Registration of this systematic review protocol has been completed in PROSPERO (CRD420251173289). We will report the protocol in line with the preferred reporting items for systematic review and meta-analysis protocols (PRISMA-P) to ensure transparent and complete reporting (25), with further information available in Supplementary File 1. Our methodological approach will follow established standards, drawing on the Cochrane Handbook for Systematic Reviews of Interventions for procedures and using the grading of recommendations, assessment, development and evaluation (GRADE) approach to assess the certainty of evidence. For the NMA, we will comply with PRISMA-NMA guidance (26), with the work planned to begin in January 2026 and conclude on 20 May 2026.

Adults with a documented diagnosis of hypertension and concurrent insomnia will be eligible. Hypertension will be considered eligible if diagnosed in the original trial using clearly stated criteria consistent with major international guidelines, including the 2017 American College of Cardiology/American Heart Association guideline (ACC/AHA), the 2023 European Society of Hypertension guideline (ESH), or the National Institute for Health and Care Excellence guideline “Hypertension in adults: diagnosis and management” (NG136; NICE), based on office blood pressure, 24-h ambulatory blood pressure monitoring, or home blood pressure monitoring with explicit thresholds (27–29). Insomnia will be considered eligible if defined using established diagnostic standards, including the Diagnostic and Statistical Manual of Mental Disorders, Fifth Edition, Text Revision (DSM-5-TR), the International Classification of Sleep Disorders, Third Edition, Text Revision (ICSD-3-TR), or the International Classification of Diseases, 11th Revision (ICD-11), or equivalent trial-defined criteria requiring difficulty initiating or maintaining sleep or early-morning awakening, accompanied by daytime impairment and explicit frequency/duration thresholds (30–32).

To preserve clinical interpretability and transitivity, we will not merge modalities a priori. If the network is sparse or disconnected, we will apply a prespecified, rule-based merging strategy only to clinically similar modalities that share invasiveness and stimulation characteristics, and we will report all merging decisions transparently and test them in sensitivity analyses. Interventions must target recognized acupoints and report session frequency and duration. Trials will be excluded if they are purely pharmacological or herbal, involve acupoint injection with drugs, use non-acupoint neuromodulation, involve massage or Tuina without an acupuncture component, or employ multi-component packages where the acupuncture effect cannot be isolated.

For multi-component interventions (e.g., acupuncture combined with moxibustion), we will handle them as follows: (i) if the combination constitutes a distinct and recurring regimen across trials, we will treat it as a separate combination node (e.g., “manual acupuncture + moxibustion”); (ii) if combinations are infrequent or heterogeneous, we will include them only when the co-intervention structure is balanced across the trial arms, and we will explore their influence via sensitivity analyses. Trials in which the specific contribution of ARTs cannot reasonably be isolated will remain excluded.

We will exclude all non-randomized designs, case series or case reports, qualitative or modeling studies, editorials, opinions, letters, protocols without results, conference abstracts without full data, and secondary research such as narrative or systematic reviews, meta-analyses, or umbrella reviews. Studies will be excluded when sleep complaints are primarily due to conditions requiring specific therapy. Trials lacking an acupuncture-related therapy arm or not allowing the effect of acupuncture to be isolated, including purely pharmacological or herbal interventions, acupoint injection with drugs, non-acupoint neuromodulation, or massage/tuina without an acupuncture component, will be excluded. Records with insufficient outcome data for the prespecified primary endpoint, after unsuccessful attempts to obtain missing information from authors or duplicate/overlapping publications, will be excluded, with the most complete dataset retained. Non-human or preclinical studies are not eligible.

We will systematically search eight bibliographic databases, from inception through January 2026, including PubMed, the Cochrane Library (CENTRAL), Embase, Web of Science Core Collection, China National Knowledge Infrastructure (CNKI), Wanfang Data, VIP (Chinese Scientific Journals Database), and SinoMed (CBM). To mitigate publication bias, we will also screen trial registries (WHO ICTRP, ClinicalTrials.gov, and the Chinese Clinical Trial Registry), and we will manually search reference lists of included studies and relevant reviews. No language restrictions will be applied; equivalent Chinese keywords will be used in Chinese databases.

Search strategies will combine controlled vocabulary (e.g., MeSH/Emtree) and free-text terms across three concepts: ① Target conditions: hypertension/high blood pressure and insomnia/sleep disturbance; ② Acupuncture and related therapies: e.g., acupuncture, electroacupuncture, auricular acupuncture, acupressure/auricular acupressure, transcutaneous electrical acupoint stimulation, moxibustion, and acupoint catgut embedding; and ③ Randomized trial design: randomized/randomised, controlled clinical trial. Full, database-specific strategies are provided in Supplementary File 2.

Records will be de-duplicated in EndNote X9. Two reviewers (Y-pZ and TF) will independently screen titles/abstracts and then full texts, against eligibility criteria; disagreements will be resolved by consensus or a third reviewer. Reasons for full-text exclusions will be recorded, and the process is summarized in a PRISMA flow diagram (Figure 1).

Data will be extracted independently and in duplicate using a standardized form, which will include:

For missing or unclear information, corresponding authors will be contacted; studies will be excluded if essential data remain unavailable after two attempts over 14 days.

We will assess the risk of bias with the Cochrane RoB 2 tool at the outcome level (33). The primary endpoint is the change in global insomnia severity at the first post-treatment assessment. Two reviewers (Y-pZ and TF) will work independently after calibration. Five domains are evaluated: randomization process, deviations from intended interventions, missing outcome data, measurement of the outcome, and selection of the reported result. Each domain and the overall judgment will be rated as low risk, with some concerns, or high risk.

For the randomization process, a low risk of bias required an adequate sequence and robust allocation concealment (e.g., computer-generated list plus centralized allocation or sequentially numbered, opaque, sealed envelopes). Quasi-random methods or unconcealed allocation indicated a high risk. For deviations from intended interventions, lack of blinding raised concern only when it plausibly altered adherence or co-interventions, and when analyses were not conducted according to the intention-to-treat principle. For missing data, substantial or unbalanced attrition without appropriate handling increased risk. For outcome measurement, unblinded assessors using subjective scales increased concern, whereas validated procedures and blinded assessment reduced it. For selective reporting, we will compare reported outcomes and time points with protocols or registries.

Disagreements are resolved by consensus or third-reviewer adjudication. We will document justifications and sources. Graphical summaries will be produced in RevMan 5.4. Sensitivity analyses will exclude studies at high risk of bias.

We will perform conventional pairwise meta-analyses in RevMan 5.4 for all direct head-to-head comparisons. Effect measures will be standardized mean differences for insomnia scales, mean differences for blood pressure outcomes, and risk ratios for dichotomous endpoints. Heterogeneity will be quantified with Q, I², and τ²; model choice (fixed vs. random effects) will follow Cochrane guidance (34). We will explore outliers and influences using leave-one-out analyses. When ≥10 studies inform a contrast, small-study effects will be assessed using funnel plots and appropriate tests. Multi-arm trials will be handled by splitting shared comparators or by using methods that account for the correlation of effect estimates to avoid double-counting. Pairwise estimates will serve as the benchmark for the subsequent network meta-analysis and will help appraise the assumptions of similarity and transitivity; if the evidence network is sparse or disconnected, the pairwise results will constitute the primary synthesis (26).

We will perform a Bayesian random-effects NMA using R (v4.4.1) with the gemtc package and summarize network geometry and league tables in Stata (v15.1), following PRISMA-NMA guidance (26). Continuous outcomes will be synthesized as mean differences (MD) when the same scale is used or as standardized mean differences (SMD) when instruments differ; dichotomous outcomes will use risk ratios (RR), all reported with 95% credible intervals (CrI). Models will be contrast-based with a common between-study heterogeneity standard deviation (τ) across comparisons. For relative treatment effects, we will use weakly informative normal priors d_k ~ N(0, 10²) for all non-reference treatments. For heterogeneity, we will use a half-normal prior: τ ~ HN(0, 1). Multi-arm trials will be modeled within likelihood to account for correlation and avoid double-counting. We will depict network geometry and report a contribution matrix. We will assess the network connectivity and geometry prior to synthesis. If the evidence network is sparse or disconnected, we will restrict the primary NMA to the largest connected component and report disconnected components separately. For interventions or comparisons that cannot be linked within a connected network, we will present conventional pairwise meta-analyses as the primary synthesis. Where clinically justified, we will consider prespecified, rule-based node-merging strategies to improve connectivity and will examine the impact of such decisions in sensitivity analyses.

Assumptions will be examined via transitivity checks on prespecified effect modifiers and coherence via global design-by-treatment tests and local node-splitting; where relevant, loop-specific inconsistency factors will be presented. We will assess the plausibility of transitivity by comparing the distribution of these prespecified effect modifiers across treatment comparisons and summarizing them in tables. Where sufficient data are available, we will explore heterogeneity related to these modifiers through prespecified subgroup analyses and, when feasible, network meta-regression. Model fit will be compared using the deviance information criterion (DIC) and posterior residual deviance. Relative rankings will be summarized using the surface under the cumulative ranking curve (SUCRA) and displayed as rankograms, interpreted alongside effect sizes, Credible intervals (Crls), heterogeneity, and coherence diagnostics. In sensitivity analyses, we will assess robustness to alternative heterogeneity priors, including τ ~ HN(0, 0.5) and τ ~ Uniform(0, 2).

We will explore heterogeneity using prespecified subgroups. When ≥10 trials contribute to a covariate, we will fit random-effects network meta-regression with study-level moderators; otherwise, we will perform stratified NMAs. Planned subgroups include baseline insomnia severity (subthreshold vs. clinical), hypertension control at baseline (controlled vs. uncontrolled), sex (proportion female ≥60% vs. <60%), screening for primary sleep disorders (obstructive sleep apnea screening reported vs. not reported), comparator type (sham/attention vs. usual care vs. pharmacotherapy vs. cognitive behavioral therapy for insomnia), treatment class (invasive vs. non-invasive), treatment dose (≥3 sessions per week or ≥12 total sessions vs. lower dose) and duration (≥4 weeks vs. <4 weeks), geographical setting, and overall risk of bias (low or some concerns vs. high). Where data permit, we will further explore dose- and intensity-related heterogeneity using reported stimulation parameters (e.g., electrical stimulation frequency/intensity for electroacupuncture/TEAS) in network meta-regression or stratified analyses. We will report interaction estimates, residual heterogeneity, and clinical plausibility, while acknowledging the ecological nature and interpretative limits of study-level subgroup analyses (35, 36).

We will test robustness by excluding studies at high risk of bias; excluding trials without explicit screening for obstructive sleep apnea; using endpoint scores instead of change scores; excluding studies with imputed variances or converted summary statistics; varying modeling assumptions (fixed-effect vs. random-effects; alternative weakly informative priors for the heterogeneity SD); removing influential studies via leave-one-out analyses; and excluding small studies (total sample <50 or <30 per arm). We will compare effect estimates, heterogeneity (τ), coherence diagnostics, and rankings across scenarios and interpret differences for decision relevance.

Small-study effects will be assessed using comparison-adjusted funnel plots (Stata 15.1, netfunnel) Analyses will be performed only for outcomes with ≥10 trials.

We will rate certainty with GRADE (37) adapted for network meta-analysis. Risk of bias will use RoB 2 at the outcome level. We will downgrade if high-risk studies contribute materially. Heterogeneity will use I² in pairwise analyses. In the network, we will use between-study SD and predictive intervals. We will downgrade for substantial, unexplained variability. Indirectness will be judged when populations, interventions, comparators, outcomes, or indirect evidence diverge from the review question. Imprecision will be judged by the 95% interval between minimally important differences and the required information size. Incoherence will be assessed through local checks and, when appropriate, global tests. We will downgrade if the inconsistency persists. Publication bias will be explored with comparison-adjusted funnel plots and registry cross-checks. We will downgrade when small-study effects or selective reporting are suspected. All judgments will be documented with concise justifications.