Criteria for considering studies for this review
Types of studies
To assess benefit, randomised controlled trials (RCTs) and controlled clinical trials (CCTs) will be searched. If no RCTs or CCTs are identified, we will include controlled before and after studies (CBAs) and interrupted time series (ITS). Registries will be searched for survival rate evaluations.
Types of participants
Participants will be adult patients with unicompartmental OA of at least grade 2 according to Ahlbäck radiologic criteria (Ahlbäck 1968) or grade 4 according to the Kellgren and Lawrence grading system (Petersson 1997).
Types of interventions
Intervention: unicompartmental knee arthroplasty.
Control: no intervention (usual care) or any other surgical techniques currently available for treating unicompartmental knee OA, particularly tibial osteotomy, TKA, or mosaicplasty.
Types of outcome measures
SF-36 (Short-Form 36) or EQ-5D (EuroQoL in 5 dimensions), VAS (visual analogue scale) pain and stiffness, WOMAC (Western Ontario and McMaster Osteoarthritis Index), and clinical and radiologic KSS (Knee Society Score) will be searched as standardized outcomes measures. Follow-ups of 6 months, 1 year, 5 years, 10 years, and 15 years or longer will be searched.
These major outcomes will be part of the summary of findings table.
Search methods for identification of studies
Studies will be searched in the following electronic databases: the Cochrane Central Register of Controlled Trials (CENTRAL) (The Cochrane Library, current issue); MEDLINE (1966 to present); CINAHL (1982 to present); EMBASE (1988 to present); and Web of Science (1900 to present). No language restriction will be applied. We will also search databases of ongoing trials: Current Controlled Trials (www.controlled-trials.com－with links to other databases of ongoing trials).
For full details of the search strategy, please see Appendix 1.
Searching other resources
We will try to identify additional studies by searching the reference lists of included trials.
Data collection and analysis
Two authors will independently assess all potential abstracts and published reports that will be identified by the literature search strategy. Consensus will be reached through discussion of any disagreements. Reasons for excluded studies will be noted. These two authors will be blinded to authors and institution but will not be blinded to the journal of the publication.
Selection of studies
With the use of reference management software program, search results will be merged, and duplicate records of the same report will be removed. Each author will examine titles and abstracts independently to remove obviously irrelevant reports (authors would be over inclusive at this stage). Full text of potentially relevant reports will be retrieved, and multiple reports of the same study will be linked together (author names, location and setting, specific details of the interventions, numbers of participants and baseline data, date and duration of the study). Full-text reports will be examined for compliance of studies with eligibility criteria. Final decisions on study inclusion will be made after comparison of selected studies by each author. Discrepancies will be resolved by consensus of two authors.
A kappa statistic will be calculated for measuring agreement between the two authors who are making simple inclusion/exclusion decisions. Values of kappa between 0.40 and 0.59 will be considered to reflect fair agreement, between 0.60 and 0.74 to reflect good agreement, and 0.75 or higher to reflect excellent agreement.
Data extraction and management
Each author will extract data independently using predesigned standardized data abstraction forms (in accordance with the checklist Table 7.3.a of the Cochrane Handbook for Systematic Reviews of Interventions; Higgins 2011a). One author will enter data into RevMan, and the other will cross-check the printout against his or her own data extraction forms. We will resolve discrepancies by consensus of two authors. We will obtain information from the primary author when the published article provides inadequate information for the review.
Assessment of risk of bias in included studies
The risk of bias of included trials will be assessed independently by two authors using the 'Risk of bias' tool of The Cochrane Collaboration (Higgins 2011b). Risk of bias will be categorized as low, uncertain, or high for each of the included studies (Table 1). Disagreements will be resolved through discussion (a third author will be asked to adjudicate if necessary). The biases listed in the table below will be assessed.
Table 1. Risk of bias tool of the Cochrane Collaboration
| Domain|| Support for judgement|| Review authors’ judgement|
|Selection bias.|| || |
| Random sequence generation.||Describe the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.||Selection bias (biased allocation to interventions) due to inadequate generation of a randomised sequence.|
| Allocation concealment.||Describe the method used to conceal the allocation sequence in sufficient detail to determine whether intervention allocations could have been foreseen in advance of, or during, enrolment.||Selection bias (biased allocation to interventions) due to inadequate concealment of allocations prior to assignment.|
|Performance bias.|| || |
| Blinding of participants and personnel Assessments should be made for each main outcome (or class of outcomes). ||Describe all measures used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. Provide any information related to whether the intended blinding was effective.||Performance bias due to knowledge of the allocated interventions by participants and personnel during the study.|
|Detection bias.|| || |
| Blinding of outcome assessment Assessments should be made for each main outcome (or class of outcomes).||Describe all measures used, if any, to blind outcome assessors from knowledge of which intervention a participant received. Provide any information related to whether the intended blinding was effective.||Detection bias due to knowledge of the allocated interventions by outcome assessors.|
|Attrition bias.|| || |
Incomplete outcome data
Assessments should be made for each main outcome (or class of outcomes).
|Describe the completeness of outcome data for each main outcome, including attrition and exclusions from the analysis. State whether attrition and exclusions were reported, the numbers in each intervention group (compared with total randomised participants), reasons for attrition/exclusions where reported, and any re-inclusions in analyses performed by the review authors.||Attrition bias due to amount, nature, or handling of incomplete outcome data.|
|Reporting bias.|| || |
| Selective reporting.||State how the possibility of selective outcome reporting was examined by the review authors and what was found.||Reporting bias due to selective outcome reporting.|
|Other bias.|| || |
| Other sources of bias.|
State any important concerns about bias not addressed in the other domains in the tool.
If particular questions/entries were prespecified in the review’s protocol, responses should be provided for each question/entry.
|Bias due to problems not covered elsewhere in the table.|
|Random sequence generation (selection bias)|
|Allocation concealment (selection bias)|
|Blinding of outcome assessment (detection bias)|
|Blinding of participants and personnel (performance bias)|
|Incomplete outcome data (attrition bias)|
|Selective reporting (reporting bias)|
Measures of treatment effect
For each study, we will calculate risk ratio, except in the cases of rare events when the Peto odds ratio (OR) is most appropriate along with 95% confidence limits for dichotomous outcomes, and we will compute standardised mean differences (SMDs) and 95% confidence limits for continuous outcomes according to the method described by Rutjes (Rutjes 2010). For continuous outcomes such as pain, measured on the same scale, mean differences will be calculated.
Unit of analysis issues
Authors will consider whether in each study, a unit-of-analysis issue arises: if groups of individuals were randomly assigned together to the same intervention (i.e., cluster-randomised trials); if individuals undergo more than one intervention (e.g., in a cross-over trial, or simultaneous treatment of multiple sites on each individual [i.e., multiple joint prothesis]); or if multiple observations have been reported for the same outcome (e.g., repeated measurements, recurring events, measurements on different body parts).
Dealing with missing data
When possible, the authors will contact the original investigators to request missing data. Authors will make explicit the assumptions of any methods used to cope with missing data, for example, that the data are assumed missing at random, or that missing values were assumed to have a particular value such as a poor outcome. Sensitivity analyses will be performed to assess how sensitive results are to reasonable changes in the assumptions that are made. In the Discussion section, we will address the potential impact of missing data on the findings of the review.
Assessment of heterogeneity
Where statistical evidence of heterogeneity is found (a Chi2 test with P < 0.10 or an I2 test with a percentage of variability in effect estimates > 50%), we will use a random-effects model. Forest plots will be visually inspected for identification of heterogeneity.
Assessment of reporting biases
Funnel plots will be used to assess for the potential existence of small study bias for primary outcomes. A number of explanations for the asymmetry of a funnel plot are known. For continuous outcomes, we will use Egger’s test for asymmetry. Therefore, we will carefully interpret results (Rutjes 2010; Sterne 2011).
If meta-analysis is possible, the Mantel Haenszel statistical method will be used. A fixed approach to the analysis will be undertaken unless evidence of heterogeneity is noted across studies, in which case the random-effects model will be used.
Subgroup analysis and investigation of heterogeneity
We will carry out subgroup analyses if one of the primary outcome parameters demonstrates statistically significant differences between intervention groups.
Subgroup analysis will be done in terms of patients' age (< 65 years or older), gender (female or male), and body mass index (< 30 kg/m2 or superior) and preoperative angular deformity in the frontal plane (mechanical axis deviation > 9°), and between lateral and medial unicompartmental arthroplasty.
A sensitivity analysis will be performed to compare studies in terms of their inclusion criteria, variations in treatment used, and study design. An analysis will be performed on study quality, which will be judged in terms of having low risk of bias as adequate allocation concealment, blinding, and limited loss to follow-up, with all trials contributing data to the review. For outcome instruments, we will compare effect size estimates and bootstrap confidence intervals when each subscale is considered independently or as a whole.
Grading the evidence
The grading system recommended by the Musculoskeletal Group and developed by the Grades of Recommendation, Assessment, Development and Evaluation Working Group (GRADE Working Group) will be used: The GRADE approach defines the quality of a body of evidence as the extent to which one can be confident that an estimate of effect or association is close to the quantity of specific interest (Schünemann 2011). The quality of a body of evidence involves consideration of within-study risk of bias (methodologic quality), directness of evidence, heterogeneity, precision of effect estimates, and risk of publication bias. The GRADE system entails an assessment of the quality of a body of evidence for each individual outcome. The GRADE approach specifies four levels of quality. The highest quality rating is used for randomised trial evidence. Review authors can, however, downgrade randomised trial evidence to evidence of moderate, low, or even very low quality, depending on the presence of the five factors. Usually, quality rating will fall by one level for each factor, up to a maximum of three levels for all factors. If very severe problems are noted for any one factor (e.g., when assessing limitations in design and implementation, all studies were unconcealed, were unblinded, and lost more than 50% of their patients to follow-up), randomised trial evidence may fall by two levels because of that factor alone (Table 2).
Table 2. Levels of quality of a body of evidence in the GRADE approach
| Underlying methodology|| Quality rating|
|Randomised trials; or double-upgraded observational studies||High|
|Downgraded randomised trials; or upgraded observational studies||Moderate|
|Double-downgraded randomised trials; or observational studies||Low|
|Triple-downgraded randomised trials; or downgraded observational studies; or case series/case reports||Very low|
The authors will downgrade randomised trial evidence to evidence of moderate, low, or even very low quality, depending on the presence of the five factors that may decrease the quality level of a body of evidence:
1. Limitations in the design and implementation of available studies suggesting high likelihood of bias.
2. Indirectness of evidence (indirect population, intervention, control, outcomes).
3. Unexplained heterogeneity or inconsistency of results (including problems with subgroup analyses).
4. Imprecision of results (wide confidence intervals).
5. High probability of publication bias.