Antibiotic therapy for pelvic inflammatory disease: a network meta‐analysis

Types of studies

We will include randomised controlled trials (RCTs) regardless of language, status, or date, including cluster‐RCTs. We will exclude quasi‐randomised trials to prevent selection bias. We will also exclude cross‐over studies, as pelvic inflammatory disease (PID) is an acute condition. We will consider conference abstracts and contact investigators as needed. Detailed criteria are in Table [38, 39, 40, 42, 42, 43].

Types of participants

Women of reproductive age (15 to 49 years, according to the World Health Organization (WHO) [6]), with a clinical or objective diagnosis of acute PID (symptoms less than 30 days), will be eligible. Accepted diagnostic criteria are based on clinical findings (e.g. CDC), laparoscopy, endometrial biopsy, or upper/lower genital tract pathogen isolation (e.g. C. trachomatis, N. gonorrhoeae) (Table). If a trial reports more than one diagnostic method, we will classify it according to the highest‐level confirmatory method (laparoscopy > endometrial biopsy > upper/lower genital tract pathogen isolation > clinical criteria alone).

To maintain clinical homogeneity and transitivity, we will analyse trials in two separate networks:

1. Network A (outpatient): women with mild‐to‐moderate PID (no tubo‐ovarian abscess) treated in an ambulatory setting;

2. Network B (inpatient): women with severe PID (tubo‐ovarian abscess or high fever) requiring hospitalisation and initial parenteral antibiotic therapy.

Primary network meta‐analyses will include only fully outpatient or inpatient studies, or those with disaggregated settings and severity data. We will exclude studies with mixed populations that lack disaggregated data from main analyses, and assess them in exploratory sensitivity analyses.

Types of interventions

We will include any systemic antibiotic regimen intended as definitive treatment for acute PID, regardless of dose, duration, or route, provided it is directed against C. trachomatis,N. gonorrhoeae, or both, with or without specific anaerobic coverage (Table). Placebo and no‐treatment arms are not eligible comparators. Regimens without explicit anaerobic coverage are eligible, and are defined as distinct nodes (Table).

We will map treatment arms to prespecified nodes by antibiotic class and the presence of nitroimidazole, ensuring clinical relevance and network transitivity. Node definitions will align with current CDC and International Union against Sexually Transmitted Infections (IUSTI) guidelines and the updated dataset. We will document any changes from the 2020 Cochrane review (e.g. splitting or lumping doses, such as cefTRIAXone 250 mg to 500 mg) in the supplementary material [36].

Guideline decision‐making will involve a decision set of current options, such as cephalosporin with doxycycline or azithromycin, fluoroquinolones, clindamycin with an aminoglycoside, and nitroimidazole variations. These will be distinguished from a supplementary set of historical or rare regimens used to enhance network connectivity. Any node adjustments will follow pharmacological criteria and be documented in a supplementary appendix.

Because treatment recommendations differ by setting and severity, we will create two separate networks: an outpatient network (Table), and an inpatient network (Table).

Critical outcomes

The critical outcomes will be [45]:

1. Clinical cure: resolution or improvement of signs and symptoms related to PID, within 30 days after treatment initiation. This captures the impact of treatment non‐adherence across multi‐day outpatient regimens and during at‐home oral continuation therapy following initial parenteral inpatient treatment.

2. Antibiotic‐related adverse effects that lead to discontinuation of treatment with antimicrobial regimens, or are grade ≥ 3, also summarised by type (gastrointestinal, allergic, other), during treatment and maximum trial follow‐up [46].

Important outcomes

The important outcomes will be:

1. Microbiological cure (N. gonorrhoeae, C. trachomatis): eradication from the upper or lower genital tract by culture or nucleic acid amplification test (NAAT), according to the author‐reported method, within 30 days after treatment initiation.

2. Treatment failure: lack of clinical improvement, including a change of antibiotics within 30 days after treatment initiation.

For clinical cure, we will prioritise the test of cure (TOC) visit (typically within 44 days post‐randomisation). If a study only reports end of therapy (EOT) results, we will extract these data, but analyse them as a distinct time point if heterogeneity arises [47, 48].

If multiple definitions exist (e.g. clinical cure), we will prioritise intention‐to‐treat analyses and extract granular outcome data, where feasible [39, 40, 42].

In studies where multiple time points are reported, we will prioritise the time period within 30 days after treatment initiation. If multiple measurements are reported within this period, we will prioritise the measurement closer to the longest follow‐up (i.e. 30 days).

If we exclude studies based only on outcomes, we will first verify that the relevant outcomes were not assessed, rather than not reported.

Electronic searches

We will search the following electronic databases [38]:

1. Cochrane Central Register of Controlled Trials (CENTRAL), via EBM Reviews Ovid, which includes studies from the World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP; https://trialsearch.who.int), the US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (https://clinicaltrials.gov), and the Cumulative Index to Nursing and Allied Health Literature (CINAHL) online platform, 1982 onwards;

2. MEDLINE Ovid: 1946 onwards;

3. Embase Ovid: 1980 onwards;

4. LILACS (Latin American and Caribbean Health Science Information database), via Web platform (IAHx interface): 1982 onwards.

For the MEDLINE search strategy, we will combine the subject‐specific search terms for PID with the Cochrane highly sensitive search strategy for identifying randomised trials (as per the Cochrane Handbook, Section 4.4) [49, 50]. We will combine the Embase search strategy with the Scottish Intercollegiate Guidelines Network (SIGN) filter.

We will not impose any language or date restrictions. The full search strategy is available in Supplementary material 1.

Searching other resources

We will identify unpublished trial abstracts via conference proceedings (e.g. ISSTDR, CDC National STD Prevention Conference) and the DANS Data Station Life Sciences repository (2016 to 2025) (https://lifesciences.datastations.nl/) [38, 49].

To avoid missing eligible trials, we will review reference lists of included studies and relevant systematic reviews. We will also contact corresponding authors, field experts, and relevant pharmaceutical manufacturers (e.g. of azithromycin and moxifloxacin) to request unpublished or ongoing trial data and clarify multi‐arm study details for network geometry [38, 51].

We will search the Epistemonikos database (https://www.epistemonikos.org), a multilingual health evidence database with the largest collection of systematic reviews.

We will search PubMed and Retraction Watch for retracted studies or expressions of concern (https://retractiondatabase.org/RetractionSearch.aspx), documenting them in each study's characteristics table.

Selection of studies

We will harmonise raw data from the prior Cochrane review with new studies [36], cross‐verifying all information against published reports. Supplemental materials will detail corrections in the same mapping table that tracks study sources, status, and discrepancies. We will cross‐check eligibility and intervention coding against the 2020 Cochrane dataset to ensure consistent network mapping and prevent misclassification of regimens and outcomes [39, 40, 47, 52].

We will use the Covidence online platform to screen the records retrieved from our electronic search. We will first use EndNote to remove any duplicates [37, 39, 53]. Three review authors (MN, MT, IT), in pairs, will independently screen the records' titles and abstracts, determine study eligibility per the review's inclusion criteria, and exclude articles that fulfil at least one exclusion criterion or are irrelevant to the research topic.

Three review authors (MN, MT, IT), in pairs, will independently screen the full texts of potentially eligible studies. We will document the excluded records and reasons in the characteristics of excluded studies table. If study status is uncertain, we will contact the authors. Another review author will resolve disagreements (CSS, MP, RFS). The selection process will be displayed in a PRISMA flow diagram.

The same review authors (MN, MT, IT), in pairs, will independently examine all included studies for trustworthiness. If there is disagreement, they will consult another review author to resolve it (CSS, MP, RFS). We will utilise the TRACT checklist [54] (see Supplementary material 2 for domains and criteria).

We will classify each item as no concerns, some concerns, not applicable, or major concerns, after examining the trial's full text, protocol, and registration (if available). We will justify each rating. Based on the ratings in each domain, we will present an overall study judgement [54]. The tool provides no definitive cut‐offs for the study‐level judgement. We will present the rating and the justification in a supplementary file.

If studies raise major concerns in multiple domains, we will request clarification from the study authors twice. If information remains inadequate, we will exclude the study or label it 'awaiting classification', with detailed reporting of concerns and author communications.

Cochrane’s Conflict of Interest Policy states that authors with trial involvement or relevant financial interests cannot make independent eligibility decisions. In such instances, a non‐involved review author will lead the study selection.

Data extraction and management

Three review authors (MN, IT, and MT) will independently extract study characteristics and outcome data, following Chapter 5 of the Cochrane Handbook. We will compile data in a piloted Excel file, using the main reports as primary sources, and contact trial authors for clarification if necessary.

To avoid bias, we will exclude review authors involved in the study from the extraction.

Extracted details will include general information, study design, participant characteristics, antibiotic regimens, and outcomes (Supplementary material 3).

Risk of bias assessment in included studies

Two review authors (MN, KS) will independently assess the risk of bias of the included studies according to Chapters 7 and 8 of the Cochrane Handbook [55, 56]. The review authors will also re‐evaluate the risk of bias judgements from the 2020 Cochrane review [36]. When the two review authors disagree, a third review author (IT, MP, CSS) will resolve the conflict.

We will use the Cochrane RoB 2 tool for RCTs, including the variant for cluster‐RCTs, if needed [43, 57]. We will evaluate the effect of assignment to the intervention (the intention‐to‐treat effect). We will present result‐level risk of bias assessments for all prespecified outcomes at the prespecified time points (see Outcome measures for details):

1. Clinical cure (at the test of cure visit, within 30 days after treatment initiation);

2. Antibiotic‐related adverse effects leading to discontinuation, or are grade ≥ 3 (during treatment and maximum follow‐up);

3. Microbiological cure (within 30 days after treatment initiation);

4. Treatment failure (within 30 days after treatment initiation).

The details on the domains of RoB 2 and judgements are available in Supplementary material 4.

If multiple time points are reported, we will prioritise the time period within 30 days after treatment initiation for the assessments. If multiple measurements exist within this time period, we will prioritise the time point closer to the longest follow‐up (i.e. 30 days). We will present all risk of bias assessments in a summary and in graphic form, as traffic light plots [43, 57].

Measures of treatment effect

All outcomes will be dichotomous. We will calculate treatment effects using odds ratios (ORs) with 95% confidence intervals (95% CIs). If necessary, we will reverse the direction of the effect in individual studies to ensure consistency across trials [38, 40, 58].

Unit of analysis issues

The unit of analysis will be the individual woman randomised. We will address potential issues related to the unit of analysis in accordance with established methodological standards [59]. If studies include multiple episodes of PID per woman, we will extract data regarding the first episode. Where this is not possible, we will note the potential for non‐independence and consider its impact in sensitivity analysis.

For multiple observations or time points per participant, we will select the most clinically relevant summary measure (e.g. proportion with at least one event within 30 days after treatment initiation) or a single time point within predefined windows per outcome.

For studies with three or more arms (e.g. Bevan and colleagues) [15], we will extract data for all relevant arms to properly account for the correlation between effect estimates within the same trial, as per the Cochrane Handbook, Section 11.4 [59].

For included cluster‐RCTs, we will adjust for clustering using effective sample sizes, based on reported intraclass correlation coefficients (ICCs). Otherwise, we will use ICCs from similar studies or perform sensitivity analyses across a range of ICCs.

Dealing with missing data

We will conduct primary analyses on an intention‐to‐treat (ITT) or modified ITT basis, using available‐case data reported by trial authors, assuming data are missing at random. We will contact trial authors to request missing outcome data.

We will not perform imputation in primary analyses because treating imputed data as observed understates within‐study variances, artificially inflates study weights, and distorts between‐study heterogeneity (Tau²) estimation and P score rankings. For studies with > 10% missing outcome data, we will perform sensitivity analyses using:

1. Complete case analysis: analysing only participants with complete follow‐up;

2. Best‐case scenario: missing participants are assumed to have achieved clinical/microbiological cure, avoided treatment failure, and experienced no adverse events;

3. Worst‐case scenario: missing participants are assumed to have experienced clinical/microbiological failure, treatment failure, and an adverse event leading to treatment discontinuation.

Reporting bias assessment

We will assess reporting bias by comparing the outcomes planned by the included studies at the registration or protocol stage with the outcomes they reported in their final reports. In cases where results of planned outcomes are unavailable, we will contact the study authors to request any unreported results [38, 40, 60].

If a network includes at least 10 studies, we will inspect comparison‐adjusted funnel plots for small‐study effects. We will order treatments by the earliest eligible trial year, testing the hypothesis that newer regimens show favourable results in smaller trials. We will only plot comparisons with two or more studies. If fewer than 10 plottable studies remain, we will not produce a plot. Plot asymmetry indicates small‐study effects from bias, quality differences, or heterogeneity, but we will not attribute it solely to reporting bias. Formal statistical tests will be omitted due to low statistical power. Any asymmetry will be incorporated into the CINeMA reporting bias assessment [61].

Synthesis methods

Trials in which all randomised arms map to the same node provide no network contrast; we will describe them narratively, list them in the characteristics of included studies table, and exclude them from network meta‐analyses (NMA). In multi‐arm trials, we will combine arms mapping to the same node before analysis, according to Section 23.3 of the Cochrane Handbook [43].

Investigation of heterogeneity and subgroup analysis

If there is important heterogeneity, inconsistency, or both, we will conduct subgroup analyses for clinical cure and any antibiotic‐related adverse effects. We will examine subgroup differences by comparing the network diagram for each subgroup, performing an NMA for each subgroup, and comparing their relative treatment effects and relative treatment ranking. We plan to carry out a subgroup analysis by (see also Table and Supplementary material 6):

1. Diagnostic criteria;

2. Country income level according to the World Bank classification;

3. Anaerobic coverage (or not).

If fewer than five studies contribute to a planned subgroup analysis, we will not emphasise subgroup findings, because the data are unlikely to support robust inferences. In such cases, we will present results descriptively, and interpret them with caution.

If we include more than 10 studies in a network, we will perform network meta‐regression analyses to explore additional potential effect modifiers. We will examine the following covariates:

1. Publication year (as a continuous variable);

2. Geographic region (e.g. North America, Europe, Africa, Asia, Latin America; as a categorical variable);

3. Baseline severity score (as a continuous variable based on pain score, fever, and laboratory values, if reported).

To ensure model stability, we will test each covariate individually, in a univariate model.

For the third secondary objective, we will compare, for each critical outcome, which antibiotic class (e.g. cephalosporin‐based, azithromycin‐based, fluoroquinolone‐based, anaerobic‐covering) occupies the highest P score tier within each network, and will describe narratively whether the same class or coverage principle (e.g. routine anaerobic coverage) is favoured in both networks. We will not apply any formal statistical test across networks.

Sensitivity analysis

For the critical outcomes of clinical cure and antibiotic‐related adverse effects, we will carry out sensitivity NMAs to evaluate the reliability of our findings, by [60]:

1. Excluding studies with imputed outcome data or considerable (over 10%) missing outcome data (see Dealing with missing data);

2. Splitting the fluoroquinolone node into anti‐anaerobic fluoroquinolones (moxifloxacin) versus non‐anti‐anaerobic fluoroquinolones (ciprofloxacin or ofloxacin). This analysis will explore potential effect modification by enhanced anaerobic activity, and test the robustness of the primary network model. Interpretation will focus on point estimates (ORs) and confidence interval precision rather than threshold tests of statistical significance or guideline validation.

3. Excluding studies with a high risk of bias or some concerns about bias;

4. Examining different ranges of ICCs (in the case of cluster‐RCTs with unknown ICC);

5. Excluding studies of women with multiple episodes of PID that do not provide separate data on the first episode;

6. Excluding studies with presumptive STI diagnosis instead of testing for N. gonorrhoeae or C. trachomatis;

7. Excluding studies that do not report adherence monitoring;

8. Including studies with mixed‐severity populations. We will exclude trials that recruited mixed‐severity populations but did not report disaggregated data by setting/severity from the primary network meta‐analyses. Instead, we will explore their impact solely in these exploratory sensitivity analyses.

9. Repeating analyses and including studies with zero cells, using the Mantel‐Haenszel approach [65].

We will judge robustness by evaluating the consistency of point estimates (ORs), the overlap and precision of 95% CIs, and the stability of relative treatment rankings (P scores) between primary and sensitivity models.

1. If sensitivity analyses show consistent findings, the primary pure‐population network estimates will remain the primary basis for clinical inferences, with no downgrading for robustness concerns.

2. If a sensitivity analysis (such as when including mixed‐severity studies or node splitting) results in substantial shifts in effect estimates, loss of precision, or altered ranking hierarchies, we will interpret the primary network with explicit caution, and highlight the sensitivity analysis findings in the Results, Discussion, and Abstract. In such instances, we may downgrade the certainty of evidence for affected comparisons by one or two levels under the indirectness domain in the CINeMA framework, due to unverified transitivity and potential confounding by effect modifiers. We will also assess unexplained discrepancies for potential downgrading under the heterogeneity and incoherence domains.

Certainty of the evidence assessment

Following the CINeMA approach and Chapter 14 of the Cochrane Handbook, we will assess certainty of evidence and create SoF tables [61]. Three authors (MN, IT, KS) will independently categorise certainty of evidence for each network estimate from high to very low for key decisions, such as azithromycin versus doxycycline effectiveness, nitroimidazole addition, and regimen rankings [37]. We will systematically evaluate comparisons informed by single studies, sparse edges, or open loops for downgrading under imprecision and indirectness/incoherence. Disagreements will be resolved through discussion by a third author (MP, CSS, RFS).

Using the NetMeta contribution matrix and CINeMA web framework, we will evaluate confidence across six methodological domains:

1. Within‐study bias (risk of bias). The overall RoB 2 assessment for each result will feed into the assessment;

2. Reporting bias (assessing potential publication bias);

3. Indirectness (evaluating transitivity across study populations, interventions, and outcomes);

4. Imprecision (95% CIs will be compared with a prespecified range of equivalence on the OR scale: 0.75 to 1.33 for clinical cure and 0.67 to 1.50 for antibiotic‐related adverse effects leading to discontinuation. A comparison whose 95% CI crosses one bound of the range will be downgraded once, and twice if it crosses both);

5. Heterogeneity (evaluating between‐study variance ‭Tau² and overlap of confidence intervals);

6. Incoherence (disagreement between direct and indirect evidence evaluated via node‐splitting and design‐by‐treatment tests).

Internal sources

• Cochrane Gynaecology and Fertility, New Zealand

  The Cochrane Gynaecology and Fertility group provided editorial and methodological support during the development of this protocol and had no role in the selection of studies, data extraction, analysis or interpretation.

• Cochrane STI, Netherlands

  The Cochrane STI group had no involvement in the development of the protocol or in conducting the review.

External sources

• none, Other

  No external sources of support received