After a narrowed neck artery is reopened (by stenting, surgery, or clot-dissolving drugs), some patients bleed into the brain. Their small brain vessels, dilated for months to cope with low flow, have lost the ability to clamp down when full pressure returns. This is cerebral hyperperfusion syndrome. Clinicians cannot tell, in real time and for the patient in front of them, whether the current blood pressure is above the level that this person's vessels can still regulate.
Two things stand in the way. Population cohorts give average thresholds that may not fit any one patient. Single-patient analyses, in turn, cannot separate a real pattern from noise, and the problem gets worse when the bedside monitor is checked again and again. We propose to turn the single patient into a statistically valid unit of inference. We build a monitoring test that ingests one patient's streaming pressure and flow signals and declares "autoregulation has failed above pressure P." The false-alarm rate is guaranteed no matter how often the clinician looks, and the guarantee requires no randomized treatment. Population data are used only to make the test detect failure sooner, never to justify its error guarantee.
Core Claim
Bedside autoregulation monitoring works by computing a rolling correlation between slow swings in arterial pressure and a brain signal. When the vessels regulate, the brain signal stays flat as pressure moves. When they fail, it rises and falls with pressure. The standard index is the pressure reactivity index, the moving correlation between arterial pressure and intracranial pressure. From it one estimates an optimal perfusion pressure and lower and upper limits of autoregulation.
These limits are point estimates fitted over long windows. They carry no error bars that stay valid when the curve is re-examined every few minutes. Our claim has three parts.
First, the question "is autoregulation impaired in this pressure band, so far?" can be posed as a hypothesis about the running conditional mean of a bounded windowed index. Such a hypothesis can be tested with a nonnegative supermartingale. Ville's maximal inequality then gives a type-I error guarantee that holds under continuous monitoring and arbitrary dependence between windows.
Second, unlike the causal N-of-1 setting, this needs no randomization or positivity assumption. The target is the association that defines autoregulatory failure, not a treatment effect.
Third, the betting fractions that drive the test can be chosen by a population model trained on large cohorts. A good population prior then shortens time-to-detection, while a wrong one costs only power, never validity.
The output is a one-sided confidence bound on each patient's upper limit of autoregulation, updated online.
Where This Sits in Prior Work
The motivating evidence comes from a tension in the literature. A study of 809 patients with traumatic brain injury and over 150,000 monitored hours, Cerebral perfusion pressure targets after traumatic brain injury: a reappraisal, found an asymmetric J-shaped risk curve: time spent above the optimal pressure was largely benign. Revascularization reports describe the opposite. Aorto-carotid bypass in patients with Takayasu arteritis describes hemorrhage after bypass. Diffuse Multifocal Intracranial Hemorrhage Following Alteplase Infusion: A Case Image Report describes fatal multifocal bleeding after a systolic surge to 197 mmHg. Control of hypertension in the critically ill: a pathophysiological approach describes how the autoregulation curve shifts and flattens in chronic ischemia.
One reading is that "above optimal pressure" and "above this patient's upper limit" are different quantities. The trauma analysis measures the first, and the upper limit is too poorly estimated to study directly. A per-patient upper bound with valid uncertainty is what would let anyone test that reading.
Two papers supply the method. Anytime-valid inference in N-of-1 trials builds martingale confidence sequences via Ville's inequality and shows that a naive t-test checked after each block reaches a 60% false-positive rate at nominal 5%. Its estimators rely on inverse-probability weighting of randomized treatment blocks. Alternating blocks of allowing and blocking reperfusion is impossible here, so we replace the causal estimand with a conditional-mean hypothesis that needs no randomization. Optimization of a Mathematical Model of Cerebral Autoregulation Using Patient Data fit a 15-parameter circuit model to one healthy subject and found only 8 parameters estimable, with no standard errors. That is a constraining result: full mechanistic fitting per patient is fragile. We use that model only as a simulator for ground-truth curves, not as the estimator.
Personalization of Large Foundation Models for Health Interventions proposes that population models trigger individual trials when uncertain. It is conceptual, with no physiological data. We make its population-to-individual handoff precise: the population model sets the bets, and validity comes from the individual's own data.
Research Program
The basic unit is a non-overlapping window $k$ of a few minutes. In each window we compute a bounded autoregulation index $x_k \in [-1, 1]$ and record the window's mean pressure. Where an intracranial pressure bolt exists, the index is the pressure reactivity index. In non-invasive revascularization monitoring, it is the correlation between finger-cuff arterial pressure and transcranial Doppler flow velocity.
Windows are assigned to pressure bands $b$. For each band, the null hypothesis is that the conditional mean of $x_k$ given all past windows is at most a prespecified failure threshold $c$. The test maintains a wealth process
$$W_{b,n} = \prod_{k \le n,\, k \in b} \left(1 + \lambda_k (x_k - c)\right),$$
where $\lambda_k \in [0, 1/(1+c)]$ is a betting fraction chosen using only past data. This range keeps every factor nonnegative. Under the null, $W_{b,n}$ is a nonnegative supermartingale, so Ville's inequality bounds the probability that it ever exceeds $B/\alpha$ by $\alpha/B$. Here $B$ is the number of bands and $\alpha$ the target error. When any band crosses this level, it is declared impaired.
The reported quantity is the lowest impaired band above optimal pressure. It acts as an anytime-valid upper bound on the patient's upper limit of autoregulation: the true limit lies below it except with probability $\alpha$. A symmetric construction bounds the lower limit.
Three design choices are studied explicitly. The first is how $\lambda_k$ is set. The default is a population-informed rule: a sequence model trained on cohort data predicts the expected index in each band for patients like this one, and the bet grows with the predicted exceedance. The fallback is a standard adaptive rule using only the patient's own history. The second is window length. Shorter windows react to the abrupt spikes that long averaging hides, but they give noisier indices. The third is handling of drug-driven pressure changes. Vasopressor and antihypertensive doses are logged, and windows can be stratified by them. This is a known confound: the index is associational and cannot by itself separate drug-induced from spontaneous pressure swings.
Baselines
The naive reference point is a fixed population blood-pressure ceiling, such as a systolic target, applied identically to every patient. It is run on the same streams by flagging any window above the ceiling. It sets the floor that any personalized method must beat on false alarms and on missed failures.
The strongest existing method for individual limits is the moving-window curve-fitting approach used in Cerebral perfusion pressure targets after traumatic brain injury: a reappraisal and The lower limit margin: a determinant of autoregulatory sensitivity to changes in cerebral perfusion pressure. It plots the reactivity index against pressure over a multi-hour window and reads off the optimal pressure and the limits. We give it the same signals, the same window index, and the same tuning budget for window length. We add a block-bootstrap interval so it also produces uncertainty, and recompute it at every monitoring step, as a clinician would.
The reported numbers for this family are outcome associations. In the 809-patient cohort, the odds ratio for worse 6-month outcome is 1.04–1.09 per hourly dose below optimal pressure and 1.11–1.26 below the lower limit. In the 234-patient cohort, a wider lower margin gives an odds ratio of 0.59 (95% CI 0.41–0.83). No reported result was found on Lacuna for upper-limit estimation accuracy, or for the outcome association of time above the upper limit.
Beating this baseline means two things. Under continuous monitoring, it must keep the false-alarm rate at or below $\alpha$ where the bootstrap curve-fit does not. On retrospective cohorts, time spent above our certified upper bound must predict outcome more strongly than time above optimal pressure, at matched alarm burden.
The ablation that isolates the key ingredient is the same test with uniform, non-informed bets. It shows how much detection speed the population model buys. A second ablation uses a population-only Bayesian hierarchical model without the martingale wrapper. It shows what is lost in validity when the population prior is wrong.
Why not just…?
Why not just enforce a fixed blood-pressure ceiling? Individual limits vary widely. Lowering pressure aggressively can push a patient below their lower limit, and in the lower-margin study 58.9% of the margin's effect on outcome ran through time spent below that limit. The case report with the 197 mmHg surge also shows that static targets do not prevent spikes. Our experiments quantify this directly by comparing missed failures and unnecessary flags against the ceiling rule.
Why not just bootstrap the standard curve fit? This is a real threat, because in practice the bootstrap may be only mildly miscalibrated. Its intervals are valid for a single look at a fixed sample, while bedside use means hundreds of looks. The N-of-1 simulation shows how badly repeated looks can inflate error (60% versus 5%). Our simulation experiment measures the bootstrap's realized error under continuous monitoring. If it stays near nominal, the case for the martingale test reduces to its earlier detection of short spikes, and we will report that.
Why not just train a population model such as XGBoost or a sequence transformer? Population models are the right source of priors, and we use one to set the bets. As a sole decision-maker they carry no individual guarantee, and they struggle with rare events. MIMIC-Extract: A Data Extraction, Preprocessing, and Representation Pipeline for MIMIC-III reports precision-recall areas often below 0.50 for rare events despite mortality discrimination of 0.85–0.90. The ENDRAS model in Development and Validation of a Web-Based Machine Learning Model for Predicting Early Neurological Deterioration Following Stroke Thrombolysis: Multicenter Study reports an AUC of 0.988, but it uses static admission features and was prospectively validated on 20 patients. It answers "who will deteriorate," not "is this pressure now too high." The hierarchical-model ablation tests what happens when a trauma-trained prior is applied to revascularization physiology.
Why not just fit a mechanistic autoregulation model per patient? In the original single-subject fit, 7 of 15 parameters were unidentifiable, and no standard errors were produced. That makes per-patient mechanistic fitting unreliable as a bedside alarm. We keep the model as a simulator only.
Proposed Experiments
The first experiment is a simulation with known truth. We draw individual autoregulation curves from the 8 identifiable parameters of the circuit model, shifted and flattened to mimic chronic ischemia. We impose realistic pressure variability, including the pattern where nearly half of hourly variability exceeds ±5 mmHg, as reported in the lower-margin cohort. We add vasopressor-like step changes. The metrics are:
- the realized false-alarm rate under checking every window, when no band is truly impaired;
- coverage of the true upper limit by the reported bound;
- time from the true crossing of the limit to an alarm;
- bound width.
The decisive check is whether our test holds error at or below $\alpha$ while the bootstrap curve-fit does not, without a large loss in detection time.
The second experiment is a retrospective replay on the Addenbrooke's trauma cohorts, which would require data access through collaboration. We use the 809-patient high-resolution cohort and the 425-patient cohort with brain oxygen. The latter allows a second index from the oxygen reactivity index, whose sustained values above +0.50 for more than 90 minutes marked high risk in Revisiting the oxygen reactivity index in traumatic brain injury: the complementary value of combined focal and global autoregulation monitoring. We compute hourly dose above our certified upper bound and regress 6-month outcome on it, alongside dose above optimal pressure.
This is the experiment that tests the J-curve tension. If dose above the certified bound predicts poor outcome while dose above optimal pressure does not, the "benign high pressure" finding reflects a poorly estimated upper limit, not safe physiology. If neither predicts outcome, the trauma finding stands, and hyperperfusion risk is specific to chronically dilated vessels.
The third experiment is a feasibility study in carotid stenting patients selected by the same high-risk criteria as the 44-patient staged-stenting series, Staged carotid artery angioplasty and stenting for patients with high-grade carotid stenosis with high risk of developing hyperperfusion injury: a retrospective analysis of 44 cases. Monitoring is entirely non-invasive, with finger-cuff pressure and transcranial Doppler for 24 to 48 hours after the procedure. Outcomes are clinical hyperperfusion syndrome and edema or hemorrhage on follow-up imaging.
This cohort will be small, so the statistical endpoint is not discrimination. It is whether alarms precede clinical events, and whether each patient's evidence, expressed as an e-value, can be combined across patients by multiplication into a valid cohort-level test. That turns a run of individual case reports into cumulative evidence rather than anecdotes. The procedure is preregistered, with the threshold $c$, band width, and window length fixed from the first two experiments.
References
- Cerebral perfusion pressure targets after traumatic brain injury: a reappraisal
- Aorto-carotid bypass in patients with Takayasu arteritis
- Diffuse Multifocal Intracranial Hemorrhage Following Alteplase Infusion: A Case Image Report
- Control of hypertension in the critically ill: a pathophysiological approach
- Anytime-valid inference in N-of-1 trials
- Optimization of a Mathematical Model of Cerebral Autoregulation Using Patient Data
- Personalization of Large Foundation Models for Health Interventions
- The lower limit margin: a determinant of autoregulatory sensitivity to changes in cerebral perfusion pressure
- MIMIC-Extract: a data extraction, preprocessing, and representation pipeline for MIMIC-III
- Development and Validation of a Web-Based Machine Learning Model for Predicting Early Neurological Deterioration Following Stroke Thrombolysis: Multicenter Study
- Revisiting the oxygen reactivity index in traumatic brain injury: the complementary value of combined focal and global autoregulation monitoring
- Staged carotid artery angioplasty and stenting for patients with high-grade carotid stenosis with high risk of developing hyperperfusion injury: a retrospective analysis of 44 cases