Worked Analysis of a Registry-Based External Control

From Registry Records to a Defined Comparison

A registry-based external control can make a single-arm trial more informative, but it does not recreate randomization. The analysis compares outcomes among trial participants receiving treatment with outcomes among eligible registry patients who did not receive that treatment. Its credibility therefore depends on a sequence of linked decisions: matching the protocol’s target question, constructing comparable cohorts, adjusting measured differences, and making the remaining uncertainty visible.

The target must be specified before fitting a model. For a time-to-event outcome, define the treatment contrast, the population to which it applies, the outcome, and the follow-up period. In this tutorial, the effect measure is a hazard ratio (HR): the treatment-group hazard divided by the external-control hazard, conditional on the chosen model. An HR below 1 favors treatment when the event is clinically undesirable.

A useful protocol-alignment checklist covers the population, treatment eligibility, index date (time zero), baseline covariates, endpoint definition, and follow-up rules. In particular, both groups must enter risk follow-up at a comparable point in the disease and care pathway. Starting registry follow-up earlier than trial follow-up can create immortal-time or disease-stage differences that adjustment at baseline may not repair. Endpoint dates and censoring rules also need to be comparable; a registry’s routine-care ascertainment may differ from trial visits.

Adjustment and Diagnostics

Let \(S=1\) indicate trial membership and \(S=0\) registry membership, and let \(X\) denote measured baseline characteristics relevant to trial participation and prognosis. One approach estimates the probability of trial membership from \(X\) in the pooled data. Registry patients can then receive weights proportional to the odds of trial membership:

The weights are scaled according to the chosen analysis convention; multiplying every registry weight by the same positive constant does not change a weighted partial-likelihood estimate. The intended effect is to give greater influence to registry patients whose measured profiles resemble those of trial participants. The relevant assumptions include adequate overlap in \(X\), a sufficiently well-specified membership model, comparable outcome definitions, and no important unmeasured differences that jointly affect source membership and outcome after conditioning on \(X\). These are substantive assumptions, not consequences of the weighting formula.

Check covariate balance before and after weighting, including clinically important prognostic factors and nonlinearities where relevant. Inspect the distribution of weights, identify extreme values, and assess whether trial patients have registry counterparts. The effective sample size (ESS) summarizes weight concentration; for weights \(w_i\), it is:

ESS is at most the number of records with positive weights, and it falls when a few records dominate. It is a diagnostic, not a replacement for the actual sample size or a guarantee of valid inference. A low value warns that the adjusted estimate may depend heavily on a small part of the registry.

For time-to-event outcomes, a weighted Cox model is one possible analysis, with treatment group as the exposure and the prespecified baseline covariates included as appropriate. Its proportional-hazards assumption should be assessed, for example by examining time patterns in residuals and treatment effects. Also inspect influential observations, censoring patterns, endpoint completeness, and whether results change materially under reasonable alternative covariate or weight specifications. If proportional hazards is implausible, a single HR may obscure time-varying effects; a prespecified alternative such as a time-specific survival contrast may be more interpretable.

Bayesian Estimation and Interpretation

A Bayesian analysis combines a likelihood for the adjusted treatment-effect estimate with a prior distribution for the log HR, denoted \(\beta=\log(\mathrm{HR})\). For a simple worked calculation, suppose the adjusted analysis provides an approximately normal likelihood, \(\hat{\beta}\mid\beta\sim N(\beta,SE^2)\), and use a normal prior \(\beta\sim N(0,100)\). The prior is centered at no effect and is very broad on the log-HR scale. This summary-likelihood calculation is a working approximation; uncertainty from estimated weights and model choices must be considered in the analysis design rather than assumed to vanish.

This result follows by multiplying the normal likelihood kernel and prior kernel. Their exponent, up to terms not involving \(\beta\), is:

The coefficient of the squared term gives the posterior precision, and its center gives the posterior mean stated above. This derivation applies to the normal summary model; it does not establish that the external-control comparison itself is unbiased.

Sensitivity, Alternatives, and Failure Modes

A credible analysis asks whether the conclusion is stable to reasonable choices. Repeat the adjustment with defensible alternative membership models or covariate specifications, and examine the consequences of truncating extreme weights as a sensitivity analysis. Truncation can reduce variance but also change the target or introduce bias; report the rule and compare estimates rather than treating truncation as a cure. Consider whether plausible residual confounding could move the log HR enough to change the clinical interpretation. Such sensitivity analyses quantify dependence on assumptions; they cannot identify the true amount of unmeasured bias from the observed data alone.

Weighting is not the only adjustment strategy. Matching may improve transparency by showing which registry records resemble trial participants, but can discard records and change the population represented. Outcome regression models the outcome given covariates and can be more efficient when correctly specified, but may extrapolate where trial and registry profiles do not overlap. Standardization predicts outcomes under each treatment strategy for the target population, while weighting rebalances the source population. These approaches answer closely related questions only when their target populations and assumptions are aligned; agreement among them is reassuring but does not prove validity.

Failure modes include poor overlap, severe weight concentration, residual imbalance on key prognostic factors, inconsistent endpoint ascertainment, differential censoring, and a treatment effect that changes over time despite a constant-HR model. If trial participants occupy covariate regions absent from the registry, weighting cannot manufacture comparable controls. If the registry misses deaths or records them with delay, a fitted survival model may be precisely estimated but systematically misleading. These issues should prompt redesign, narrower target-population claims, or a different estimand—not merely a more elaborate prior.

Common mistake. “The weighted groups are balanced on measured covariates, so the external comparison is equivalent to a randomized trial.” Balance only addresses the measured variables used and checked; it does not rule out unmeasured confounding, selection bias, or differences in care and outcome recording. The correction is to interpret the posterior as conditional on explicit design and modeling assumptions, and to test how sensitive the estimate is to plausible departures from them.