We will conduct a living systematic review and meta-analysis according to the Cochrane methods [12] and PRISMA-P (Preferred Reporting Items for Systematic Reviews and Meta-Analyses Protocols) guidelines [13]. The protocol is registered in PROSPERO [14] under registration CRD420251077829. Scheduled surveillance updates will occur at least monthly, with rapid updates during peak publication periods.

The population consists of pregnant persons, postpartum persons, and infants born at any gestational age, including preterm infants and those admitted to neonatal intensive care. Infant age will be defined chronologically from live birth to 12 months. Gestational age at birth will be extracted and classified as term (≥37 weeks) or preterm (<37 weeks), with subcategories used where reported. Results based on corrected age will be identified and considered separately.

We will include studies reporting efficacy or effectiveness outcomes with sample sizes of at least 50 participants and immunogenicity outcomes with at least 10 participants. The intervention to be evaluated is the RSVPreF vaccine (ABRYSVO) administered during pregnancy within nationally licensed gestational windows as a single 0.5-mL intramuscular dose after reconstitution. The primary effectiveness comparison will be maternal RSVPreF vaccination vs no maternal RSVPreF vaccination. For infant outcomes, comparison groups will comprise infants born to pregnant individuals who did not receive the RSVPreF vaccine; for maternal outcomes, comparison groups will comprise unvaccinated pregnant or postpartum individuals. Placebo-controlled trials, if eligible, will be synthesized separately from observational studies. Alternative preventive products, including infant nirsevimab, will not be pooled with inactive comparators; direct active comparator evidence will be analyzed as a separate comparative effectiveness question. Infant RSV monoclonal prophylaxis will be extracted as a potential cointervention where appropriate. In test-negative studies, cases and controls will be defined by RSV test status, whereas maternal vaccination status will define the exposure comparison.

Study designs will include randomized controlled trials (RCTs; phase 2 and 3) and real-world postlicensure observational studies (eg, cohort, case-control, test-negative, or quasi-experimental studies). Systematic reviews will be used only as a source to identify primary studies. Case series will be described narratively and excluded from quantitative synthesis. Animal studies will be excluded.

We will search MEDLINE (PubMed), Embase (Ovid), Cochrane Library, LILACS, Science Citation Index Expanded, China National Knowledge Infrastructure, the Chinese Biomedical Literature Database, the Chinese Science Citation Database, ClinicalTrials.gov, the European Union Clinical Trials Register, the WHO International Clinical Trials Registry Platform, and gray literature from public health agencies (the Centers for Disease Control and Prevention, UK Health Security Agency, UK Joint Committee on Vaccination and Immunisation, and WHO; Multimedia Appendix 1). Coverage will encompass January 2023 onward (postlicensure era) up to April 2028, with no language restrictions. A peer-reviewed strategy will combine controlled vocabulary and text words for RSV, RSVPreF and ABRYSVO, pregnancy, and immunogenicity; test-negative and other RWE designs will be explicitly captured. Hand searching of references and expert consultation will complement electronic searches. Pairs of reviewers will independently screen titles and abstracts and full texts using the Nested Knowledge platform [15], extract data via piloted and validated REDCap forms (Vanderbilt University) [16], and resolve disagreements through consensus or third-party adjudication. All screening will be performed by human reviewers; no machine learning or automated classification tool will be used for study selection. Extracted data will include study setting, design, population, vaccination details (gestational age, interval to delivery, and coadministration), outcomes and definitions, effect measures (adjusted and unadjusted), follow-up windows, and funding and conflicts. Standardized procedures, including peer verification and automated consistency checks, will ensure data quality and traceability. The living systematic review will maintain a public changelog documenting updates, versioning, and any resolved discrepancies.

Efficacy and effectiveness outcomes include RSV laboratory-confirmed infection, RSV acute respiratory illness, RSV LRTD, RSV hospitalization, RSV complications (including secondary bacterial infection, respiratory failure, multi-organ failure, and death), all-cause LRTD, all-cause LRTD hospitalization, and antibiotic use in infants with RSV infection (Table 1 and Multimedia Appendix 2). We will prioritize laboratory confirmation of RSV via nucleic acid amplification testing (eg, real-time polymerase chain reaction) or validated antigen assays for case ascertainment in both infants and mothers. Immunogenicity outcomes will include quality and quantity of humoral and cellular immune responses and RSV viral load (Table 2).

We will assess risk of bias using version 2 of the Cochrane risk-of-bias tool for randomized trials (RoB 2) [17] and the Risk of Bias in Nonrandomized Studies of Interventions (ROBINS-I) for nonrandomized comparative studies [18]. National Institutes of Health quality assessment tools will be used for noncomparative studies [19]. Two reviewers will perform independent assessments with consensus resolution.

We will conduct design-specific meta-analyses (eg, separate pools for RCTs vs observational studies) using random-effects models for efficacy and effectiveness outcomes and for selected immunogenicity outcomes. Continuous immunogenicity outcomes will not be quantitatively pooled due to the anticipated heterogeneity in laboratory assays, measurement scales, and reporting formats across studies. Rather, these outcomes will be summarized descriptively using the values reported in the original studies. Random-effects models were selected a priori independent of the magnitude of statistical heterogeneity due to the anticipated clinical and methodological diversity across included studies, including differences in study design, settings, RSV seasonality, gestational timing of vaccination, and interval between vaccination and delivery.

For analyses including a comparator group, random-effects models will be performed using inverse variance weighting to calculate pooled effect estimates with corresponding 95% CIs. Between-study variance (τ²) will be estimated using the restricted maximum likelihood method. CIs for pooled estimates will be calculated using the Hartung-Knapp-Sidik-Jonkman adjustment based on the t distribution with k − 1 df when applicable.

For noncomparative studies reporting proportions, proportional meta-analyses will be conducted using random-effects models. Proportions will be transformed using the Freeman-Tukey double arcsine transformation to stabilize variances and account for the binomial distribution and between-study heterogeneity.

For efficacy and effectiveness outcomes, dichotomous effect measures, including risk ratios (RRs), hazard ratios, odds ratios (ORs), incidence rate ratios, risk differences (RDs), and VE, will be extracted according to the study design and outcome definition. For observational studies, the most fully adjusted effect estimates will be preferentially extracted whenever available. For RCTs, when VE, RRs, or ORs are not reported, RR estimates will be calculated from available data (number of events and total sample size). VE will be used as the preferred summary measure whenever feasible and will be derived from reported effect estimates using standard formulas when not directly reported.

For binary immunogenicity outcomes, comparative studies will be summarized using RRs, ORs, or RDs as appropriate. For noncomparative studies where only proportions are available, results will be synthesized using proportional meta-analysis as described above.

For continuous immunogenicity outcomes, mean differences or standardized mean differences with corresponding 95% CIs (or SEs) will be extracted for comparative studies. For single-arm studies, means or geometric means with their corresponding 95% CIs (or SEs) will be extracted.

Prespecified subgroup analyses will be performed using predefined categories of the following variables: time since vaccination, time from vaccination to delivery, infant age, country income level, geographic region, study design, gestational age at time of vaccination, gestational age at birth, RSV seasonal pattern, infant risk status, maternal risk status, RSV subtype, coadministration with other routinely recommended vaccines in pregnancy, and other maternal risk factors and characteristics.

Heterogeneity will be assessed through visual inspection of forest plots and consideration of the magnitude and direction of effects, CI overlap, and clinical and methodological diversity, as well as using the Cochran Q, I², and τ². I² will not be interpreted using solely fixed thresholds (Table 3).

Sensitivity analyses will be conducted by excluding studies classified as having a high risk of bias to assess the robustness of the findings.

Potential small-study effects will be assessed using funnel plots and appropriate statistical tests for funnel plot asymmetry (eg, Egger, Harbord, or Peters tests as appropriate) when at least 10 studies are available. Funnel plot asymmetry will be interpreted cautiously as it may reflect publication bias as well as clinical or methodological heterogeneity, selective outcome reporting, or chance [20].

Potential sources of missing data will be assessed, including unreported outcomes, missing summary statistics, and unavailable study-level characteristics. When missing values can be derived from other reported information (eg, CIs, P values, or graphical data), they will be calculated using appropriate methods. When missing data cannot be obtained through derivation, analyses will be conducted using the available nonmissing data. All assumptions, derivations, and decisions regarding missing data will be documented to ensure transparency and reproducibility. The final dataset of pooled data will then be summarized and mapped using Microsoft Power BI [21] to create an interactive dashboard for data visualization programmed by the Institute for Clinical Effectiveness and Health Policy team based on this protocol. This platform will allow users to explore maternal and neonatal effectiveness and immunogenicity outcomes through various figures, tables, and maps. Meta-analyses will be performed using R (R Foundation for Statistical Computing) and Shiny (RStudio language) [22], incorporating random-effects models and proportional meta-analyses to synthesize the data based on algorithms that select and automatically calculate the meta-analyses on the Shiny application. Provided that data are available and methodologically suitable, aggregate meta-analyses will be performed for each comparison in accordance with the Cochrane Handbook for Systematic Reviews of Interventions using random-effects meta-analysis for primary analyses.

We will apply the Grading of Recommendations Assessment, Development, and Evaluation (GRADE) approach [23] to rate certainty for critical outcomes, downgrading for risk of bias, inconsistency, indirectness, imprecision, and publication bias. Summary of findings tables will be prepared for key infant outcomes and maternal outcomes.

No patients will be involved in review development. Dissemination materials will be designed for policymakers and clinicians; lay summaries will be considered as evidence accumulates.

We will use published and routinely collected anonymized data; ethics approval is not required.

Findings will be disseminated through peer-reviewed publications and conference presentations and, on a continuous basis, through a publicly accessible interactive dashboard providing real-time meta-analyses [24].

Any protocol amendments will be documented with dates, rationale, and implications for interpretation and reflected in PROSPERO and in a public changelog.

We anticipate that maternal RSVPreF vaccination will be associated with clinically meaningful reductions in RSV-associated disease among infants, particularly RSV hospitalization and severe RSV LRTD, and with a direct protection against RSV illness among pregnant and postpartum individuals. Drawing on evidence from the MATISSE trial and early postlicensure evidence, we expect pooled VE against infant RSV hospitalization to be highest in the first 3 months of life. We further hypothesize that effectiveness will be higher when vaccination occurs at least 14 days before delivery, consistent with the time required for active transplacental maternal immunoglobulin G transfer, and broadly stable across the various gestational age windows during which the vaccine is currently implemented (eg, from 28 to 32 weeks). Immunogenicity outcomes are expected to characterize maternal neutralizing antibody responses and maternal-infant transfer ratios and, where data permit, explore their association with observed effectiveness. These measures are intended to provide mechanistic insights rather than establish clinical protection directly. As this is a living systematic review, these estimates are provisional and will be updated as evidence accumulates.

Previous systematic reviews of maternal RSV vaccination during pregnancy, largely based on randomized trials of different vaccine candidates, have reported VE estimates of approximately 50% to 67% against RSV hospitalization and 74% to 81.9% against severe RSV LRTD in infants under 3 months of age. The present review is intended to complement and extend that body of work in 4 important ways. First, it focuses specifically on the licensed RSVPreF (ABRYSVO) vaccine and evidence generated during the postlicensure real-world period rather than pooling prelicensure trial data. Second, it uses a living review framework with at least monthly surveillance updates available on the online platform, enabling continuous incorporation of rapidly emerging effectiveness data. Third, it prospectively integrates infant and maternal effectiveness and immunogenicity outcomes and prespecifies design-appropriate synthesis methods, including separate pooling of randomized and nonrandomized studies and standardization of adjusted estimates to VE. Fourth, it emphasizes clinically and programmatically actionable relevant subgroups, particularly the timing of vaccination relative to delivery and gestational age at vaccination. Consequently, this review is expected to provide estimates that better reflect vaccine performance under routine programmatic conditions across diverse settings and RSV seasons while also helping characterize the limited evidence regarding the direct benefits of vaccination for pregnant and postpartum individuals.

The principal strengths of this review include its exclusive focus on RWE generated under routine programmatic conditions; its living design that enables timely updating in a rapidly evolving field; inclusion of studies from different countries and health system settings; evaluation of clinically meaningful infant and maternal outcomes such as RSV hospitalization, severe RSV LRTD, and intensive care unit admission; prespecified, policy-relevant subgroup analyses; the use of standardized methods for study selection, data extraction, risk-of-bias assessment (RoB 2 and ROBINS-I), and certainty of evidence assessment (GRADE); and the absence of language restrictions, which further reduces the risk of selection bias. The design also has inherent limitations. Postlicensure effectiveness estimates will rely primarily on observational studies, most commonly test-negative and cohort designs, which are susceptible to residual confounding despite statistical adjustment. Variability in outcome definitions and laboratory confirmation methods across studies may introduce outcome misclassification. Early RWE is concentrated in a limited number of high-income countries, potentially restricting generalizability. Several outcomes and subgroups may be informed by only 1 or 2 studies with modest sample sizes and wide CIs, warranting cautious interpretation. Data on preterm infants, protection beyond 6 months of age, and maternal and postpartum outcomes are also likely to remain limited in the near term. Immunogenicity outcomes may be difficult to pool because of heterogeneity in assays and reporting metrics. These limitations will be mitigated through prespecified eligibility criteria, design-stratified random-effects meta-analyses, formal risk-of-bias and certainty (GRADE) assessment, sensitivity analyses excluding studies at high risk of bias, and transparent version control with a publicly accessible changelog.

As the evidence base expands, future iterations of this review will incorporate data from underrepresented settings, including low- and middle-income countries; longer-term follow-up extending beyond 6 months of age; preterm and other high-risk infants; more comprehensive assessments of maternal and postpartum protection; comparisons between maternal vaccination and infant monoclonal antibody prophylaxis; and analyses of antibody durability and potential correlates of protection. Safety outcomes are beyond the scope of this review and will be addressed separately.

This living systematic review and meta-analysis will provide a continuously updated, methodologically rigorous synthesis of RWE on the effectiveness and immunogenicity of maternal RSVPreF vaccination in infants and pregnant and postpartum individuals. By generating timely, design-appropriate estimates both overall and within policy-relevant subgroups, the review is intended to inform clinical decision-making, maternal immunization programs, and future research priorities as the evidence base continues to evolve.