Efficacy of non-surgical treatments for acute non-specific low back pain: protocol for systematic review and network meta-analysis of randomised controlled trials

Abstract

Introduction

Acute low back pain (LBP) is a prevalent condition with various non-surgical treatment options, yet no comprehensive network meta-analysis has systematically compared their relative efficacy for pain and disability. This study aims to fill that gap by synthesising available evidence on the efficacy of different types of non-surgical interventions for acute LBP, such as various medications, manual therapies and education-based therapies. Our coprimary objectives are to (1) compare each active treatment to an inert reference for measures of LBP and related disability and (2) rank the efficacy of treatments.

Methods and analysis

We will conduct a systematic search across multiple databases, including grey literature, to identify randomised controlled trials evaluating non-surgical treatments for acute LBP. Eligible studies must report on pain and/or disability outcomes in adults. The risk of bias will be assessed using the Risk of Bias tool, and the certainty of evidence will be graded using CINeMA (Confidence in Network Meta-Analysis). We will use a frequentist network meta-analysis to pool standardised mean differences in pain and disability, employing random-effects models to account for heterogeneity. A qualitative analysis will assess study characteristics and transitivity, while a quantitative analysis will evaluate efficacy and inconsistency. Results will be presented using network geometry, p-scores, forest plots, funnel plots, Egger’s test, Q-statistics and league tables to visualise both direct and indirect evidence and to identify potential biases.

Ethics and dissemination

This review protocol does not involve any primary research with human participants, animal subjects or medical record review. Consequently, this work did not require approval from an institutional review board or ethics committee. Results will be submitted to a peer-reviewed journal and presented at conference(s). De-identified data will be made available in a public repository.

STRENGTHS AND LIMITATIONS OF THIS STUDY.

• The study will include a comprehensive search strategy and employ standardised tools to assess trial quality and evidence certainty.

• By focusing exclusively on acute non-specific low back pain, the review avoids heterogeneity that could arise from combining populations with varied durations of low back pain.

• The inclusion of a broad range of non-surgical treatments enables a novel comparison of their relative efficacy using the network meta-analysis approach; yet this strategy relies on the transitivity assumption being met.

• While the grouping of interventions is informed by available evidence and a multidisciplinary author team, this strategy may obscure small differences within categories such as usual care, inert treatments, exercise or others, potentially contributing to heterogeneity and inconsistency.

Introduction

Low back pain (LBP) is a common disorder that can lead to disability, diminished quality of life, inability to work and incurs high direct and indirect costs.^{1 2} The global prevalence of LBP ranged from 1% to 20% in 2019, with higher rates typically observed in high-income countries.³ Acute LBP, defined as symptoms lasting less than 6 weeks,⁴ is most often non-specific, meaning it lacks identifiable structural pathology or major neurological deficits.⁵,⁷ Compared with chronic LBP, acute LBP has a favourable prognosis and significantly improves within 6 weeks, yet its recovery slows over time.⁸ Among patients with acute LBP, about 69% experience a recurrence of LBP within a year,⁹ approximately one in four develop chronic symptoms,¹⁰ while about one in five develop persistent severe symptoms.¹¹

Clinical practice guidelines recommend a wide range of non-surgical treatments for acute LBP, including non-steroidal anti-inflammatory drugs (NSAIDs), exercise, spinal manipulative therapy, heat and education as first-line interventions.^{12 13} However, guideline recommendations vary and often lack certainty, especially regarding the comparative efficacy of these interventions,¹²¹⁴,¹⁶ which limits clinicians’ decision-making. These limitations may be because meta-analyses mainly have focused on chronic LBP or examined mixed populations of acute, subacute and/or chronic LBP, thereby limiting insights specific to acute presentations.¹⁷,²⁰ Furthermore, prior network meta-analyses (NMAs) have often examined interventions within single categories such as analgesic medications,²¹ acupuncture¹⁹ and exercises²² rather than across diverse treatment modalities. This fragmented approach does not allow for comparisons across different types of non-surgical treatments, leaving gaps in knowledge for clinicians treating acute LBP and hindering guideline synthesis and implementation.

There is a general research gap in evidence specific to acute LBP compared with chronic LBP. Illustratively, a recent meta-analysis of non-surgical treatments for LBP included 301 randomised controlled trials (RCTs), of which only 52 (17%) focused on acute LBP, while the remainder included chronic LBP or mixed-duration populations.²³ The review results were not stratified by LBP duration, limiting insights into acute LBP. Similarly, a global review of 22 clinical practice guidelines for LBP found that while 13 (59%) provided recommendations for acute LBP, only 1 (5%) was focused exclusively on this population, with the remainder focusing on chronic or mixed durations.¹⁶ These findings indicate that although a body of trial evidence on acute LBP exists, it has received comparatively less attention in evidence synthesis and guideline development. As a result, clinicians and policymakers are left with less specific guidance for managing acute LBP, despite its high prevalence and potential for progression to chronic symptoms.^{9 11}

There is a need for evidence that informs clinical decision-making and guideline development for acute LBP. Clinicians are often faced with choosing among multiple non-surgical treatment options, yet lack clear guidance on how these options compare in terms of efficacy and may encounter conflicting recommendations across clinical practice guidelines.¹⁶ An NMA that evaluates a broad range of interventions can offer relevant comparisons that inform clinical decision-making.²⁴ Given their ability to incorporate both direct and indirect evidence across multiple treatments, NMAs are also increasingly used to inform clinical practice guidelines and health policy decisions.²⁴,²⁶ Identifying efficacious interventions for acute LBP may therefore help clinicians and other decision-makers to minimise pain and disability but also help prevent LBP from becoming chronic, reduce unnecessary care escalation and optimise healthcare resource use.²⁷,²⁹

Current practice often diverges from guideline recommendations.^{30 31} Many clinicians employ non-guideline-recommended treatments, such as passive modalities and opioids, which may reflect uncertainty about the most effective therapies, distrust of guidelines and/or a gap between research evidence and clinical implementation.^{27 32 33} Research suggests that non-concordant care is associated with higher healthcare utilisation, increased costs, worse outcomes and greater risk of developing chronic LBP.²⁷,²⁹ Despite the relatively good prognosis of acute LBP, this remains a potentially costly condition especially for those with high amounts of initial healthcare utilisation.³⁴ These issues underscore the need to clarify efficacious treatments for acute LBP for clinicians, stakeholders creating practice guidelines and patients who seek to streamline their recovery and avoid unnecessary or costly interventions.

Rationale and objectives

We aim to conduct a systematic review and NMA to address the existing gap in the literature regarding the efficacy of various non-surgical treatments for acute non-specific LBP. Our co-primary objectives are to (1) rank the efficacy of treatments for LBP and disability and (2) compare each active treatment to an inert reference for measures of LBP and related disability. To our knowledge, this will be the first NMA to synthesise evidence specific to acute LBP across a broad range of non-surgical treatments.

Methods

Study reporting will adhere to The PRISMA Extension Statement for Reporting of Systematic Reviews Incorporating Network Meta-analyses of Health Care Interventions (PRISMA-NMA).³⁵

Eligibility criteria

Given the need to meet the transitivity assumption in NMA, we plan to adopt a selective approach in defining study eligibility criteria. By focusing on specific age ranges, symptom duration, care settings and other factors, we aim to ensure that the interventions examined are comparable and applicable to a relatively homogeneous population.

Population

We will include studies of adults (≥18 years old) with a new episode of acute, non-specific LBP. Acute symptoms should be either defined as a duration of less than 6 weeks,⁴ stated in the eligibility criteria, or evident via the range in duration of symptoms in the baseline characteristics. Studies focused on symptoms of more than 6 weeks, for instance those that describe subacute or chronic LBP, will be excluded. We will also exclude studies that describe ‘acute’ or ‘recent onset’ symptoms without specifying the duration, as these terms can be ambiguous, considering some authors use a 12-week cut-off for acute LBP.^{36 37} We will not require a clean period prior to the episode as there is no consensus regarding the duration of such a washout, and this would be impractical to implement.³⁸ Non-specific LBP will be defined as pain that is not attributed to a specific pathology or nerve compression.⁵,⁷

We will exclude studies involving surgical candidates and patients treated in acute care settings such as emergency departments, trauma care and urgent care clinics. Standardisation of the population and care setting aims.³⁹ Standardisation of the population and care setting aims to maintain the transitivity assumption, as many non-pharmacological interventions are not available in acute settings. We will exclude patients with specific lumbar spine disorders such as radiculopathy, neurogenic claudication, inflammatory arthropathy or serious pathology like fracture, infection or neoplasm.⁵,⁷ Additionally, we will exclude animal studies and studies focused exclusively on populations with worker’s compensation injury, sick leave status or pregnancy, given potential differences in prognosis and/or available treatments.

Interventions

We will include any non-surgical interventions, such as medications, education, exercise, passive modalities, manual therapies, inert treatments like placebo or sham, usual care and others. Surgical interventions such as discectomy or fusion will be excluded. We will exclude studies that solely compare interventions within the same therapy type, such as different dosages or routes of administration of the same medication, or delivery approaches of a manual therapy, as our aim is to compare the efficacy of distinct therapy types. We will also exclude studies that allow patients to self-select treatments as opposed to being randomised.

Comparisons

We will include any available comparisons between eligible non-surgical interventions, as previously described, provided they do not involve surgical treatments or intervention arms with three or more combined therapies. Comparisons may include usual care, placebo/sham interventions, no treatment or active controls, allowing for a variety of study designs to be synthesised. This broad strategy aims to minimise comparator bias by incorporating data from optimal comparator groups as well as suboptimal comparators (ie, ineffective, minimal treatment or unknown effectiveness) that are often used in RCTs of LBP treatments.⁴⁰

Outcome

Included studies must report at least one type of continuous measure for pain outcomes, such as the Numerical Pain Rating Scale or Visual Analogue Scale, and/or disability assessments, including the Oswestry Disability Index (ODI), Modified Oswestry or Roland-Morris Disability Questionnaire (RMDQ). We will require follow-up measures taken between 1 week and 3 months, as this aligns with the Cochrane Back Group’s definition of short-term follow-up⁴¹ and reflects our study’s aims. This time frame captures symptom recurrence while avoiding regression to the mean, considering that acute LBP typically shows significant improvement within 3 months.⁴² We will exclude studies that only report categorical outcomes (eg, mild/moderate/severe pain, levels of improvement) or unrelated measures (eg, straight leg raise, surgery rates, range of motion). Included studies must also provide or plot mean or median values along with a measure of variance (eg, SD, 95% CIs or range) for the reported outcomes, enabling data imputation or scraping. For studies less than 10 years post-publication with missing data, we will reach out to the authors’ institutional email address a maximum of two times to attempt to obtain this de-identified raw outcomes data.

Study design

We will include only RCTs to ensure robust evidence, excluding observational studies.

Other

We will exclude studies that do not provide an English abstract or are published in non-English languages. This is to avoid issues with duplicate data extraction, quality scoring and overall interpretability by the entire research team.

Information sources

We will search PubMed, Scopus, Web of Science and CINAHL from inception to the date of query. The starting date of eligible studies will therefore be unrestricted, and the maximum end date will correspond with the final search date, projected to be 15 August 2025. We will conduct citation tracking of included articles and have coauthors to submit relevant articles from their personal collections which were missed by the aforementioned searches. We will search the reference lists of previous systematic reviews of RCTs on the topic acute LBP.¹⁷,1921 22 43 44

Search strategy

The search will focus on RCTs of non-surgical treatments examining acute LBP and was created with a research librarian. An example search strategy for MEDLINE, via PubMed, is shown in online supplemental file 1.

Selection process

Article selection and de-duplication will be conducted using Covidence (Covidence systematic review software, Veritas Health Innovation, Melbourne, Australia, 2024). Articles will first be screened by title and abstract, then by full text for inclusion. Two authors will independently conduct each phase of article screening. Disagreements will be resolved by discussion. The article selection process will be visualised using a flow diagram.

Data collection process

Data extraction will be conducted independently by two authors, who will discuss and resolve any potential discrepancies, involving a third author if necessary. The following data items will be extracted into a Microsoft Excel workbook: study characteristics, including the author surname and publication year; the duration of LBP for inclusion; the age of patients; the total number of patients enrolled; the types of interventions used in each group; and the outcome assessments used for measuring pain and disability. Finally, we will extract mean post-treatment pain and disability scores along with their SDs, with the option to impute missing data if needed, for the outcome window closest to 4 weeks.

Considering we are only including randomised groups, we will conduct NMA using post-treatment scores rather than change scores. While both approaches are valid, post-treatment scores may provide more conservative estimates.⁴⁵ Additionally, using post-treatment scores may streamline the data collection process and require fewer calculations, as change scores are often missing.²⁰

Data items

Our team will strategically lump and split treatments into nodes based on both the similarity of the interventions and their efficacy, as guided by prior systematic reviews. For instance, we will consider using drug classes as individual nodes (eg, opioids, NSAIDs, corticosteroids) rather than specific medications within each class. This approach is supported by findings from a recent NMA,²¹ which suggested a lack of meaningful differences in efficacy between individual analgesics for acute LBP. Additionally, we will group placebo and sham therapies into a single node, as a meta-analysis demonstrated no clinically relevant between-group differences in pain outcomes among various sham interventions for LBP.⁴⁶ Similarly, previous systematic reviews justify lumping different exercise therapies, given the lack of significant outcome differences between specific exercise approaches.^{22 47} This strategy aims to maintain a connected network, avoiding a fragmented structure that could complicate analyses. A tentative description of each possible treatment node is listed in table 1.

Table 1. Taxonomy for lumping with proposed nodes. This list is iterative and may change depending on the therapies encountered among included studies.

Node	Definition and examples	Reference(s) supporting lumping
Acetaminophen	Non-opioid analgesic used for pain	NA
Acupuncture	Insertion of one or more filiform needles into acupoints or tender points (ie, ‘Ashi’ points) based on Traditional Chinese Medicine principles	67
Anticonvulsants	Adjuvant analgesics used for pain such as gabapentin and pregabalin	21
Antidepressants	Medications that may alleviate pain through mechanisms involving serotonin and norepinephrine (eg, amitriptyline, duloxetine)	21
Benzodiazepines	Sedatives that may aid in pain relief through muscle relaxation or anxiolytic effects (eg, diazepam, lorazepam)	21
Corticosteroids	Steroid hormone-based anti-inflammatories such as prednisone and dexamethasone	21
Cold therapy (cryotherapy)	Use of freezing or near-freezing ice or gel packs, or other methods to cool the body	NA
Dry needling	Insertion of one or more filiform needles into specific trigger points or sensitised areas within symptomatic soft tissue	67
Education	Delivery of general or patient-specific advice for activities of daily living, ergonomics, activity modification, reassurance, pain neuroscience and other purposes to manage pain	17 68
Exercise	Any of a variety of therapeutic movements, stretches or strengthening techniques, including directional preference, stability, range of motion exercises, yoga or Tai chi	22 47
Inert	Any of a variety of inactive treatments such as placebo medications, sham spinal manipulation or needling therapies, or others	46
Muscle relaxants	Medications that reduce muscle tension or spasm (eg, cyclobenzaprine, tizanidine)	21
NSAIDs	Non-steroidal anti-inflammatory drugs (eg, ibuprofen, naproxen, diclofenac, meloxicam)	21
Opioids	Drugs that act on opioid receptors including hydrocodone and tramadol	21
Soft tissue techniques	Passive therapies addressing muscle or other soft tissue including massage	69
Spinal manipulation	Manual techniques with or without thrust directed to the spinal joints (eg, chiropractic or osteopathic manipulation, flexion-distraction, Chuna, Tuina, spinal mobilisation)	43
Superficial heat therapy	Application of heat therapies achieved through hot packs, towels, saunas, heat wraps or other similar methods	70
Usual care (ie, standard care)	A variety of commonly used, conservative interventions that may vary by country and year, potentially determined at the discretion of a clinician. Usual care may include analgesics, NSAIDs and/or muscle relaxants, along with recommendations for activity modification and patient education	31 71

NA, not applicable; NSAIDs, non-steroidal anti-inflammatory drugs.

Imputing missing data

We will attempt to include studies meeting criteria when pertinent data are missing, by imputing and/or scraping data. We will aim to include these studies because excluding them may lead to biased effect estimates, considering studies with non-significant findings are more likely to have missing variance data.⁴⁸ For scraping, we will use PlotDigitizer, which has been previously validated for this purpose.⁴⁹ For imputing, we will use previously established formulas.⁵⁰ Briefly, this may include estimation of SD values from the mean and SE, CIs, range, as well as imputing the mean from the median and quartiles. When no other method is possible, we will substitute missing SD, which is reasonable given the short-term follow-up window of our study.^{51 52} We will conduct a sensitivity analysis with studies with imputed data excluded, to examine the potential impact of this strategy.

Prioritisations

We will prioritise outcome measures based on guidance from previous publications and favour commonly used measures. When an article reports multiple disability scores, such as the ODI and the RMDQ, we will prioritise the score that is most often used across studies. Regardless, data from multiple disability scales can be analysed when reported across different studies. We will synthesise the results for both, given our aim of using standardised mean differences (SMDs) to account for variations between scales. For pain assessments, we will prioritise pain at rest, rather than pain during movement or at night.

If multiple available data points are given for multiple time windows, we will adhere to the Cochrane Back Review Group’s definition of short-term follow-up as outcomes that are measured closest to 4 weeks after randomisation, from a minimum of 1 week to a maximum of 12 weeks.^{4 41}

When both intent-to-treat and per-protocol data are available, we will prioritise the intent-to-treat analysis. This approach minimises bias by including all participants as randomised, regardless of whether they completed the study or adhered to the intervention protocol.

To maintain network connectivity, we will reclassify comparisons involving interventions combined with usual care versus usual care alone by synthesising them as active treatment versus usual care alone. This approach is necessary as it would be infeasible to consider individual components of usual care as distinct nodes, given the variability in this treatment category.³¹ Additionally, usual care is often used in acute LBP trials as an ethical alternative to a placebo intervention.^{20 46 53} Accordingly, our strategy aims to preserve relevant active treatment outcome data while assuming that outcomes are independent of usual care.

Similarly, we will list an active treatment combined with placebo (eg, Treatment A+placebo) under the same node as the active treatment (ie, Treatment A). This prevents the creation of a unique treatment node that could disconnect the network. This simplification will help ensure that outcomes for Treatment A are pooled and enable greater insights about treatment efficacy.

Geometry of the network

We will use R and the netmeta package to visualise network connections.^{54 55} We will create a graph that displays the individual treatment nodes, direct comparisons and the number of studies for each comparison (figure 1). We will assess whether the network is fully connected and report the total number of studies, pairwise comparisons and unique treatments. Additionally, we will discuss potential biases related to the network geometry, such as imbalances in the number of studies across comparisons.

Figure 1. Mock network graph representing the relationships between various interventions. This hypothetical network contains 12 studies, 18 pairwise comparisons and 11 interventions. Each node indicates an intervention, and to avoid misinterpreting this as actual data, hypothetical active treatments were assigned letters. The numbers of comparisons are displayed overlying the lines, which vary in thickness based on the inverse SE, reflecting the precision of the evidence. Interventions were generated using a random generator in Excel, drawing from an iterative list. Random participant numbers were also simulated, ranging from 10 to 50 per arm. Redundant arms within studies were replaced with ‘Inert’ to avoid errors, leading to a greater number of comparisons with an inert reference, which we expect given previous studies on the topic.¹⁸,²¹.

Risk of bias within individual studies

We will assess the risk of bias in individual studies using the Cochrane Risk of Bias 1 (RoB 1) tool, which evaluates potential bias at the study level across several domains (ie, randomisation, deviations, missing data, measurement and selection).⁵⁶ Two independent reviewers will respond to the RoB 2 signalling questions to identify potential bias in trial design, conduct and reporting, with any disagreements resolved through discussion. Judgements regarding RoB for each domain will be categorised as ‘Low’, ‘Some Concerns’ or ‘High’ based on the reviewers’ assessments. Scores will be stored in Covidence due to its blinding feature and integration with RoB 1 and exported for use in R. This process will be done via Robvis⁵⁷ and ggplot,⁵⁸ including an individual study plot indicating the judgements for each domain and a summary plot showing the overall judgements across studies for each domain (figure 2).

Figure 2. Mock individual study risk of bias (RoB) scores (A) and summary scores (B). The (A) traffic light-style plot illustrates the risk of bias ratings for each included hypothetical study, from RoB 1 judgements. Each row represents a study, while the columns indicate the domains of bias: sequence generation (D1), allocation/concealment (D2), blinding of participants and personnel (D3), blinding of outcome assessment (D4), incomplete outcome data (D5), selective reporting (D6) and other sources of bias (D7), followed by an overall score. The summary score plot (B) presents an aggregated view of the risk of bias across all studies. The colour-blind-friendly colours indicate the following: tan indicates ‘Low’, orange represents ‘Unclear’ and red represents ‘High’ risk of bias; both plots follow the same legend.

Summary measures

Forest plots

This primary outcome will use forest plots to compare interventions against an inert reference, using SMD as the effect estimate (figure 3). These plots will visualise effect estimates from both direct evidence for pairwise comparisons for both disability and pain. SMD values with a magnitude of 0.2, 0.5 and 0.8 will be considered small, moderate and large effects, respectively,⁵⁹ with negative values indicating a reduction in pain or disability.

Figure 3. Mock forest plot indicating the standardised mean difference (SMD) for various interventions compared with the inert reference group. Negative SMD values indicate a favourable effect of treatment relative to the inert reference. Hypothetical data, randomly generated in Microsoft Excel, were used for demonstrative purposes. Active treatments are labelled with letters to avoid confusion with real data. The size of the squares represents the precision of the estimates, with larger squares indicating greater precision. Error bars denote 95% CIs.

P-score

This primary outcome will include a frequentist ranking of treatments (ie, p-score) based on their efficacy for disability and pain. This measure quantifies the probability that a treatment is more efficacious than another treatment in the network.⁶⁰ We will further visualise this metric using cumulative ranking plots for both pain and disability outcomes (figure 4).

Figure 4. Mock cumulative ranking plot. This figure displays the treatment rankings based on the p-scores, which reflect the probability of a treatment being more efficacious than all others in the network. The colours in the plot range from green to red, with green (left of figure; top of key) indicating higher p-scores and red (right of figure; top of key) representing lower p-scores. This ranking is based on a hypothetical network of treatments, where treatments are assigned arbitrary labels (eg, ‘A’, ‘B’, ‘C’) to avoid confusion with real-world data.

League table

As a sensitivity analysis, we will create a league table for both disability and pain outcomes, displaying pairwise comparisons of treatment efficacy ranked from most to least efficacious. Each cell will indicate the SMD effect estimate along with its 95% CIs, with direct evidence shown in the upper triangle and indirect evidence in the lower triangle. Online supplemental file 2 shows a mock league table for pairwise comparisons. Treatments are indicated in letters due to use of hypothetical data. From the top left to bottom right, these are ranked from most to least efficacious. Each cell shows the standardised mean deviation and its 95% CIs, with direct evidence shown in the upper triangle and indirect evidence in the lower triangle.

Planned methods of analysis

We will provide a qualitative overview of the included studies, assessing follow-up durations, outcome measures used and the number of patients per intervention. This will include a histogram of follow-up durations and a general overview of age distribution across studies, including variability in reported age metrics (eg, mean (SD), range, median). We will also summarise the proportion of male and female patients. This information will help determine whether the transitivity assumption is met. All analyses will be performed using R (V.4.2.2, Vienna, Austria⁶¹) using the netmeta package,⁵⁴ with other packages mentioned accordingly herein.

For our statistical NMA approach, we will synthesise the effects of included interventions on post-treatment pain and disability in patients with acute LBP. For studies with multiple treatment arms, we will use pairwise comparisons of each treatment against the other treatments and an inert reference, ensuring that all relevant comparisons are included. We will use a random effects model given the expected variability in effect estimates, follow-up duration and interventions across studies.²⁰ For completeness and to adhere to PRISMA-NMA, we will calculate and present SMDs with corresponding 95% CIs for each study-specific pairwise comparisons. These estimates will be derived without the NMA methods.

Given our goal of comparing the efficacy of a range of interventions, we will require at least 10 trials, including at least 5 direct comparisons within the network. This threshold is achievable based on prior similar NMAs¹⁹,²¹ and is supported by statistical considerations.⁶² For example, with a trial count ratio of 1:2, approximately 4.5 indirect trials provide the same precision as 1 direct trial. Accordingly, 5 direct trials offer precision equivalent to approximately 22.5 indirect trials. With a conservative estimate of 40 patients per group,²⁰ this combination of direct and indirect evidence should yield a sufficiently large effective sample size to produce precise and clinically meaningful effect estimates.

Assessment of inconsistency

We will evaluate inconsistency using Cochran’s Q-statistic derived from a random effects model for the entire network, which compares treatment effects from direct comparisons with those inferred through indirect comparisons.⁶³ A significant Q-statistic value (ie, greater than the df with p<0.05) indicates heterogeneity among included studies. Additionally, we will calculate I^² values, with values of 25%, 50% and 75% interpreted as small, moderate and high levels of heterogeneity, respectively.⁶⁴ Finally, we will assess the consistency of the network using node-splitting forest plots (figure 5). These plots will compare SMD for pain and disability outcomes in pairwise comparisons where both direct and indirect evidence are available. We will visually evaluate consistency by noting any lack of overlap between the 95% CIs, which would suggest inconsistency between the direct and indirect evidence.

Figure 5. Mock node-splitting forest plot. This plot compares hypothetical standardised mean difference (SMD) values for outcomes (ie, pain or disability) across pairwise comparisons with both direct and indirect evidence. The plot uses a random effects model to account for between-study variability. Squares represent the point estimates for each comparison, with the size of the squares proportional to the precision of the estimates (larger squares indicate more precise estimates). The 95% CIs are represented by the horizontal lines. Comparisons with overlapping CIs between direct and indirect evidence suggest consistency, while non-overlapping CIs indicate inconsistency between the two types of evidence. Treatments are represented by letters to avoid confusion with real data.

Risk of bias across studies

We will examine for potential publication bias by visually inspecting comparison-adjusted funnel plots for direct comparisons of pain and disability outcomes⁵⁴ (figure 6). Comparison-adjusted funnel plots are modified from traditional funnel plots to account for heterogeneity among studies, enabling the comparison of multiple interventions within a network.⁶⁵ A symmetrical funnel plot will suggest low risk of bias, while asymmetry may suggest the presence of publication bias. We will provide a statistical assessment of publication bias using Egger’s regression test, interpreting a resulting p value of <0.05 as indicative of potential bias.

Figure 6. Mock comparison-adjusted funnel plot. This plot assesses for potential publication bias for outcomes (ie, pain or disability) using hypothetical data. Each point represents a direct treatment comparison, plotted by effect size (standardised mean difference) on the x-axis and SE on the y-axis. The plot adjusts for heterogeneity between comparisons. Asymmetry in the plot may indicate the presence of publication bias. Egger’s regression test (p=0.6540) suggests an absence of publication bias in this mock dataset. Treatments are ordered with ‘Inert’ as the reference comparator, facilitating meaningful comparison across treatment pairs.

Additional analyses

We will conduct sensitivity analyses by excluding studies that had imputed or scraped values. This approach is recommended to reduce the risk of bias, as imputed data can introduce uncertainty and may not accurately reflect the original data distribution.^{48 51 52} By excluding these studies, we aim to assess the robustness of our main outcomes. Specifically, we will repeat our analyses for the primary outcomes, including the p-scores and forest plots, for both pain and disability outcomes.

Certainty assessment

We will evaluate the certainty of evidence for our primary forest plot outcomes for pain and disability using the CINeMA (Confidence in Network Meta-Analysis) framework, which grades confidence levels as high, moderate, low or very low.⁶⁶ We will use a minimum relevant SMD threshold of ±0.1, which indicates a small effect size. We will incorporate the RoB 1 scores from our earlier analyses into CINeMA, manually assess indirectness of the evidence, enter the scores from reporting bias, while the software will automatically compute imprecision, heterogeneity and incoherence based on our NMA findings. Using the online CINeMA tool (https://cinema.ispm.unibe.ch), we will rate each comparison as having ‘No Concerns’, ‘Some Concerns’ or ‘Major Concerns’, with ratings discussed among multiple authors to ensure consensus. For assessing within-study bias, we will focus on the average RoB 1 score for each pairwise comparison as a guideline. Consistent with CINeMA guidelines, we will not downgrade our overall confidence more than once for related domains such as imprecision and heterogeneity.

Patient and public involvement

Patients and/or the public were not involved in the design, or conduct, or reporting, or dissemination plans of this research.

Ethics and dissemination

This review protocol does not involve any primary research with human participants, animal subjects or medical record review. Consequently, this work did not require approval from an institutional review board or ethics committee.