A growing body of clinical work argues that how much a patient's lab values or vital signs wobble over time predicts outcomes, separately from their average level. The clearest statistical version comes from joint longitudinal-survival models. These fit a smooth curve to each patient's measurements, take the integrated squared second derivative of that curve as a "roughness" score, and find that this score predicts cardiovascular events. In irregularly sampled clinical records, though, roughness is entangled with three things that are not biology. Assay noise adds wobble. Measurement timing changes how many bends a fitted curve can have. And in hospitals, sicker patients get measured more often. A patient can look volatile simply because they were sampled densely and noisily.
This note proposes to borrow the central tool of neural-data statistics, the structure-preserving surrogate, and adapt it to sparse, irregularly timed clinical series. A surrogate is a synthetic copy of the data that destroys the one pattern being tested and keeps everything else. For each patient we generate hundreds of surrogate series that keep that patient's exact measurement timestamps, exact distribution of values, and a stationary mean-reverting correlation structure with realistic assay noise, but contain no excess instability. A patient's roughness is then reported as excess roughness: how far it sits above their own surrogate distribution. The question is whether volatility's prognostic signal survives once sampling and noise are held fixed. The answer matters both for clinical risk scores and for the generative trajectory models now being built on clinical time series.
Core Claim
We claim that a substantial and measurable fraction of the prognostic value of raw trajectory roughness in ICU laboratory series is a sampling artifact, driven by measurement density and assay noise. We further claim that a surrogate-calibrated excess-roughness score separates genuine physiological instability from this artifact. Concretely, for patient $i$ with observed roughness $R_i$ and surrogate roughnesses $R_i^{(1)},\dots,R_i^{(B)}$ computed by the identical spline pipeline on the identical timestamps, we define
$$z_i = \frac{R_i - \overline{R_i^{(b)}}}{\mathrm{sd}(R_i^{(b)})},$$
where the bar and sd are taken over the $B$ surrogates. Because the surrogates share the patient's timestamps, any roughness induced by spacing or knot placement appears equally in the numerator's two terms and cancels. The claim is falsifiable in both directions. If $z_i$ predicts mortality no better than raw $R_i$ after adjusting for sampling density, the surrogate machinery is unnecessary. If raw $R_i$ loses its effect once $z_i$ and sampling density are in the model, published volatility effects need reinterpretation.
Where This Sits
The direct starting point is Weighted biomarker variability in joint analysis of longitudinal and time-to-event data. It couples a B-spline mixed-effects curve to a Cox model and reports a hazard ratio of 1.14 per standard deviation of systolic blood pressure roughness in the MRC elderly trial. Its own stated limitations motivate this proposal. The roughness estimate is sensitive to knot number and placement, the Laplace approximation degrades when patients have few measurements, and significance is assessed only parametrically. We reuse its roughness statistic unchanged and change only how it is calibrated. Its regular-visit trial setting is also exactly where sampling artifacts should be smallest, so the ICU, with its severity-driven sampling, is the harder and more informative test.
The surrogate side supplies the method and the cautionary evidence. Questions and controversies in the study of time-varying functional connectivity in resting fMRI reviews how windowed estimators produce apparent dynamics out of stationary autocorrelated noise unless tested against stationary surrogates matched in covariance and spectrum. That is the same failure we suspect in clinical roughness. ASSET builds time-varying background rates into its null and shows the constraint our design must respect: misestimating the background during rapid shifts produces false positives. This is why we estimate the null's correlation structure hierarchically rather than per patient from a handful of points. Finding neural assemblies with frequent item set mining and the phase-randomized controls in Learned Motor Patterns Are Replayed in Human Motor Cortex during Sleep provide the design rule: keep the marginal statistics and spectrum, destroy only the structure under test. Their methods assume dense, regularly sampled signals, and adapting them to five to thirty irregular points is the technical gap. Correcting Biased Centered Kernel Alignment Measures is the constraining negative result. A metric that looks meaningful can reflect sample geometry, and it shows high scores even on shuffled data. Roughness computed from few points is the clinical analogue of that small-sample bias.
On the trajectory-modeling side, Trajectory Flow Matching and Longitudinal Flow Matching for Trajectory Modeling learn generative models of patient trajectories with uncertainty, and neither offers a hypothesis test. Our work does not compete with them as forecasters. Instead, TFM's learned uncertainty becomes a competing way to score "surprising" instability, and we treat it as a baseline. Clinical motivation comes from trajectory studies that rely on change scores without any null. These include albumin change after myocardial infarction, lymphocyte counts at different post-chemoradiotherapy time points, and the hsCRP latent trajectory classes. Yet Another ICU Benchmark supplies both the data harmonization and a warning: preprocessing choices can move results more than model choice, so every comparison here shares one fixed pipeline.
Research Program
The core artifact is a surrogate generator for short, irregular series. For a given biomarker, we first fit a population-level stationary null across all patients. This is a mean-reverting Gaussian process (Ornstein–Uhlenbeck-type, with a Matérn kernel) plus a nugget term for assay noise. Its correlation time is pooled hierarchically across patients, and the nugget is anchored to replicate-measurement variability where the data allow. For patient $i$, we draw a sample path from this process at the patient's exact timestamps. We then rank-remap the draw onto the patient's own observed values, following the amplitude-adjustment logic of iterated amplitude-adjusted Fourier surrogates. We iterate the remapping and a re-conditioning step until the empirical variogram (how differences between values grow with time gap) stabilizes. The result keeps the timestamps exactly, the marginal distribution of values exactly, and the correlation structure approximately, while removing any patient-specific instability beyond what a stationary noisy process would produce.
We also build a second, stricter null. It keeps the patient's own slow trend, estimated with a heavily penalized spline, and randomizes only the residuals. This asks whether wobble exceeds what is expected around the patient's own drift. This null connects to the flow-matching literature's assumption that smooth momentum is real. Roughness, excess roughness, and their sampling covariates are computed by one shared code path. The study then has three parts: validating the generator on simulations with known ground truth, estimating how much published-style roughness effects shrink under calibration on real ICU data, and testing whether the calibrated score transfers across centers.
Baselines
The naive reference point is raw roughness from the published B-spline pipeline, entered into a Cox or logistic model alongside the biomarker's mean level. The same model is also run with the simple variability summaries clinicians actually use, the within-patient standard deviation and coefficient of variation. A second naive model adds measurement count and median inter-measurement interval as covariates. This is the cheapest possible "adjust for sampling" fix and the most important bar to clear.
The strongest existing method is the joint longitudinal-survival roughness model of Weighted biomarker variability. The file reports its result as a hazard ratio of 1.14 per 1-SD increase in SBP roughness for cardiovascular events in the MRC elderly trial. No discrimination metric for it was found on Lacuna. We will refit it on our cohorts with the same knot grid, covariates, and landmark window as our method, and report its hazard ratio, concordance, and knot sensitivity side by side with ours. For context on the ICU task, YAIB reports mortality AUROCs of 0.84 to 0.87 for full multivariate models. Our landmark task uses single-biomarker features, so those numbers are a ceiling for orientation, not a target. The NLR mortality study shows how small realistic gains from one lab feature are: adding NLR moved SAPS I AUC from 0.746 to 0.757.
The model-based competitor is a per-patient "surprise" score from Trajectory Flow Matching, run from its public code. We train it on the same training split with a matched hyperparameter search budget. The score averages the standardized residual of each observation under TFM's predicted mean and uncertainty flow. No reported result was found on Lacuna for TFM as a volatility or prognostic score.
Two ablations isolate the key ingredient, which is preserving each patient's timestamps and correlation structure. In the first, surrogates resample timestamps from the population interval distribution instead of keeping the patient's own. In the second, surrogates keep the timestamps but permute values freely, which is the unconstrained shuffle. We beat the field if excess roughness meets three conditions. First, it retains a significant association with outcome after adjustment for mean level and sampling covariates. Second, it improves concordance over raw roughness plus sampling covariates, with a bootstrap confidence interval on the difference excluding zero. Third, it shows lower dependence on knot choice than the joint model. Both ablations should do measurably worse on the simulations, where truth is known.
Why not just…?
Why not just add the number of measurements and the sampling interval as covariates? This is the most serious threat, and it is a baseline above. Covariate adjustment removes only the average linear effect of density on roughness. It cannot correct a patient-specific interaction between their particular gap pattern and the spline's knots, which is the sensitivity the joint-model paper itself flags. The simulations settle it directly: we generate patients with identical true instability but severity-driven sampling and check whether covariate adjustment recovers a null effect. If it does as well as surrogates on simulation and real data, we will report that the cheap fix suffices and keep the surrogate machinery only for per-patient testing.
Why not just parametric-bootstrap from the fitted joint model? That is also a surrogate, but its null inherits the B-spline random-effects structure and the Laplace approximation, both of which the source paper says degrade with few measurements per patient. Our null is deliberately model-light, keeping the empirical marginals exactly. The comparison is part of the experiments: on simulations with non-Gaussian marginals and heavy-tailed assay noise, we compare false-positive rates of per-patient tests under both nulls. If the parametric bootstrap is equally calibrated, the contribution narrows to the evaluation protocol.
Why not just use a generative trajectory model's uncertainty, such as TFM's? TFM measures surprise relative to learned population dynamics. Those dynamics are fit on the same severity-sampled data, so the learned uncertainty can absorb the very sampling confound we want to remove. The file also notes that TFM's history conditioning weakens in sparse settings. It is a real competitor for prediction, and the TFM-surprise baseline will show whether it captures the same signal. If it matches excess roughness in concordance but fails the simulation calibration check, it is a good predictor but not a valid test.
Why not just shuffle the values within each patient? This is the second ablation. The fMRI connectivity debate and the CKA results both show that unconstrained shuffles destroy autocorrelation and yield nulls that are trivially rejected. We expect almost every smooth ICU series to look "significantly rough" relative to shuffled copies, and the experiment will quantify this.
Proposed Experiments
The first experiment is simulation with known truth. Synthetic patients follow mean-reverting processes in which a known subset has elevated true instability tied to a hazard. Assay noise is added, and observation times follow either regular schedules or severity-driven schedules where higher latent risk triggers denser sampling. We measure per-patient false-positive rates at nominal 5% and power. We also measure the bias of the estimated volatility hazard ratio under raw roughness, covariate-adjusted roughness, the joint model, parametric bootstrap, TFM surprise, and both ablations. The decisive check is that under severity-driven sampling with no true instability effect, raw roughness shows a spurious hazard and excess roughness does not.
The second experiment is on MIMIC-IV and eICU, harmonized through the YAIB pipeline and the ricu concept definitions. We use a landmark design in which roughness is computed from serial albumin, absolute lymphocyte count, creatinine, and lactate over the first 48 hours, and in-hospital mortality after the landmark is the outcome. We report adjusted hazard ratios and concordance for each score, and the shrinkage of the raw-roughness effect when excess roughness enters the model. The decisive check is a stratified analysis by sampling density. A genuine instability signal should hold its effect size across density strata, whereas an artifact should be concentrated where sampling is densest. We also test transfer by training on eICU and evaluating on MIMIC-IV, following YAIB's observation that multi-center training generalizes better.
The third experiment covers the sparse regime. If longitudinal plasma or imaging biomarkers with at least three visits are available in ADNI, we repeat the analysis for progression to dementia. This tests whether the generator remains calibrated with very few points, and it speaks to the suggestion in the p-Tau217 survival study that trajectories should sharpen prognosis. If the MRC trial data are accessible, we refit the 1.14 hazard ratio with excess roughness as a direct replication check in the setting where sampling artifacts should matter least. A small or absent shrinkage there, alongside large shrinkage in the ICU, would be the cleanest single result the project could produce.
References
- Weighted biomarker variability in joint analysis of longitudinal and time-to-event data
- Questions and controversies in the study of time-varying functional connectivity in resting fMRI
- ASSET: Analysis of Sequences of Synchronous Events in Massively Parallel Spike Trains
- Finding neural assemblies with frequent item set mining
- Learned Motor Patterns Are Replayed in Human Motor Cortex during Sleep
- Correcting Biased Centered Kernel Alignment Measures in Biological and Artificial Neural Networks
- Trajectory Flow Matching with Applications to Clinical Time Series Modelling
- Longitudinal Flow Matching for Trajectory Modeling
- Association between albumin changes and prognosis in older patients with acute myocardial infarction
- Effectiveness and mechanisms of lymphocytes at different time points in predicting consolidation immunotherapy following adaptive chemoradiotherapy in locally advanced non-small cell lung cancer
- Association Between High-Sensitivity C-Reactive Protein Trajectories and the Incidence of Metabolic Syndrome:A Retrospective Cohort Study
- Yet Another ICU Benchmark: A Flexible Multi-Center Framework for Clinical ML
- The association between the neutrophil-to-lymphocyte ratio and mortality in critical illness: an observational cohort study
- Predicting Progression from Mild Cognitive Impairment to Alzheimer’s Disease using Survival Analysis