May 06, 2026
Cerebral Autoregulation-Guided BP Targets in Neurocritical Care
- Felipe Figueiredo1,
- Andre M.S. Guio2,
- Abhijit V. Lele3
- 1Universidade Federal de Minas Gerais;
- 2Faculdade Multivix Cachoeiro;
- 3Harborview Medical Center, University of Washington
- Felipe Figueiredo
Protocol Citation: Felipe Figueiredo, Andre M.S. Guio, Abhijit V. Lele 2026. Cerebral Autoregulation-Guided BP Targets in Neurocritical Care. protocols.io https://dx.doi.org/10.17504/protocols.io.36wgqxwjxlk5/v1
License: This is an open access protocol distributed under the terms of the Creative Commons Attribution License, which permits unrestricted use, distribution, and reproduction in any medium, provided the original author and source are credited
Protocol status: Working
We use this protocol and it's working
Created: May 05, 2026
Last Modified: May 06, 2026
Protocol Integer ID: 316366
Keywords: guided bp targets in neurocritical care, cerebral autoregulation, neurocritical care, acute brain injury, guided arterial pressure management, delayed cerebral ischemia, guided bp target, cerebral ischemia, arterial pressure management, separate evidence streams of prognostic, brain oxygenation, comparative studies for the primary intervention, therapeutic intensity, severe tbi, outcomes in adult patient, systematic review
Abstract
This protocol (prepared in accordance with PRISMA-P) outlines a systematic review and meta-analysis to evaluate whether continuous autoregulation-guided arterial pressure management (using indices such as PRx, ORx, etc., to set individualized CPP/MAP targets) improves outcomes in adult patients with acute brain injury (mainly severe TBI, with subgroup analyses for aSAH and ICH) compared to fixed guideline-based pressure targets. Secondary aims include characterizing associations between deviations from personalized targets and outcomes. We will include RCTs (e.g. COGiTATE 2021pilot RCT) and high-quality nonrandomized comparative studies for the primary intervention-effect question, while mapping separate evidence streams of prognostic/association studies (e.g. percent time below CPPopt vs outcome). The primary outcomes are functional outcome (~6-month GOSE or mRS) and mortality (30/90/180 days). Secondary outcomes include delayed cerebral ischemia, ICP crises, brain oxygenation/metabolism metrics, therapeutic intensity, complications, and feasibility metrics (time in/out of target range). We will search multiple databases (MEDLINE, Embase, CENTRAL, etc.) with no date/language restrictions, including trial registries and gray literature. Two reviewers will screen studies, extract data, and assess risk of bias (RoB2 for RCTs, ROBINS-I for nonrandomized comparatives, QUIPS for association studies). We plan random-effects meta-analysis of effect measures (risk ratios or odds ratios for binary outcomes, mean differences for continuous outcomes), with ordinal analysis for GOSE/mRS if feasible (otherwise dichotomized GOSE≥5 vs <5, mRS≤3 vs >3). Heterogeneity will be assessed via I² and explored by subgroups (pathology, monitoring modality, index type, target derivation, study design, risk of bias). Sensitivity analyses will include RCT-only, low-risk studies only, etc. Certainty of evidence will be appraised using GRADE (Summary of Findings tables for primary outcomes). Since direct evidence is scant, we anticipate a mixed-design review: a small RCT evidence base (COGiTATE 2021 [Tas et al. J Neurotrauma 2021] found feasibility but no outcome difference), possibly some comparative cohorts if available, plus separate narrative synthesis of observational correlations (e.g. studies linking % time below CPPopt to poor outcomes).
Guidelines
- Assessment of heterogeneity: Clinical heterogeneity will be assessed by comparing populations, interventions, and outcomes. Methodological heterogeneity will also be examined. Statistical heterogeneity will be quantified with I² and τ². Subgroup and meta-regression analyses will be conducted if data allow.
- Subgroup analyses: Preplanned candidate subgroups include pathology, monitoring modality, autoregulation index, target type, update frequency, age or severity strata, study quality/design, and exposure type.
- Sensitivity analyses: Robustness of findings will be examined by excluding studies at high RoB, including only randomized trials, and other criteria.
- Meta-bias assessment: Funnel plot asymmetry and Egger’s test will be used if ≥10 studies are pooled.
- Certainty of evidence (GRADE): GRADE will be used to rate confidence in effect estimates for main outcomes.
Pooling decisions
We will meta-analyze outcomes only when at least two studies of similar design and measure exist. Ordinal outcomes (GOSE/mRS) will be meta-analyzed using a proportional odds model if data (category counts) are available; if not, dichotomies as above will be pooled. Continuous outcomes (e.g. PbtO2) will be combined by mean differences (or standardized differences if scales differ). In cases of skewed data, medians/IQR may be reported descriptively.
Risk-of-bias assessment
Two reviewers will independently assess risk of bias for each study. RCTs will use the Cochrane RoB 2 tool (domain judgements for bias arising from the randomization process, deviations from intended interventions, missing data, measurement of outcome, and selective reporting). For cluster RCTs (if any), we will include the cluster-randomization domain in RoB 2. Nonrandomized comparative studies will be assessed with ROBINS-I, evaluating confounding (e.g. age, injury severity, center), selection of participants, classification of interventions, deviations from intended interventions, missing data, outcome measurement, and selective reporting. We will give special attention to confounders such as baseline ICP/CPP, injury severity scores, and therapy intensity; by default, studies without adjustment for key confounders will be rated as higher risk. For association-only (prognostic/observational) studies, we will use the QUIPS (Quality in Prognostic Studies) criteria or PROBAST-like principles, focusing on study participation, attrition, prognostic factor measurement (exposure), outcome measurement, confounding (adjustment for severity, etc.), and analysis/reporting. (For example, a study correlating %time below CPPopt with outcome would be at higher bias if it did not account for baseline injury severity.) We will resolve disagreements by discussion. Summary RoB judgments (low/some concerns/high) will be tabulated.
Effect measures
For dichotomous outcomes (mortality, dichotomized GOSE/mRS), we will use relative risk (RR) with 95% confidence intervals as the primary measure, consistent with Cochrane. If odds ratios (OR) are reported, we may convert to RR if needed. We will also present ORs where appropriate (e.g. in GRADE tables). For continuous outcomes, we will use mean difference (MD) with 95% CI; if different scales are used for the same outcome, we will use standardized mean difference (SMD). Ordinal outcomes (full GOSE/mRS) will be analyzed via a common odds ratio (proportional odds assumption).
Handling of missing or adjusted data
We will preferentially extract adjusted effect estimates (e.g. adjusted OR) from observational studies, but ensure separate pooling of adjusted vs unadjusted if mixed (we may perform separate meta-analyses or use the more adjusted estimate if only one type is available). For studies not reporting sufficient statistics, we will contact authors. If only graphical data are available, we will use digital extraction.
Synthesis strategy
We anticipate few RCTs (e.g. only COGiTATE to date), so we will first narratively summarize study characteristics and outcomes. If ≥2 RCTs or similar observational studies are found, we will meta-analyze them. We will stratify pooling by study design: RCTs alone, and nonrandomized comparatives separately (since combining can bias estimates). We will use the Hartung–Knapp–Sidik–Jonkman random-effects method to account for heterogeneity (or DerSimonian–Laird if few studies, but random-effects is preferred to accommodate between-study variance).
We will compute the I² statistic and χ² test for heterogeneity. If I²≥50%, we will interpret with caution; sources of heterogeneity will be explored (see below). We will compute 95% prediction intervals if ≥3 studies per outcome, to reflect uncertainty for a future study. Publication bias and small-study effects will be assessed by funnel plots and Egger’s test if ≥10 studies are pooled. If meta-analysis is infeasible (e.g. only one study or incomparable outcomes), we will provide structured narrative synthesis and/or tabulate results.
We will not forcibly pool across different pathologies or indices unless clinically justified. For example, if RCTs exist only in TBI, we will not pool them with SAH observational data. Any meta-analysis will ensure that all comparisons are “autoregulation-guided vs non-guided” with similar cointerventions. If a trial has multiple intervention arms (e.g. different target algorithms), we will combine relevant arms or split the control group appropriately (per Cochrane Handbook rules) to avoid double-counting. Overlapping cohorts (e.g. one center publishing multiple papers on the same patient sample) will be handled by using the most complete data.
Assessment of heterogeneity
We will assess clinical heterogeneity by comparing populations (injury type, severity), interventions (target algorithm, frequency of target recalculation, modality), and outcomes definitions. Methodological heterogeneity (study design, risk of bias) will also be examined. Statistical heterogeneity will be quantified with I² and τ². If I² 3e50%, we will investigate via subgroup and meta-regression if data allow. Potential effect modifiers include: injury pathology (TBI vs aSAH vs ICH), autoregulation index used (PRx vs ORx vs OSRx vs TCD vs LAx), modality (invasive vs noninvasive), target definition (CPPopt vs MAPopt vs LLA/ULA), timing of intervention (early [ 3c72h] vs late monitoring), baseline severity (GCS/IMPACT score strata), study design (RCT vs observational), and RoB category (low vs high). We will conduct subgroup analyses and, if ≥10 studies, meta-regression on key variables. We will interpret subgroup differences cautiously, noting they are exploratory.
Subgroup analyses
Candidate subgroups (preplanned):
Pathology: TBI vs aSAH vs ICH (each compared separately vs their own controls). We will not pool across pathology if heterogeneity is excessive.
Monitoring modality: invasive ICP-based (PRx/ORx) vs noninvasive (TCD/LAx/NIRS).
Autoregulation index: PRx/PAx vs oxygen-based (ORx, OSRx) vs TCD-based vs LAx.
Target type: CPPopt vs MAPopt vs LLA/ULA-based targets.
Update frequency: continuous (algorithmically continuous) vs intermittent (e.g. 4–6 hourly recalculation as in COGiTATE).
Age or severity strata: e.g. adults 3c65 vs ≥65, or Glasgow Coma Scale splits if reported.
Study quality/design: RCTs vs observational, or low vs high RoB studies.
Exposure type: intervention studies vs association studies (for narrative contrast).
Subgroup analyses will be conducted only if there is a reasonable number of studies in each subgroup. We will report p-values for interaction.
Sensitivity analyses
We will examine robustness of findings by: excluding studies at high RoB; including only randomized trials; excluding small studies (e.g. N 3c30); excluding noninvasive-only studies; excluding studies that did not clearly define their target derivation method; using alternative categorizations of outcomes (e.g. GOSE≥4 vs 3c4); and using fixed-effects models. If we use imputed or converted statistics, we will assess impact by sensitivity analysis.
Meta-bias (reporting bias) assessment
If ≥10 studies are pooled for an outcome, we will assess funnel plot asymmetry and perform Egger’s test. We will search for unpublished trials (through registries) to detect outcome reporting bias. If selective reporting is suspected (e.g. study protocol or registry lists outcomes not published), we will note it qualitatively.
Certainty of evidence (GRADE)
We will use GRADE to rate confidence in effect estimates for main outcomes. For each outcome in a Summary-of-Findings table, certainty will start at ‘High’ for RCT evidence and ‘Low’ for observational evidence, and be downgraded or (rarely) upgraded per GRADE criteria (risk of bias, inconsistency, indirectness, imprecision, publication bias). If meta-analysis combines both RCTs and observational data, we will present overall certainty judiciously (likely low or very low if any observational data contribute significantly). We will explicitly state any assumption (e.g. “We assumed similar relative effect across TBI and other brain injuries for pooling”).
Registration
We will register this protocol on PROSPERO (or other appropriate registry) before data extraction. Any protocol amendments will be documented with dates and rationale.
Ethics and dissemination
No ethical approval is needed (no primary human data). We plan to submit findings to a peer-reviewed journal and present at neurosurgery/critical care conferences. Data (e.g. extraction sheets) will be available on request.