The primary outcomes will include the following:

The secondary outcomes will include the following:

We will not use the outcomes above as criteria for including or excluding studies (ie, studies will not be excluded for not reporting a particular outcome). However, these outcomes will serve as the basis for data extraction and analysis.

We will conduct a comprehensive search of major biomedical databases for eligible studies with no restrictions on language or publication date. The following databases will be searched from their inception to the present:

Our search strategy will use combinations of terms for CCA (eg, “Bile Duct Neoplasms” and “Bile Duct Cancer”) and neoadjuvant therapy (eg, “Neoadjuvant Therapy,” “Neoadjuvant chemotherapy,” “Neoadjuvant immunotherapy,” “Neoadjuvant radiotherapy,” “Cis/Gem,” “Neoadjuvant Capecitabine,” “Gem Cis durvalumab,” “GEMOX,” “Neoadjuvant CapOx,” and “Neoadjuvant Gemcitabine”) in various spellings. Because we aim to include both RCTs and observational studies, we will not apply a study design filter that could exclude nonrandomized studies. In databases that filter (eg, MEDLINE), we will avoid the highly sensitive RCT filter to retain observational evidence. Search strategies will be developed in consultation with an information specialist and peer reviewed in accordance with best practices (eg, PRESS [Peer Review of Electronic Search Strategies] guidelines). A full MEDLINE and Embase search strategy illustrating the combination of MeSH (Medical Subject Headings) terms and keywords has been provided in Multimedia Appendix 1. We will also ensure that our search covers any relevant non–English-language literature (any language), and if needed, we will have non–English-language studies translated or assessed by persons proficient in that language.

In addition to electronic databases, we will search other resources to identify unpublished or ongoing studies. We will hand search the reference lists of all included studies and relevant review articles for additional citations not captured by database searches. We will contact content experts and the corresponding authors of included trials or studies to inquire about any unpublished data or ongoing studies. We will contact them at least twice before declaring them as nonresponders with an interval of 10 working days. Where applicable, we will review conference abstract books (eg, American Society of Clinical Oncology or European Society for Medical Oncology) and proceedings for the past 5 years to identify any trials in progress or results reported in abstract form. If we identify a conference abstract, trial registry entry, or other report of a study that lacks a full publication, we will attempt to contact the study investigators for further information or data.

We will also search regulatory agency websites and thesis or dissertation databases (eg, ProQuest) to ensure that we capture any relevant trials or observational studies in gray literature. All references identified through these sources will be imported into a reference management software, and duplicates will be removed prior to screening.

We will follow a 2-stage screening process to select studies as recommended by the Cochrane Handbook for Systematic Reviews of Interventions. First, 2 reviewers will independently screen all titles and abstracts yielded by the search against the predefined eligibility criteria. We will obtain the full text of any article that appears to meet the inclusion criteria or for which eligibility is uncertain. The 2 reviewers will then independently assess the full-text articles for inclusion using a standard eligibility checklist. Any disagreements or uncertainties regarding a study’s eligibility will be resolved through discussion. If consensus cannot be reached, a third reviewer will act as an arbiter. We will record the reasons for excluding any studies at the full-text screening stage.

The completed systematic review will document the study selection process in a PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) 2020 flow diagram (Figure 1) detailing the number of records identified, screened, excluded, and included. All excluded studies at the full-text screening stage will be listed in a table with the reasons for exclusion.

Using a standardized data extraction form (developed a priori), 2 review authors will independently extract data from each included study. Before starting data extraction for all studies, we will pilot the data extraction form on a sample of studies (eg, 2 included trials) to ensure consistency and completeness, refining the form as necessary. Each reviewer will extract data, and a cross-check will be performed to compare entries. Disagreements or discrepancies in data extraction will be resolved through discussion between the 2 reviewers; if any issues remain unresolved, a third reviewer will be consulted to arbitrate. We will not be blinded to study authors or journals during data extraction as blinding is not practicable, and all included studies will undergo a full risk-of-bias assessment.

For each included study, we will extract the following information:

All extracted data will be managed using Review Manager (The Cochrane Collaboration) or other appropriate software. One reviewer will enter the data into Review Manager, and a second reviewer will cross-check the entries for accuracy. If information is missing or unclear, we will contact the study authors for clarification. In the event of multiple publications or reports from the same study, we will extract data from all available sources to ensure completeness and use the most comprehensive or final dataset for analysis (while noting any discrepancies among sources).

Two review authors will independently assess the risk of bias for each included study using prespecified tools according to study design. For RCTs, we will use version 2 of the Cochrane risk-of-bias tool for randomized trials [13], which assesses bias in the randomization process, deviations from intended interventions, missing outcome data, measurement of outcomes, and selection of the reported results. Each domain, and the overall study result, will be rated as “low risk of bias,” “some concerns,” or “high risk of bias” in accordance with guidance from this tool. For nonrandomized comparative studies, including retrospective and prospective observational cohort studies, we will use the Risk of Bias in Nonrandomized Studies of Interventions tool [14]. This tool evaluates bias due to confounding, participant selection, classification of interventions, deviations from intended interventions, missing data, measurement of outcomes, and selection of the reported results. Each domain will be rated as having a low, moderate, serious, or critical risk of bias, and an overall risk-of-bias judgment will be assigned for each study. Any disagreements between reviewers will be resolved through discussion, with consultation with a third reviewer if necessary. The risk-of-bias assessments will be incorporated into the interpretation of findings and will inform the Grading of Recommendations Assessment, Development, and Evaluation (GRADE) assessment of certainty of evidence [15].

For each outcome, we will extract or calculate summary measures of effect comparing neoadjuvant therapy followed by surgery with upfront surgery, and we will analyze resectable and initially unresectable CCA separately. For dichotomous outcomes, such as R0 resection and postoperative complications, we will calculate risk ratios with 95% CIs. If events are very rare, we may use the Peto odds ratio method as appropriate for sparse data. Time-to-event outcomes, including overall survival and relapse-free or disease-free survival, will be analyzed primarily using HRs with 95% CIs. If HRs are not directly reported, we will derive or approximate them from other available summary statistics or survival curves using established methods [16,17]. For continuous outcomes, where applicable, we will use mean differences (MDs) with 95% CIs when studies report outcomes on the same scale or standardized MDs with 95% CIs when different instruments are used to measure the same construct.

If continuous data are reported as medians with IQRs, ranges, or both, we will estimate corresponding means and SDs using established statistical methods where appropriate [18,19]. If conversion is not feasible or is judged methodologically inappropriate, these results will be summarized narratively. When outcome data cannot be meaningfully pooled because of incompatible reporting formats, insufficient data, or substantial clinical or methodological heterogeneity, we will provide a qualitative synthesis instead of a pooled effect estimate.

We anticipate that the unit of analysis will be the individual patient in all included studies. Cluster randomized trials or crossover trial designs are unlikely in this context (it is improbable to cluster by center or to cross patients over between direct surgery and neoadjuvant therapy). If we do encounter a cluster randomized trial, we will ensure appropriate analysis by checking that clustering has been accounted for in the published analysis or by adjusting the effective sample size using intracluster correlation coefficients if necessary according to the Cochrane handbook. For any crossover trials (also unexpected in this context), we will use data from the first phase only (to avoid carryover effects) or otherwise treat them cautiously as outlined in the handbook. If multiple observations per participant are reported (eg, repeated measurements over time), we will either choose a consistent time point for analysis or use methods for longitudinal data if a meta-analysis is feasible, ensuring that each participant’s data are analyzed only once for each outcome. In summary, any unit-of-analysis issues identified will be handled in accordance with Cochrane recommendations to avoid unit-of-analysis errors.

We will contact the study authors to request any missing outcome data or information that could not be obtained from the published report. If important data remain missing despite our requests, we will assess the potential impact on the findings. Where applicable, we will perform analyses on an intention-to-treat basis. For dichotomous outcomes, we will assume that participants lost to follow-up did not experience the event unless this is clearly inappropriate. For continuous outcomes, if only a per-protocol or completer analysis is available, we will note that and use whatever data are reported. We will record the extent of incomplete outcome data for each study (eg, numbers lost to follow-up or withdrawn) and consider how the study authors dealt with missing data. If feasible, we may conduct sensitivity analyses to assess the robustness of the results to assumptions about missing data (eg, by comparing best- and worst-case scenarios for dichotomous outcomes). We will not impute missing outcome data ourselves except for standard methods of calculating missing SDs (eg, from SEs or CIs) when necessary for meta-analysis following guidance in the Cochrane handbook.

We will assess heterogeneity among studies by examining the clinical and methodological characteristics of the included trials and through statistical measures. If studies are sufficiently similar in terms of participants, interventions, outcomes, and timing, we will consider pooling their results in a meta-analysis. Statistical heterogeneity will be evaluated using the chi-square test (with a significance threshold of P<.10 indicating potential heterogeneity) and the I² statistic. The I² value describes the percentage of total variation across studies that is due to heterogeneity rather than chance. As a rough guide, we will consider an I² value of more than 50% to represent moderate heterogeneity and of more than 80% to represent substantial (or considerable) heterogeneity. If heterogeneity is detected (chi-square P<.10 and/or I²>50%), we will first examine possible sources by considering differences in study design, populations, interventions, or risk of bias.

Given the likely variability in patient populations (stages and site of the malignancy) and neoadjuvant treatment protocols across studies, we anticipate at least moderate heterogeneity a priori. Therefore, we plan to use a random-effects model for meta-analysis by default, which is more appropriate when treatment effects may vary between studies. A random-effects model (eg, the DerSimonian-Laird method) [20] provides an average treatment effect while accounting for between-study variability. If heterogeneity is extremely high (I²>80%) and cannot be readily explained, we may refrain from computing an overall pooled effect and instead provide a descriptive summary of results. In such cases, we will still attempt to explore heterogeneity via subgroup analyses (see below) to determine whether specific subgroups of studies are more homogeneous.

If we include 10 or more studies in a meta-analysis for a given outcome, we will assess potential publication bias (small-study effects) using a funnel plot. We will visually inspect funnel plots for asymmetry. Additionally, we will perform statistical tests for funnel plot asymmetry (such as the Egger regression test) [21] when appropriate, with a significance level of a P value below .10 as recommended for these tests due to their low power. If asymmetry is detected, we will consider possible reasons (eg, true heterogeneity, selective nonreporting of small studies, or publication bias).

Statistical tests and graphical methods used to detect reporting bias (such as funnel plots and the Egger test) have very low power and reliability when fewer than 10 studies are available. In this situation, true biases may easily go undetected, but potential bias remains a real concern as each study represents a large portion of the total. To resolve this, we will use qualitative judgment, such as providing a narrative assessment based on the context, study designs, and comprehensiveness of the search. We will also use structured tools such as the Risk of Bias Due to Missing Evidence tool [22] and document limitations.

We will conduct meta-analyses using the Review Manager software [23]. A meta-analysis will be carried out if multiple studies are sufficiently homogeneous (clinically and methodologically) to justify a combined quantitative synthesis. For dichotomous outcomes, we will typically use the Cochran-Mantel-Haenszel method [24] to calculate pooled risk ratios or odds ratios with 95% CIs. For continuous outcomes, we will use the inverse variance method to pool MDs or standardized MDs. Time-to-event outcomes will be combined using the generic inverse variance method (incorporating log HRs and their SEs). As noted, we will use a random-effects model [20] for primary analyses to account for between-study variation; however, we will also check results under a fixed-effects model in a sensitivity analysis to see whether conclusions differ. All analyses will be 2 tailed with a threshold of a P value below .05 for statistical significance unless otherwise specified.

If meta-analysis is not possible (eg, due to an insufficient number of studies or excessive heterogeneity), we will provide a narrative synthesis of the results. This will involve describing and tabulating study findings and possibly grouping studies by conceptual categories (such as site and stage of CCA or neoadjuvant treatment used) to qualitatively summarize patterns. Where outcomes are reported without adequate detail for analysis (eg, “improved” vs “not improved” without numeric data), we will attempt to obtain additional data from the authors or, if unavailable, report the outcomes narratively.

We will prepare a summary of findings table for the main comparison (neoadjuvant therapy followed by surgery to upfront surgery for treating patients with CCA) and key outcomes following the GRADE approach to assess the certainty of evidence. Outcomes in the summary of findings table will likely include patients with R0 resection, occurrence of complications, relapse-free survival, and overall survival, among others, as mentioned in the Outcomes section (as these reflect both benefits and harms and are of high importance to decision-makers). We will use the GRADEpro software (McMaster University and Evidence Prime) to construct this table and will justify any downgrading or upgrading of evidence quality in footnotes according to the GRADE [15] criteria (risk of bias, inconsistency, indirectness, imprecision, and publication bias).

If sufficient data are available, we will perform subgroup analyses to explore potential sources of heterogeneity and examine effects in specific subpopulations. Anticipated subgroup analyses include the following.

We will repeat the primary analyses including only studies judged to have an overall low risk of bias (for RCTs, those with low risk in domains such as randomization and allocation concealment; for observational studies, those that adequately addressed confounding and other bias domains). This will show whether any particular risk of bias drives the results.

We will perform analyses excluding studies with high attrition (eg, more than 20% of participants not accounted for in the primary outcome analysis). This will test whether the results are sensitive to the inclusion of studies with potential attrition bias.

If our review includes both RCTs and observational studies, we will compare the results of an analysis including all eligible studies to those of an analysis restricted to RCTs. This will help determine whether the inclusion of nonrandomized data influences the effect estimates.

We will compare the meta-analysis results using a fixed-effects model to our default random-effects approach to assess the impact of model choice on the conclusions, especially in the presence of few studies or when heterogeneity is low.

For all sensitivity analyses, we will note any changes in the magnitude or significance of the effect estimates. If the conclusions remain consistent across these analyses, this will increase confidence in the robustness of the findings. Conversely, if results differ substantially under different assumptions, we will discuss these differences and their implications for the certainty of the evidence in our review.