Stroke is a leading cause of death and disability worldwide, and the burden of stroke-related disability remains substantial in China [1,2]. Poststroke dysphagia is one of the most clinically important sequelae because it is associated with malnutrition, dehydration, aspiration pneumonia, reduced quality of life, prolonged hospitalization, and increased mortality [3,4].

Current dysphagia management after stroke includes early screening, compensatory strategies, behavioral swallowing therapy, diet modification, and instrumental assessment when indicated [5-7]. Treatment selection and delivery should be individualized according to swallowing physiology, aspiration risk, and clinical status [3,5]. In practice, implementation may still be constrained by patient cooperation, equipment availability, institutional resources, and variable response in patients with persistent swallowing dysfunction [3,7].

In traditional Chinese medicine, poststroke dysphagia is commonly interpreted as impaired regulation of channel qi and obstruction of the throat orifice after stroke [8]. A recent multicenter randomized controlled trial suggested that acupuncture may improve swallowing function in patients with poststroke dysphagia [9]. Updated evidence syntheses also indicate potential benefit, although certainty is limited by the methodological quality and heterogeneity of the included trials [10,11]. A recent scoping review identified substantial variation in acupoint selection, stimulation mode, intervention dose, and reporting quality [12]. Experimental and clinical mechanistic studies suggest that acupuncture may influence swallowing-related cortical, brain stem, and peripheral sensory-motor pathways [13-15].

The comparator is conventional acupuncture at the same 4 nape acupoints delivered via standard needle insertion, deqi, and 30-minute retention. It is not intended as a positive control in the pharmacological sense of a treatment with established efficacy used to demonstrate assay sensitivity. Rather, it serves as a standard reference treatment that represents current routine acupuncture practice for poststroke dysphagia in Chinese rehabilitation settings [16]. Against this reference, the trial estimates the incremental effect of adding the interactive manipulation component, and the comparison is therefore framed as a pragmatic superiority evaluation of two clinically implementable procedures rather than a mechanistic isolation of a single sensory element. This choice is consistent with the revised pragmatic-explanatory continuum indicator summary (PRECIS-2) framework, which emphasizes alignment between trial design decisions and the intended use of the results and recognizes usual care as an appropriate comparator in pragmatic trials [17].

Because the experimental and reference procedures differ in retention time and patient task engagement, performance-related differences may arise. This is a deliberate consequence of the design: task engagement and the timing of stimulation are constituent elements of the interactive intervention as it would be delivered in practice, and the trial evaluates the intervention as a whole rather than an isolated procedural element. In PRECIS-2 terms, these features relate to the domain of flexibility (delivery) because they define how the intervention is implemented under clinically feasible conditions rather than under an idealized mechanistic design. To limit bias, outcome assessors, data managers, and statisticians will remain blinded; allocation will be concealed before assignment; and intervention fidelity will be monitored using prespecified checklists in both arms.

Interactive acupuncture is conceptualized as a task-synchronized needling procedure that combines local nape acupoint stimulation with active swallowing-related movement. The proposed mechanism is that time-locked peripheral stimulation and task performance may enhance sensory-motor integration in swallowing networks. This trial will evaluate the clinical effectiveness and safety of interactive acupuncture and explore related functional and objective indicators.

This is a prospective, multicenter, parallel-group randomized controlled trial with a 1:1 allocation ratio. A total of 100 participants will be enrolled after eligibility screening, baseline assessment, and written informed consent. Participants will receive 14 treatment sessions over approximately 2 to 3 weeks followed by a 1-month follow-up. The protocol follows the SPIRIT (Standard Protocol Items: Recommendations for Interventional Trials) 2025 recommendations for clinical trial protocols, and the intervention description was strengthened according to the TIDieR (Template for Intervention Description and Replication) principles [18,19].

The primary time point is after the 14th treatment session. Additional assessments will be performed after sessions 3 and 7 and at 1 month after treatment completion to describe the trajectory and durability of response.

The trial will be conducted at Hengshui Hospital of Traditional Chinese Medicine in Hebei Province and the Second Affiliated Hospital of Tianjin University of Traditional Chinese Medicine. The study timeline and trial flowchart are shown in Table 1 and Figure 1, respectively.

During the design phase, structured interviews and questionnaire surveys were conducted with patients with poststroke dysphagia and their family members. Their feedback informed the operational procedure, the timing of assessments, and approaches to improving acceptability and adherence.

Protocol deviations will be classified as minor or major before database lock. Database lock refers to the formal finalization of the trial database for the final statistical analysis after completion of data entry, data cleaning, and query resolution, after which no further routine data changes are permitted. Minor deviations include brief scheduling variation, incomplete checklist fields that can be resolved from source documents, or small deviations in treatment timing without expected impact on safety or the primary outcome. Major deviations include incorrect allocation, use of nonassigned intervention, failure to receive the allocated intervention course sufficiently for per-protocol inclusion, unblinding of outcome assessors, enrollment despite clear ineligibility, or concurrent treatment in another interventional trial likely to affect swallowing outcomes. All deviations will be documented with date, reason, corrective action, and assessment of impact. Major deviations will be reviewed by the principal investigator and considered in sensitivity and per-protocol analyses.

All adverse events during the study, including local pain, bleeding, hematoma, dizziness, syncope, choking, coughing, aspiration-related symptoms, or other unexpected events, will be documented. Serious adverse events will be reported to the ethics committee according to institutional requirements and managed promptly.

The target sample size was determined before participant recruitment based on preliminary clinical data obtained during the trial development stage. For sample size planning, change in WST grade was treated numerically. The preliminary data suggested a mean grade improvement of 1.5 (SD 1.2) in the control group and 2.5 (SD 1.2) in the intervention group, corresponding to an anticipated between-group difference of 1.0. To provide external support for the plausibility of the control group estimate, we cite a published clinical study in which the mean WST score decreased from 4.17 (SD 0.91) before treatment to 2.50 (SD 1.14) after treatment, corresponding to an observed improvement of 1.67 [28]. This published study is used as external corroboration of the original control group assumption rather than as the source of the original preliminary data.

With the original assumptions, a 2-sided α of .05, power of 90%, and a 1:1 allocation ratio, the PASS (NCSS LLC) calculation required 32 participants per group. During the original protocol development stage, a Bonferroni adjustment was applied by dividing the 2-sided α of .05 by 4 planned WST assessment comparisons (adjusted α=.0125), increasing the calculated sample size to 42 participants per group. After allowing for 15% attrition, the target sample size was set at approximately 50 participants per group, or 100 participants in total. We acknowledge that this Bonferroni adjustment was conservative and is not required once session 14 is explicitly specified as the single primary efficacy comparison. It is reported here only to transparently describe how the original prerecruitment target sample size was derived. The primary hypothesis test will use a 2-sided α of .05, and the session 3 and session 7 assessments will be analyzed as supportive longitudinal measurements. No sample size re-estimation based on accumulating efficacy data or interim between-group comparisons has been performed during recruitment.

Eligible participants will be randomly assigned to either group in a 1:1 ratio. The sequence will be generated by an independent statistician using block randomization. Allocation concealment will be maintained with sequentially numbered, opaque, sealed envelopes opened by an independent coordinator only after enrollment and completion of the baseline assessment. Treating practitioners cannot be blinded because of the nature of acupuncture procedures. Participants will be informed that 2 active acupuncture procedures are being compared but will not be told the investigators’ hypothesis regarding superiority. Outcome assessors, data managers, and statisticians will remain blinded to allocation until the primary analysis is completed.

The full analysis set will include all randomized participants and will follow the intention-to-treat principle. Participants will be analyzed according to their randomized group regardless of adherence or treatment discontinuation, and missing primary outcome data will be handled using prespecified missing data methods. The per-protocol set will include participants who complete at least 80% of assigned treatment sessions, have primary outcome data at session 14, and have no major protocol deviations judged to affect efficacy evaluation. The safety set will include all participants who receive at least one session of the assigned intervention or control procedure and will be analyzed according to the treatment actually received.

Study data will be collected using standardized case report forms. Two trained researchers will independently enter the data into a dedicated electronic database, followed by cross-checking and logical validation. Personal identifiers will be stored separately from research data. An independent quality monitoring team will review consent documentation, intervention fidelity, completeness of outcome data, adverse event reporting, and protocol deviations at the mid-enrollment stage and study completion.

Baseline characteristics will be summarized by group but not subjected to significance testing for comparability. Continuous variables will be summarized using means and SDs or medians and IQRs, and categorical variables will be summarized using frequencies and percentages.

The primary efficacy comparison concerns the change in WST grade from baseline to session 14 in the full analysis set. Because the WST is ordinal, the primary model will use proportional odds ordinal regression to compare session 14 WST grades between randomized groups while adjusting for baseline WST grade, study center, and prespecified clinically relevant covariates such as age and time since stroke onset [29]. The treatment effect will be reported as a common odds ratio with a 95% CI. If the proportional odds assumption is not met, alternative ordinal models and a Mann-Whitney U test on change scores will be used as sensitivity analyses. The overall response rate is a supportive secondary analysis and will be compared using a chi-square test or Fisher exact test with effect estimates and 95% CIs.

Repeated postbaseline outcomes will be analyzed using mixed-effects models or generalized estimating equations including group, time, group-by-time interaction, baseline value, and study center. Continuous outcomes such as SSA, FOIS, SWAL-QOL, sEMG, thermography, and inflammatory markers will be analyzed using linear mixed models when assumptions are met and appropriate transformations or nonparametric methods otherwise. Binary or ordinal outcomes, including penetration and aspiration categories, will be analyzed using generalized linear mixed models. Adherence will be summarized as number and percentage of planned sessions completed and will be reported by group.

Missing outcome data will be described by group and reason. Multiple imputation will be considered for missing primary outcome data under a missing at random assumption; sensitivity analyses, including complete-case and conservative imputation scenarios, will be used to assess robustness [30]. All tests will be 2 sided. The primary outcome will use a 2-sided α level of .05, whereas secondary outcomes will be interpreted as supportive and exploratory.

The current amended protocol, informed consent form, and related study documents were reviewed and approved by the Medical Ethics Committee of Hengshui Hospital of Traditional Chinese Medicine on August 25, 2026 (approval 2026-KY-09; protocol version date: August 25, 2026). This approval includes the protocol amendment correcting the planned sample size from 99 to 100 participants (50 participants per group). The Second Affiliated Hospital of Tianjin University of Traditional Chinese Medicine, as the other participating study center, also provided institutional ethics approval for participation in this multicenter trial (approval Y2025-053-01). The study will be conducted in accordance with the Declaration of Helsinki, relevant Chinese laws and regulations, and the International Council for Harmonisation of Technical Requirements for Pharmaceuticals for Human Use E6 (R3) guideline for good clinical practice [31]. Written informed consent will be obtained from all participants or legally authorized representatives before enrollment.

The design emphasizes clinical feasibility, standardized intervention delivery, blinded outcome assessment, and multidimensional evaluation of swallowing function.

The trial responds to two limitations in the current acupuncture literature for poststroke dysphagia. First, recent randomized and evidence synthesis studies suggest potential benefit [9,10], but aspiration-focused studies and scoping reviews continue to identify low-certainty evidence, intervention heterogeneity, and incomplete reporting [11,12]. Second, prior studies often provide insufficient detail regarding practitioner training, intervention fidelity, and handling of deviations. The present protocol, therefore, includes a manualized intervention procedure, competency assessment, fidelity monitoring, and prespecified analysis populations.

The active comparator design allows for the evaluation of the incremental clinical value of interactive manipulation beyond the effects of acupoint selection and routine acupuncture contact. This choice may reduce assay sensitivity for placebo-related effects, but it is appropriate for a pragmatic comparison between two clinically applicable acupuncture strategies.

Mechanistically, the study is informed by an animal circuit study showing modulation of motor cortex inputs to brain stem swallowing pathways [13], clinical neuroimaging evidence of swallowing-related brain remodeling [14], and experimental evidence linking electroacupuncture-related peripheral sensory signaling with cortical regulation of swallowing [15]. The interactive procedure may combine peripheral acupoint stimulation with task-specific swallowing input, potentially facilitating sensory-motor integration. This hypothesis will require further mechanistic validation beyond the clinical outcomes of this trial.

The study has limitations. Participants and practitioners cannot be fully blinded. The sample size is powered for the primary swallowing outcome rather than mechanistic indicators. VFSS may not be repeated in every participant if safety or clinical feasibility prevents assessment. These limitations will be mitigated through blinded assessment, standardized data collection, and transparent reporting of adherence, missing data, and deviations.

The results will be disseminated through peer-reviewed publications, conference presentations, and updates to the trial registry. Authorship will follow standard authorship criteria.

This randomized controlled trial will evaluate whether an interactive, task-synchronized acupuncture procedure provides additional benefit over conventional acupuncture at the same nape acupoints for poststroke dysphagia. The findings will provide comparative evidence on swallowing outcomes and safety, while the manualized intervention and fidelity-monitoring procedures may support replication in future studies.