Snapshot-Honest Cohorts: Separating Clinical Time from Reporting Time in Registry Studies

Many retrospective cohort studies are built from national surveillance registries: researchers pull a snapshot of the database, define a cohort, and estimate how some exposure relates to an outcome. An example would be how the delay between symptom onset and hospital admission relates to death. Each record in such a registry carries two clocks. The first is clinical time, meaning when symptoms began, when the patient was admitted, and when the patient died. The second is reporting time, meaning when each of those events actually reached the database.

The standard analysis treats the snapshot as if it were the finished history. During an epidemic, when these studies are most wanted, it is not. Recent patients are missing or incomplete, and which patients are missing depends on what happened to them. Deaths, long hospital stays and late admissions reach the registry on different schedules. The result is a selection bias that operates at the level of individual patients. It is the patient-level counterpart of the well-known "artificial downturn" in epidemic curves. That aggregate effect was shown dramatically in Gaussian process nowcasting: the raw data said the epidemic was shrinking ($R_t<1$) when it was in fact growing.

We propose to make each cohort estimate honest about its snapshot date. Every cohort definition, including who is eligible, how exposure is measured and what counts as an outcome, is split into two separate conditions. One is a predicate about the patient's clinical history. The other is a condition about whether each event the first predicate relies on would plausibly have been reported by the snapshot date. We model the second part separately as a delay surface that depends on the outcome, and we use it to reweight the cohort. The Brazilian SIVEP-Gripe registry is re-released over time, so we can take later, converged releases as "data from the future" and measure how far early-snapshot cohort estimates were wrong, and whether the correction fixes them.

Core Claim

Hazard ratios and delay distributions computed from mid-crisis registry snapshots are biased in a direction the snapshot date predicts. The bias comes mainly from reporting delays that differ by outcome and by exposure, not from delay as such. The claim is that a clinical-time/reporting-time decomposition removes most of this bias at useful snapshot lags, and that a model with a single, outcome-blind delay distribution does not. This claim is falsifiable. If reporting delay turns out to be roughly independent of outcome in SIVEP-Gripe, the simpler corrections will match ours, and we will report that.

Where the Pieces Come From

The three research directions play unequal roles.

Retrospective cohort methodology supplies the estimands and the thing we want to protect. Timing to intubation COVID-19 patients is the template. It is a single-hospital cohort of 592 ventilated patients that estimated an adjusted hazard ratio (the relative risk of death, after adjustment) of 1.018 per day of onset-to-intubation delay. It adjusted for confounding with Cox models (a standard survival regression) and a clinical risk score, but it treated all timestamps as fixed facts. Its data came from one institution after the fact. We ask what happens when the same kind of estimand is computed from a live national registry.

Surveillance-latency work supplies both the evidence that this matters and the modeling tools. Inference of COVID-19 epidemiological distributions from Brazilian hospital data fit onset-to-death and onset-to-admission distributions across Brazilian states from SIVEP-Gripe. It found that using state-specific rather than national delays changed estimated active infections by up to 18%. It also acknowledged reporting lag and censoring as unresolved limitations, and that gap is exactly what we target. Gaussian process nowcasting models death counts indexed by event date and reporting delay with a two-dimensional Gaussian process, a flexible smooth surface fitted to the "reporting triangle". It evaluates that model against later registry releases. Bayesian imputation of COVID-19 positive test counts treats observed counts as a random thinning of true counts. It flags that its delay priors break when the reporting pipeline itself changes.

All of these methods correct aggregate daily counts. None of them corrects a patient-level estimand whose inclusion depends on the outcome. We reuse their delay-surface machinery but condition it on individual clinical trajectories.

Temporal property decomposition supplies the design principle, not a verifier. Analyzing Timed Systems Using Tree Automata verifies timed systems by splitting the check in two. One part asks whether the timing constraints can be realized at all, and it does not depend on the particular system. The other part checks the system's own discrete rules. VerX turns temporal specifications about past events into ordinary checks by recording execution history in the program. We borrow both moves.

A cohort definition is written as a past-time predicate over a patient's event history. An example is "admitted within $k$ days of onset, and died or was discharged within 28 days." That predicate is compiled into two parts. The first is a check on the clinical record, which does not depend on the snapshot. The second is a requirement that every event the predicate refers to has a reporting time no later than the snapshot date $s$.

This matters in practice. Hand-written cohort code routinely mixes the two clocks. For example, it may silently require a discharge date to exist, which excludes patients who are still hospitalized or whose discharge has not yet been reported. We do not claim any formal verification of epidemiology. The formal-methods side contributes the discipline of separating the two conditions and a mechanical way to generate the reporting requirement for any cohort query.

Research Program

We first build a record-level history of SIVEP-Gripe from successive public releases. For each record we reconstruct when each field first appeared or changed. This gives, per patient and per event, a clinical timestamp and a first-seen date.

Next, we fit a reporting-delay model $P(R_e \le s \mid \text{event } e, \text{outcome}, \text{state}, t)$. Here $R_e$ is the reporting time of event $e$, $s$ is the snapshot date, and $t$ is the calendar time of the event. The model follows the two-dimensional Gaussian-process delay surface of the GP nowcasting paper. It adds stratification by outcome type and by state, using the partial pooling across states (sharing strength between states while allowing them to differ) of the Brazilian distributions paper.

The compiled reporting requirement then defines, for each patient in the converged cohort, the probability $\pi_i(s)$ that they would have qualified in the snapshot taken at $s$. Cohort estimates at snapshot $s$ are computed by inverse-probability weighting, where each included patient is up-weighted by $1/\pi_i(s)$. This is fitted using only information available at $s$. Delay parameters are estimated from earlier, already-converged periods and then projected forward.

To address the known fragility of delay priors, we add a monitor. It compares recent partial triangles against the projected surface and widens the uncertainty when the reporting process shifts. This targets the failure mode noted by Jersakova and Lomax.

Baselines

The naive reference point is the ordinary analysis of the snapshot as it stands. We define the cohort, fit a Cox model and read off the hazard ratio, adjusting for the same covariates as every other arm. This is what a researcher would do by default, and it is the thing we claim is biased.

The strongest practical competitor is window truncation. It drops all patients whose index date falls within the last $w$ weeks before the snapshot, with $w$ tuned on earlier converged periods to minimize bias. This is what careful epidemiologists do, and it may work well. To keep the comparison fair, it gets the same tuning data and the same budget of candidate windows as our delay model gets for its hyperparameters. We count our method as beating it only if it achieves lower bias or better interval coverage at matched effective sample size, or equal bias with materially more retained patients.

The strongest existing modeling approach is aggregate nowcasting followed by a cohort analysis. We apply the two-dimensional Gaussian-process nowcast of Gaussian process nowcasting to rescale outcome counts by stratum and then fit the survival model. That paper reports that it matched or beat the NobBS baseline on RMSE and CRPS (squared error and a score for probabilistic forecasts). However, no reported result was found on Lacuna for its exact scalar RMSE or CRPS values, and it reports no patient-level estimand at all. We will therefore rerun it on the same releases.

The key ablation keeps our full pipeline but uses a single delay distribution that ignores outcome and exposure. It isolates whether conditioning delay on the outcome is what does the work.

The clinical anchor is Sternlicht et al.'s aHR of 1.018 per day. It comes from a different, single-center cohort, so it is a plausibility check on direction and magnitude, not a target to beat.

Why not just…?

Why not just drop the last few weeks of data? This is the real threat. If SIVEP-Gripe's delay tail is short relative to the outcome window, truncation removes most of the bias and our method adds complexity for nothing. Two things work against it. The onset-to-death mean of about 15 days nationally, varying from 11.2 to 17.8 days by state, implies that the needed window differs by state. And the bias from outcome-dependent delay does not vanish at a fixed window; it only shrinks. Neither point is decisive, so the experiment plots bias against window length and against retained sample. If truncation dominates across that curve, we will say so and recommend it.

Why not just nowcast the aggregate counts and plug them in? Aggregate nowcasts fix the number of events per day. They do not fix which patients are in the cohort or how their exposures are distributed. A hazard ratio for admission delay depends on whether late-admitted fatal cases are underrepresented, which a count-level correction cannot see. The nowcast-then-analyze baseline tests this directly. If it matches our method, the patient-level decomposition is unnecessary.

Why not just use standard survival methods for truncated data? Survival analysis already has methods for right-truncated and delayed-entry data. Our weighting belongs to that family, and we do not claim a new estimator. What those methods usually assume is a single truncation time per patient that does not depend on the outcome. What we add is a truncation mechanism built from the reporting requirement of the specific query, involving several events per patient with delays that depend on the outcome. The single-delay ablation is exactly that textbook assumption, so the experiments settle whether the extra structure matters.

Proposed Experiments

The main experiment is a snapshot-replay study on SIVEP-Gripe covering 2020 to 2021. We take snapshot dates every two weeks, run each method using only information available at each date, and compare the estimates with those from the converged release at least six months later.

We use three estimands:

  1. The per-day hazard ratio of onset-to-admission delay for in-hospital death, adjusted for age, sex and state.
  2. State-level mean onset-to-death, comparable to the Brazilian distributions paper.
  3. The ICU-versus-ward mortality contrast.

A fourth estimand, a ventilation-timing hazard ratio in the style of Sternlicht, will be added only if the ventilation fields turn out to be well populated. We have not verified this.

The metrics are absolute bias relative to the converged estimate, 95% interval coverage, and effective sample size, all as a function of snapshot lag.

The decisive checks are three.

First, does the naive estimate's bias shrink predictably as the snapshot ages? This confirms that the phenomenon exists.

Second, does the outcome-dependent delay model beat the single-delay ablation? This tests the key ingredient.

Third, does our method beat tuned truncation at matched effective sample size? This tests practical value.

A synthetic study with known clinical and reporting processes, where the reporting delays either depend on the outcome or do not, checks that the method gives no gain when delays are independent of outcome.

Finally, we stress-test the monitor on periods that bracket abrupt reporting changes identified in the release history, and check whether coverage holds up there.