Radiofrequency ablation, which burns a ring of scar around the pulmonary veins to block the electrical triggers of atrial fibrillation (AF), is often judged by retrospective chart reviews: did the patient's AF come back within a year? In routine care, "come back" means "was caught on a scheduled Holter monitor or prompted a symptomatic visit." Much of returning AF is silent. In a randomized trial, patients who recorded handheld ECGs several times a day showed 64.2% AF-free survival, compared with 78.9% under scheduled Holter follow-up (Portable Device Improves the Detection of Atrial Fibrillation After Ablation). Retrospective studies that link a blood biomarker to recurrence are therefore studying a mix of two things. One is whether the biomarker predicts the disease. The other is whether it predicts being looked at. The same visit that draws a blood sample usually also records an ECG, so the schedule that produces biomarker measurements also produces outcome detection.
We propose a model for retrospective post-ablation cohorts that treats true recurrence time as hidden. It describes how often and how intensively each patient was monitored as a recorded, patient-specific process. It uses serial post-ablation biomarker values, not a single admission draw, as predictors. The central question is empirical. When detection depends on factors that also drive biomarker testing, do published-style biomarker hazard ratios and discrimination figures change materially? Can the joint model recover the answer that continuous monitoring would have given? We test this by taking patients who had continuous rhythm monitoring and deliberately hiding most of their data.
Core Claim
Outcome misclassification in post-ablation cohorts is probably differential, not uniform. Patients with worse metabolic or neurohormonal profiles see clinicians more often. They get more ECGs and more blood draws, so their silent recurrences are caught more often. This can inflate the apparent prognostic value of a biomarker. It can also distort the shape of its trajectory effect. A fixed correction such as "assume 15% of recurrences are missed" cannot fix that kind of distortion.
Our claim is that the full observation record can be written down and used as data: the dates of visits, the type and duration of each rhythm recording, and which recordings came with blood draws. Doing so yields biomarker effects that agree with continuous-monitoring ground truth, where both naive Cox regression and uniform misclassification correction do not. If the agreement fails, the method is not worth its complexity, and the experiments are built so that this outcome is visible.
Research Program
The model has three linked parts. The first is a latent recurrence time $T$ after a blanking period. It has a proportional hazard that depends on baseline covariates and on the current smoothed level and slope of each tracked biomarker.
The second is a sub-model for each biomarker trajectory, such as the stress–hyperglycemia ratio (acute glucose normalized by chronic HbA1c), BNP, or CRP. It is a mixed-effects curve over post-ablation time, so sparse and irregular draws inform a patient-specific level and slope.
The third is the inspection process. Each recorded rhythm assessment $j$ happens at time $t_j$ and lasts $d_j$, ranging from a 10-second ECG to a 72-hour Holter. If AF has already recurred ($T < t_j$), the assessment detects it with a probability that rises with recording length:
$$ P(\text{detect at } j \mid T < t_j) = 1 - \exp(-\rho\, d_j), $$
Here $\rho$ is a patient-level rate of AF burden. It is shared across that patient's recordings and gets a population prior. The exponential form follows from treating episodes as arriving at rate $\rho$ during recording.
Visit times themselves are modeled with a hazard that may depend on the biomarker trajectory and on symptoms. This is what lets the model represent informative observation, the open problem noted for sparse EHR panels in Deep Survival Analysis. That paper handled irregular sampling and time-zero alignment but treated an absent event code as a non-event. Our likelihood instead sums over the possibility that recurrence occurred and was missed at every inspection.
The parameter $\rho$ cannot be learned from intermittent data alone. We anchor it with a validation subset of patients who had near-continuous monitoring, such as implantable loop recorders. We also place an informative prior on it derived from the Holter-versus-handheld detection gap in the Huang trial.
The gap is not itself a sensitivity. It is a difference in survival between randomized arms, and the handheld arm also had a nightly blind spot. We therefore use it only as a prior, not a fixed value. Loop recorders have their own sensing errors, which differ between devices (Comparison of Electrocardiogram Characteristics of Two Commercially Available Implantable Loop Monitors). We model their sensitivity as high but below one.
As an optional fourth input, sinus-rhythm ECGs taken at follow-up can be scored by a waveform model of hidden AF substrate. Two such models exist: Deep Learning of Electrocardiograms in Sinus Rhythm From US Veterans to Predict Atrial Fibrillation and the beat-level network of A Deep Learning Method for Beat-Level Risk Analysis and Interpretation of Atrial Fibrillation Patients during Sinus Rhythm. The score enters as a noisy indicator of $T < t_j$. Neither model was trained on scarred post-ablation atria, so this input is tested as an ablation, not assumed to help.
The cohort is a multicenter retrospective set of first radiofrequency pulmonary vein isolations, extracted from EHRs. It includes procedure data, all post-procedure ECG and Holter records with their durations, and all laboratory draws. A loop-recorder or intensive-monitoring subset is required. Without it the identification argument collapses and we would report only sensitivity analyses.
Relation to Prior Work
Two retrospective post-ablation studies motivate the proposal. Relationship between the stress–hyperglycemia ratio and atrial fibrillation recurrence risk after radiofrequency catheter ablation linked a single admission stress–hyperglycemia ratio to recurrence, reporting AUC 0.79 and adjusted HR 3.379. A predictive model using left atrial function and B‐type natriuretic peptide level combined pre-ablation echocardiography with BNP, reporting AUC 0.814 versus 0.703 for BNP alone. Both used single snapshots and routine follow-up. We reuse their biomarkers but measure them over time, and we model how recurrence was ascertained.
The trajectory literature supplies the motivation for using level and slope. That literature includes albumin change after myocardial infarction (Association between albumin changes and prognosis), hsCRP trajectory groups (Association Between High-Sensitivity C-Reactive Protein Trajectories and the Incidence of Metabolic Syndrome), and serial NLR in critical illness (The association between the neutrophil-to-lymphocyte ratio and mortality). None of these studies addresses outcomes that go unseen.
The claims-based study Predicting Atrial Fibrillation Ablation Outcomes constrains the design. Its near-chance AUC of 0.528 under a labels-from-reinterventions definition shows that neither scale nor a stronger classifier fixes misclassified outcomes.
Baselines
The naive reference is a Cox model with the admission biomarker snapshot and standard right censoring, replicating the Li et al. specification. Its published counterpart reports AUC 0.79 and HR 3.379 for the stress–hyperglycemia ratio. It is run on our intermittent-only data with identical covariates.
The second baseline is a Cox model with time-varying biomarker values and right censoring. It isolates the value of trajectories without any misclassification modeling.
The strongest existing method for sparse longitudinal EHR survival is Deep Survival Analysis, which reported a C-index of 73.11% versus 65.57% for Framingham on coronary heart disease. No reported result was found on Lacuna for it on post-ablation recurrence. We will refit it on our cohort with the same inputs and a matched hyperparameter search budget.
The fourth baseline is quantitative bias analysis. A standard Cox fit is corrected by a single uniform detection sensitivity, set from the validation subset or from the Huang prior.
Two ablations isolate the key ingredients. The first removes the biomarker dependence of the visit-time process, which tests whether differential detection matters. The second removes the waveform-score input.
Beating a baseline has a concrete meaning here. Biomarker hazard ratios must be closer to the continuous-monitoring estimate, measured as absolute log-HR error with bootstrap intervals that exclude the baseline's error. The C-index and calibration against held-out continuous-monitoring labels must also be higher. A gain in C-index against intermittent labels alone does not count.
Why not just…?
Why not just apply a uniform misclassification correction? If detection sensitivity is roughly the same across biomarker strata, this simple approach will do as well as ours, and that is a real threat. We settle it directly. In the continuous-monitoring subset we estimate detection probability under the intermittent schedule, stratified by biomarker level. If it is flat, we report that the simple correction suffices and the visit-process component is unnecessary.
Why not just adjust for the number of follow-up ECGs as a covariate? Monitoring intensity is caused partly by symptoms of recurrence and partly by biomarker-driven clinical concern. Conditioning on it mixes the outcome into the predictors. The masking experiment compares this adjusted Cox model against ground truth, and we expect it to bias the hazard ratios in the direction opposite to the naive model.
Why not just restrict analysis to patients with uniform protocol Holters? This removes differential detection but keeps a uniform under-detection that, per Huang et al., is large. It also discards most of a real-world cohort and selects patients who were protocol-adherent. It appears as a sensitivity arm. If it matches our model on hazard ratio error, we would recommend it for its simplicity.
Why not just relabel silent recurrences with a sinus-rhythm ECG model? The published models were trained on general screening populations whose labels were themselves underreported. Their discrimination, AUC 0.86 to 0.93 in Yuan et al. and 0.7591 at beat level in Lei et al., is unproven on post-ablation scar. Hard relabeling would carry their errors in with false confidence. We therefore use the score only as a soft indicator, and the ablation shows whether it helps.
Proposed Experiments
The decisive check uses masking. Take the loop-recorder subset, where recurrence time is close to known. Delete every rhythm observation except those that coincide with the patient's actual routine ECG and Holter encounters, and keep all laboratory draws. Fit every model on the masked data. Then compare its biomarker hazard ratios, C-index, and one-year calibration with a Cox fit on the unmasked continuous labels. Because real encounter schedules are kept, any dependence between biomarkers and visits is the real one, not a simulated one.
A semi-synthetic study complements this. We vary how strongly visit rates depend on biomarkers in order to map when differential detection overturns conclusions. The study also checks that $\rho$ is recoverable at validation-subset sizes from 50 to 500 patients.
A replication check asks whether the snapshot stress–hyperglycemia ratio effect survives. We re-estimate it under our model on the full cohort. A shrinkage of the hazard ratio toward one would show that part of the published association reflected surveillance. A stable estimate would make that association more credible than before.
Finally, we score the masked loop-recorder subset again to estimate the fraction of recurrences that routine follow-up misses in our own data. We compare that fraction with the roughly 15-point gap reported by Huang et al. We also report it stratified by biomarker trajectory, since that stratification is the quantity the proposal turns on.
References
- Portable Device Improves the Detection of Atrial Fibrillation After Ablation
- Deep Survival Analysis
- Comparison of Electrocardiogram Characteristics of Two Commercially Available Implantable Loop Monitors: Impact of These Characteristics in the Correct Adjudication of Recorded Events and Minimized Undersensing and Oversensing of Events
- Deep Learning of Electrocardiograms in Sinus Rhythm From US Veterans to Predict Atrial Fibrillation
- A deep learning method for beat-level risk analysis and interpretation of atrial fibrillation patients during sinus rhythm
- Relationship between the stress–hyperglycemia ratio and atrial fibrillation recurrence risk after radiofrequency catheter ablation: a retrospective study
- A predictive model using left atrial function and B‐type natriuretic peptide level in predicting the recurrence of early persistent atrial fibrillation after radiofrequency ablation
- Association between albumin changes and prognosis in older patients with acute myocardial infarction
- Association Between High-Sensitivity C-Reactive Protein Trajectories and the Incidence of Metabolic Syndrome:A Retrospective Cohort Study
- The association between the neutrophil-to-lymphocyte ratio and mortality in critical illness: an observational cohort study
- Predicting Atrial Fibrillation Ablation Outcomes: Machine Learning Model Development and Validation Using a Large Administrative Claims Database