A wearable blood-pressure ring or a smartphone pulse sensor is useful clinically only if it can stand in for the reference instrument: its readings must agree with the cuff or the lab closely enough that a clinician would act the same way on either. The standard test for this is Bland-Altman analysis. It plots the difference between the two methods against their average and reports the mean difference (the bias) and a band that should contain 95% of future differences (the limits of agreement). In practice this test is run once, on pooled data, after the model is built. Feature selection and model fitting are driven by squared error or correlation instead. We propose to run the agreement test inside feature selection. It would be applied separately in each operating context, such as rest versus exertion, incline versus level, day versus night, and at each elapsed time since the device was last calibrated.
The quantity we select for is the agreement horizon: how long after calibration, in a given context, a feature set keeps the estimator's limits of agreement inside a prespecified clinical margin. Two feature sets with the same pooled error can differ sharply here. One may drift out of tolerance within days during exertion. The other may stay interchangeable for weeks. That difference determines how often a patient must recalibrate and when a reading can be trusted. The aim is a selection rule and an evaluation protocol that turn a single pooled agreement statistic into a map of when and where a wearable can replace the reference.
Core Claim
The claim is empirical first and methodological second. Empirically, estimators whose features were chosen to minimize pooled error will often pass a pooled Bland-Altman check while failing it in particular contexts or after a certain calibration age. We expect the failures where earlier work saw them. Tomlinson et al. found that disagreement between manual and continuous vital signs is not uniform: it widens as patients move into pathological ranges. Slade et al. found that muscle-activity signals carry the metabolic signal on level ground, while foot-force signals take over on inclines and under load. Methodologically, we claim that choosing features per context to maximize the worst-context agreement horizon yields estimators that stay interchangeable in more contexts, for longer between calibrations, than three alternatives given the same calibration budget: pooled-error selection, worst-group-error selection, and a single model that takes context as an input.
Formally, let $d_{i,t}$ be the difference between the wearable estimate and the reference for subject $i$ at time $t$. Let $c$ index context, $\tau$ the time since the last calibration, and $m$ the measurement magnitude (the Bland-Altman average). For feature set $S$ we fit a variance-components model of the differences within each context. From it we compute the worst-case absolute limit of agreement over the clinically relevant range $M$ of magnitudes:
$$L_c(\tau; S) = \max_{m \in M} \left| \beta_{0,c}(\tau) + \beta_{1,c}(\tau)\, m \right| + 1.96\sqrt{\sigma^2_{b,c}(\tau) + \sigma^2_{w,c}(\tau)}.$$
Here $\beta_{0,c} + \beta_{1,c} m$ is the bias, allowed to grow with magnitude (proportional bias). The terms $\sigma^2_{b,c}$ and $\sigma^2_{w,c}$ are the between-subject and within-subject variances of the differences. They are separated because repeated readings from one person are correlated, and naive limits computed as if all pairs were independent come out too narrow. The agreement horizon for margin $\delta$ is
$$\tau^*_c(S) = \sup\{\tau : L_c(\tau'; S) \le \delta \text{ for all } \tau' \le \tau\},$$
and selection maximizes $\min_c \tau^*_c(S_c)$ over context-specific feature sets $S_c$, with a penalty on the number of distinct sets.
Research Program
The work has three parts. The first is an estimator of $L_c(\tau; S)$ that remains honest on small longitudinal cohorts. It uses the variance components above, subject-level bootstrap intervals, and smoothing of $\tau$-dependence with a monotone spline, because drift from biofouling and skin-contact change is expected to worsen rather than oscillate. The horizon is computed from the upper confidence bound of $L_c$, not the point estimate. This way a small cohort yields a short, conservative horizon instead of an optimistic one.
The second part is the selection procedure. Candidate features come from the literature where it exists. For blood pressure these are the general waveform features of the one-month cuffless study, which avoid fragile landmarks such as the dicrotic notch. For EMG we use the fourteen features that Grimmer et al. found stable across load and exoskeleton tasks, and for gait we use EMG together with insole force. Search is greedy forward selection over features within each context, followed by merging of contexts whose selected sets agree. The whole procedure is nested inside leave-one-subject-out cross-validation. Selecting on a statistic and then reporting that same statistic would otherwise overstate the result.
The third part is a pre-registered falsification test of the premise. If pooled-error-selected models essentially never fail context-conditional agreement while passing pooled agreement, then the problem we target is rare. In that case we report the protocol as an evaluation tool only.
Baselines
The naive reference point is the published feature set and calibration scheme, evaluated with pooled, independence-assuming Bland-Altman limits. That is how agreement is reported today, for example in the smartphone heart-rate-variability study. On the one-month cuffless blood-pressure data, the strongest existing method is the individual Gaussian process regression model with sparse recalibration every 20 samples. That study reports MAE 5.1 mmHg systolic and 4.6 mmHg diastolic, with error standard deviations of 6.2 and 5.4 mmHg (Discussion of Cuffless BP). We rerun it on identical splits and use the same regression model for every selection rule, so that only the features differ.
On the inclined and loaded walking data, the reference is the Slade et al. data-driven estimator. It reports mean absolute percent error of 6.1% for novel conditions, 9.7% for novel subjects and 11.7% for both novel (Slade et al.). On GlucoBench's Weinstock data the reference is the Transformer at RMSE 13.22 (GlucoBench). For the Ring-CPT cold-pressor data, PITN reports 7.0 mmHg systolic RMSE and 77% correlation. No reported result was found on Lacuna for Bland-Altman limits on any of these datasets, so we compute agreement for every baseline ourselves.
Three further baselines isolate the key ingredient. The first is worst-group squared-error selection, which picks features that minimize the largest per-context mean squared error. The second is context-as-input, a single model with context indicators and calibration age added as covariates and all features available. The third is pooled Bland-Altman selection, which applies our agreement statistic without conditioning on context or calibration age.
All methods share the same candidate features, the same regression model family, an equal hyperparameter search budget, and the same number of reference calibrations per subject. Beating the baselines means two things, both measured on held-out subjects with subject-bootstrap intervals that exclude zero. First, a longer worst-context agreement horizon at a fixed margin, or equivalently fewer calibrations needed to keep every context inside the margin. Second, a higher fraction of contexts passing the margin.
Why not just…?
Why not just minimize mean squared error, since it already contains bias and spread? The mean squared difference equals squared bias plus the variance of the differences. Pooled squared-error minimization therefore already shrinks pooled limits of agreement. This is a real threat to any "Bland-Altman loss" pitched on its own. It is why we do not make that pitch. What squared error misses is the structure: disagreement concentrated in one context, disagreement growing with magnitude (as Tomlinson et al. found), disagreement growing with calibration age, and the correlation between repeated readings from one person. The pooled-selection baseline tests whether that structure changes which features are chosen.
Why not just use worst-group squared error across contexts? This is the strongest competitor, and it may well recover most of the benefit. It differs from our criterion in three ways: it ignores magnitude-dependent bias, it ignores calibration-age drift, and it does not measure against a clinical margin. If the two select the same features and reach the same horizons, the contribution shrinks to the agreement-horizon evaluation protocol. We will report that outcome plainly.
Why not just feed context into one flexible model? A single model given context flags can in principle learn to reweight features on its own. GlucoBench shows the cost on small cohorts, where shallow models matched or beat deep ones (GlucoBench). With 11 blood-pressure subjects, a context-conditional model has little data per context. Explicit per-context feature sets may be more sample-efficient, but this is an empirical question that the context-as-input baseline settles directly.
Why not just recalibrate more often? Frequent recalibration clearly helps; the sparse scheme was what made individual blood-pressure models work in the one-month study. Recalibration, however, is the burden a patient bears. The agreement horizon measures that burden, and the comparison asks whether better features buy the same agreement with fewer calibrations.
Proposed Experiments
The first experiment tests the premise. It uses the one-month cuffless blood-pressure data, the inclined and loaded walking data, GlucoBench (with day and night, and meal windows, as contexts), and Ring-CPT (rest versus cold pressor), provided each can be obtained. On each, we count how often the pooled-error-selected model passes pooled agreement but fails agreement in at least one context or calibration age.
The blood-pressure data offers only calibration age and session as context, because activity was not recorded. The walking data offers incline and load but no longitudinal span. We therefore treat each dataset as testing one axis, time or context, rather than pretending any single dataset tests both.
The second experiment compares agreement-horizon selection with every baseline, reporting worst-context horizon, calibrations required, and fraction of passing contexts. We sweep the margin $\delta$ over a prespecified range rather than fixing one value, so the conclusion does not hinge on a single threshold.
The third experiment measures the gap between point-estimate and confidence-bound horizons as cohort size shrinks. This shows whether conclusions from 11-subject longitudinal studies can be trusted at all. The decisive result is a longer worst-context horizon for our selector than for worst-group squared error at matched calibration budget, with held-out-subject intervals excluding zero. If that result is absent, we report agreement horizons as an evaluation method rather than a selection method.
References
- Smoothing Effect in Vital Sign Recordings: Fact or Fiction? A Retrospective Cohort Analysis of Manual and Continuous Vital Sign Measurements to Assess Data Smoothing in Postoperative Care
- Rapid energy expenditure estimation for ankle assisted and inclined loaded walking
- Discussion of Cuffless Blood Pressure Prediction Using Plethysmograph Based on a Longitudinal Experiment: Is the Individual Model Necessary?
- Electromyography (EMG)-Based Feature Selection for Detecting Movement Effort in Human-in-the-Loop Optimization of Lower Limb Exoskeletons
- Extraction of Heart Rate Variability from Smartphone Photoplethysmograms
- GlucoBench: Curated List of Continuous Glucose Monitoring Datasets with Prediction Benchmarks
- PITN: Physics-Informed Temporal Networks for Cuffless Blood Pressure Estimation