Criteria for considering studies for this review
Types of studies
Randomised and quasi-randomised (method of allocating participants to a treatment which is not strictly random: e.g. by hospital number) controlled clinical trials which evaluate exercise therapy for patellofemoral pain syndrome will be included.
Types of participants
Adolescents and adults with patellofemoral pain syndrome (designated by the trial author(s) as such or as 'anterior knee pain syndrome', 'patellar dysfunction', 'chondromalacia patellae' or 'chondropathy').
Studies focusing on other named knee pathologies such as Hoffa's syndrome, Osgood Schlatter syndrome, Sinding-Larsen-Johansson syndrome, iliotibial band friction syndrome, tendinitis, neuromas, intra-articular pathology including osteoarthritis, rheumatoid arthritis, traumatic injuries (such as injured ligaments, meniscal tears, patellar fractures and patellar luxation), plica syndromes, and more rarely occurring pathologies, will be excluded (Nissen 1998; Thomee 1999).
Types of interventions
We will include studies evaluating exercise therapy for patellofemoral pain syndrome. Exercises can be applied on their own or in combination with other non-surgical interventions, provided the same other intervention is applied to the whole population in the comparison. Exercises can be performed at home or under supervision of a therapist.
Exercise therapy versus control (no treatment, placebo or waiting list controls). This also includes 'exercise therapy + another intervention (e.g. taping) versus the other intervention alone (e.g. taping)'.
Exercise therapy versus different conservative interventions (e.g. taping).
Comparisons of different exercises
Delivery of exercises or exercise programmes (e.g. supervised versus home exercise; group versus individual supervision).
Medium of exercises or exercise programmes (water versus land based exercise).
Types of exercise (e.g. closed versus open kinetic chain exercises; dynamic versus isometric).
Target of exercise (strengthening of hip or abdominal muscles versus quadriceps muscles)
Duration of exercises or exercise programmes (e.g. long duration (more than three months) versus shorter duration (less than three months)).
Intensity of exercises or exercise programmes (e.g. high intensity (several times per week) versus low intensity (once weekly)).
The intervention groups for comparisons of different exercises will be defined as the most novel intervention (and first listed) of the two exercises being compared. For instance, the intervention is supervised exercise and the control is home exercise in the first comparison of 3a. Consideration will also be given to consistency in the choice of control groups.
Combined interventions or treatment packages including exercise will not be tested in this review, with the exception of exercises provided with instructions or advice, where exercise is the predominant intervention.
Types of outcome measures
Knee pain measured by validated self reporting methods (Visual Analog Scale [VAS], numerical rating scale [NRS] of McGill Pain questionnaire) (Melzack 1987). Pain scores are reported for pain in daily life (usual pain), for worst pain and for pain at activities (e.g. sports) if available (Crossley 2004).
Functional ability (i.e. knee function in activities of daily living). Questionnaires focusing on knee function (such as Functional Index Questionnaire (Chesworth 1989), WOMAC Osteoarthritis Index (McConnell 2001), Kujala Patellofemoral Function Scale (Kujala 1993) and Lysholm scale (Lysholm 1982)).
Functional performance tests (squatting, hopping on one leg, etc) (Loudon 2002).
Subjective perception of recovery. Recovery from patellofemoral pain syndrome is a outcome measure inconsistently reported in studies and different methods are used to describe recovery. In this review, 'number of patients no longer troubled by symptoms' or 'perceived recovery' measured on a Likert scale will be included as a secondary outcome measure (van Linschoten 2006).
Adverse events (e.g. knee swelling or substantially increasing pain levels as a direct effect of treatment).
Changes in knee function measured on impairment level only (e.g. range of motion, muscle strength) do not directly represent changes in the symptoms of patellofemoral pain or the resulting disability, and will therefore not be considered clinically relevant outcome measures in this review (Dursun 2001; Gobelet 1992).
Timing of outcome measurement
Outcomes measured within three months after the baseline measurement will be considered short term outcomes of exercise therapy, and measurements from three months and longer will be considered long term outcomes.
Search methods for identification of studies
We will search the Cochrane Bone, Joint and Muscle Trauma Group Specialised Register, the Cochrane Central Register of Controlled Trials (The Cochrane Library), MEDLINE (1946 to present), EMBASE (1980 to present), PEDro - The Physiotherapy Evidence Database (to present), CINAHL (1982 to present) and AMED (1985 to present). We will also search the WHO International Clinical Trials Registry Platform and Current Controlled Trials for ongoing and recently completed trials.
In MEDLINE (Ovid Online), a subject-specific strategy will be combined with the sensitivity-maximizing version of the Cochrane Highly Sensitive Search Strategy for identifying randomised trials (Lefebvre 2011). Search strategies for MEDLINE and the Cochrane Central Register of Controlled Trials are shown in Appendix 1.
No language restrictions will be applied.
Searching other resources
Reference lists of included studies and other relevant articles will be checked for additional trials, and institutions and experts in the field will be contacted in order to identify unpublished studies. Furthermore, conference abstracts will be searched from specific patellofemoral pain syndrome conferences such as the international patellofemoral research retreat (Davis 2010).
Data collection and analysis
Selection of studies
Two review authors (RAH and NEL) will select potentially eligible articles by reviewing the title and abstract of each citation. After obtaining full articles, both authors will independently perform study selection. In cases of disagreement, a consensus will be reached through discussion.
Data extraction and management
Two review authors (RAH and NEL) will independently extract the data within included trials using a piloted data collection form. Any disagreements will be resolved by consensus. Where data are missing or incompletely reported, authors of trials will be contacted. Where pooling is possible and if necessary, pain scores (VAS, NRS) will be converted to a 0 to 10 scale and function scores to 0 to 100 scale.
Assessment of risk of bias in included studies
Two review authors (RAH and NEL) will independently assess the risk of bias of the included studies using The Cochrane Collaboration's 'Risk of bias' tool (Higgins 2011). The following domains will be assessed: random sequence generation; allocation concealment; blinding of participants and personnel; blinding of outcome assessment; incomplete outcome data; selective reporting; and other bias. Other sources of bias will include bias from major imbalance in baseline characteristics and performance bias such as from lack of comparability in clinician's experience with the interventions under test or differences in care other than the interventions under test.
Each of these criteria will be explicitly judged using: low risk of bias; high risk of bias; and unclear risk of bias (where 'unclear' relates to a lack of information or uncertainty over the potential for bias). Disagreements between review authors regarding the risk of bias for domains will be resolved by consensus.
Measures of treatment effect
Risk ratios with 95% confidence intervals will be calculated for dichotomous outcomes. Mean differences with 95% confidence intervals will be calculated for continuous outcomes as appropriate. When two or more studies present their data derived from the same instrument of evaluation (with the same units of measurement), data will be pooled as a mean difference (MD). Conversely, we will use the standardised mean difference (SMD) when primary studies express the same variables through different instruments (and different units of measurement).
Unit of analysis issues
The unit of randomisation in the studies likely to be included in this review is usually the individual participant. Exceptionally, as in the case of trials including people with bilateral complaints, data for trials may be evaluated for knees, instead of individual patients. Where such unit of analysis issues arise and appropriate corrections have not been made, we will consider presenting the data for such trials only where the disparity between the units of analysis and randomisation is small. Where data are pooled, we will perform a sensitivity analysis to examine the effects of pooling these incorrectly analysed trials with the other correctly analysed trials.
For multi-comparison studies, we will attempt to combine data where two or more of the groups test interventions in the same category. Should combining not be appropriate but the data are presented for the difference comparisons are presented in the same analysis, the number of participants in the shared comparison will be divided (e.g. halved where this intervention appears twice) in order to avoid the 'double-counting' of participants for the 'shared comparison' in the meta-analyses. For cross-over trials, we will present data collected prior to the crossover of the intervention.
Dealing with missing data
We will contact trial authors where further details of methodology or data are required for trial inclusion.
Where possible we will perform intention-to-treat analyses to include all people randomised. However, where drop-outs are identified, the actual numbers of participants contributing data at the relevant outcome assessment will be used. We will be alert to the potential mislabelling or non-identification of standard errors and standard deviations (SDs). Unless missing standard deviations can be derived from confidence intervals or standard errors, we will consider whether it is appropriate to estimate values based on comparable data included in this review in order to present these in the analyses. We will make clear for which trials imputed data have been used (e.g. footnotes in the forest plots).
Where data are presented as the median (inter-quartile range), we will not attempt to transform data to achieve normality or to estimate the mean and SD.
Assessment of heterogeneity
Heterogeneity will be assessed by visual inspection of the forest plot (analysis) along with consideration of the chi² test for heterogeneity and the I² statistic (Higgins 2011). Heterogeneity will be considered statistically significant at P < 0.1. Studies will also be examined for methodological and clinical heterogeneity, particularly if significant statistical heterogeneity is identified.
Assessment of reporting biases
Where data for at least 10 studies are available for pooling, we will assess for publication bias by using funnel plots (Higgins 2011).
When considered appropriate, results of comparable groups of trials will be pooled using both fixed-effect and random-effects models. The choice of the model to report will be guided by a careful consideration of the extent of heterogeneity and whether it can be explained, in addition to other factors such as the number and size of studies that are included.
Subgroup analysis and investigation of heterogeneity
Where data permit, we will perform the following subgroup analyses:
We will inspect the overlap of confidence intervals and perform the test for subgroup differences available in RevMan to test whether subgroups are statistically significantly different from one another.
Where appropriate, we will perform sensitivity analyses investigating the effects of risks of bias by excluding trials with high or unclear risk of bias (such as for trials with lack of allocation concealment and lack of random sequence bias) and trials reported in abstracts only. Sensitivity analyses will also be performed to explore the differences between different models (fixed-effect versus random-effects) for pooling data where there is heterogeneity. Furthermore, we will perform sensitivity analysis for the trials with imputed data.
'Summary of findings' tables
Where there are sufficient data, we will summarise the results for the main comparisons described in the Types of interventions in 'Summary of findings' tables. We shall use the GRADE approach to assess the quality of evidence related to each of the primary outcomes listed in the Types of outcome measures (Higgins 2011; see section 12.2).