## Introduction

There are numerous systematic reviews, literature reviews and clinical practice guidelines summarising the effectiveness of different physiotherapy interventions for people with spinal cord injuries (SCIs).1, 2, 3, 4, 5, 6, 7, 8, 9, 10, 11, 12 However, most include non-randomised studies that are highly vulnerable to bias. There are some high-quality Cochrane Systematic Reviews, but they often include interventions not typically administered by physiotherapists or include people with different types of neurological conditions. They are also very detailed, which can limit their accessibility.11, 13, 14, 15 We wanted to provide an unbiased but very accessible summary of the evidence underpinning physiotherapy practice as part of a larger project devoted to adding 'evidence tips' to the physiotherapy module of www.elearnSCI.org. For this reason, we conducted 22 brief reviews that were restricted to randomised controlled trials. The reviews are 'brief' because each examines the effectiveness of an intervention on one primary outcome. The results of each review are pooled in this one paper to provide an overall summary of the evidence about the effectiveness of a range of different but commonly administered physiotherapy interventions.

## Materials and methods

Twenty-two brief reviews were conducted. Each brief review looked at the effectiveness of an intervention on one primary outcome (Table 1), and each intervention/outcome pair was considered independently. The interventions and outcomes were selected a priori and reflected those of most interest to physiotherapists, and those described within www.elearnSCI.org. The list of interventions and outcomes is not exhaustive, and unlike a typical systematic review we did not look at all the possible effects of any single intervention.

## Identification and selection of studies

The following electronic databases were searched for publications up until December 2015: Medline, CINAHL, Embase, the Cochrane Central register of controlled trials and the Physiotherapy Evidence Database (PEDro). A search strategy for randomised controlled trials7 was used along with the following terms: parapleg$, quadripl$, tetrapleg$, wheelchair$ and spinal cord. This search strategy was adjusted for each database.

Two reviewers screened publications by title and abstracts against the inclusion criteria. Full copies of potentially eligible trials were retrieved and again screened for eligibility. Any disagreements between the two reviewers were resolved by a third independent reviewer.

## Inclusion criteria

### The participants

The participants of interest were people with SCI. Trials involving people with conditions other than SCI were only included if at least 75% of the participants had sustained a SCI. Trials involving predominantly children were excluded.

### The interventions

The interventions of interest were seated mobility training, wheelchair mobility training, electrical stimulation (ES), hand training (with and without ES), overground gait training (with and without ES), bodyweight supported treadmill training (BWSTT, with and without ES), robotic gait training, strength training (for non-paralysed and partially paralysed muscles, with and without ES), stretch, passive movements, fitness training, cycling with ES, general exercise and transcutaneous electrical nerve stimulation (TENS). Trials were only included if the intervention was administered on more than one occasion.

### The comparison

Trials were included if they compared the interventions of interest with no intervention or a sham intervention. Robotic and BWSTT were also compared with overground walking. Trials that included co-interventions or usual care were included if the co-interventions or usual care were administered to both groups to make it possible to determine the added benefit of the intervention of interest.

### The outcomes

One outcome was pre-determined for each brief review (Table 1). For example, the primary outcome for the review about BWSTT was gait, and the primary outcome for the review about stretch was joint range of motion. The primary outcome for each review was one of the following: seated mobility, wheelchair mobility, hand function, gait, voluntary strength, joint mobility, fitness and pain. If a trial included two or more measures of the same outcome (for example, Walking Index for Spinal Cord Injury (WISCI) and 10 m walk test to reflect gait), then one measure was chosen, which best reflected the outcome of interest. This measure was chosen without looking at the results of the trial and using a decision rule that prioritised measures according to whether they were:

1. 1

Identified by the authors as the primary outcome (either in the paper or in the trial registry)

2. 2

Easily interpretable by clinicians

3. 3

Reported in sufficient detail to determine mean between-group differences or risk ratios and corresponding 95% confidence intervals.

### Types of studies

Only randomised controlled trials written in English were included. Cross-over trials were included provided allocation to the treatment schedule was randomised. Trials with more than two parallel comparisons were included provided two of the comparisons met the inclusion criteria. If trials were published more than once or interim analyses were published prior to the completion of the trial, then the most recent or most relevant publication was retrieved.

## Data extraction

One reviewer extracted study characteristics and two reviewers extracted outcome data from the included studies onto a standardised Excel spreadsheet. Data from only one time period were used for each trial and reflected the first time period after the intervention ceased. For example, if a trial examined a 6-week gait training programme and included an assessment at 6 weeks and 12 weeks, then only the data from the 6-week assessment were included.

We planned to deal with any type of data that may be extracted including time-to-event and count data; however, only continuous and dichotomous data were ultimately retrieved. The mean between-group differences (95% confidence interval) and risk ratios were extracted, respectively. If these were not provided, then available post or change data were used to derive between group differences using the methodology recommended by Cochrane.16

### Methodological quality of the included trials

The methodological quality of each trial was assessed using the PEDro scale (Table 2). The PEDro scale has 10 items that address key issues of bias. A total score of ten indicates minimal susceptibility to bias. The scores were attained from the PEDro website for all trials, except two, which were scored by the authors because they were not on the website.17, 18 The scores on the PEDro website have been verified by two independent and formally trained raters from the Centre of Evidence-Based Physiotherapy.

## Data synthesis

### Statistical analysis

Data from trials for each brief review (that is, for each combination of intervention and outcome) were pooled if possible using meta-analyses provided there was not statistical (I2>60%) or clinical heterogeneity. The 'metan' and 'admetan' commands of Stata (StataCorp, College Station, TX, USA) were used to generate forest plots and conduct all meta-analyses. Results were cross-checked using RevMan 5.1 software. A random-effects model was used for all meta-analyses. If continuous outcomes were similar across trials, then a weighted mean difference was calculated. If continuous outcomes measuring the same construct were different, then results were pooled using a standardised mean difference. A risk ratio was calculated for dichotomous data.

### Definition of treatment effectiveness

The results of each brief review were defined as effective, ineffective or inconclusive according to the between group differences. The overall between-group difference was used for the brief reviews with a meta-analysis, and the between-group difference of individual trials was used for the brief reviews without a meta-analysis. The following decision rule was used:

1. 1

Effective. An intervention was classified as effective if the lower end of the 95% confidence interval (CI) of the between-group difference fell above the minimally worthwhile treatment effect.

2. 2

Ineffective. An intervention was classified as ineffective if the upper end of the 95% CI of the between-group difference fell below the minimally worthwhile treatment effect.

3. 3

Inconclusive. An intervention was classified as inconclusive if the 95% CI of the between-group difference spanned the minimally worthwhile treatment effect.

The minimally worthwhile treatment effect was defined according to the value articulated by the authors of the original trial provided it was defined prior to the commencement of the trial. When a minimally worthwhile treatment effect was not articulated by authors a priori or when there was more than one trial in a brief review, the minimally worthwhile treatment effect was set as equivalent to 10% of mean post-values for the control groups. The minimally worthwhile treatment effect was set as 0.2 s.d. for brief reviews with meta-analyses expressed in standardised mean differences.

### Grading the strength of evidence

The strength of evidence was only rated for brief reviews that indicated a treatment was either effective or ineffective. It was not rated for brief reviews with inconclusive findings. The Grading of Recommendations Assessment, Development and Evaluation (GRADE) methodology was used.19 GRADE uses a four-point scale (high quality, moderate quality, low quality and very low quality) based on a number of factors including the risk of bias in the trials, consistency of results across trials, the precision of estimates and the size of treatment effects. The PEDro scores for each trial were used to guide judgments about the risk of bias, although other potential sources of serious bias not captured by the PEDro scores were also considered.

## Results

### Flow of studies through the review

The search retrieved 15 784 papers. A total of 147 papers were randomised controlled trials involving people with SCI and were potentially eligible, but after evaluating the full text and excluding duplicate publications only 38 trials met the inclusion criteria (Table 2).17, 18, 20, 21, 22, 23, 24, 25, 26, 27, 28, 29, 30, 31, 32, 33, 34, 35, 36, 37, 38, 39, 40, 41, 42, 43, 44, 45, 46, 47, 48, 49, 50, 51, 52, 53, 54, 55

### Description of the trials

Seven trials did not provide sufficient data for analysis.17, 18, 20, 21, 22, 30, 32 The remaining 31 trials were relevant to 15 of the 22 brief reviews (Table 1). One trial had three arms and included two relevant comparisons.43 Another two trials had interventions and outcomes that were relevant to more than one of the brief reviews.42, 48 Data from these trials were therefore used in more than one brief review. Meta-analysis was appropriate for 8 of the brief reviews.

### Findings

Four reviews indicated that treatments were effective (Table 1 and Figure 1). The treatments were fitness training, wheelchair mobility training, hand training and TENS. These four reviews included 8 trials of 201 participants or limbs (for trials using within-subject designs). The GRADE strength of evidence for each of these reviews was either moderate or very low.

One review indicated that a treatment was ineffective (see Table 1 and Figure 2). The treatment was stretch for joint range of motion. This review included three trials of 100 participants or limbs (for trials using within-subject designs). The GRADE strength of evidence for this review was moderate.

The results of 10 reviews were inconclusive (Table 1 and Figure 3)—that is, they failed to rule in or rule out a possible therapeutic effect. The treatments included BWSTT (with or without ES) and robotic gait training compared with overground gait training, strength training (with or without ES), passive movements, seated mobility training and general exercise (for pain).

There were no trials with useable data relevant to seven reviews. The treatments included overground gait training, robotic gait training and BWSTT (with and without ES) compared with no or sham intervention, hand training with ES and cycling with ES.

## Discussion

Many papers, systematic reviews and clinical practice guidelines have summarised the evidence underpinning different physiotherapy interventions for people with SCI. However, our summary of the evidence is unique because of its wide scope and because it examines the effectiveness of commonly administered physiotherapy interventions in one paper. We defined a primary outcome for each review and we worked to a protocol. Our protocol was driven by clinical questions expressed in PICO format where P reflects participants, I reflects intervention, C reflects comparison and O reflects outcome. In addition, we interpreted our results with respect to a pre-defined minimally worthwhile treatment effect for each brief review. This approach minimises the risk of spurious findings and conclusions.

The results of our brief reviews indicate evidence to support four interventions; however, the strength of evidence is not high for any of these interventions and only moderate for two of them (i.e., fitness training and TENS). The results of the remaining brief reviews are either inconclusive or in the case of stretch indicate that the treatment is ineffective. Interestingly, there were no trials with usable data for 7 of the 22 brief reviews. Importantly, lack of evidence does not mean that interventions are ineffective. Lack of evidence does, however, justify reconsidering our confidence about the effectiveness of some widely accepted interventions and should prompt us to question some long-held assumptions about what physiotherapists should and should not do. The failure of physiotherapy research to demonstrate treatment effectiveness is not unique to physiotherapy and SCI, nor is it unique to rehabilitation.

Other summaries of evidence include non-randomised trials and soft evidence. Some argue that we need to revert to this type of evidence because of the paucity of randomised controlled trials. However, this type of evidence is highly vulnerable to different sources of bias that tend to exaggerate treatment effectiveness. It therefore gives a distorted impression of the real situation and may only serve to give misplaced confidence about the efficacy of different interventions. This type of evidence is particularly vulnerable to publication bias because non-randomised trials and soft evidence are unlikely to be published if the results are negative.

The interpretation of each brief review relies on our definitions of minimally worthwhile treatment effects. Our use of minimally worthwhile treatment effects enabled us to consider the size of treatment effects and distinguish between results that are inconclusive and results that provide evidence that a treatment is ineffective. Some may disagree with our definitions of minimally worthwhile treatment effects, and this may slightly change the conclusions of some reviews. The review most likely to be affected by a change in the definition of its minimally worthwhile treatment effect is the review comparing BWSTT with overground gait training. We concluded that it is not clear whether BWSTT is superior to overground gait training on the basis of how fast control participants of the included studies walked. However, regardless, some physiotherapists and patients may want to see an added treatment benefit of at least 0.1 m/sec in gait velocity to justify the use of BWSTT. If this is the case, then the results of our brief review indicate that BWSTT is not superior to overground gait training. Clearly, clinicians and patients need to make their own decisions about minimally worthwhile treatment effects and then interpret the results of each brief review accordingly.

The findings of all the brief reviews need to be interpreted in the context of the comparisons. For example, the failure to demonstrate that stretch applied by a physiotherapist is ineffective does not mean that stretch as typically incorporated into routine care is also ineffective. Clinical trials can only answer questions about the relative effectiveness of the two interventions examined in the trial. Dosage is also clearly a critical aspect of a trial, and the failure of some trials to demonstrate treatment effectiveness may reflect insufficient treatment dosages. For example, perhaps strengthening and stretching exercises need to be applied at much higher dosages than typically applied in clinical trials and perhaps for many months or even years.

The 22 selected interventions reflect those most widely administered in clinical practice. They were chosen on the basis of studies that have systematically quantified the types of interventions commonly administered by physiotherapists56, 57, 58, 59, 60 and on the basis of the physiotherapy module of www.elearnSCI.org. Of course some may disagree with our choice of the 22 most widely administered interventions and the primary outcomes that we selected to reflect their effectiveness. Future studies could use a Delphi process to get consensus among physiotherapists around the world to clarify these issues or repeat existing observational studies that have attempted to clarify the most widely used physiotherapy interventions on a larger sample of SCI units from many different countries. Interestingly the majority of research attention is being directed at BWSTT and robotic gait training with comparatively little research attention being directed at some of the more mundane but widely administered interventions such as strengthening and stretching exercises.56, 57, 58, 59, 60

There are three main limitations of this systematic review. First, we may have introduced bias when selecting the relevant outcomes from each trial. We think that this is unlikely because as far as possible we made decisions about the choice of outcomes prior to examining the results of trials. Second, we did not include trials that compared different types of interventions (except for BWSTT and robotic gait training, which were compared with overground gait training). We restricted our inclusion criteria in this way to keep the review manageable but also to restrict conclusions to the effectiveness of interventions per se. The relative effectiveness of different interventions is a more complex question. It becomes particularly complex when results fail to demonstrate that one treatment is superior to another because without a control group it is not known whether both treatments are effective or both treatments are ineffective. Thus, as a first step to summarising the evidence, it is important to examine the effectiveness of interventions compared with no intervention or sham interventions (or usual care provided both groups received usual care). The third limitation of this study is that we only looked at the effectiveness of each intervention on one outcome. We selected each outcome for each intervention a priori and on the basis of the most common reason why an intervention is administered by physiotherapists. For example, BWSTT is most widely used to improve gait. Hence, for this intervention, the outcome of interest was gait. However, BWSTT may also have other therapeutic benefits that were not captured.

This systematic review provides an overview of the existing evidence related to common questions about the effectiveness of different physiotherapy interventions for people with SCI. It indicates initial evidence for four interventions. However, there are a lot of uncertainties about most of the widely used physiotherapy interventions for people with SCI. Without a strong evidence base for current clinical practice, all new and innovative interventions and all trials designed to compare different interventions are building on shifting and possibly incorrect assumptions about the effectiveness or ineffectiveness of current physiotherapy treatments. Therefore, future research needs to not only explore new interventions but also build a strong evidence base to current practice. A strong evidence base relies on research that is void of bias.