Types of studies

We included randomised controlled trials (RCTs). If the process of randomisation was unclear, we contacted the trial authors to obtain further information. If we were unable to contact the authors, we included the trial in the review and considered it to be at unclear risk of bias. To be eligible, trials had to compare at least one of the active interventions of interest versus placebo or versus another active treatment. We used both abstracts and full‐text publications if they reported adequate information about study design, participant characteristics and interventions.

We did not include quasi‐randomised trials (assigned to a treatment, procedure or intervention by methods that are not random) due to lack of proper randomisation.

We only included trials that had been prospectively registered, unless the final trial report was published before 2010. The decision to exclude unregistered (or retrospectively registered) trials was taken due to the evidence highlighting issues surrounding false data (Carlisle 2021; Roberts 2015) and has now become the policy of Cochrane Injuries (Broughton 2021; Cochrane policy). Prospective registration reduces the chance of publication bias, and has been compulsory for randomised controlled trials since 2005, suggesting that those that have not been registered (or were registered retrospectively) since then are less likely to be of high quality (Roberts 2015). We have used a cut‐off of 2010 as this allowed studies that commenced before the introduction of compulsory registration in 2005 to complete and publish.

Types of participants

We included any person who had undergone an elective hip or knee replacement or revision surgery. We included people who had total knee replacements, partial or unicondylar knee replacements, hip replacements, and revision hip or knee surgery. We excluded people with known bleeding disorders such as haemophilia. We placed no restrictions on ethnicity or gender.

If an eligible trial contained a mixed population of people, then we only used data contributed from our population of interest. If no subgroup data were given, and we were unable to contact the corresponding author to provide this information, at least 80% of the sample size had to be from our population of interest for the trial to be eligible for inclusion.

Types of interventions

We included trials that compared one or more of the following interventions:

• antifibrinolytics:

  • tranexamic acid;

  • aprotinin;

  • epsilon‐aminocaproic acid;

• desmopressin;

• factor VIIa and factor XIII;

• fibrinogen;

• fibrin sealants/glue (not including surface dressings);

• non‐fibrin sealants (not including surface dressings).

Drugs and treatments that are not listed above were not used in the NMA. Acceptable comparators included placebo or one of the active interventions listed above. We excluded trials that used standard of care as the comparator.

We considered interventions given at a range of threshold doses, and as single or multiple doses via intravenous, subcutaneous, intranasal, oral or topical routes of administration. We also considered the timing of the interventions.

Types of outcome measures

We assessed the relative hierarchy ranking of the interventions using the following outcome measures.

Electronic searches

Searching other resources

To complement the database searches, we handsearched the reference lists of recent systematic reviews to identify additional trials potentially missed by the electronic searches, but also to ensure that we collected as much of the available evidence as possible. We contacted the corresponding authors of the reviews to determine whether they were aware of any further trials in this area. In addition, we contacted authors of ongoing trials to obtain any unpublished data. We also examined any relevant retraction statements and errata for the included studies.

Selection of studies

Independently, two review authors (VNG, RC) screened all titles and abstracts identified by the electronic searches for eligibility and they excluded any citations deemed irrelevant. Independently, these review authors (VNG, RC) screened the full texts of all potentially relevant trials for eligibility against the criteria set out in the protocol. We resolved disagreements through discussion or, if required, through consultation with a third review author (LJE). We requested information from trial authors when there was insufficient information from trial reports to make a decision about eligibility. We kept the records of the selection process, as well as details of our reasons for exclusion at the full‐text stage. These were used to populate a PRISMA flowchart to demonstrate the selection of studies (Moher 2009; Page 2021). We used colleagues or Cochrane resources such as Task Exchange for translation of articles written in languages that the review authors cannot read and we thank and acknowledge these colleagues.

Data extraction and management

Independently, VNG and RC undertook data extraction of the included trials, using standardised, piloted forms designed according to the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). The review authors were not blinded to institutions, authors or outcomes of the trials. Colleagues who provided translation of studies written in languages other than English also extracted data from these studies. We piloted the data extraction forms on a random sample of 10 included trials (split equally between the review authors) and made adjustments. If a trial was identified as relevant by one author but not by the other, the authors discussed the rationale behind their assessments. If a consensus was not reached between the two authors, LJE served as the arbitrator. We contacted the corresponding authors of included trials up to three times to request additional trial data. If no response was received within four weeks, we deemed the data unobtainable. If there was conflict over data sources, we gave preference to published data over unpublished, as published data have been through a peer review process.

There were a large number of possible combinations for each intervention and data synthesis was difficult to determine prior to data extraction. Taxonomy of interventions took place prior to outcome data extraction, with help from an external expert panel to create clinically meaningful groups ready for data analysis. The external panel consisted of two haematologists (blood specialist doctors), two orthopaedic surgeons (bone and joint specialist doctors) and two anaesthetists. The panel were blinded to the outcome data and were given information on the study design, types of studies included and intervention information. The panel recommended nodes consisting of intervention name, mode of administration, total dose of intervention and timing. For tranexamic acid, the panel recommended doses were grouped into 1 g, 2 g, 3 g and > 3 g, and for the interventions EACA, aprotinin and desmopressin they recommended grouping all the studies together, as they are likely to be weight‐adjusted doses. The panel recommended timing be subdivided into pre‐incision (prior to making a surgical incision), intraoperative, postoperative within six hours of surgery, and postoperative administered within 6 to 24 hours. Where a study reported weighted doses of the interventions (e.g. mg/kg), we converted these doses to a uniform dose. We used the average weight of the patient population of the country in which the study was conducted according to published literature (Walpole 2012).

We extracted the following information.

• General information: name of review author carrying out data extraction; date of when data extraction was done; study ID (and any other unique trial identifiers); surname and contact address of first author of included trial; citation of included trial; language of trial and details of any duplicate publications.

• Trial information: trial design ‐ type of RCT; location of trial; setting; sample size; duration of trial; power calculation; treatment arms; randomisation; inclusion and exclusion criteria; comparability of groups and length of follow‐up.

• Characteristics of participants: age; sex; ethnicity; breakdown of total numbers for those recruited, randomised and analysed; type of surgery; numbers lost to follow‐up; dropouts (percentage in each arm) with reasons; protocol violations and co‐morbidities.

• Characteristics of interventions: number of treatment arms; description of experimental arm(s); description of control arm; timing, dose and route of administration of intervention; and other differences between intervention arms.

• Outcomes: need for blood transfusion within 30 days postoperatively; number of units of red blood cells transfused; mortality due to any cause within 30 days postoperatively; proportion of participants requiring each type of transfusion; and adverse effects (transfusion reactions, thromboembolism and drug reactions), re‐operation due to bleeding and length of hospital stay. (We extracted exactly how ‘adverse effects’ and ‘serious adverse effects’ were defined in each study.)

• Quality assessment: allocation concealment; blinding (participants, personnel, outcome assessors); incomplete outcome data; selective outcome reporting; other sources of bias. (Blinding was not possible for some comparisons.)

We utilised arm‐level data rather than study‐level data from both abstracts and full‐text papers. We obtained maximal data by extracting data from all publications available but used one data extraction form per trial. We contacted the primary or corresponding author of a trial, study groups or companies for additional data, if insufficient information was provided in the trial reports.

We also collected and have presented data on costs reported in the included studies. Although this does not constitute a formal economic evaluation, it provides useful additional information that may be of value in a decision‐making context.

Three review authors (VNG, RC, CK) entered the data into RevMan 5 and cross‐checked entries for accuracy.

Assessment of risk of bias in included studies

We performed quality assessment on all the included trials using the methods described in Chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b). We used the Cochrane risk of bias tool (RoB tool) (Higgins 2016). We tested the RoB tool in a small, random sample of trials. Three review authors (VNG, RC, CK) independently assessed risk of bias for each trial to assign each a classification of high, low or unclear risk. We created a Characteristics of included studies table and outlined the judgement process. We compared the review authors’ statements and reached a consensus on the classification of risk of bias. If necessary, a third author (LJE) was consulted.

Using this information, we explored statistical heterogeneity in each study and performed a sensitivity analysis. We followed the Cochrane methods for assessing risk of bias and addressed the following domains:

• selection bias (random sequence generation and allocation concealment);

• reporting bias (selective reporting);

• attrition bias (incomplete outcome data);

• performance bias (blinding of participants, personnel and outcome assessors);

• detection bias (blinding of outcome assessment);

• other forms of bias.

We assigned each of the domains listed above a classification of risk:

• low risk ‐ if the criterion has been adequately fulfilled in the study;

• high risk ‐ if the criterion has not been fulfilled in the study;

• unclear risk ‐ if the study report does not provide enough information with which to reach a clear decision.

We resolved any conflicts through discussion between the review authors (VNG, RC, CK) or by involving another author (LJE).

If a publication stated that participants were randomised but the method of randomisation used was not described, we contacted the trial authors. If this information was unobtainable, then we included the trial and considered it to be at an 'unclear' risk of bias as per the Cochrane risk of bias tool (Higgins 2011b).

We included both abstracts and full‐text publications.

Measures of treatment effect

When extracting data for dichotomous outcomes (number of participants with at least one bleeding episode, number of participants with at least one severe or life‐threatening bleeding episode, mortality, proportion of participants needing an allogeneic blood transfusion, adverse events), we documented the number of events and number of participants in the intervention and control arms.

For continuous outcomes (number of units of allogeneic blood transfused per participant, length of hospital stay), we documented the mean, standard deviation and total number of participants in both the intervention and control arms. If only study‐level data were available we recorded the reported effect size and the associated standard error.

We presented direct treatment comparisons and grouped the comparisons by treatment nodes; we compared and produced the forest plots using RevMan (Review Manager Web). We produced these to provide transparency on all outcome data collected for all studies.

Unit of analysis issues

In pairwise meta‐analyses, we treated trials with multiple treatment group comparisons as individual, independent two‐arm studies. The placebo group acted as a node in the NMA, which helped with indirect analyses and formation of a hierarchy of interventions. In the NMA, we included all comparisons where there were sufficient data to do so. These trials were analysed appropriately to take into account the respective treatment effects. The NMA method accounted correctly for correlations in relative effects from trials with more than two arms. We performed our analyses using the participant as the unit of analysis.

In future updates, in the event that we include one or more cluster‐RCTs, we will follow the guidance in Chapter 23 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022), using a method of generic inverse variance in RevMan. We will also carefully consider the potential risk of bias associated with the method of randomisation described.

Dealing with missing data

Where there were missing data from any study, we contacted a corresponding author, by email, to obtain missing data. We attempted to contact the authors, by email, up to a maximum of three times to obtain the information. If we were still unable to obtain the information, and where missing data were thought to introduce serious bias, we performed a sensitivity analysis to evaluate the impact of missing outcome data.

We recorded the number of participants lost to follow‐up in each trial. In trials that also included other populations, such as those undergoing non‐elective hip or knee replacement, we extracted data for the elective hip or knee subgroup.

Continuous outcomes are often reported as a median and a measure of spread, such as a range or interquartile range (IQR) when the distribution is skewed. We considered using an assumption of log‐normality to obtain estimates of mean and SD from medians and range/IQR. However, neither of our continuous outcomes (units of blood product transfused and length of hospital stay) are granular enough for this approach to be reasonable, and small sample sizes posed an additional problem where range was the only available measure of spread.

Assessment of heterogeneity

Assessment of reporting biases

At the protocol stage, we planned to explore the existence of small‐study effects in our pairwise meta‐analyses (when there were more than 10 studies) by producing funnel plots, and by using meta‐regression in our NMA. We deemed a P value below the threshold of 0.10 to be statistically significant. The association between study effect size and funnel plot asymmetry is affected by several factors. We assumed that a lack of studies in areas of non‐significance would be indicative of publication bias. In the event, we were unable to action these plans, due to insufficient numbers of studies in the pairwise analyses.

Data synthesis

Subgroup analysis and investigation of heterogeneity

Sensitivity analysis

If trials contained mixed populations (e.g. included those requiring trauma surgery), then we used data only from the elective hip and knee subgroups, if available. If no subgroup data were presented and the corresponding author was not contactable for the information, we specified that at least 80% of the sample size had to be from our population of interest for the trial to be included.

We planned to assess the strength of the overall results by performing sensitivity analyses excluding trials deemed to be at high risk of bias. In the event, the network was too fragile to allow sensitivity analysis; we considered risk of bias in our interpretation of results.

Summary of findings and assessment of the certainty of the evidence

We did not specify any information related to the summary of findings table in our protocol. We produced an NMA summary of findings table as recommended by Yepes‐Nuez et al (Yepes‐Nuñez 2019).

We used the CINeMA framework (Confidence in Network Meta‐Analysis) to evaluate the confidence of the evidence for the summary of findings table (Nikolakopoulou 2020). We used the CINeMA framework rather than GRADEpro (Schünemann 2022) to develop a summary of findings table as the CINeMA framework has been created specifically to assess confidence in the results of a network meta‐analysis where there are a large number of interventions.

We used the online CINeMA tool to assess confidence for each comparison within the network based on: within‐study bias, across‐studies bias, indirectness, imprecision, heterogeneity and incoherence. We provide justifications in the summary of findings table for any decisions made to downgrade the certainty of the evidence to aid the reader's understanding of the review. We also included the relative effect with 95% credible intervals, the anticipated absolute effect with 95% credible intervals, the median nodal ranking point with 95% credible intervals and the probability of intervention ranking first (%).