison, suppose the endpoint standard deviation is 12 points and the target difference is 4 points. Assume the observed participants are representative for the endpoint contrast, so this calculation concerns loss of precision rather than selection bias.

The expected observed count is \(120(0.85)=102\) per arm. The approximate standard error is:

SE = 12\sqrt{\frac{1}{102}+\frac{1}{102}} = \sqrt{\frac{288}{102}} = 1.680 \text{ points}.

For a two-sided 5% test, the standardized signal is \(4/1.680=2.381\). The normal-approximation power is:

P(Z>1.960-2.381)+P(Z<-1.960-2.381) = \Phi(0.421)+\Phi(-4.341) \approx 0.663.

The endpoint-only analysis therefore has approximately 66.3% power under these assumptions, below a 90% target. Earlier measurements could improve precision under an appropriately specified longitudinal model and suitable missingness assumptions, but their benefit cannot be inferred from the 85% endpoint-observation rate alone. If the missing visits are more common among participants with poorer unobserved outcomes, the representative-observed-participants assumption also fails, and the estimated effect may be biased.

Event Strategies Can Change the Effect and the Required Sample

When an intercurrent event changes the outcome included in the estimand, it can change the assumed treatment effect itself. For a continuous endpoint under the same variance and test assumptions, sample size is proportional to \(1/\delta^2\). A smaller target effect therefore requires a much larger sample. The calculation is meaningful only if \(\delta\) refers to the estimand actually being targeted.

Worked Example: Treatment Policy Versus Hypothetical Strategy

Consider hypothetical endpoint values on a scale where higher is better. In the treatment arm, assume 60% remain on assigned treatment with mean 10 points and 40% discontinue with mean 4 points; all continue endpoint assessments. In the control arm, assume 80% do not receive rescue therapy with mean 5 points and 20% receive rescue with mean 8 points; all are assessed. For illustration, assume the within-arm endpoint standard deviation is 10 points under either strategy, with equal allocation and the same 5% two-sided test and 90% power as above.

Under a treatment-policy strategy, the arm means include outcomes after these events:

\bar{\mu}_{T}=0.60(10)+0.40(4)=7.6, \qquad \bar{\mu}_{C}=0.80(5)+0.20(8)=5.6, \qquad \delta_{\text{TP}}=7.6-5.6=2.0 \text{ points}.

The required sample size under these assumed means is:

n_{\text{TP}} = \left\lceil \frac{2(10^2)(3.242)^2}{2^2} \right\rceil = \lceil525.5\rceil = 526 \quad\text{per arm}.

A hypothetical strategy that targets outcomes as if discontinuation and rescue had not occurred might instead posit means of 10 and 5 points, giving \(\delta_{\text{hyp}}=5\) points. Under the same illustrative variance and test assumptions:

n_{\text{hyp}} = \left\lceil \frac{2(10^2)(3.242)^2}{5^2} \right\rceil = \lceil84.08\rceil = 85 \quad\text{per arm}.

The contrast and sample sizes differ because the strategies target different effects, not because one arithmetic method is preferable. The hypothetical means are assumptions, not values identified merely by excluding participants who discontinued or received rescue. Estimating that hypothetical effect requires a defensible model for the unobserved outcomes and sensitivity analysis for departures from its assumptions.

Diagnostics, Alternatives, and Limitations

A power plan should make visible where its information comes from and what could invalidate the assumptions. Useful checks include comparing anticipated missingness and event rates by arm; describing reasons and timing of missed visits; examining whether missingness is associated with observed baseline or prior outcomes; and checking whether follow-up continues after treatment discontinuation or rescue. These summaries can reveal an implausible assumption of equal, outcome-independent dropout, but cannot establish MAR rather than MNAR.

Planning or analysis approach	Useful when	Main caution
Simple dropout inflation	Endpoint loss is plausibly independent, and the target effect is unchanged among observed participants	Increases randomized numbers but does not correct selection bias or redefine the estimand
Likelihood-based longitudinal model	Repeated outcomes are available and MAR is plausible conditional on modeled history	Depends on the specified mean and covariance models; power depends on the visit pattern
Multiple imputation under MAR	Missing values can be imputed from a suitable model using relevant observed information	Results depend on the imputation model and do not by themselves address MNAR
MNAR sensitivity analysis	Unobserved outcomes may differ from MAR predictions	Requires clinically defensible departures and a clear account of how conclusions change

For planning, simulate the full design when event rates, assessment patterns, or longitudinal models make the simple formulas inadequate. Simulation should generate intercurrent events and missing assessments separately, apply the intended estimand and analysis, and estimate power as the proportion of simulated trials meeting the prespecified decision rule. Vary plausible event rates, missingness assumptions, and outcome-model parameters. This connects the power claim to the actual analysis rather than to an idealized count of complete cases.

The main failure modes are to count discontinuation as dropout when outcomes are still collected; to assume that an observed-case analysis is unbiased just because randomization occurred; to inflate for a missingness percentage while retaining an effect size that belongs to a different estimand; and to regard MAR as proven by observed data. Each mistake confuses the number of observations with the treatment effect or assumptions those observations support.

Key takeaway: Define the event strategy and the endpoint data-collection plan before translating a target effect into sample size. Attrition inflation addresses expected loss of observations under restrictive assumptions; it does not resolve estimand changes, missingness bias, or uncertainty about unobserved outcomes.

Check Your Understanding

Answer each question, then compare with the brief solutions.

A participant discontinues study drug but completes the primary endpoint assessment. Is the endpoint missing? Explain.
In a two-arm continuous-endpoint trial, 90 evaluable participants per arm are required and 10% are expected to have no endpoint. How many should be randomized per arm using the simple inflation formula?
Give the distinction between MAR and MNAR in terms of observed information and the unobserved outcome.
Why can a treatment-policy strategy and a hypothetical strategy imply different sample sizes?
Does adding participants correct bias from outcome-dependent missingness? Explain.

Solutions. (1) No. The endpoint is observed; discontinuation is an intercurrent event whose handling depends on the estimand strategy. (2) \(\lceil90/(1-0.10)\rceil=\lceil100\rceil=100\) per arm, assuming the simple inflation conditions hold. (3) Under MAR, missingness is independent of the unobserved outcome conditional on modeled observed information; under MNAR, it still depends on that outcome after conditioning. (4) They target different outcomes or event conditions and can therefore have different treatment effects and variances; since sample size for a mean contrast scales with \(1/\delta^2\), a smaller assumed contrast needs more participants. (5) No. Increasing sample size may improve precision, but it does not eliminate bias caused by an analysis or model that fails to account for outcome-dependent missingness.