Abstract
Background
Advanced technologies and complementary or adjunctive interventions are increasingly used for chronic or recurrent orofacial pain (OP), but comparative evidence remains fragmented across diagnoses, modalities, and outcomes.
Main body
We conducted a systematic evidence map with selective meta-analyses (PROSPERO CRD420251270501) following PRISMA 2020. Six databases were searched from inception to 31 December 2025 for randomized and non-randomized intervention studies in adults with temporomandibular disorders (TMD), burning mouth syndrome (BMS), trigeminal neuralgia (TN), and other chronic or recurrent orofacial pain phenotypes. Two reviewers independently screened records, extracted data, assessed risk of bias using validated tools, and rated certainty with GRADE. Random-effects meta-analyses of randomized comparisons used standardized mean differences within prespecified follow-up windows and reported prediction intervals. Pain intensity was prioritized, and disability, jaw function, quality of life, global improvement, medication outcomes, and adverse events were extracted when available. We included 130 studies (n = 6879 participants). Non-randomized intervention studies were retained to widen the evidence map and to capture feasibility, durability, and safety signals that are often underrepresented in early randomized trials. These studies were synthesized narratively and did not contribute to pooled comparative estimates or to certainty upgrading. Low risk of bias was uncommon, and reporting of function, quality of life, and harms was inconsistent, which limited pooling. Safety outcomes were not reported in 37 of 130 included studies, and denominators were often unclear, which limits risk–benefit interpretation. In BMS, photobiomodulation or low-level laser therapy (PBM/LLLT) versus inactive control reduced short-term pain (k = 6, N = 200, standardized mean difference − 0.81, 95% CI − 1.35 to − 0.27). The 95% prediction interval crossed the null (− 1.80 to 0.17), while certainty was moderate. Most pharmacologic and supplement interventions for BMS showed uncertain or inconsistent effects. For TMD, effects varied by modality and comparator and were generally low or very low certainty. Evidence for TN and digital therapeutics was sparse, and adverse-event reporting was inconsistent.
Short conclusion
PBM/LLLT shows the clearest short-term analgesic signal for BMS versus inactive control, but transportability remains uncertain given null-crossing prediction intervals and limited long-term data. Future trials should standardize outcomes, extend follow-up, and report harms transparently to support diagnosis-stratified care.
Supplementary Information
The online version contains supplementary material available at 10.1186/s10194-026-02300-7.
Keywords: Orofacial pain, Temporomandibular joint disorders, Burning mouth syndrome, Trigeminal neuralgia, Neuromodulation, Low-level light therapy, Complementary therapies, Evidence mapping, Systematic review, Meta-analysis
Highlights
Evidence map of 130 studies across TMD, BMS and TN interventions.
PBM/LLLT shows the strongest pooled short-term analgesia in BMS.
Most pharmacologic/supplement options for BMS show uncertain benefits.
Needling/manual therapies show mixed results and variable trial quality.
TN and interventional clusters are emerging and evidence remains limited.
For TMD effects differ across interventions and comparators.
Supplementary Information
The online version contains supplementary material available at 10.1186/s10194-026-02300-7.
Introduction
Orofacial pain (OP) refers to pain perceived in the face, jaws, or oral cavity and may arise from musculoskeletal, neuropathic, neurovascular, idiopathic, or disease-related mechanisms [1]. The International Classification of OP provides a shared taxonomy, and continuity with headache-related phenotypes is supported by the International Classification of Headache Disorders, 3rd edition [1, 2]. For temporomandibular disorders (TMDs), the Diagnostic Criteria for Temporomandibular Disorders (DC/TMD) remain the dominant framework for classifying painful and intra-articular phenotypes while integrating psychosocial domains relevant to prognosis and treatment response [3]. Expanded TMD taxonomies reinforce the value of phenotypic precision and avoidance of overly broad labels that can promote ineffective or unnecessary interventions [4, 5]. Prevalence estimates vary because studies sample different settings and age structures, apply non-uniform diagnostic criteria and recall windows, and differ in whether diagnoses are confirmed clinically or inferred from self-report [6].
TMDs constitute a major component of chronic non-odontogenic OP, with recent meta-analyses suggesting pooled prevalence estimates around 30–34% in adults and substantial regional variation [7, 8]. Burning mouth syndrome (BMS) is less prevalent yet clinically salient, with population-based prevalence around 1.7% and higher proportions reported in clinical samples, and estimates vary by age, sex, and region [9]. Trigeminal neuralgia (TN) remains rare but high impact, with prevalence estimates ranging from about 0.03% to 0.3% depending on ascertainment and diagnostic verification [10, 11]. Persistent idiopathic facial pain is also uncommon, with population-based work suggesting prevalence near 0.03%, but it contributes to diagnostic uncertainty and repeated healthcare contacts [12, 13]. Clinical burden extends beyond pain intensity and includes disability, impaired oral function, sleep disturbance, emotional distress, and reduced health-related quality of life (QoL). Systematic evaluation has demonstrated substantial quality-of-life impairment in BMS, supporting the relevance of outcomes that capture function and well-being rather than symptom intensity alone [14].
These diagnostic entities differ in presentation and primary tissues, yet they share cross-cutting features relevant to treatment selection, including mixed peripheral and central drivers and frequent co-occurrence of psychosocial amplification processes [1, 2]. Many adjunctive and technology-enabled interventions used in practice target shared pain-modulation pathways rather than a single anatomic site, which supports an overarching synthesis framework while preserving diagnosis-stratified interpretation. Given the breadth of diagnoses, interventions, and outcomes, we approached the review as an evidence map and performed meta-analyses only when clinical and methodological comparability supported pooling. Cross-condition contrasts are therefore interpreted conceptually rather than as direct comparative effectiveness claims.
Comparative work across chronic OP cohorts has also reported marked quality-of-life impact and functional consequences that often dominate the patient experience [15]. Healthcare utilization studies for TMDs describe substantial service use and costs, reflecting repeated cycles through dental, medical, and allied health care before access to specialized assessment [16]. National-level assessments highlight fragmentation across the dental-medical divide, and pathway research in persistent OP documents complex referral trajectories that can amplify unmet needs when treatments are applied sequentially without a coherent plan [17, 18]. Qualitative evidence in TN describes diagnostic delay and misdirection across services, and interprofessional perspectives emphasize coordinated, mechanism-informed care planning [19, 20]. Therapeutic practice has expanded beyond splints and analgesic escalation, yet guidance remains uneven across modalities. Key-point statements and clinical practice guidelines for temporomandibular disorder–related pain emphasize conservative, biopsychosocial management as a foundation while acknowledging that many patients seek additional options when first-line care is insufficient [21, 22]. Professional position statements situate minimally invasive interventions within a broader continuum for intra-articular temporomandibular joint (TMJ) pain and dysfunction [23].
Clinical and systematic review evidence links painful TMDs with psychological distress and anxiety, strengthening the rationale for integrated behavioral targets [24, 25]. Observational research supports the relevance of central sensitization and somatization features in subsets of TMD populations, which may help explain heterogeneous responses to peripheral interventions [26]. Network meta-analysis in TMD pharmacotherapy illustrates a growing evidence base, yet heterogeneous case mix and outcome reporting still limit guidance on individualized sequencing [27]. Complementary and advanced interventions coexist in contemporary pathways, yet comparative interpretation remains difficult across diagnoses and modalities. Acupuncture synthesis for OP suggests potential benefits, while protocol and comparator heterogeneity limits phenotype-specific recommendations [28]. Evidence syntheses in TMDs have evaluated dry needling and manual therapy and have highlighted how variability in delivery and outcome choice constrains inference [29, 30]. Neuromodulation approaches have been synthesized for TN and neuropathic OP, while protocol standardization, follow-up duration, and adverse-event reporting remain important limitations [31–34]. BMS evidence has been summarized through network meta-analysis and systematic reviews of photobiomodulation or low-level laser therapy (PBM/LLLT), yet uncertainty persists around optimal parameters and long-term benefit despite clinical uptake [35–37]. Platelet-rich plasma injections and botulinum toxin (BTX) have been synthesized for TMD phenotypes, reinforcing the need to evaluate benefit and harm jointly when repeated interventions are considered [38–40].
Despite a growing body of syntheses, unresolved clinical questions persist because most reviews focus on single modalities within a single diagnosis, leaving clinicians without an overarching map of what has been tested across major chronic OP phenotypes and where evidence is sufficiently comparable for quantitative pooling. Existing work provides modality-specific estimates for acupuncture [28], dry needling and manual therapy in TMDs [29, 30], neuromodulation for neuropathic OP [31–34], PBM/LLLT in BMS [35–37], and injectables such as platelet-rich plasma and BTX in TMD phenotypes [38–40]. During protocol development, we conducted targeted scoping searches and citation screening to identify recent and widely cited systematic reviews and meta-analyses across these modalities and diagnoses. This review landscape was used to predefine where a diagnosis-stratified cross-modality evidence map, consistent outcome-family handling, and prediction-interval interpretation could add value beyond single-modality syntheses. Patient-relevant outcomes and harms are not consistently captured across these literatures, which limits confident comparison and sequencing across intervention families. We therefore conducted a systematic evidence-mapping review with selective meta-analyses. Several reviews in this field have applied date cut-offs, which may preferentially capture more recent studies while omitting earlier clinically influential trials. This is particularly relevant for device-based and procedural interventions, where older reports may provide longer follow-up and more informative safety and durability signals. For these reasons, we planned the search from database inception and managed heterogeneity and reporting limitations through prespecified grouping, risk-of-bias appraisal, and sensitivity analyses rather than imposing a priori date restrictions. In adults with clinically diagnosed chronic or recurrent OP disorders, we evaluated advanced and complementary or integrative interventions versus inactive or active comparators and synthesized effects on pain intensity and prespecified patient-relevant outcomes, including pain-related disability, oral-jaw function, QoL, global improvement, medication use, and adverse events.
Materials and methods
Protocol, registration, and reporting standard
This systematic review was planned and reported in accordance with the Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) 2020 statement [41]. The completed PRISMA 2020 checklist is provided in Supplementary Material 1. The review was registered in the International Prospective Register of Systematic Reviews (PROSPERO) (CRD420251270501) on 21 December 2025. No standalone protocol document was produced beyond the PROSPERO record, and the registration entry was treated as the primary a priori specification of eligibility criteria, outcome families, follow-up windows, and the synthesis framework. The PROSPERO record prespecified pain intensity as the primary outcome domain and secondary patient-relevant domains, including pain interference or disability, jaw or oral function, QoL, global improvement, medication use, and adverse events. Follow-up window grouping and decision rules to select one outcome and one time point per window were prespecified and are detailed in Supplementary Material 2 (Appendix S1).
PICO evaluation and review framework
The review question was structured using the Population, Intervention, Comparator, and Outcomes (PICO) framework to define the target population, intervention families, comparators, and prespecified outcome domains, consistent with methodological guidance for systematic reviews [42, 43]. The population comprised adults (≥ 18 years) with chronic or recurrent OP in which pain was the primary complaint and was localized to the face, jaws, oral cavity, temporomandibular region, or trigeminal distribution. Intervention families were classified a priori before data extraction to avoid result-driven relabelling and to support structured mapping across modalities. Advanced intervention families included neuromodulation approaches, PBM/LLLT therapies delivered with reproducible parameters, minimally invasive procedures not involving open surgery, and pharmacological or biologic innovations intended to modify pain modulation or neuroinflammatory mechanisms. Complementary and integrative families included acupuncture and related needling techniques, structured psychological interventions, standardized manual therapies addressing the cranio-cervico-mandibular system, and multimodal programs grounded in biopsychosocial frameworks. Eligible comparators included sham or placebo conditions when feasible, usual care or guideline-based management, wait-list controls, and active comparators. Comparators were coded a priori as inactive controls versus active therapeutic comparators, and synthesis was stratified accordingly when comparator content was not clinically exchangeable because these contrasts address different clinical questions. The review was conducted as a systematic evidence map with selective meta-analyses. Quantitative pooling was restricted to comparisons that were clinically and methodologically comparable within prespecified outcome families and follow-up windows. Multi-arm trials were handled by combining clinically similar intervention arms or splitting shared comparator groups for variance estimation, and crossover trials were analyzed using paired methods when within-person information was available or first-period data when reported.
Inclusion criteria
Eligible records were full-text primary intervention studies in humans evaluating advanced, complementary, or integrative interventions, or structured combinations of these modalities, for chronic or recurrent orofacial pain in adults. Randomized controlled trials, including parallel-group and cross-over designs, were eligible for comparative effectiveness synthesis and for quantitative pooling when prespecified comparability criteria were met. Non-randomized intervention studies were also eligible when the design and reporting supported clinically meaningful interpretation of change over time, but these studies were retained primarily to widen the evidence map, to capture feasibility, durability, and safety signals, and to characterize the maturity of evidence clusters. Non-randomized studies were synthesized narratively and did not contribute to pooled comparative-effect estimates.
Eligibility required clinically diagnosed orofacial pain phenotypes with explicit diagnostic framing supported by stated criteria or by a recognized framework. For TMDs, diagnoses based on DC/TMD or clearly compatible operational criteria were eligible, including painful and intra-articular phenotypes. TN and related trigeminal pain syndromes were eligible when diagnostic framing aligned with the International Classification of Headache Disorders and the International Classification of Orofacial Pain and when symptom descriptions supported a trigeminal distribution phenotype [1–3]. BMS and persistent idiopathic facial pain were eligible when diagnostic framing was consistent with recognized orofacial pain taxonomies, including chronicity and typical pain distribution as reported [1, 2]. When diagnostic criteria were incompletely reported, eligibility was retained only when the diagnostic framing was explicit and the dominant clinical phenotype was clearly orofacial, and this decision was documented during extraction.
Studies were eligible if they reported at least one pain-related outcome measured at baseline and at a clearly defined follow-up time point using a validated or widely accepted instrument. Pain intensity measures included visual analogue scales (VAS) and numeric rating scales (NRS), and Brief Pain Inventory (BPI) subscales when used to quantify intensity or interference [44–46]. Disability, jaw or oral function, QoL, global improvement, medication outcomes, and adverse events were extracted when available, but were not required for eligibility. Intervention reporting had to be sufficiently detailed to support classification and interpretation, including dose, session schedule, device settings or procedural characteristics, and background care.
Exclusion criteria
Records were excluded if they did not provide original clinical outcome data, were not interventional, were preclinical, were case reports, or were conducted in pediatric populations. Studies were excluded when the index condition was not a chronic or recurrent OP phenotype or when reporting did not allow the target condition to be distinguished from acute odontogenic pain or procedure-related dental pain. Trials in which pain was explicitly attributable to an acute dental pathology or to a procedural context, such as pain following extraction, endodontic procedures, implant surgery, or orthodontic adjustment, were excluded because the natural history, mechanisms, and outcome trajectories differ from chronic or recurrent OP.
Primary headache disorders were excluded when the primary diagnostic framing, therapeutic intent, and prespecified primary outcomes were headache endpoints, even if facial or jaw pain was collected as a secondary symptom. The dominant orofacial phenotype concept was operationalized by requiring that recruitment and eligibility were anchored to chronic or recurrent pain perceived in the face, jaw, oral cavity, temporomandibular region, or trigeminal distribution, that the intervention was delivered with explicit intent to treat the OP condition, and that at least one prespecified outcome was reported as an OP endpoint. Mixed samples were eligible only when the dominant phenotype was clearly orofacial based on these criteria or when orofacial subgroup data were reported separately.
Information sources and search strategy
A comprehensive electronic search was conducted in PubMed, Web of Science, Embase, EBSCOhost, the Cochrane Library, and Scopus. The final search was executed on 31 December 2025. Searches were run from database inception without date limits to reduce time-lag bias and to capture earlier clinically influential evidence, including longer-term safety and durability data for device-based and procedural interventions. This approach also reduces the impact of date restrictions used in several modality-specific syntheses in this field and increases the likelihood of capturing early clinically influential trials that inform durability and tolerability. Eligibility assessment was restricted to English-language full texts to preserve appraisal and extraction accuracy, and this restriction was considered when interpreting potential language and dissemination bias. Reference lists of included studies and relevant reviews were hand-searched, and forward citation tracking was undertaken for key trials using citation indexes available within Web of Science and Scopus. Clinical trial registries and other grey literature sources were not systematically searched. This decision was made because the quantitative synthesis required peer-reviewed full texts with extractable outcomes and reproducible intervention parameters. Whenever included trials reported a registration identifier or linked protocol, these sources were consulted to inform the RoB 2 domain on selection of the reported result. Specific search strings are visualized in supplementary material 2.
Study selection process
All records retrieved from the electronic searches were exported and deduplicated prior to screening using a prespecified, rule-based workflow implemented in Microsoft Excel (Microsoft Corporation, Redmond, WA, USA), with manual adjudication of flagged pairs to avoid erroneous removals and to retain multiple reports from the same study for subsequent linkage at the study level. Two reviewers (A.C., D.M.) independently screened titles and abstracts against prespecified eligibility criteria using a locked screening workbook with standardized decision fields, validation rules, and a date-stamped audit trail. Before formal screening, both reviewers piloted the criteria on a calibration set to harmonize interpretations and to operationalize concepts that required clarification, including clinically diagnosed phenotypes, mixed presentations, and acceptable outcome instruments. Full texts were obtained for records considered potentially eligible and were assessed independently by the same reviewers. Disagreements at either stage were resolved through discussion, and a third senior reviewer (R.S.C.) adjudicated when consensus could not be reached. Reasons for exclusion at the full-text stage were recorded prospectively at the report level, and reports that could not be retrieved were documented. Because screening decisions were ultimately resolved by consensus, we emphasize the calibration procedures, locked decision fields, and documented decision rules as the most informative safeguards for reproducibility rather than relying on κ as a proxy for the final decision process [47].
Data extraction and management
Data extraction was performed independently by two reviewers using a standardized, piloted extraction form developed for this project. Data management was performed using locked templates with validation rules and an audit trail (e.g., timestamped versioning) to standardize entries, reduce transcription errors, and enable reproducible derivation of analysis datasets. Extracted items included study design, setting, participant characteristics and diagnostic criteria, intervention and comparator details (including reproducible parameters), follow-up schedule, and outcome data. When outcomes were presented only graphically, numeric values were extracted by figure digitization and recorded in the extraction log. When numerical outcome data were not reported in text or tables, we attempted reconstruction from graphs using digitization and from ancillary statistics such as confidence intervals, p values, or test statistics using prespecified formulas. If key numerical data remained unavailable after these steps, the outcome was coded as not extractable for quantitative synthesis, and the study was retained for evidence mapping and narrative synthesis within the relevant diagnosis and intervention family. Discrepancies were reconciled by consensus and, if needed, third-reviewer arbitration. To prevent double counting, multiple reports arising from the same trial (e.g., secondary analyses or extended follow-up publications) were linked and treated as a single study unit for quantitative synthesis; in such cases, the most complete dataset for each prespecified outcome and time window was prioritized, and longer-term follow-up results were extracted for durability analyses without duplicating participants. When multiple reports presented overlapping outcomes at similar timepoints, the report with the most complete outcome dataset and clearest analytic approach was prioritized, while additional reports were used to extract non-overlapping outcomes or longer follow-up without duplicating participants.
Data items and outcome handling
Outcome handling followed a prespecified construct-based framework to reduce multiplicity and avoid construct mixing in a literature with heterogeneous endpoint definitions. Outcomes were grouped into distinct families, with pain intensity as the primary domain, alongside pain interference or disability, pain relief or responder outcomes, and other patient-relevant domains, including jaw or oral function, QoL, global improvement, medication use, and safety. Quantitative synthesis prioritized pain intensity when available. Other constructs were synthesized within their own families and were not pooled with pain intensity. Mechanosensitivity outcomes were treated as a separate construct and were not pooled with self-reported pain intensity. When trials reported multiple pain intensity instruments within the same time window, selection followed a prespecified hierarchy: (i) trial-defined primary pain intensity outcome; (ii) NRS/VAS pain intensity; (iii) multidimensional instruments’ intensity subscore. If only pain interference/disability was reported (without an intensity measure), the study remained eligible but was synthesized within the interference/disability outcome family. For TN and other neuropathic facial pain phenotypes, paroxysm-related endpoints and attack frequency were treated as distinct constructs and were synthesized separately from average pain intensity to avoid implicit interchangeability across outcome types. Selection was implemented within each follow-up window and within each comparison to ensure that the same outcome definition (post-intervention or change-from-baseline) was available across arms. In such cases, the study contributed to the interference/disability family only and was not imputed into pain-intensity analyses, avoiding construct substitution. Additional outcomes, including jaw function and mastication-related endpoints, health-related QoL measures, patient global impression of change, analgesic consumption, and safety/adverse events, were extracted when available but were not required for eligibility. Follow-up times were grouped into clinically meaningful windows to distinguish short-term response from durability, based on each trial’s assessment schedule. Unless otherwise prespecified for a given modality, “short-term” was defined as immediate post-intervention up to 4 weeks, “mid-term” as > 4 to 12 weeks, and “long-term” as > 12 weeks. Because expected onset and durability may differ across modalities (e.g., device-based analgesia vs. biologic injectables), modality-specific sensitivity analyses explored alternative window definitions where this was clinically justified and consistently reported. When multiple assessments fell within a window, the assessment closest to the end of the window was selected to reduce selective timepoint bias; sensitivity analyses explored alternative choices when relevant. Adverse events were extracted verbatim as reported, including the number of participants experiencing any adverse event, serious adverse events when defined, and withdrawals due to adverse events. Extraction followed a structured template aligned with CONSORT harms recommendations, capturing whether adverse events were actively solicited or passively recorded, the severity framing when provided, and the denominators used for safety reporting. When adverse-event reporting was absent, this was coded as “not reported” rather than assumed absent, and when authors explicitly stated that no adverse events occurred, this was coded as “none reported” to preserve the distinction. For adverse events, denominators were defined as the number of participants who received at least one session or procedure when available, and otherwise the number randomized was used with the assumption documented.
Risk of bias assessment
Risk of bias for RCTs was assessed using the revised Cochrane risk-of-bias tool (RoB 2), applied across the five standard domains (bias arising from the randomization process, deviations from intended interventions, missing outcome data, measurement of the outcome, and selection of the reported result), leading to an overall judgment for each outcome within each study [48]. The selection of the reported result domain explicitly considered within-study multiplicity (multiple scales/timepoints/analyses). When a trial registry entry or methods paper was available, outcome/timepoint consistency was checked against those sources; otherwise, internal consistency within the article was assessed using the prespecified decision rules. Cross-over randomized trials were assessed using the same RoB 2 domain framework, with additional attention to design-specific threats (e.g., carryover, period effects, and washout adequacy) considered within the relevant standard domains, rather than introducing non-standard domains. In crossover RCTs, potential carryover and period effects were explicitly evaluated and reflected within standard RoB 2 domains: washout adequacy and evidence of carryover informed judgments on deviations from intended interventions and outcome measurement, while differential attrition across periods informed missing outcome data. Non-randomized studies, if present among included records, were assessed with ROBINS-I [49]. Risk-of-bias judgments were performed independently by two reviewers (AC and DM), with disagreements resolved by consensus and adjudication as needed. Furthermore, risk-of-bias judgments were recorded at the outcome level (not only at the study level) for the primary pain outcome and for safety outcomes when meta-analyzed and were incorporated into sensitivity analyses that excluded high-risk evidence. High-risk evidence was defined as an overall RoB 2 judgment of High for randomized trials and an overall ROBINS-I judgment of Serious or Critical for non-randomized studies.
Effect measures and data transformations
For continuous outcomes (e.g., pain intensity scales), treatment effects were summarized as mean differences (MD) when studies used the same scale, and as standardized mean differences (SMD; Hedges’ g) when different instruments were used to measure a conceptually similar outcome (e.g., pain intensity on VAS vs. NRS). When feasible, VAS/NRS pain scales were transformed to a common 0–10 metric to improve interpretability and minimize reliance on SMD. VAS reported on a 0-100 scale (including 0–100 mm) was converted to a 0–10 metric by dividing by 10. When scales were oriented in the opposite direction (higher scores indicating improvement), values were reversed prior to analysis to ensure consistent directionality. For dichotomous outcomes (e.g., adverse events), risk ratios (RR) with 95% confidence intervals (CI) were calculated; odds ratios (OR) were used when required by reporting constraints. Effect directions were harmonized so that negative values (for MD/SMD) indicated a reduction in pain (benefit), and RR/OR < 1 indicated fewer events in the intervention group where the event was undesirable. For continuous outcomes, effects were computed as (Intervention − Control), so that negative MD/SMD values indicate benefit after any necessary direction reversals. When studies reported outcomes as medians and interquartile ranges, or otherwise lacked sufficient dispersion metrics, standard conversion approaches recommended in the Cochrane Handbook were applied where assumptions were reasonable; otherwise, the study was synthesized narratively for that outcome [43]. If change-from-baseline scores were reported without accompanying standard deviations, standard deviations were derived from standard errors, confidence intervals, p values, or t statistics where possible. When derived from standard errors (SE), standard deviation (SD) was computed as SD = SE × √n. When derived from 95% CI around a mean, SE was computed as (Upper − Lower) / (2 × t_{df,0.975}) with df = n − 1, and SD = SE × √n. If dispersion could not be reconstructed using standard conversions, the study was not included in the base-case meta-analysis for that specific outcome and follow-up window. A prespecified sensitivity analysis then assessed the impact of conservative SD imputation, using the 75th percentile (Q3) of observed SDs among clinically comparable studies for the same outcome domain and follow-up window. For each meta-analysis, the number of contrasts using imputed SDs is reported, and complete-case and imputed pooled estimates are presented side-by-side. Where both post-intervention scores and change-from-baseline scores were available, post-intervention scores were preferred unless baseline imbalance was evident or change scores were the only consistently reported metric within a given comparison, in which case change scores were used. Score type (post-intervention vs. change-from-baseline) was recorded for each extracted outcome and applied consistently within each comparison and time window. In dental and OP research, within-person designs (e.g., split-mouth or other paired designs) were analyzed using paired methods when the necessary correlation structure was available and otherwise, conservative correlation-based approximations were applied and tested in sensitivity analyses to avoid unit-of-analysis errors. When imputation was unavoidable (e.g., deriving change-score SDs requiring within-participant correlation), a prespecified correlation of r = 0.5 was used, with sensitivity analyses at r = 0.25 and r = 0.75 [43].
Meta-analysis and synthesis plan
Quantitative synthesis was conducted when at least two studies were sufficiently comparable in population, intervention, comparator, outcome construct, and time window. When fewer than two studies contributed to a prespecified comparison, no pooled estimate was calculated and results were synthesized narratively for that outcome and follow-up window. Random-effects meta-analysis was used as the default approach to accommodate expected clinical and methodological heterogeneity across diagnoses and modalities. Between-study heterogeneity was quantified using τ² and the I² statistic, with I² interpreted as the proportion of variability due to heterogeneity rather than sampling error [50]. Meta-analyses were restricted to randomized comparisons, and non-randomized intervention studies did not contribute to pooled comparative-effect estimates. Between-study variance (τ²) was estimated using restricted maximum likelihood (REML) as the primary estimator. Analyses were conducted in R (packages meta and metafor). As a robustness check, selected pooled estimates were replicated in Stata (meta suite) when model convergence or sparse-data behavior warranted confirmation. Where informative, 95% prediction intervals were reported to convey the range of effects that may be expected across clinical settings. Prediction intervals were reported only when at least three independent studies contributed to a meta-analysis (n studies ≥ 3). Throughout, n studies denotes the number of unique studies contributing to a pooled estimate, k denotes the number of contrasts/effect estimates (which may exceed n studies in multi-arm trials), and N denotes total participants without double counting. Given the frequent presence of small trials, Hartung-Knapp-Sidik-Jonkman adjusted CI were used as the default for random-effects models, particularly when the number of studies per comparison was small; conventional random-effects intervals were reported only in sensitivity analyses where they materially differed [51]. When pooling was inappropriate due to extreme heterogeneity, incompatible outcome definitions, or insufficient data, results were synthesized narratively with structured reporting by diagnosis and intervention class. Multi-arm trials were handled to prevent double counting by combining clinically similar intervention arms or splitting shared comparator groups for variance estimation only. Crossover trials were analyzed using paired methods when within-person information was reported, and first-period results were prioritized when available to reduce carryover concerns [43]. If such data were not reported, analyses prioritized first-period results (when reported) to minimize carryover bias, or used conservative approximations with explicit sensitivity analyses. Splitting was used for variance calculation only; participant totals (N) were not inflated, and k may exceed the number of unique studies when multi-arm trials contribute more than one eligible contrast. Missing data were addressed by extracting intention-to-treat estimates when reported; where only completer analyses were available, this was documented and considered in risk-of-bias judgments and sensitivity analyses. Authors were contacted when key outcome data were missing and contact details were available; when data could not be obtained, the study was retained for qualitative synthesis. When meta-analysis was not appropriate, narrative synthesis followed a structured, prespecified grouping framework (by diagnosis, modality, comparator type, and time window), and results were summarized using consistent direction-of-effect rules to reduce interpretive flexibility.
Subgroup and sensitivity analyses
To support clinically meaningful interpretation, subgroup analyses were planned a priori by diagnosis and modality. Stratified reporting prioritized protocol features that are plausibly effect-modifying and that were sufficiently reported, including dosing schedule, delivery setting, and core technical parameters for device-based interventions. For PBM/LLLT, we recorded wavelength band, energy delivery metrics, number of sessions, treatment sites, and whether delivery was clinic-based or home-based, and sham comparators were distinguished from inactive usual-care controls because these contrasts address different estimands. For procedural and injectable interventions, synthesis was stratified by comparator class and procedure subtype when feasible, recognizing that sham procedures, saline injection, arthrocentesis-only pathways, and active pharmacologic comparators can lead to clinically non-exchangeable estimates. When quantitative subgroup pooling was not estimable because strata were too sparse, these features were reported in a standardized protocol-level narrative to support parameter-aware interpretation. Non-randomized studies were not used to upgrade certainty ratings and were not used to increase certainty for pooled comparative effect estimates. Accordingly, summary of findings tables and certainty judgments for comparative effects were based on randomized evidence, while non-randomized evidence was used only to contextualize feasibility, durability, and safety signals. They were used to map feasibility, durability, and safety signals when available, with ROBINS-I informing internal validity appraisal. To limit false-positive subgroup signals, subgroup analyses were conducted only when at least two studies were available per subgroup and were interpreted as hypothesis-generating unless a consistent interaction pattern was observed across outcomes and time windows. Diagnostic subgroups included TMD, BMS, TN and other trigeminal neuropathic pain syndromes, and mixed/other chronic OP populations. Intervention modality subgroups included PBM/LLLT, neuromodulation (e.g., repetitive Transcranial Magnetic Stimulation (rTMS), transcranial Direct Current Stimulation (tDCS), cranial electrotherapy stimulation), minimally invasive interventions and injectables (e.g., arthrocentesis, hyaluronic acid, platelet-rich plasma, BTX, prolotherapy), needling/manual therapy approaches, and psychological or integrative behavioral interventions (e.g., cognitive behavioral therapy (CBT), mindfulness, relaxation/biofeedback, multimodal biopsychosocial programs). Within TMDs, analyses were further stratified (where data allowed) by phenotype (muscular vs. joint-dominant; DC/TMD where reported) and by injectable/procedure subtype. Active comparators were grouped by comparator class when clinically heterogeneous, and results were pooled only when comparators were reasonably exchangeable; otherwise, synthesis followed a structured SWiM approach. Where data supported it, analyses were further stratified by follow-up window to distinguish short-term response from longer-term effects. Sensitivity analyses examined the robustness of pooled estimates to key assumptions and biases, including exclusion of studies judged at high risk of bias, alternative imputation choices for missing dispersion metrics, alternative handling of cross-over designs, and the use of MD versus SMD where scaling choices materially affected interpretability. When a sensitivity restriction (e.g., excluding high risk-of-bias evidence or omitting one study) reduced the remaining evidence to fewer than two studies (< 2 studies), the meta-analysis was reported as not estimable. In addition, fixed-effect inverse-variance models were fitted as a robustness check against the primary random-effects specification. Influence was evaluated using leave-one-out analyses, summarized as the range of pooled effects when each study was omitted in turn (reported when ≥ 3 studies). Leave-one-out analyses were performed at the study level, and if a multi-arm trial contributed more than one comparison, all comparisons from that study were removed together. A study was flagged as influential when omitting it changed the pooled effect estimate by ≥ 20% or changed whether the 95% CI excluded the null. For device-based and neuromodulation interventions, additional sensitivity analyses explored the influence of sham credibility (adequate sensory equivalence vs. unclear/inadequate) when sufficient studies were available.
Reporting bias and small-study effects
When at least 10 studies were available within a given meta-analysis, small-study effects and potential publication bias were assessed visually using funnel plots and statistically using Egger’s regression test, recognizing the limitations of these methods in the presence of heterogeneity and outcome-dependent reporting [52]. For meta-analyses with fewer than 10 studies, publication bias assessments were considered unreliable and were not emphasized. Where funnel plot asymmetry was suspected, we explored whether patterns were more consistent with heterogeneity or risk-of-bias differences than with selective publication alone, and we avoided definitive conclusions based on asymmetry tests in small evidence sets.
Certainty of evidence
The certainty of evidence for each major comparison and outcome was assessed using the Grading of Recommendations Assessment, Development and Evaluation (GRADE) approach, considering risk of bias, inconsistency, indirectness, imprecision, and publication bias [53]. GRADE assessments were performed independently by two reviewers (AC and DM) and reconciled by consensus, with explicit footnotes documenting the rationale for downgrading or upgrading decisions. When pain intensity could not be pooled but pain interference/disability could, separate GRADE ratings were produced for each outcome family to avoid indirectness through construct substitution. Evidence profiles and “Summary of Findings” tables were planned for key clinical comparisons within each diagnostic category, prioritizing pain-related outcomes as the minimum common endpoint while incorporating function, QoL, and safety when consistently available. Summary of Findings tables was generated separately by diagnosis and prioritized modality comparisons, with pain intensity as the primary outcome and adverse events as a co-primary safety endpoint when reported consistently. Where available, thresholds for clinical interpretability (e.g., minimal important differences reported in the OP literature) were used to contextualize imprecision, and when such thresholds were unavailable, we prioritized transparent reporting of absolute scale units and prediction intervals. Non-randomized studies were not used to upgrade certainty ratings and did not increase certainty for pooled comparative effects. Table 1 contains the methodology used for this systematic review and meta-analysis. Full reproducibility details, including software versions, imputation rules, and analytic syntax (R/Stata), are provided in supplementary material 2 (appendix S1).
Table 1.
Methodology schematic for the systematic review and meta-analysis on chronic or recurrent orofacial pain
| Section | Methodology | Details |
|---|---|---|
| Search Strategy | Databases and overall scope | Electronic searches were conducted in PubMed, Web of Science, Embase, EBSCOhost, the Cochrane Library, and Scopus. Backward reference checking and forward citation tracking were performed (39 reports), but they did not identify additional unique records beyond the database searches (n = 0). |
| Conceptual blocks | Search logic combined diagnosis/phenotype terms (temporomandibular disorders; burning mouth syndrome; trigeminal neuralgia and related facial pain syndromes) with intervention-family terms covering complementary, integrative, and advanced modalities. | |
| Search String 1 | String 1: (“temporomandibular disorder” OR “temporomandibular joint disorder” OR “temporomandibular dysfunction” OR “temporomandibular joint dysfunction” OR “TMJ disorder” OR TMD) AND (“low level laser” OR “laser therapy” OR photobiomodulation OR LLLT OR PRP OR “platelet rich plasma” OR botulinum OR “botulinum toxin” OR CBT OR “cognitive behavioral therapy”) AND (VAS OR “visual analogue scale” OR “numeric rating scale” OR arthralgia OR “jaw pain”); | |
| Search String 2 | String 2: (“burning mouth syndrome” OR glossodynia OR stomatodynia OR “burning mouth”) AND (“low level laser” OR “laser therapy” OR photobiomodulation OR LLLT OR clonazepam OR capsaicin OR “alpha lipoic acid” OR “alpha-lipoic acid” OR thioctic OR “thioctic acid”) AND (VAS OR “visual analogue scale” OR “numeric rating scale” OR burning); | |
| Search String 3 | String 3: (“trigeminal neuralgia” OR “painful trigeminal neuropathy” OR “post-traumatic trigeminal neuropathy” OR “trigeminal nerve injury” OR “trigeminal nerve injuries”) AND (botulinum OR “botulinum toxin” OR TENS OR “transcutaneous electrical nerve stimulation” OR rTMS OR “repetitive transcranial magnetic stimulation” OR tDCS OR “transcranial direct current stimulation” OR “pulsed radiofrequency” OR radiofrequency OR photobiomodulation OR “low level laser” OR “laser therapy” OR LLLT) AND (VAS OR “visual analogue scale” OR “numeric rating scale”). | |
| Search period and execution | The final search was executed on 31 December 2025. Searches were run from database inception without a priori date limits. English-language full texts were included at eligibility assessment to preserve appraisal and extraction accuracy. Grey literature and trial registries were not systematically searched. Whenever included trials reported a registration identifier or linked protocol, these sources were consulted to inform selective-reporting assessment. Database-specific search strategies and record counts are provided in Supplementary Material 2. | |
| Study Selection | Screening process and PRISMA 2020 | After deduplication, titles/abstracts and full texts were screened in duplicate against prespecified eligibility criteria. The selection process was reported using PRISMA 2020, with explicit reasons recorded for all full-text exclusions and reports not retrieved. Multiple reports of the same trial were linked and treated as a single study unit. |
| Inter-rater agreement and adjudication | Two independent reviewers conducted screening. Inter-rater agreement was quantified using Cohen’s kappa with 95% CI at both screening stages. Disagreements were resolved by consensus discussion and adjudication by a third senior reviewer when needed. | |
| Inclusion Criteria | Population and setting | Adults (≥ 18 years) with clinically diagnosed orofacial pain localized to the face, jaws, oral cavity, temporomandibular region, or trigeminal distribution. Eligible diagnostic entities included temporomandibular disorders, trigeminal neuropathic pain syndromes (including trigeminal neuralgia), burning mouth syndrome, and persistent idiopathic facial pain when framed as orofacial. |
| Exposure and comparator requirements | Eligible interventions comprised advanced modalities (e.g., device/energy-based therapies, neuromodulation, minimally invasive procedures/injectables) and complementary/integrative approaches (e.g., acupuncture and related needling, manual therapies, structured psychological interventions). Eligible comparators included sham/placebo, usual care, wait-list, and active comparators. | |
| Outcomes, designs, and other limits | Studies were eligible if they reported at least one extractable pain-related outcome at baseline and at a clearly defined follow-up time point using a validated or widely accepted instrument. Randomized and non-randomized designs in humans were eligible when reporting allowed clinically meaningful interpretation. Non-randomized studies were retained primarily to map feasibility, durability, or safety signals and were not used to upgrade certainty ratings. | |
| Exclusion Criteria | Setting and population exclusions | Acute odontogenic or procedural dental pain and non-orofacial primary pain phenotypes were excluded. Mixed samples were excluded when orofacial outcomes were not separable. Records without sufficient diagnostic framing to classify participants into eligible orofacial phenotypes were excluded at full-text review. |
| Intervention and outcome exclusions | Studies were excluded when intervention descriptions were insufficient for classification into prespecified modality families, when outcome measurement lacked interpretability, when follow-up timing was unclear, or when adverse-event reporting could not be attributed to the intervention period. | |
| Design, attribution, and data quality | Non-original publications and designs without a comparator were excluded when they could not support credible effect estimation. Studies were considered not extractable when numeric outcome data could not be obtained from text, tables, figures, supplements, or author contact. | |
| PICO Evaluation | Population | Adults (≥ 18 years) with clinically diagnosed chronic or recurrent orofacial pain. Prespecified condition strata included temporomandibular disorders, burning mouth syndrome, trigeminal neuralgia/trigeminal neuropathic pain, and persistent idiopathic facial pain when explicitly framed as orofacial. |
| Intervention | Prespecified intervention-family framework covering complementary/integrative and advanced modalities, including acupuncture and related needling, manual therapy/dry needling, photobiomodulation/ low-level laser therapy, neuromodulation (e.g., rTMS, tDCS, TENS/CES), and minimally invasive procedures/injectables (e.g., PRP, hyaluronic acid, prolotherapy, botulinum toxin), plus structured psychological or integrative programs when reported. | |
| Comparison | Sham/placebo, usual care, wait-list/no intervention, and active comparators. Comparator content (including sham credibility and contact-time balance) and background care/co-interventions were captured to support attribution, risk-of-bias judgments, and indirectness appraisal. | |
| Outcome | Outcome families were prespecified and extracted with consistent direction-of-effect rules: pain intensity, pain-related disability/interference, jaw function, quality of life, and safety when available. Follow-up time points were mapped to prespecified windows; a single preferred timepoint per window and effect metric per outcome family were selected using a priori decision rules to limit multiplicity and selective timepoint reporting. | |
| Setting, Delivery & Dose | Intervention delivery and dose parameters | Intervention parameters were extracted in reproducible fields (dose/session frequency and duration; device settings; procedural characteristics; therapeutic content; provider expertise when reported). Background care and co-interventions were recorded to inform deviations-from-intended-interventions judgments and indirectness considerations. |
| Comparator integrity and exposure quantification | Comparator conditions were characterized for interpretability (sham plausibility and sensory equivalence; usual-care content; active comparator content). Within-person and cross-over designs were flagged during extraction to ensure design-appropriate synthesis and to avoid unit-of-analysis errors. | |
| Data Extraction | Templates, items, and procedures | Two reviewers independently extracted data using a piloted template with version control and validation rules. Extracted items included diagnosis stratum, intervention family, comparator, follow-up timing/time-window classification, outcome definitions, and the summary statistics required for synthesis. Discrepancies were resolved by consensus and adjudication when required. |
| Comparators, outcomes, and analytic features | Outcome families were maintained as distinct constructs (pain intensity; pain interference/disability; jaw function; quality of life; safety). Scale direction was harmonized so that negative values for mean difference or standardized mean difference indicated pain reduction (benefit). Safety denominators were defined using the safety population when reported; otherwise, randomized participants were used and this assumption was documented. | |
| Risk of Bias & Tools | Risk-of-bias instruments | Randomized controlled trials were assessed using RoB 2 across the five standard domains with an overall judgment per outcome. Non-randomized intervention studies were assessed using ROBINS-I. Judgments were performed independently by two reviewers and resolved by consensus, with documentation retained for auditability and for use in sensitivity analyses. |
| Domains of bias and confounding | Assessment focused on randomization integrity, deviations from intended interventions (including blinding and adherence), missing outcome data, outcome measurement, and selective reporting. Cross-over randomized trials were assessed using standard RoB 2 domains, incorporating carryover and washout considerations within relevant domains. | |
| Registration & Reporting | Protocol registration and transparency | The review was registered in PROSPERO (CRD420251270501; 21 December 2025). The registration record served as the primary a priori specification of eligibility criteria, outcome families, follow-up windows, and synthesis rules. Pain intensity was prespecified as the primary outcome domain, with secondary patient-relevant domains and decision rules detailed in Supplementary Material 2 (Appendix S1). |
| Reporting standards | Reporting followed PRISMA 2020, and the completed checklist is provided in Supplementary Material (1) The PRISMA flow diagram is presented in the Results, and a document-level log of reports not retrieved and full-text exclusions is provided in Supplementary Material (2) Data-handling and analytic decision rules were reported to minimize analytic flexibility and enhance reproducibility. | |
| Meta-analysis and Synthesis Approach (SWiM) | Grouping and stratification of studies | Quantitative synthesis was conducted when at least two studies were sufficiently comparable in population, intervention, comparator, outcome construct, and time window. When pooling was inappropriate, narrative synthesis followed a structured SWiM framework with prespecified grouping by diagnosis, intervention class, comparator type, and time window. |
| Effect measures and direction-of-effect rules | Continuous outcomes were summarized as mean differences (MD) when the same scale was used and standardized mean differences (SMD; Hedges’ g) when different instruments measured the same construct. VAS reported on 0–100 (including 0–100 mm) was converted to 0–10 by dividing by 10 when feasible. Scale direction was harmonized so that negative MD/SMD indicated pain reduction (benefit). Dichotomous outcomes were summarized as risk ratios (RR) with 95% confidence intervals. | |
| Effect-size derivation, dispersion, and within-person designs | Standard deviations were derived from standard errors, confidence intervals, p values, or t statistics where possible. Post-intervention scores were preferred over change scores unless baseline imbalance was evident or change scores were the only consistently reported metric. Within-person and cross-over designs were analyzed using paired methods when within-person correlation was reported; otherwise, conservative correlation-based approximations were applied. When imputation of within-person correlation was required, a prespecified r = 0.50 was used with sensitivity analyses at r = 0.25 and r = 0.75. | |
| Meta-analysis model, heterogeneity, and inference | Random-effects meta-analysis was the default approach to accommodate expected clinical and methodological heterogeneity across diagnoses and modalities. Heterogeneity was quantified using τ² and I². Between-study variance (τ²) was estimated using restricted maximum likelihood as the primary estimator, with Paule–Mandel explored in sensitivity analyses when sparse evidence produced instability. Where informative, 95% prediction intervals were reported. Prediction intervals were reported only when at least three independent studies contributed to a meta-analysis (n studies ≥ 3). Hartung–Knapp–Sidik–Jonkman adjusted CI were used for random-effects models to improve inferential robustness in meta-analyses with few studies. | |
| Unit-of-analysis safeguards and complex trials | Multi-arm trials were handled to avoid double counting by combining clinically appropriate intervention arms or splitting shared comparator groups proportionally across comparisons. For cross-over trials, paired analyses were preferred; when paired data were unavailable, first-period results were prioritized when reported to minimize carryover bias, or conservative approximations were applied with explicit sensitivity analyses. When a study contributed more than one contrast to the same meta-analysis, dependence was addressed in sensitivity analyses using a study-clustered approach (e.g., robust variance estimation with small-sample correction or a three-level model), and results were compared with the primary analysis. | |
| Missing data and author contact | Intention-to-treat estimates were extracted when reported; where only completer analyses were available, this was documented and considered in risk-of-bias judgments and sensitivity analyses. Authors were contacted when key outcome data were missing and contact details were available; when data could not be obtained, the study was retained for qualitative synthesis, and non-extractability was documented. | |
| Reporting bias, small-study effects, and certainty | Small-study effects were explored when at least 10 studies were available within a meta-analysis using funnel plots and Egger’s regression test, recognizing limitations under heterogeneity. Certainty of evidence for pooled key outcomes was assessed using GRADE and linked explicitly to risk-of-bias judgments and synthesis limitations. Non-randomized evidence was not used to upgrade certainty ratings. | |
| Supplementary Methods (S2) | Software and reproducibility | Supplementary Material 2 (Appendix S1) reports software versions, data-harmonization and imputation rules, handling of multi-arm and cross-over designs, and reproducibility materials, including database-specific search strategies and PRISMA accounting. |
Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA); International Prospective Register of Systematic Reviews (PROSPERO); Population, Intervention, Comparison, Outcome (PICO); Risk of Bias 2 tool (RoB 2); Risk Of Bias In Non-randomized Studies - of Interventions (ROBINS-I); Synthesis Without Meta-analysis (SWiM); Repetitive transcranial magnetic stimulation (rTMS); Transcranial direct current stimulation (tDCS); Transcutaneous electrical nerve stimulation (TENS); Cranial electrotherapy stimulation (CES); Platelet-rich plasma (PRP); Visual analogue scale (VAS); Mean difference (MD); Standardized mean difference (SMD); Risk ratio (RR); Confidence interval (CI); Between-study variance (τ²); Inconsistency statistic (I²); R statistical computing environment (R)
Results
We searched six electronic databases (PubMed, Web of Science, Cochrane Library, Embase, EBSCOhost, and Scopus) and identified 6,587 records (PubMed n = 463; Web of Science n = 518; Cochrane Library n = 385; Embase n = 1,008; EBSCOhost n = 215; Scopus n = 3,998). After removing 2,218 duplicate records and 27 non-English articles, 4,342 records remained for screening. Title screening excluded 3,476 records, and abstract screening excluded a further 720 records. Full texts were sought for 146 reports, of which 7 could not be retrieved despite reasonable retrieval attempts (including database searches and author contact). Thus, 139 reports were assessed for eligibility, and 9 were excluded at full-text assessment. Overall, 130 studies were included in the review (Fig. 1) [54–183]. Citation searching identified 39 reports; 6 were not retrieved, and 33 were assessed for eligibility and excluded (out of scope n = 16; outcomes not eligible n = 17), yielding no additional included studies. A document-level log of reports not retrieved and full-text exclusions is provided in Supplementary Material 2 (Table S4).
Fig. 1.
PRISMA 2020 flow diagram of evaluated studies
Study characteristics and evidence map overview
The 130 included studies spanned five diagnostic strata, dominated by TMDs (n = 79), followed by BMS (n = 29) and TN (n = 19), while neuropathic or mixed facial pain cohorts (n = 1) and other facial pain phenotypes framed within chronic or recurrent OP (n = 2) were uncommon. Studies were conducted across 37 countries, with the largest contributions from Brazil (n = 22), China (n = 13), Turkey (n = 10), Spain (n = 9), the USA (n = 8), and India (n = 8). Most studies were parallel-group RCTs (n = 105), with fewer crossover RCTs (n = 9) and non-randomized intervention studies (n = 16). Interventions clustered into PBM/LLLT delivered in clinic-based and home-based protocols [69, 70, 73, 75, 89, 112, 113, 123, 145], manual therapy and dry needling strategies [56–58, 74, 95], acupuncture and related approaches [61, 68, 81, 129, 149], neuromodulation and electrotherapy (tDCS, rTMS, and transcutaneous electrical nerve stimulation (TENS) [55, 79, 86, 87, 110], injectables and intra-articular procedures including arthrocentesis-based pathways and biologic injectables [54, 66, 76, 80, 109, 120, 134, 136, 150, 156, 174], radiofrequency techniques targeting trigeminal pathways [121, 164, 169, 170], and digital therapeutics for TMD care [65]. Pain intensity was most commonly captured using VAS and less frequently NRS or BPI, while function and jaw-related outcomes and quality-of-life measures were reported less consistently across intervention families (Supplementary Table 3). Study-level details on outcome scales, time windows, extractability, and data reconstruction are reported in Supplementary Table 4, while Table 2 provides an evidence map summary of study characteristics.
Table 2.
Evidence-map summary of included study characteristics (n = 130)
| Diagnosis stratum (studies, n) | Common diagnostic framing | Sample size per study | Countries most represented (top contributors) | Study designs | Intervention categories evaluated | Outcome domains frequently reported | Clinical findings linked to pooled results |
|---|---|---|---|---|---|---|---|
| Temporomandibular disorders (n = 79) | DC/TMD and/or RDC/TMD; arthrogenous phenotypes often imaging-confirmed (MRI/CBCT). | Median N = 40 (range 12–395) | Brazil (n = 19), Turkey (n = 9), USA (n = 9) | Parallel RCTs (n = 65); Cross-over RCTs (n = 4); Non-randomized (n = 10) | PBM/LLLT; injectables and intra-articular procedures; neuromodulation/electrotherapy; acupuncture; manual/needling; behavioral/psychological; digital therapeutics (limited). | Pain intensity; jaw function (mouth opening) and disability/interference; mechanosensitivity (subset); quality of life and harms variably reported; harms often not reported. | Effects varied by modality and comparator. PBM/LLLT effects were often heterogeneous and imprecise, with prediction intervals crossing the null in several windows. Injectable and intra-articular procedures showed pooled pain reductions versus active comparators in some windows, while uncertainty persisted due to heterogeneity, comparator diversity, and risk-of-bias constraints. |
| Burning mouth syndrome (n = 29) | Primary BMS framed clinically (normal mucosa; exclusion of local/systemic causes); occasional ICHD-based definitions. | Median N = 42 (range 15–200) | Spain (n = 7), Brazil (n = 5), Croatia (n = 4) | Parallel RCTs (n = 25); Cross-over RCTs (n = 2); Non-randomized (n = 2) | PBM/LLLT; pharmacological agents and supplements; neuromodulation/electrotherapy; behavioral/psychological (limited). | Pain/burning intensity; quality of life; psychosocial/sleep outcomes (subset); harms inconsistently reported; harms often not reported. | PBM/LLLT showed the clearest pooled short-term pain reduction versus inactive control, while prediction intervals crossed the null, indicating uncertain transportability. Pharmacological agents and supplements yielded imprecise and heterogeneous pooled estimates across routes and dosing regimens. Harms reporting was frequently incomplete, limiting risk–benefit interpretation. |
| Trigeminal neuralgia (n = 19) | Classical/idiopathic TN per neurological diagnosis and/or ICHD; background pharmacotherapy common. | Median N = 45 (range 14–120) | China (n = 7), India (n = 3), Egypt (n = 2) | Parallel RCTs (n = 14); Cross-over RCTs (n = 2); Non-randomized (n = 3) | Radiofrequency procedures; botulinum toxin and other injectables; adjunct PBM/LLLT; neuromodulation (limited). | Pain intensity; attack frequency/responder outcomes; medication use (subset); harms variably reported; harms often not reported. | Evidence most frequently evaluated botulinum toxin and radiofrequency techniques, but quantitative synthesis was often limited by endpoint non-interchangeability and technique heterogeneity. Background pharmacotherapy was common and reporting of follow-up and harms varied across trials. Certainty remained constrained by small trials and variable reporting. |
| Neuropathic or mixed facial pain cohorts (n = 3) | Mixed facial pain cohorts (e.g., post-traumatic trigeminal neuropathic pain, persistent idiopathic facial pain, chronic facial pain) in specialist settings. | Median N = 30 (range 20–55) | Czech Republic (n = 1), Finland (n = 1), France (n = 1) | Parallel RCTs (n = 1); Cross-over RCTs (n = 1); Non-randomized (n = 1) | Neuromodulation protocols (mainly rTMS). | Pain intensity and related endpoints; disability/global improvement (study-specific); harms variably reported; harms often not reported. | Evidence was sparse and mainly evaluated neuromodulation protocols in small cohorts. Heterogeneous diagnoses and endpoints limited quantitative synthesis. Findings were best interpreted as evidence mapping signals and feasibility information. |
BMS, burning mouth syndrome; CBCT, cone-beam computed tomography; DC/TMD, Diagnostic Criteria for Temporomandibular Disorders; ICHD, International Classification of Headache Disorders; MRI, magnetic resonance imaging; PBM/LLLT, photobiomodulation or low-level laser therapy; RDC/TMD, Research Diagnostic Criteria for Temporomandibular Disorders; rTMS, repetitive transcranial magnetic stimulation; TMD, temporomandibular disorders; TN, trigeminal neuralgia
Outcome extractability and reporting completeness
Outcome reporting varied across conditions and modalities. Dispersion metrics were frequently missing, post-intervention values were not always numerically extractable, and several outcomes were reported only graphically or as within-group change supported mainly by p values [64, 71, 74, 77, 96, 101, 104, 106, 120, 124, 132, 139–141, 151, 153, 154, 159, 165, 177, 179–181]. These patterns reduced eligibility for quantitative synthesis in several clinically relevant domains and limited the stability of pooled estimates in some comparisons. Sensitivity diagnostics for eligible meta-analyses are reported in Supplementary Table 5. Safety reporting was inconsistent across the evidence base and frequently insufficient for risk–benefit interpretation. Safety outcomes were not reported in 37 of 130 included studies, including 25 of 79 TMD studies, 9 of 29 BMS studies, and 2 of 19 TN studies. When harms were reported, denominators were often unclear and studies rarely specified whether adverse events were actively solicited or passively recorded, which limits structured synthesis of tolerability and increases uncertainty when interventions are considered for repeated or longer-term use.
Quality of included studies – risk of bias
Across randomized trials, low overall risk of bias was uncommon, and most outcomes were judged as “some concerns” or “high risk,” with patterns that varied by modality and by the feasibility and credibility of sham procedures for self-reported pain. Non-randomized intervention studies were less frequent and were commonly judged at serious risk of bias, with confounding and incomplete reporting of background care and co-interventions as recurring limitations. Figs 2 and 3 summarize domain-level judgments and inform interpretation of both pooled estimates and narrative evidence mapping.
Fig. 2.
Risk of Bias (RoB) of included RCT studies (first part). A Risk of Bias (RoB) of included RCT studies (second part). B Risk of Bias (RoB) of included RCT studies (third part)
Fig. 3.
Cochrane Risk of Bias in Non-randomized Studies of Interventions (ROBINS-I)
RoB 2 (randomized trials)
Low overall risk of bias was uncommon, and “some concerns” and “high risk” judgments predominated across outcomes. Common limitations included incomplete reporting of sequence generation and allocation concealment in some trials [56, 69, 73], and the limited feasibility of participant and provider blinding in hands-on and behavioral interventions [56–58, 68, 103]. For technology-enabled interventions, reporting of sham procedures and blinding checks was often incomplete, particularly for PBM/LLLT and neuromodulation trials where sensory equivalence and credibility are important for interpretability of self-reported pain endpoints [73, 75, 89]. Concerns about selective reporting were frequent when multiple scales and time points were reported without prespecified prioritization and when reporting did not consistently distinguish primary from secondary outcomes, especially in smaller trials [69, 73, 89]. Missing outcome data and unclear intention-to-treat handling were more common in longer follow-up studies, with attrition details and handling of missingness not always reported in a way that allowed outcome-level appraisal [76, 121]. Several crossover RCTs provided limited information on washout adequacy and first-period results, which contributed to uncertainty in design-specific risk-of-bias judgments for some outcomes [120]. These limitations were particularly consequential for pain intensity outcomes because they are self-reported and sensitive to expectation effects and comparator credibility.
ROBINS-I (non-randomized intervention studies)
Non-randomized intervention studies were less frequent than randomized trials and were commonly judged to have a serious risk of bias. Confounding was the most frequent concern because allocation to intervention could reflect baseline prognosis, symptom duration, prior treatment exposure, comorbid distress, and clinician preference, and adjustment strategies were uncommon or insufficiently described [49]. Several studies also provided limited information on co-interventions and background care, which complicated attribution of observed changes to the index intervention when concurrent care could plausibly influence pain outcomes [49]. Selection bias was also frequent because recruitment often occurred in specialist settings and among treatment-seeking cohorts, and eligibility criteria and referral pathways were not always reported in a way that allowed clear assessment of representativeness [97, 114]. Outcome measurement and selective reporting concerns persisted because endpoints were largely self-reported, masking was limited, and prespecified analysis plans were often unavailable, particularly when multiple outcomes or time points were reported without a clearly defined hierarchy [49]. These judgments are summarized in Fig. 3 and were used to contextualize the narrative evidence map rather than to strengthen pooled comparative conclusions. As a result, within-group improvements in non-randomized cohorts are interpreted as feasibility and hypothesis-generating signals and are not treated as evidence of comparative effectiveness.
A phenotype-first map of the evidence: condition-stratified synthesis
The condition-stratified results below are organized by diagnosis and intervention family and are reported separately for inactive control and active comparator contrasts when these estimands are not clinically exchangeable. Pooled estimates are presented only for randomized comparisons judged sufficiently comparable for the same outcome construct and follow-up window, while non-randomized studies are summarized narratively within the evidence map. Within each diagnosis, pain intensity is reported first, followed by prespecified patient-relevant outcome families such as function, QoL, and safety, using consistent terminology and scale-orientation rules described in the Methods.
Burning mouth syndrome: photobiomodulation or low-level laser therapy, pharmacological agents, and supplements
In BMS, short-term pain intensity meta-analysis favored PBM/LLLT versus inactive control, with n = 3 studies contributing k = 6 effects across N = 200 participants (SMD − 0.81; 95% CI − 1.35 to − 0.27; I² = 33%). Trials contributing to this body of evidence included sham-controlled designs using clinic-based protocols and standardized pain scales [77, 82, 89, 145]. The 95% prediction interval crossed the null (− 1.80 to 0.17). Table 3; Fig. 4 summarize PBM/LLLT trials, comparators, dosing features, and key endpoints, including pain and QoL. PBM/LLLT protocols in this cluster varied in wavelength band, delivered dose, number of sessions, and application sites, and sham procedures differed in the extent to which sensory equivalence and credibility were described. Comparators were mainly sham or inactive controls, so the pooled estimate reflects an efficacy contrast under controlled conditions rather than comparative effectiveness against established active therapies. Because only three trials contributed to pain intensity pooling and parameters were not harmonized, quantitative subgroup analyses by dose or wavelength were not estimable. Protocol features and dosing schedules are therefore reported explicitly to support parameter-aware interpretation alongside the pooled mean and the prediction interval.
Table 3.
Primary meta-analyses summary. Each row reports one prespecified primary meta-analysis defined by condition × intervention family × comparator type × outcome domain × follow-up window. “n studies; k/N” indicates the number of unique studies (n), the number of included contrasts/comparisons (k), and the total number of participants contributing to that meta-analysis (N; not double-counted). Pooled effects are from the base-case random-effects model (τ² estimated by restricted maximum likelihood and Hartung–Knapp–Sidik–Jonkman adjusted confidence intervals). For continuous outcomes, effects are computed as (Intervention − Control) and oriented so that negative MD/SMD values favour the intervention (after any required direction reversals). Heterogeneity is summarised using I² and τ²
| Condition / population group | Intervention family | Comparison | Outcome | Follow-up window | Studies (n) / contrasts (k) / participants (N) | Model | Pooled effect (95% CI) | Heterogeneity (I²; τ²) |
|---|---|---|---|---|---|---|---|---|
| Burning mouth syndrome | Pharmacological/supplements | Pharmacological / supplements vs. inactive control | Pain intensity (SMD). | Mid-term | 3 studies; 4 contrasts; N = 144 | Random-effects (REML-HKSJ) | -0.29 (-1.31 to 0.73) [SMD] | I²=68%; τ²=0.29 |
| Burning mouth syndrome | Pharmacological/supplements | Pharmacological / supplements vs. inactive control | Pain intensity (SMD). | Short-term | 2 studies; 2 contrasts; N = 126 | Random-effects (REML-HKSJ) | -0.40 (-7.46 to 6.66) [SMD] | I²=86%; τ²=0.53 |
| Burning mouth syndrome | Photobiomodulation/low-level laser therapy | Photobiomodulation / low-level laser therapy vs. inactive control | Pain intensity (SMD). | Short-term | 3 studies; 6 contrasts; N = 200 | Random-effects (REML-HKSJ) | -0.81 (-1.35 to -0.27) [SMD] | I²=33%; τ²=0.08 |
| Burning mouth syndrome | Photobiomodulation/low-level laser therapy | Photobiomodulation / low-level laser therapy vs. inactive control | Quality of life (SMD). | Short-term | 2 studies; 5 contrasts; N = 156 | Random-effects (REML-HKSJ) | -0.82 (-1.42 to -0.21) [SMD] | I²=16%; τ²=0.03 |
| Temporomandibular disorders | Dry needling/manual therapy | Dry needling / manual therapy vs. active comparator | Jaw function (MD). | Mid-term | 3 studies; 7 contrasts; N = 221 | Random-effects (REML-HKSJ) | -1.94 (-5.97 to 2.08) [MD] | I²=83%; τ²=15.67 |
| Temporomandibular disorders | Dry needling/manual therapy | Dry needling / manual therapy vs. active comparator | Jaw function (MD). | Short-term | 5 studies; 9 contrasts; N = 336 | Random-effects (REML-HKSJ) | 2.11 (-1.40 to 5.62) [MD] | I²=97%; τ²=17.64 |
| Temporomandibular disorders | Injectables/intra-articular procedures | Injectables / intra-articular procedures vs. active comparator | Jaw function (MD). | Long-term | 7 studies; 11 contrasts; N = 221 | Random-effects (REML-HKSJ) | -0.32 (-1.95 to 1.32) [MD] | I²=33%; τ²=0.72 |
| Temporomandibular disorders | Injectables/intra-articular procedures | Injectables / intra-articular procedures vs. inactive control | Jaw function (MD). | Mid-term | 4 studies; 4 contrasts; N = 200 | Random-effects (REML-HKSJ) | -1.41 (-3.39 to 0.58) [MD] | I²=2%; τ²=1.00 |
| Temporomandibular disorders | Photobiomodulation/low-level laser therapy | Photobiomodulation / low-level laser therapy vs. inactive control | Jaw function (MD). | Short-term | 5 studies; 9 contrasts; N = 391 | Random-effects (REML-HKSJ) | 1.01 (-1.85 to 3.87) [MD] | I²=96%; τ²=13.13 |
| Temporomandibular disorders | Dry needling/manual therapy | Dry needling / manual therapy vs. active comparator | Pain intensity (SMD). | Mid-term | 3 studies; 7 contrasts; N = 221 | Random-effects (REML-HKSJ) | -0.31 (-1.17 to 0.55) [SMD] | I²=87%; τ²=0.72 |
| Temporomandibular disorders | Dry needling/manual therapy | Dry needling / manual therapy vs. active comparator | Pain intensity (SMD). | Short-term | 5 studies; 9 contrasts; N = 336 | Random-effects (REML-HKSJ) | -0.55 (-1.65 to 0.55) [SMD] | I²=92%; τ²=1.87 |
| Temporomandibular disorders | Injectables/intra-articular procedures | Injectables / intra-articular procedures vs. active comparator | Pain intensity (SMD). | Long-term | 9 studies; 13 contrasts; N = 272 | Random-effects (REML-HKSJ) | -0.46 (-0.85 to -0.08) [SMD] | I²=53%; τ²=0.19 |
| Temporomandibular disorders | Injectables/intra-articular procedures | Injectables / intra-articular procedures vs. active comparator | Pain intensity (SMD). | Short-term | 7 studies; 9 contrasts; N = 201 | Random-effects (REML-HKSJ) | -0.40 (-0.73 to -0.08) [SMD] | I²=7%; τ²=0.03 |
| Temporomandibular disorders | Injectables/intra-articular procedures | Injectables / intra-articular procedures vs. inactive control | Pain intensity (SMD). | Mid-term | 4 studies; 4 contrasts; N = 200 | Random-effects (REML-HKSJ) | -1.37 (-3.12 to 0.38) [SMD] | I²=92%; τ²=1.10 |
| Temporomandibular disorders | Injectables/intra-articular procedures | Injectables / intra-articular procedures vs. inactive control | Pain intensity (SMD). | Short-term | 4 studies; 4 contrasts; N = 200 | Random-effects (REML-HKSJ) | -0.88 (-2.00 to 0.23) [SMD] | I²=85%; τ²=0.43 |
| Temporomandibular disorders | Photobiomodulation/low-level laser therapy | Photobiomodulation / low-level laser therapy vs. inactive control | Pain intensity (SMD). | Mid-term | 3 studies; 3 contrasts; N = 82 | Random-effects (REML-HKSJ) | -0.91 (-3.47 to 1.65) [SMD] | I²=89%; τ²=0.94 |
| Temporomandibular disorders | Photobiomodulation/low-level laser therapy | Photobiomodulation / low-level laser therapy vs. inactive control | Pain intensity (SMD). | Short-term | 10 studies; 19 contrasts; N = 462 | Random-effects (REML-HKSJ) | -0.45 (-1.06 to 0.17) [SMD] | I²=88%; τ²=1.41 |
Random-effects model (RE); Restricted maximum likelihood (REML); Hartung–Knapp–Sidik–Jonkman adjustment (HKSJ); Confidence interval (CI); Number of studies (n); Number of contrasts/comparisons (k); Total participants (N); Mean difference (MD); Standardized mean difference (SMD); I-squared statistic (I²); Tau-squared (τ²)
Fig. 4.
Summary forest plot of the primary outcome (pain intensity): pooled primary meta-analyses. Each row reports the contrast, n/k/N (number of studies/number of effects/total participants), and the pooled standardized mean difference (SMD) with 95% CI from random-effects models. Negative values favour the intervention, whereas positive values favour the comparator (inactive controls such as placebo/sham/usual care/no intervention, or active controls, as specified in each row). ST/MT/LT indicate short-/medium-/long-term follow-up. Burning mouth syndrome (BMS); Temporomandibular disorders (TMD); Short-term (ST); Mid-term (MT); Long-term (LT); Standardized mean difference, Hedges’ g (SMD); Confidence interval (CI); Photobiomodulation/low-level laser therapy (PBM/LLLT); Pharmacological agents and/or supplements (Pharm/Supp); Dry needling (Dry need.)
QoL outcomes also favored PBM/LLLT at short-term follow-up, based on n = 2 studies contributing k = 5 effects across N = 156 participants (SMD − 0.82; 95% CI − 1.42 to − 0.21; I² = 16%). The 95% prediction interval crossed the null (− 1.70 to 0.06). Leave-one-out analyses indicated that omission of Spanemberg et al. 2015 yielded an estimate whose CI included the null [89]. Safety reporting permitted only limited synthesis. Short-term adverse events were uncommon and imprecisely estimated, with n = 2 studies contributing k = 2 effects (RR 0.55; 95% CI 0.30 to 1.00) [89, 145]. Across BMS trials, safety outcomes were not reported in 9 of 29 studies, which limits interpretation of tolerability even when short-term efficacy signals are observed.
Pharmacological and supplement interventions versus inactive control did not show stable pooled benefit for pain intensity. Short-term pooling was extremely imprecise, with n = 2 studies contributing k = 2 effects across N = 126 participants (SMD − 0.40; 95% CI − 7.46 to 6.66; I² = 86%). Mid-term pooling included n = 3 studies contributing k = 4 effects across N = 144 participants (SMD − 0.29; 95% CI − 1.31 to 0.73; I² = 68%). The 95% prediction interval was wide (− 2.99 to 2.41). This cluster included topical clonazepam regimens, oral clonazepam dosing protocols, and oral alpha-lipoic acid supplementation with variable doses and treatment durations [91, 92, 94, 108, 122, 175, 180]. Additional studies examined capsaicin rinses and Hypericum perforatum [90, 115]. Overall, sensitivity analyses supported the robustness of the primary meta-analytic findings (Table 4).
Table 4.
Sensitivity analyses of primary meta-analyses. This table tests robustness of each primary meta-analysis to prespecified analytic decisions. The base-case column reports the main random-effects model (REML with HKSJ). The “exclude high RoB” column re-estimates the pooled effect after removing studies judged high risk of bias (overall RoB 2 = High); if exclusion leaves n < 2, the result is reported as not estimable. The fixed-effect column provides an inverse-variance fixed-effect robustness check. The SD-imputation column applies the prespecified Conservative imputation when dispersion could not be reconstructed (using the third quartile, Q3, of observed SDs among clinically comparable studies within the same outcome domain and time window). The leave-one-out summary reflects study-level omission (all contrasts from a multi-arm study removed together) to show the range of pooled effects under influence diagnostics
| Primary meta-analysis | Base-case (REML-HKSJ) | Excluding high RoB studies | Fixed-effect | Including SD imputation (Q3) | Leave-one-out range (point estimate) |
|---|---|---|---|---|---|
| Burning mouth syndrome; Pharmacological / supplements; Inactive control; Pain intensity; Mid-term. | -0.29 (-1.31 to 0.73) [SMD] | -0.60 (-1.71 to 0.52) [SMD] | -0.26 (-0.63 to 0.11) [SMD] | -0.29 (-1.31 to 0.73) [SMD] | -0.60 to 0.29 |
| Burning mouth syndrome; Pharmacological / supplements; Inactive control; Pain intensity; Short-term. | -0.40 (-7.46 to 6.66) [SMD] | Not estimable (n < 2 after exclusion). | -0.50 (-0.90 to -0.11) [SMD] | -0.40 (-7.46 to 6.66) [SMD] | Not applicable (n < 3). |
| Burning mouth syndrome; Photobiomodulation / low-level laser therapy; Inactive control; Pain intensity; Short-term. | -0.81 (-1.35 to -0.27) [SMD] | -1.00 (-1.98 to -0.03) [SMD] | -0.76 (-1.09 to -0.43) [SMD] | -0.81 (-1.35 to -0.27) [SMD] | -1.00 to -0.47 |
| Burning mouth syndrome; Photobiomodulation / low-level laser therapy; Inactive control; Quality of life; Short-term. | -0.82 (-1.42 to -0.21) [SMD] | Not estimable (n < 2 after exclusion). | -0.81 (-1.20 to -0.42) [SMD] | -0.82 (-1.42 to -0.21) [SMD] | -1.16 to -0.46 |
| Temporomandibular disorders; Dry needling / manual therapy; Active comparator; Jaw function; Mid-term. | -1.94 (-5.97 to 2.08) [MD] | Not estimable (n < 2 after exclusion). | -3.26 (-4.66 to -1.85) [MD] | -1.94 (-5.97 to 2.08) [MD] | -4.13 to -0.74 |
| Temporomandibular disorders; Dry needling / manual therapy; Active comparator; Jaw function; Short-term. | 2.11 (-1.40 to 5.62) [MD] | Not estimable (n < 2 after exclusion). | 0.51 (0.31 to 0.72) [MD] | 2.11 (-1.40 to 5.62) [MD] | 0.49 to 3.00 |
| Temporomandibular disorders; Injectables / intra-articular procedures; Active comparator; Jaw function; Long-term. | -0.32 (-1.95 to 1.32) [MD] | -1.57 (-4.99 to 1.86) [MD] | -0.14 (-1.14 to 0.86) [MD] | -0.32 (-1.95 to 1.32) [MD] | -0.80 to 0.22 |
| Temporomandibular disorders; Injectables / intra-articular procedures; Inactive control; Jaw function; Mid-term. | -1.41 (-3.39 to 0.58) [MD] | -1.41 (-3.39 to 0.58) [MD] | -2.07 (-2.66 to -1.47) [MD] | -1.41 (-3.39 to 0.58) [MD] | -2.15 to 0.05 |
| Temporomandibular disorders; Photobiomodulation / low-level laser therapy; Inactive control; Jaw function; Short-term. | 1.01 (-1.85 to 3.87) [MD] | 2.46 (-5.98 to 10.89) [MD] | 0.11 (-0.42 to 0.64) [MD] | 1.01 (-1.85 to 3.87) [MD] | -1.03 to 1.90 |
| Temporomandibular disorders; Dry needling / manual therapy; Active comparator; Pain intensity; Mid-term. | -0.31 (-1.17 to 0.55) [SMD] | Not estimable (n < 2 after exclusion). | -0.57 (-0.82 to -0.32) [SMD] | -0.31 (-1.17 to 0.55) [SMD] | -0.72 to -0.12 |
| Temporomandibular disorders; Dry needling / manual therapy; Active comparator; Pain intensity; Short-term. | -0.55 (-1.65 to 0.55) [SMD] | Not estimable (n < 2 after exclusion). | -0.51 (-0.72 to -0.29) [SMD] | -0.55 (-1.65 to 0.55) [SMD] | -0.89 to -0.14 |
| Temporomandibular disorders; Injectables / intra-articular procedures; Active comparator; Pain intensity; Long-term. | -0.46 (-0.85 to -0.08) [SMD] | -0.70 (-1.21 to -0.19) [SMD] | -0.44 (-0.66 to -0.21) [SMD] | -0.46 (-0.85 to -0.08) [SMD] | -0.55 to -0.31 |
| Temporomandibular disorders; Injectables / intra-articular procedures; Active comparator; Pain intensity; Short-term. | -0.40 (-0.73 to -0.08) [SMD] | -0.37 (-0.89 to 0.15) [SMD] | -0.41 (-0.67 to -0.14) [SMD] | -0.40 (-0.73 to -0.08) [SMD] | -0.46 to -0.28 |
| Temporomandibular disorders; Injectables / intra-articular procedures; Inactive control; Pain intensity; Mid-term. | -1.37 (-3.12 to 0.38) [SMD] | -1.37 (-3.12 to 0.38) [SMD] | -1.68 (-2.00 to -1.36) [SMD] | -1.37 (-3.12 to 0.38) [SMD] | -1.66 to -0.87 |
| Temporomandibular disorders; Injectables / intra-articular procedures; Inactive control; Pain intensity; Short-term. | -0.88 (-2.00 to 0.23) [SMD] | -0.88 (-2.00 to 0.23) [SMD] | -1.15 (-1.44 to -0.86) [SMD] | -0.88 (-2.00 to 0.23) [SMD] | -1.11 to -0.49 |
| Temporomandibular disorders; Photobiomodulation / low-level laser therapy; Inactive control; Pain intensity; Mid-term. | -0.91 (-3.47 to 1.65) [SMD] | -0.91 (-3.47 to 1.65) [SMD] | -0.71 (-1.09 to -0.33) [SMD] | -0.91 (-3.47 to 1.65) [SMD] | -1.41 to -0.35 |
| Temporomandibular disorders; Photobiomodulation / low-level laser therapy; Inactive control; Pain intensity; Short-term. | -0.45 (-1.06 to 0.17) [SMD] | -0.40 (-1.26 to 0.46) [SMD] | -0.42 (-0.61 to -0.23) [SMD] | -0.45 (-1.06 to 0.17) [SMD] | -0.62 to -0.16 |
Random-effects model (RE); Fixed-effect model (FE); Restricted maximum likelihood (REML); Hartung–Knapp–Sidik–Jonkman adjustment (HKSJ); Confidence interval (CI); Standard deviation (SD); Third quartile (Q3); Risk of bias (RoB); Risk of Bias 2 tool (RoB 2); Risk Of Bias In Non-randomized Studies of Interventions (ROBINS-I); Inverse-variance (IV); Leave-one-out (LOO); Number of contrasts/comparisons (k); Total participants (N)
Narrative synthesis covered non-poolable modalities. Behavioral interventions and neuromodulation approaches were tested in small studies with heterogeneous protocols and limited replication, which limited quantitative integration [83, 85, 117]. Adverse event reporting across BMS interventions was often limited to brief narrative statements and frequently lacked explicit denominators or clarity on ascertainment, which restricts risk–benefit interpretation and limits structured comparison across agents and protocols [77, 89, 112, 117].
Temporomandibular disorders: technology-enabled therapies, manual and needling interventions, injectables, and adjunct modalities
TMD evidence spanned multiple phenotypes and intervention families. PBM/LLLT versus inactive control at short-term follow-up showed an imprecise pooled effect, with n = 10 studies contributing k = 19 effects across N = 462 participants (SMD − 0.45; 95% CI − 1.06 to 0.17; I² = 88%). The 95% prediction interval was wide (− 3.03 to 2.13). Trials varied by wavelength, dosing schedules, delivery approaches, and care setting, including home protocols [69, 70, 73, 75, 123]. Mid-term PBM/LLLT pooling remained uncertain, with n = 3 studies contributing k = 3 effects across N = 82 participants (SMD − 0.91; 95% CI − 3.47 to 1.65; I² = 89%), and the prediction interval was very wide (− 15.40 to 13.58) [73, 105, 123]. Interpretation of PBM/LLLT in TMDs is constrained by clinically meaningful heterogeneity in phenotype definitions and protocol delivery. Trials enrolled myofascial pain, arthralgia, disc displacement-related pain, or mixed phenotypes, and baseline symptom duration and background care differed across studies. PBM/LLLT protocols spanned red and near-infrared wavelengths with wide variation in irradiance, fluence, number of sessions, and application sites, and home-based delivery introduced additional adherence uncertainty in some studies. Comparator content also varied, ranging from sham light to usual care or co-interventions delivered in both arms. These differences are plausible effect modifiers and are consistent with wide prediction intervals that cross the null, so pooled means should be interpreted as averages rather than as guarantees of consistent benefit.
Dry needling and manual therapy trials were frequently conducted against active comparators. Short-term pain intensity pooling for dry needling versus comparators was imprecise, with n = 5 studies contributing k = 9 effects across N = 336 participants (SMD − 0.55; 95% CI − 1.65 to 0.55; I² = 92%), and the prediction interval crossed the null (− 3.97 to 2.87) [56–58, 129, 130]. Functional outcomes were variably reported and not consistently extractable across trials, which limited pooled conclusions even when pain intensity pooling was feasible [73, 75]. Heterogeneity in these trials was driven by variability in needling technique and target muscles, number and spacing of sessions, and the content and intensity of active comparator care.
Injectable and intra-articular procedures formed a heterogeneous subgroup spanning arthrocentesis-based pathways, hyaluronic acid, platelet concentrates, adjunct intra-articular medications, prolotherapy, and BTX [54, 66, 76, 80, 109, 120, 134, 135, 150, 156, 174]. Because these procedures represent distinct mechanisms and care pathways, pooled estimates should be interpreted as family-level summaries within the stated comparator class rather than as evidence that products or techniques are interchangeable.
Pooled pain intensity effects depended on comparator class. Inactive-control comparisons at short-term follow-up included n = 4 studies contributing k = 4 effects across N = 200 participants (SMD − 0.88; 95% CI − 2.00 to 0.23; I² = 85%; prediction interval − 4.11 to 2.34), while mid-term pooling also crossed the null (n = 4; k = 4; N = 200; SMD − 1.37; 95% CI − 3.12 to 0.38; I² = 92%; prediction interval − 6.48 to 3.75). Active-comparator comparisons showed pooled reductions at short-term (n = 7; k = 9; N = 201; SMD − 0.40; 95% CI − 0.73 to − 0.08; I² = 7%; prediction interval − 0.92 to 0.11) and long-term follow-up (n = 9; k = 13; N = 272; SMD − 0.46; 95% CI − 0.85 to − 0.08; I² = 53%; prediction interval − 1.49 to 0.56). Sensitivity and influence diagnostics for these meta-analyses, including scenarios where omission of a single study changes whether the CI includes the null, are reported in Supplementary Table 5. Safety synthesis was feasible for a subset of injectable comparisons at short-term follow-up and showed fewer events in intervention groups, with n = 3 studies contributing k = 3 effects (RR 0.84; 95% CI 0.72 to 0.98) [54, 66, 80]. Even in this subset, harms interpretation remains constrained by variable definitions and inconsistent reporting of safety denominators across trials.
Neuromodulation and electrotherapy adjuncts included TENS, tDCS, and rTMS, with limited replication and protocol diversity [55, 79, 86, 110]. Ultrasound-based therapies expanded modality breadth and added heterogeneity in exposure and outcome constructs [138, 162]. Digital therapeutics were evaluated in sham-controlled designs, but comparator content and endpoint frameworks differed from conventional trials, limiting harmonized pooling despite clinical relevance [65]. These clusters were summarized descriptively because protocol diversity, comparator content, and outcome frameworks were often non-exchangeable across trials, limiting harmonized pooling despite clinical relevance (see Table 5).
Table 5.
Heterogeneity and influence diagnostics for primary meta-analyses. For each primary meta-analysis, the table reports the base-case pooled effect from the random-effects model (τ² via REML with HKSJ confidence intervals), alongside heterogeneity (I² and τ²) and, where eligible, 95% prediction intervals computed only when ≥ 3 studies. Leave-one-out diagnostics are performed at the study level (i.e., if a multi-arm trial contributes more than one contrast, all contrasts from that study are removed together). A study is flagged as influential when omission changes the pooled estimate by the prespecified influence rule (material change in magnitude and/or whether the 95% CI crosses the null). For continuous outcomes, negative values are oriented to favour the intervention (Intervention − Control)
| Condition/population group | Intervention family | Comparison | Outcome | Follow-up window | N studies | k contrasts/N participants | Pooled effect (95% CI) | Heterogeneity (I²; τ²) | 95% prediction interval | Leave-one-out pooled effect range | Influential study (Author, year) | Robustness summary |
|---|---|---|---|---|---|---|---|---|---|---|---|---|
| Burning mouth syndrome | Pharmacological / supplements | Pharmacological / supplements vs. inactive control | Pain intensity (SMD) | Mid-term | 3 | 4 / 144 | -0.29 (-1.31 to 0.73) [SMD] | I²=68%; τ²=0.29 | -2.99 to 2.41 | -0.60 to 0.29 | Castillo-Felipe et al. 2022 [172], Heckmann et al. 2012 [89], López-Jornet et al. 2009 [105] | Sensitive; influential study detected |
| Burning mouth syndrome | Pharmacological / supplements | Pharmacological / supplements vs. inactive control | Pain intensity (SMD) | Short-term | 2 | 2 / 126 | -0.40 (-7.46 to 6.66) [SMD] | I²=86%; τ²=0.53 | Not applicable | Not applicable (n < 3) | Not applicable (n < 3) | Not applicable (n < 3) |
| Burning mouth syndrome | Photobiomodulation / low-level laser therapy | Photobiomodulation / low-level laser therapy vs. inactive control | Pain intensity (SMD) | Short-term | 3 | 6 / 200 | -0.81 (-1.35 to -0.27) [SMD] | I²=33%; τ²=0.08 | -1.80 to 0.17 | -1.00 to -0.47 | Garcia Martinez et al. 2024 [59], Spanemberg et al. 2015 [86] | Sensitive; influential study detected |
| Burning mouth syndrome | Photobiomodulation / low-level laser therapy | Photobiomodulation / low-level laser therapy vs. inactive control | Quality of life (SMD) | Short-term | 2 | 5/ 156 | -0.82 (-1.42 to -0.21) [SMD] | I²=16%; τ²=0.03 | -1.70 to 0.06 | -1.16 to -0.46 | Garcia Martinez et al. 2024 [59], Spanemberg et al. 2015 [86] | Sensitive; influential study detected |
| Temporomandibular disorders | Dry needling / manual therapy | Dry needling / manual therapy vs. active comparator | Jaw function (MD) | Mid-term | 3 | 7 / 221 | -1.94 (-5.97 to 2.08) [MD] | I²=83%; τ²=15.67 | -13.00 to 9.12 | -4.13 to -0.74 | Brochado et al. 2018 [127], Dunning et al. 2024 [54], Ferreira et al. 2024 [55] | Sensitive; influential study detected |
| Temporomandibular disorders | Dry needling / manual therapy | Dry needling / manual therapy vs. active comparator | Jaw function (MD) | Short-term | 5 | 9 / 336 | 2.11 (-1.40 to 5.62) [MD] | I²=97%; τ²=17.64 | -8.46 to 12.67 | 0.49 to 3.00 | Brochado et al. 2018 [127], Dunning et al. 2024 [54], Ferreira et al. 2024 [55], Yu et al. 2025 [126] | Sensitive; influential study detected |
| Temporomandibular disorders | Injectables / intra-articular procedures | Injectables / intra-articular procedures vs. active comparator | Jaw function (MD) | Long-term | 7 | 11 / 221 | -0.32 (-1.95 to 1.32) [MD] | I²=33%; τ²=0.72 | -2.72 to 2.09 | -0.80 to 0.22 | Abbadi et al. 2022 [51], Bayramoglu et al. 2023 [132], Jacob et al. 2022 [63], Cömert Kiliç et al. 2015 [153], Kilic et al. 2016 [77], Cömert Kılıç S. Does glucosamine et al. 2021 [131], Singh et al. 2021 [147] | Sensitive; influential study detected |
| Temporomandibular disorders | Injectables / intra-articular procedures | Injectables / intra-articular procedures vs. inactive control | Jaw function (MD) | Mid-term | 4 | 4 / 200 | -1.41 (-3.39 to 0.58) [MD] | I²=2%; τ²=1.00 | -7.03 to 4.21 | -2.15 to 0.05 | Louw et al. 2019 [73], Mathpati et al. 2024 [112] | Sensitive; influential study detected |
| Temporomandibular disorders | Photobiomodulation / low-level laser therapy | Photobiomodulation / low-level laser therapy vs. inactive control | Jaw function (MD) | Short-term | 5 | 9 / 391 | 1.01 (-1.85 to 3.87) [MD] | I²=96%; τ²=13.13 | -8.06 to 10.09 | -1.03 to 1.90 | Bertolucci et al. 1995 [125], Chamani et al. 2024 [128], Herpich et al. 2020 [72], Shousha et al. 2021 [140] | Sensitive; influential study detected |
| Temporomandibular disorders | Dry needling / manual therapy | Dry needling / manual therapy vs. active comparator | Pain intensity (SMD) | Mid-term | 3 | 7 / 221 | -0.31 (-1.17 to 0.55) [SMD] | I²=87%; τ²=0.72 | -2.68 to 2.06 | -0.72 to -0.12 | Brochado et al. 2018 [127], Dunning et al. 2024 [54], Ferreira et al. 2024 [55] | Sensitive; influential study detected |
| Temporomandibular disorders | Dry needling / manual therapy | Dry needling / manual therapy vs. active comparator | Pain intensity (SMD) | Short-term | 5 | 9 / 336 | -0.55 (-1.65 to 0.55) [SMD] | I²=92%; τ²=1.87 | -3.97 to 2.87 | -0.89 to -0.14 | García-de la-Banda-García et al. 2023 [53], Brochado et al. 2018 [127], Ferreira et al. 2024 [55], Yu et al. 2025 [126] | Sensitive; influential study detected |
| Temporomandibular disorders | Injectables / intra-articular procedures | Injectables / intra-articular procedures vs. active comparator | Pain intensity (SMD) | Long-term | 9 | 13 / 272 | -0.46 (-0.85 to -0.08) [SMD] | I²=53%; τ²=0.19 | -1.49 to 0.56 | -0.55 to -0.31 | Abbadi et al. 2022 [51] | Sensitive; influential study detected |
| Temporomandibular disorders | Injectables / intra-articular procedures | Injectables / intra-articular procedures vs. active comparator | Pain intensity (SMD) | Short-term | 7 | 9 / 201 | -0.40 (-0.73 to -0.08) [SMD] | I²=7%; τ²=0.03 | -0.92 to 0.11 | -0.46 to -0.28 | Abbadi et al. 2022 [51], Karadayi et al. 2021 [171], Zarate et al. 2020 [130] | Sensitive; influential study detected |
| Temporomandibular disorders | Injectables / intra-articular procedures | Injectables / intra-articular procedures vs. inactive control | Pain intensity (SMD) | Mid-term | 4 | 4 / 200 | -1.37 (-3.12 to 0.38) [SMD] | I²=92%; τ²=1.10 | -6.48 to 3.75 | -1.66 to -0.87 | Ernberg et al. 2011 [145], Kim et al. 2023 [106], Mathpati et al. 2024 [112] | Sensitive; influential study detected |
| Temporomandibular disorders | Injectables / intra-articular procedures | Injectables / intra-articular procedures vs. inactive control | Pain intensity (SMD) | Short-term | 4 | 4 / 200 | -0.88 (-2.00 to 0.23) [SMD] | I²=85%; τ²=0.43 | -4.11 to 2.34 | -1.11 to -0.49 | Ernberg et al. 2011 [145], Mathpati et al. 2024 [112] | Sensitive; influential study detected |
| Temporomandibular disorders | Photobiomodulation / low-level laser therapy | Photobiomodulation / low-level laser therapy vs. inactive control | Pain intensity (SMD) | Mid-term | 3 | 3 / 82 | -0.91 (-3.47 to 1.65) [SMD] | I²=89%; τ²=0.94 | -15.40 to 13.58 | -1.41 to -0.35 | Emshoff et al. 2008 [102], Monteiro et al. 2020 [70] | Sensitive; influential study detected |
| Temporomandibular disorders | Photobiomodulation / low-level laser therapy | Photobiomodulation / low-level laser therapy vs. inactive control | Pain intensity (SMD) | Short-term | 10 | 19 / 462 | -0.45 (-1.06 to 0.17) [SMD] | I²=88%; τ²=1.41 | -3.03 to 2.13 | -0.62 to -0.16 | Bertolucci et al. 1995 [125], Chamani et al. 2024 [128], Shousha et al. 2021 [140] | Sensitive; influential study detected |
Meta-analysis (MA); Random-effects model (RE); Restricted maximum likelihood (REML); Hartung–Knapp–Sidik–Jonkman adjustment (HKSJ); Confidence interval (CI); I-squared statistic (I²); Tau-squared (τ²); Prediction interval (PI); Leave-one-out (LOO); Standardized mean difference (SMD); Mean difference (MD); Number of contrasts/comparisons (k); Total participants (N)
Trigeminal neuralgia and neuropathic or mixed facial pain: pharmacological, neuromodulation, and procedural interventions
TN and other neuropathic or mixed facial pain studies targeted trigeminal and related pathways, but pooling was often restricted by diagnostic and endpoint heterogeneity. BTX type A was evaluated in double-blind placebo-controlled RCTs that varied by dose, background pharmacotherapy control, and endpoint choice [88, 90, 96, 183]. Differences in attack frequency outcomes versus average pain intensity outcomes reduced comparability even within the same intervention family. To preserve construct validity, attack frequency, pain intensity, and responder outcomes were treated as separate outcome families and were not pooled across constructs even when interventions appeared similar. Adjunct PBM/LLLT approaches for TN expanded modality coverage but varied in background medication control and dosing parameters, which limited harmonized quantitative synthesis [59, 63]. Neuromodulation evidence included patient-administered tDCS and rTMS protocols, with heterogeneity in targets, dosing, maintenance strategies, and adherence verification [67, 84, 87].
Procedural interventions were increasingly represented. Radiofrequency approaches included randomized and prospective designs, but technique variation in target site, puncture trajectory, and conventional versus pulsed parameters limited cross-study pooling [124, 167, 172, 173]. Safety reporting in neuropathic and procedural studies was variably defined and often lacked explicit denominators, which restricted structured harms synthesis and limits risk–benefit interpretation for interventions that may be repeated or entail tissue injury. Safety outcomes were not reported in 2 of 19 TN studies, and even when reported, ascertainment methods were rarely described. Table 6 summarizes data provenance and analytical handling summary across included studies and extracted outcomes.
Table 6.
Data provenance and analytical handling summary across included studies and extracted outcomes. This audit-style table summarises extraction and analytic handling decisions that affect quantitative synthesis (e.g., variance reconstruction, digitisation, multi-arm and cross-over handling, and outcome scale diversity). “Observed frequency” reports counts drawn from the meta-analysis extraction workbook under the prespecified rules; denominators May differ across rows because some items apply only to the subset of studies contributing extractable quantitative outcomes (e.g., variance-related items) rather than all included studies. The pain-scale diversity row lists the number of distinct pain intensity scale units encountered among extracted records and highlights the most frequent units to justify MD vs. SMD selection and harmonisation
| Item | Operational definition / rule | Observed frequency |
|---|---|---|
| Included studies | Total number of eligible studies included in the systematic review. | 130. |
| Planned pairwise comparisons | Unique intervention–control contrasts prespecified for quantitative synthesis. | 170 comparisons across 130 studies. |
| Multi-arm studies | Studies contributing more than one prespecified contrast; shared comparator groups were handled via control-group splitting for variance calculations. | 30 studies. |
| Cross-over designs | Studies with a cross-over design requiring prespecified unit-of-analysis handling. | 8 studies. |
| Primary meta-analyses performed | Distinct primary meta-analyses (condition × intervention family × comparator type × outcome × follow-up window). | 17 meta-analyses. |
| Effect metric selection | MD used when a common scale/unit was available; SMD used when outcomes were measured on different scales. | 12/17 meta-analyses used SMD; 5/17 used MD. |
| Substantial heterogeneity | Meta-analyses with I²>50% (reported alongside τ²). | 12/17 meta-analyses (I²>50%). |
| Prediction interval eligibility | 95% prediction intervals computed only when at least three independent studies contributed to the meta-analysis. | 15/17 meta-analyses (≥ 3 studies). |
| Variance directly available | At least one extracted outcome record reported Mean with SD (or an equivalent SD-reporting form). | 89/118 studies. |
| Variance reconstructed | At least one extracted record required variance reconstruction (e.g., SD derived from SE/SEM or other convertible statistics). | 9/118 studies. |
| Digitized continuous data | At least one extracted record was digitized from figures where numerical values were not directly tabulated. | 4/118 studies. |
| Non-reconstructable variance | At least one extracted record lacked reconstructable dispersion statistics and was excluded from the base-case (eligible for SD-imputation sensitivity). | 15/118 studies. |
| Pain intensity scale diversity | Number of distinct self-reported pain intensity scales/encodings; mechanosensitivity outcomes (e.g., pressure pain threshold) were tracked separately. | 40 distinct scales/units. Top self-reported pain intensity scales/encodings: VAS (0–10) (n = 593), NRS (0–10) (n = 111), 0–10 (n = 64), VAS/NRS (0–10) (n = 47). Mechanosensitivity measures were extracted separately (e.g., pressure pain threshold in kg/cm²; n = 58). |
| RoB-exclusion estimability | Meta-analyses where excluding high RoB studies yielded < 2 contributing studies, precluding re-estimation in sensitivity analyses. | 6/17 meta-analyses. |
Mean difference (MD); Standardized mean difference (SMD); Standard deviation (SD); Standard error (SE); Standard error of the mean (SEM); Visual analogue scale (VAS); Numeric Rating Scale (NRS); Risk of bias (RoB); Risk of Bias 2 tool (RoB 2); I-squared statistic (I²); Tau-squared (τ²); Prediction interval (PI); Number of contrasts/comparisons (k); Total participants (N)
Discussion
Integrated synthesis of the evidence base and key findings
This systematic evidence map with selective meta-analyses synthesizes 130 interventional studies across major chronic or recurrent OP phenotypes [41]. The evidence base is uneven across diagnoses and intervention families and is shaped by variability in diagnostic framing, intervention delivery, follow-up timing, and outcome selection. These features limit the extent to which pooled estimates can be generalized without qualification, even when a statistically favorable pooled mean is observed. The analysis therefore prioritizes diagnosis-stratified interpretation and preserves construct separation across outcome families, consistent with the prespecified framework [41, 43].
A consistent pattern across conditions is the predominance of pain intensity endpoints, while patient-relevant outcomes beyond pain intensity, including function, QoL, and harms, are less consistently reported. This imbalance reduces the interpretability of effect estimates when clinical meaning depends on participation, jaw use, daily functioning, and tolerability. Variability in reporting quality also shaped extractability and the feasibility of quantitative synthesis, which contributed to reliance on standardized effect metrics in several comparisons and reduced translation into absolute units [43]. These constraints are important for interpreting both pooled and narrative findings.
Within this landscape, the clearest pooled short-term signal emerged for PBM/LLLT in BMS versus inactive control [77, 89, 145]. Trials in TMDs and TN were more heterogeneous in protocol structure, comparator content, and endpoint choice, which frequently limited pooling or reduced the stability of pooled inference [69, 73, 75, 88, 90, 96]. Non-randomized intervention studies were uncommon and were used primarily to map feasibility, durability, and safety signals, rather than to upgrade certainty or to strengthen pooled comparative-effect conclusions [49, 53]. Keeping these studies in the evidence map reduces the risk that absence of randomized evidence is misinterpreted as absence of clinical use or feasibility, while design-stratified synthesis avoids strengthening comparative claims on potentially confounded data.
Interpreting pooled effects, prediction intervals, and clinical implications in a heterogeneous evidence base
Between-study heterogeneity is central to interpreting pooled results in chronic or recurrent OP. Confidence intervals quantify uncertainty around the pooled mean effect, while prediction intervals incorporate between-study heterogeneity and describe the range of effects that may be expected in a new setting similar to those represented in the meta-analysis [43, 50, 51]. When prediction intervals cross the null, the true effect in some comparable settings could be close to no effect, even if the pooled mean favors the intervention. This distinction is particularly important in evidence bases where protocols differ meaningfully across trials, because transportability can be limited by parameter selection, delivery context, comparator content, phenotype definitions, baseline severity, symptom duration, and background care. In TMDs, heterogeneity is expected because trials often mix myogenous and arthrogenous phenotypes and frequently combine the index modality with splints, exercises, or other background care that varies across settings. Under these conditions, pooled estimates should be interpreted as averages across the included settings rather than guarantees of consistent benefit in every context, and statistically significant pooled means should not be treated as direct clinical recommendations when certainty is low or heterogeneity is substantial [43, 50, 51].
A condition-stratified view helps translate statistical signals into practical interpretation while preserving uncertainty. In BMS, pooled short-term effects for PBM/LLLT versus inactive control support a potential analgesic signal, yet prediction intervals cross the null, and follow-up is often short-term, which limits conclusions about transportability and durability [77, 89, 112, 113, 145]. These findings support cautious, parameter- and protocol-aware interpretation rather than general claims of effectiveness. For pharmacological agents and supplements in BMS, pooled estimates are highly imprecise and heterogeneous across active agents, routes, and dosing regimens, and the current evidence is best characterized as limited and inconsistent rather than definitively negative [41, 92, 94, 108, 122, 175, 180]. In TMDs, pooled effects vary by intervention family and comparator class, with frequent heterogeneity and sensitivity to individual trial contributions, which reduces confidence in escalation-style conclusions when comparator content and co-interventions differ across studies [43, 69, 73, 75, 80]. For TN and related neuropathic or mixed facial pain phenotypes, synthesis is often constrained by endpoint non-interchangeability, because attack frequency, average pain intensity, and responder thresholds capture distinct clinical constructs, while procedural studies add further heterogeneity through technique and follow-up variation [88, 90, 96, 124, 167, 173]. Taken together, these patterns support a practical approach in which clinical interpretation prioritizes diagnosis-stratified decision-making, explicit endpoint selection, cautious translation of pooled averages when prediction intervals cross the null, and an emphasis on standardized outcomes, longer follow-up, and transparent harms reporting to enable durable, patient-relevant inferences.
Clinical translation map: matching phenotype to dose, timing, and patient-relevant endpoints
Clinical implications should be framed as conditional on the stability and transportability of statistical signals rather than as class-level recommendations when certainty is limited. For BMS, PBM/LLLT shows the clearest short-term pooled signal versus inactive control, but prediction intervals crossing the null indicate that benefit may not be reproduced uniformly across settings with different parameters and delivery protocols [77, 89, 112, 113, 145]. This supports a parameter- and protocol-aware interpretation and highlights durability as a central unresolved issue given the predominance of short-term follow-up in the available trials [112, 113].
For pharmacological agents and supplements in BMS, pooled estimates are imprecise and heterogeneous across active agents, routes of administration, dosing regimens, and treatment durations, which limits stable inference and reduces the appropriateness of broad clinical generalizations [41, 92, 94, 108, 122, 175, 180]. Endpoint hierarchies and responder definitions would improve interpretability and reduce dependence on multiple exploratory outcomes [41].
For TMDs, clinical interpretation is constrained by frequent heterogeneity and sensitivity of several pooled comparisons to individual trial contributions, especially where comparator content and co-interventions vary across studies [43, 69, 73, 75, 80]. This pattern supports a cautious approach that prioritizes phenotype definition, clarity on comparator content, and patient-relevant outcomes beyond pain intensity, including function and tolerability, when planning treatment pathways.
Incomplete harms reporting limits shared decision-making across intervention families, particularly for procedures and injectables where uncommon but clinically important events may not be captured in small trials. Absence of reported adverse events should not be interpreted as evidence of safety when denominators and ascertainment methods are unclear. This gap is clinically relevant when patients consider repeated sessions or escalation to invasive options, because long-term functional sequelae and tolerability often drive real-world adherence.
For TN and related neuropathic or mixed facial pain phenotypes, clinical translation is further limited by endpoint non-interchangeability and technique diversity. Trials often measure distinct constructs such as attack frequency, average pain intensity, and responder thresholds, while procedural studies vary in technique parameters and follow-up structure [88, 90, 96, 124, 167, 173]. Practical interpretation therefore requires explicit endpoint selection aligned to the clinical construct of interest and careful avoidance of implicit interchangeability across outcome types.
Contextualization with existing guidance and prior syntheses
Existing guidance in OP management emphasizes conservative biopsychosocial foundations for TMD-related pain and frames minimally invasive procedures within a broader continuum for TMJ pain and dysfunction. This perspective aligns with the evidence-map pattern observed here, where comparative evidence for adjunct and technology-enabled interventions is uneven, follow-up is frequently short-term, and outcomes beyond pain intensity are inconsistently captured. The present evidence map adds value by integrating diagnosis-stratified signals across intervention families while maintaining a clear separation between statistical signals and clinical implications when certainty is low [21–23].
Prior umbrella-level work has also highlighted that prevalence and burden estimates are sensitive to diagnostic framing and verification procedures, which reinforces the importance of phenotype clarity when interpreting comparative trials across OP conditions. In turn, this sensitivity supports a diagnosis-stratified approach to synthesis and interpretation, rather than relying on broad cross-condition comparisons as if diagnoses were fully interchangeable [6].
In relation to modality-specific syntheses, the present review differs by mapping multiple intervention families across multiple OP phenotypes using prespecified outcome families and selective pooling. This structure allows readers to identify where evidence is concentrated and where it remains sparse, and it clarifies that clinical translation should be driven by the stability and transportability of signals rather than by pooled means alone. This approach is consistent with contemporary standards for transparent synthesis in heterogeneous evidence bases [41, 43].
“Reality check in high definition”: strengths and limitations of this systematic review and meta-analysis
Interpretation is constrained by several limitations that affect transportability and long-term inference. Follow-up was predominantly short-term, and longer-term conclusions were frequently limited by attrition and incomplete timepoint reporting. Outcome heterogeneity was substantial, with variable scales and reporting formats that reduced pooling feasibility and often required standardized effect metrics. Several evidence clusters showed wide between-study variability, null-crossing prediction intervals, or sensitivity to individual studies, which limits confidence in generalizing pooled averages. Many meta-analyses included fewer than 10 studies, so assessments of small-study effects are underpowered and should be interpreted cautiously.
PRISMA-aligned reporting was strengthened by providing a document-level log of reports not retrieved and full-text exclusions. Citation tracking was implemented but did not identify additional unique records beyond database searching, and residual dissemination-bias risk is therefore addressed mainly through cautious interpretation and certainty assessment. English-language restriction and incomplete capture of unpublished evidence may further increase this risk in sparse evidence clusters.
Internal validity constraints were common across intervention families, and non-randomized intervention studies were used only to support evidence mapping and to explore feasibility, durability, and safety signals, not to upgrade certainty or strengthen pooled comparative conclusions. Harms reporting remained inconsistent, and missing denominators limited risk–benefit synthesis. When adverse events were not described, they were coded as “not reported” rather than assumed absent, improving transparency while underscoring residual uncertainty. Safety outcomes were not reported in 37 of 130 included studies, including 25 of 79 TMD studies and 9 of 29 BMS studies, which materially limits inference on tolerability even in clusters with favorable pooled mean effects.
Several design choices strengthened transparency and reduced analytic flexibility. Eligibility criteria were anchored to established taxonomies, prespecified construct families, and time-window rules limited construct substitution, and sensitivity diagnostics characterized robustness when pooling was feasible. Random-effects models and heterogeneity-aware interpretation were prioritized, and prediction intervals were reported when estimable to support transportability-focused interpretation. Certainty was evaluated with explicit downgrading logic and supporting decision records, but residual uncertainty remains substantial in clusters characterized by short follow-up, heterogeneous outcomes, and incomplete harms reporting (see supplementary Table 6).
Blueprints for the next generation: standardising dose, endpoints, and pathways
Future trials should prioritize standardized outcome sets that include function, QoL, and harms alongside pain intensity, and prespecify endpoint hierarchies to reduce multiplicity and improve comparability [41]. Follow-up should be extended to address durability and safety, and harms reporting should include explicit denominators and clear definitions to enable pooled harms synthesis and risk–benefit interpretation [49]. For TN and related neuropathic facial pain phenotypes, trials should prespecify whether the primary construct is attack frequency, average pain intensity, or a responder threshold, and should report these constructs with compatible time windows to improve comparability without construct substitution. Comparator credibility should be reported explicitly, particularly for sham-controlled designs, and blinding checks should be reported when feasible because control validity influences interpretability of self-reported endpoints [48].
For PBM/LLLT, reproducible reporting of key parameters remains essential, including wavelength, irradiance, fluence, spot size, exposure time, sites, and schedules [69, 73, 75, 89]. For neuromodulation, targets, dosing schedules, adherence verification, and maintenance strategies should be reported consistently to improve replication and interpretability [55, 86, 110]. Procedural interventions would benefit from standardized technique descriptors and harmonized follow-up frameworks to improve cross-study comparability [124, 167, 173]. Adequately powered RCTs with transparent reporting will be essential to support diagnosis-stratified care and shared decision-making across OP phenotypes [41, 43, 53].
Conclusion
Comparative evidence from 130 interventional studies on chronic or recurrent OP remains heterogeneous across diagnoses, intervention families, and outcome frameworks. PBM/LLLT in BMS showed a pooled short-term reduction in pain versus inactive control, while prediction intervals crossed the null, indicating uncertainty in transportability across settings. Evidence for pharmacological agents and supplements in BMS was inconsistent and imprecise, with limited stability across agents, routes, and dosing regimens. In TMDs, pooled effects varied by modality and comparator, and several estimates were imprecise or highly heterogeneous, which limits confidence in broad class-level conclusions. For injectables and intra-articular procedures, pooled reductions versus active comparators were observed in some follow-up windows, but uncertainty remains due to heterogeneity, variable comparators, and risk-of-bias constraints. In TN and other neuropathic or mixed facial pain phenotypes, the evidence base is clinically important but often difficult to pool because trials use non-interchangeable endpoints and heterogeneous procedural techniques. Non-randomized evidence broadened the evidence map and informed feasibility, durability, and safety signals, but it did not contribute to pooled comparative estimates, and incomplete harms reporting remains a major barrier to confident risk–benefit assessment across modalities. Future research should prioritize adequately powered RCTs with longer follow-up, prespecified endpoint hierarchies, and standardized outcome sets that include function, QoL, and harms with explicit denominators. Trials should report intervention parameters and comparator content transparently and should support diagnosis-stratified inference to improve clinical interpretability and shared decision-making.
Supplementary Information
Below is the link to the electronic supplementary material.
Acknowledgements
None.
Abbreviations
- BMS
Burning Mouth Syndrome
- BPI
Brief Pain Inventory
- BTX
Botulinum Toxin
- CBT
Cognitive Behavioral Therapy
- CI
Confidence Interval
- DC
Diagnostic Criteria
- DC/TMD
Diagnostic Criteria for Temporomandibular Disorders
- df
Degrees of Freedom
- DOI
Digital Object Identifier
- Emtree
Embase subject headings (Emtree)
- FU
Follow-up
- GRADE
Grading of Recommendations, Assessment, Development and Evaluation
- HKSJ
Hartung-Knapp-Sidik-Jonkman (adjustment)
- I²
I-squared statistic
- LLLT
Low-Level Laser Therapy
- LT
Long-term
- MD
Mean Difference
- MeSH
Medical Subject Headings
- MT
Mid-term
- N
Total number of participants
- NRS
Numeric Rating Scale
- OP
Orofacial Pain
- OR
Odds Ratio
- PBM
Photobiomodulation
- PICO
Population, Intervention, Comparator, Outcomes
- PRF
Platelet-Rich Fibrin
- PRISMA
Preferred Reporting Items for Systematic Reviews and Meta-Analyses
- PROSPERO
International Prospective Register of Systematic Reviews
- PRP
Platelet-Rich Plasma
- QoL
Quality of Life
- RCT
Randomized Controlled Trial
- REML
Restricted Maximum Likelihood
- RoB
Risk of Bias
- RoB 2
Revised Cochrane risk-of-bias tool for randomized trials
- ROBINS-I
Risk Of Bias In Non-randomized Studies of Interventions
- RR
Risk Ratio
- rTMS
Repetitive Transcranial Magnetic Stimulation
- SD
Standard Deviation
- SE
Standard Error
- SMD
Standardized Mean Difference
- ST
Short-term
- tDCS
Transcranial Direct Current Stimulation
- TENS
Transcutaneous Electrical Nerve Stimulation
- TMD
Temporomandibular Disorders
- TMJ
Temporomandibular Joint
- TN
Trigeminal Neuralgia
- VAS
Visual Analogue Scale
- τ²
Tau-squared (between-study variance)
Author contributions
Conceptualization: R. S. C., A. C., A. M. Methodology: R. S. C., A. C., L. B. Investigation: R. S. C., A. C., L. B., D. M., A. M. Resources: R. S. C., A. M. Data curation: A. C., L. B. Writing—original draft: A. C., L. B. Writing—review and editing: R. S. C., A. C., L. B., D. M., A. M. Visualization: A. C. Supervision: R. S. C. Project administration: R. S. C. Funding acquisition: R. S.C. All authors read and approved the final manuscript.
Funding
This study was supported by Current Research Funds 2026, Ministry of Health, Italy.
Data availability
No datasets were generated or analysed during the current study.
Declarations
Ethics approval and consent to participate
Not applicable. This study is a systematic review and meta-analysis based exclusively on previously published studies; no new human participants were recruited and no new identifiable data were collected. Therefore, ethics approval and informed consent were not required.
Consent for publication
Not applicable.
Competing interests
The authors declare no competing interests.
Footnotes
Publisher’s note
Springer Nature remains neutral with regard to jurisdictional claims in published maps and institutional affiliations.
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Associated Data
This section collects any data citations, data availability statements, or supplementary materials included in this article.
Supplementary Materials
Data Availability Statement
No datasets were generated or analysed during the current study.