Types of studies

We will only include studies with a randomized controlled study design that are single‐blinded (outcome assessor) trials. Because regional anaesthesia causes numbness of the affected body part, neither patient nor anaesthesia provider can be reliably blinded to the intervention. We insist on blinding of the outcome assessor, that is, the nurse or surgeon evaluating the joint function three, six or 12 months after the surgery.

We will exclude studies that are not randomized, and studies in which the outcome assessor is not blinded.

Types of participants

We will include studies on patients undergoing elective major joint replacement surgery of the knee, hip or shoulder.

We will exclude studies including children or patients undergoing revision arthoplasty.

Types of interventions

We will include studies that compare continuous or single‐injection postoperative regional analgesia with placebo. We will not include studies comparing one regional technique versus another.

Regional analgesia may include epidural anaesthesia, plexus or nerve blocks, or wound or joint infiltration. This may be the primary comparison in the study or a comparison between subgroups. Studies will be included without regard to the type of anaesthesia used (general or regional) for the surgery proper. Pharmacological multimodal analgesia (non‐steroidal anti‐inflammatory drug (NSAID), paracetamol, gabapentin or pregabalin, ketamine, etc.) may or may not be used, but they will have to be comparable in the experimental and control groups.

Types of outcome measures

Electronic searches

In order to be relevant to the current practice, we will limit our search to the last 15 years. We will search in the current issue of the Cochrane Central Registrar of Controlled Trials (CENTRAL) (The Cochrane Library); MEDLINE on OvidSP (1997 to date); EMBASE on Ovid SP (1997 to date); and CINAHL on EBSCOhost )1997 to date). We will combine a free text search with a controlled vocabulary search. To prevent language bias, we will not impose a language restriction.

Our MEDLINE search terms are reproduced in Appendix 1 and will be adapted for searching other databases.

Searching other resources

We will search the reference lists of identified relevant studies for additional citations. We will search conference abstracts (2011 to 2012) of the American Society of Anesthesiologists, the American Society of Regional Anesthesia, The European Society of Anaesthesiology, and the European Society of Regional Anaesthesia. We will also search two trial registries (http://www.controlledtrials.com and http://www.clinicaltrials.gov) for relevant studies.

Selection of studies

Two review authors (AA and GSS) will screen the abstracts of all publications obtained by the results of the above searches. We will independently screen all titles and abstracts for eligibility. For trials that appear to be eligible RCTs, we will obtain and inspect the full articles to assess their relevance based on preplanned criteria for inclusion. For the studies identified and reviewed in full, we will note the reasons for study exclusion and report them in a table.

In the case of disagreement between AA and GSS, MHA will act as a referee. Decisions will be reached by consensus; if no consensus can be reached, MHA will cast the decisive vote. In the case that further information is needed, which is not available in the published article, we will contact the corresponding author and request the necessary information.

Data extraction and management

We will develop a standard data collection form (Appendix 2). We will record details of trial design, preoperative assessment, interventions and outcome measures. We will perform a pilot run and revise the data sheet accordingly. For each study, two authors (AA and GSS) will independently extract information and enter the data in the Cochrane Review Manager (RevMan 5.1). In the case of bilateral procedures, the average score of the two joints will be used.

We will extract as primary outcome data the composite function score used for the joint being studied.

The following secondary outcomes will be extracted, where provided:

1. quality of life (appropriate score such as the SF‐36, based on the data available in the articles and from the authors;

2. complications (medico‐surgical and block‐related) at three, six and 12 months.

Two authors (AA and GSS) will independently extract, collect and record data in the data extraction form. A copy of this form is in Appendix 2. We will resolve any discrepancies between the data extracted by discussion. If we are unable to reach a consensus we will consult with a third author (MHA). If information on data or trial methodology is not reported in the published articles, GSS or AA will contact the corresponding author of the relevant trial to solicit the missing information.

Assessment of risk of bias in included studies

Two review authors (AA, GSS) will independently evaluate each report meeting the inclusion criteria. We will contact authors for missing information regarding their methods. We will grade study quality on the basis of a checklist of design components: random sequence generation, allocation concealment, blinding of participants and personnel, blinding of outcome assessment, incomplete outcome data, selective reporting and other bias. We will accept single‐blinding as the obvious effects of regional anaesthesia make blinding of participants and care givers all but impossible. We will insist on an adequate description of outcome observer blinding.

We will achieve consensus by informal discussion. A third author (MHA) will serve as final arbiter, where needed.

We will consider a trial as having a low risk of bias if all domains are assessed as adequate. We will consider a trial as having a high risk of bias if one or more domain is assessed as inadequate or unclear. We will list all omitted studies and detail the reason for each exclusion (Moher 1999).

We will report the 'Risk of bias' table as part of the table 'Characteristics of included studies' and present a 'Risk of bias summary' figure which will detail all of the judgements made for all included studies in the review.

Measures of treatment effect

Joint function will be measured with continuous outcome scores. There are outcome scores specific for each joint. We will endeavour to use the appropriate score for each joint (for example, the Knee Society Score following total knee arthroplasty). The minimal clinically significant difference for the score used for each joint will be clearly stated in the review.

We will evaluate primary and secondary outcomes separately for each joint (hip, knee, shoulder). In other words, we will stratify the included trials according to the joint replaced (total hip, knee and shoulder replacement). We feel that the anatomical and physiological differences between shoulder, hip and knee surgery argue against pooling or comparing studies on different joints (Higgins 2011).

We expect that studies will not all report the outcome using the same scale, even for the same joint. In this case we will employ the standardized mean difference as our summary statistic. As discussed in chapter 9.2.3.2 of the Cochrane Handbook for Systematic Reviews of Interventions, these outcome scales, while not actual continuous outcomes, can be reviewed using the same statistical methods (Higgins 2011). The use of different scales does not reflect real differences in variability among study populations but rather subjective preferences by the study authors. For studies that do not report a continuous score, we will extract from the published data or solicit from the authors the information needed to score the included patients.

For the secondary outcomes:

1. quality of life will also be expressed as a score, as discussed above the standardized mean difference will be used if studies use different scales;

2. complications and adverse events (medico‐surgical and block‐related) are dichotomous events and we will use the risk ratio as a measure to compare intervention group versus control group risk.

We will use the mean difference or the standardized mean difference, as appropriate.

Unit of analysis issues

Our unit of analysis is the patient rather than each operated joint. If studies include patients operated on bilaterally, that is the left and the right knee on the same day, we will use (and expect the authors to report) an average of the joint scores of both knees.

We will exclude (or given the nature of the condition and intervention studied we are not expecting) cluster‐randomized trials, crossover trials, or individuals undergoing more than one intervention. In the case of studies with multiple treatment groups, groups using different techniques of regional analgesia and groups not using regional analgesia, respectively, will be pooled. In the case that there are multiple observations at different time points for the same outcome, we will choose the one closest to the interval being studied.

Dealing with missing data

We will contact the corresponding authors of included studies to obtain any missing information or clarify data inconsistencies. Should we encounter significant skew in the outcome data, we will solicit individual patient data from the primary authors.

We will calculate missing standard deviations from the standard errors or confidence intervals. Where standard deviations cannot be calculated, we will impute these using the mean of the reported standard deviations from the other trials.

We will conduct an intention‐to‐treat (ITT) analysis.

Assessment of heterogeneity

As our primary approach to address heterogeneity between studies, we will stratify studies based on the joint replaced, as described above (see Measures of treatment effect). Secondly, we will group studies based on differences in rehabilitation and the type of regional analgesia interventions, for example, continuous versus single injection peripheral nerve blocks or epidural analgesia versus peripheral nerve blocks, as discussed below (see Subgroup analysis and investigation of heterogeneity).

We will investigate study heterogeneity between studies on each joint using a Chi² test and calculation of the I² statistic (Higgins 2002). However, we will use the random‐effects model regardless of the I² statistic for the reasons discussed (see Data synthesis). If the I² statistic falls between 30% and 60% for studies on one joint, we will consider this to possibly represent moderate heterogeneity and will pool our data only if we can clearly identify a credible explanation for the heterogeneity (see Subgroup analysis and investigation of heterogeneity) (Higgins 2011). We will abstain from pooling our data if the I² statistic is above 60% (Higgins 2011) for studies of one joint.

Assessment of reporting biases

We will contact authors to request missing data. We will counter time lag bias by repeating our search just prior to the submission of our work. To prevent language bias, we will not impose a language restriction.

We will examine publication bias using graphical and statistical tests (funnel plot, Egger’s test), as appropriate. We will report the funnel plot of all included studies, provided there are at least 10 studies, for outcomes at six months, distinguishing subgroups.

Data synthesis

We will calculate the standardized mean difference (SMD) of the various continuous scores between the groups stratified for each joint, as described in chapter 9.2.3.2. of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will ensure that all scales point in the same direction.

We will pool the standardized mean differences using the random‐effects model meta‐analysis with the RevMan 5.1 software provided by The Cochrane Collaboration, as detailed in chapter 8.6.5 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). A random‐effects model meta‐analysis will better incorporate the clinical heterogeneity that is typical among small studies of the long‐term effects of regional anaesthesia (Andrea 2008).

We will chose the random‐effects model because we want to address the question ‘what is the average intervention effect?’ (Higgins 2011). We assume that the different studies are estimating randomly different yet related intervention effects (Higgins 2011). By choosing the more conservative random‐effects model, confidence intervals for the average intervention effect will be wider. We anticipate between study heterogeneity (including but not limited to subtle variance in regional anaesthesia delivery) and prefer the random‐effects model because of its more cautious estimate of any treatment effect (DerSimonian 1986).

We will test for skewing of the outcome data by calculating the observed mean minus the lowest possible value (or the highest possible value minus the observed mean) and dividing this by the standard deviation, as suggested by Altman 1996.

Should we encounter significant skew, we will log transform the original data to reduce the skew after obtaining individual patient data from the original authors (Altman 1996).

We will translate the result of our evidence synthesis back into the recommended clinically used score to make the result easier to understand by clinicians.

Even though we will extract dichotomous data on adverse effects, these are typically reported inconsistently and anecdotally. Because the event rates of the typical adverse events after regional anaesthesia are too low, and the studies are far too small, our review will be underpowered to detect any possible differences in adverse event rates between the experimental and control groups. For this reason we will not attempt to pool them.

Subgroup analysis and investigation of heterogeneity

Choice of anaesthesia for the joint replacement proper, adjuvant medications and multimodal pain therapy, differences in rehabilitation, exclusion criteria and co‐morbidities, as potential sources of heterogeneity, will undergo subgroup analysis.

We will accept different choices of local anaesthetics as comparable treatments because we consider the pharmacodynamic differences between the typical local anaesthetics used to be negligible and the pharmacokinetic differences will be obliterated by the use of continuous blocks. However, the duration of action of a single‐shot block differs substantially enough from a continuous infusion and an epidural technique differs enough from a plexus or nerve block technique; hence we will consider a subgroup analysis to investigate the differences between single‐injection versus continuous analgesia interventions, and between epidural versus plexus or nerve block techniques.

We will investigate the sensitivity of our effect measure to the exclusion of studies that do not have similar pain control schemes in both groups. An example would be studies in which an NSAID is administered locally in the experimental group, along with a local anaesthetic, while the control group does not receive NSAIDs by any route.

We will scrutinize the forest plot for between study heterogeneity and consider the differences in rehabilitation that we were able to extract as potential sources of heterogeneity. Should we find both pragmatic and explanatory trials, we will exclude the explanatory trials to test if the pragmatic trials alone still show an effect in spite of the inclusion of a wider range of participants and hence possibly larger standard deviations.

Sensitivity analysis

We will carry out a sensitivity analysis on the quality characteristics of the included studies, primarily reflected by our judgements described in the risk of bias tables, to explore the influence of the high risk of bias studies on the overall pooled result. We will investigate if choosing a fixed‐effect model versus a random‐effects model would have changed the result of our evidence synthesis.