Simulation Study for Link Misspecification

Why Simulate Link Misspecification?

A joint model connects a subject’s longitudinal biomarker trajectory to the event hazard through an association structure. In practice, the scientific link is rarely known with certainty. A model using the current latent biomarker value may therefore be fitted when the data-generating association depends on a slope or another feature of the trajectory. A simulation study makes this uncertainty concrete: specify a plausible mechanism, generate many hypothetical data sets from it, fit the competing links, and measure how the choice affects estimates and conclusions.

The purpose is not to identify a universally correct link from simulated data. It is to learn how particular fitted models behave under clearly stated conditions. A useful study separates link misspecification from changes in trajectory modeling, baseline-hazard flexibility, visit schedules, or censoring. If several components change at once, a difference in results cannot be attributed specifically to the link.

Define the Data-Generating Mechanism

For subject \(i\), let \(Y_{ij}\) be the biomarker measurement at visit time \(t_{ij}\), and let \(m_i(t)\) be the subject’s latent biomarker trajectory. Let \(T_i\) be the event time and \(C_i\) the censoring time; the observed time is \(\tilde T_i=\min(T_i,C_i)\), with event indicator \(\delta_i=I(T_i\leq C_i)\). A simple longitudinal model is

Here \(b_i=(b_{0i},b_{1i})^\mathsf{T}\) represents subject-specific random effects, and \(\epsilon_{ij}\) is measurement error. For example, a current-value data-generating hazard could be

The coefficient \(\alpha\) describes the log-hazard change for a one-unit increase in the latent biomarker, conditional on the covariates and the rest of the model. If the biomarker is standardized, that unit is one standard deviation; otherwise, it is the measurement unit used for \(m_i(t)\). An alternative data-generating mechanism could replace \(m_i(t)\) with \(m_i'(t)\), or with another prespecified trajectory feature. The simulation must state which mechanism is treated as true in each scenario.

A defensible design states the assumptions used to generate data. These may include the random-effects distribution and covariance, the measurement-error distribution, the visit schedule, the baseline hazard, covariate distributions, and the censoring mechanism. For a typical conditional simulation, the event hazard depends on the latent trajectory and specified covariates; the observed biomarker measurements arise from the trajectory plus measurement error; and censoring is independent of the event time conditional on the modeled covariates and other stated conditioning variables. If visits stop at the event, the simulation should impose that rule. If the visit process itself is informative, it must be modeled or studied as an additional source of misspecification.

Generate event and censoring times according to the stated mechanisms, then construct \(\tilde T_i\) and \(\delta_i\). Fit each candidate joint model to the same simulated data set. To isolate link sensitivity, keep the longitudinal structure, covariates, baseline-hazard specification, and estimation settings the same across candidate fits unless a planned scenario deliberately varies one of them.

Choose Targets Before Comparing Models

Simulation summaries are meaningful only when their target is clear. When a fitted link has the same parameter meaning as the generating link, coefficient bias can be summarized directly. When link functions differ, their association coefficients generally have different meanings and units. A current-value coefficient and a slope coefficient should not be compared as if both estimated the same parameter.

For different links, define a common scientific contrast. For instance, choose two prespecified latent trajectories, A and B, and a time \(t^\ast\). The target may be their log-hazard contrast at that time under the generating mechanism. Each fitted model can then be used to predict the same contrast for those trajectories. This puts the comparison on a common scale even when the fitted link coefficients are not directly comparable. The trajectories and time should be selected for scientific relevance, not chosen after inspecting the results.

For a parameter \(\theta\) with known generating value \(\theta_0\), let \(\hat\theta_r\) be the estimate in replicate \(r\), for \(r=1,\ldots,R\). The estimated bias is the average estimation error across replicates. Its Monte Carlo standard error (MCSE) describes the simulation noise in that estimated average, not the standard error within a fitted data set.

Here \(s_{\hat\theta}\) is the sample standard deviation of the replicate estimates. The MCSE decreases as the number of independent replicates increases. It does not measure uncertainty about whether the chosen data-generating mechanism is realistic.

Measure Uncertainty and Substantive Errors

Bias alone does not describe all consequences of a wrong link. A model can have modest average bias but produce confidence intervals that are too narrow, or it can yield unstable conclusions in a clinically important subset of scenarios. For a nominal 95% confidence interval, empirical coverage is the proportion of simulation replicates in which the interval contains the target value. If \(K\) of \(R\) intervals cover, the estimated coverage is \(\hat p=K/R\), with approximate MCSE \(\sqrt{\hat p(1-\hat p)/R}\), since each replicate contributes a cover-or-not indicator.

A substantive conclusion also needs an explicit rule. For example, a directional rule might declare evidence of a positive association only when a two-sided 95% confidence interval lies entirely above zero. When the generating association is positive, the proportion of replicates declaring a negative association estimates the frequency of a wrong-direction conclusion under that scenario. The proportion declaring no positive association can also be informative, but it is not the same quantity as bias or interval coverage.

For comparisons across different links, calculate the prespecified common contrast in every replicate and evaluate its bias, interval coverage, or decision error. A coefficient from one link may not be a valid target for a coefficient from another. When the target is a contrast, describe the trajectories, time, covariate values, and units that define it.

Design and Analyze the Simulation

A useful study varies the feature most relevant to its scientific question while avoiding an unmanageable collection of scenarios. Possible factors include sample size, strength of association, random-effects variability, measurement error, number and timing of visits, event rate, and censoring proportion. A baseline scenario can reflect plausible conditions; additional scenarios can stress the design, such as sparse visits or weaker event information. Changing factors systematically helps distinguish a robust pattern from one particular configuration.

Using identical data within each replicate is especially valuable: a difference between two model summaries then reflects their differing fits on the same simulated sample, rather than unrelated random samples. Still, a simulation must report convergence and boundary problems. Silently dropping failed fits can make a model appear more reliable than it is, especially if failures occur more often in difficult data sets.

Diagnostics, Alternatives, and Limitations

Before interpreting link comparisons, check whether the simulation is behaving as intended. Confirm that generated event rates, censoring proportions, visit counts, and biomarker distributions match the design. Check that the fitting procedure recovers parameters reasonably under a correctly specified link; poor performance even in that setting points to an implementation, estimation, or information problem rather than an isolated link issue. Inspect convergence rates, extreme estimates, estimated random-effects covariance matrices, and interval widths by scenario and fitted link. Summaries based only on successful fits should be accompanied by the failure rate and a discussion of how failures could affect conclusions.

The main alternative to a simulation study is a sensitivity analysis on observed data: fit several plausible links and compare their estimates, uncertainty, predictions, or decisions. That analysis shows how the conclusions for the observed sample vary across specifications; it does not reveal which fit would perform best under a known generating process. Simulation supplies that controlled benchmark, but its conclusions are conditional on its assumptions. The two approaches answer different questions and can complement one another.

A common mistake is to fit alternative links, observe different coefficient estimates, and call the difference “bias.” That reasoning is incorrect when the coefficients represent different trajectory features or use different units. The correction is to compare each coefficient only with its matching generating parameter, or to translate each fit into a shared estimand such as a prespecified log-hazard contrast. A second pitfall is treating a small estimated bias as proof of general validity. Small bias in one scenario says nothing by itself about coverage, decision errors, other scenarios, or departures from the chosen data-generating mechanism.

Simulation results are not universal rankings of association structures. They depend on the trajectory distribution, event information, measurement schedule, censoring, sample size, and fitting implementation. They also cannot reproduce every feature of real data. Report the generating assumptions and scenarios transparently so readers can judge which conditions are relevant to their application.