Efficacy of electromyographic biofeedback compared with conventional physical therapy for upper-extremity function in patients following stroke: a research overview and meta-analysis.

[Moreland J, Thomson MA Efficacy of electromyographic biofeedback compared with conventional physical therapy for upper-extremity function in patients following stroke a research overview and meta-analysis. Phys Ther 1994,74534-547.]

Key Words: Cerebrovascular disorders; Electromyography, Feedback,. Meta-analysis, Upper extremity, general.

Rehabilitation of the upper extremity in patients who have sustained a stroke poses a major challenge to physical therapists. In a review of studies on upper-extremity recovery, Gowland[1] stated that only 4% to 9% of patients regained normal function, 23% to 43% regained some useful function, and 16% to 28% did not have return of any voluntary movement in the upper limb. One technique used to improve upper-extremity movement following stroke is electromyographic (EMG) biofeedback. Knowledge of its efficacy is important for decisions related to patient care and the utilization of limited rehabilitation resources.

The following question was addressed in this research overview: In patients following a stroke, is EMG biofeedback efficacious for improving upper-extremity function compared with conventional physical therapy? In this context, electromyographic biofeedback was defined as the use of instrumentation applied to the patient's muscle(s) with external electrodes to capture motor unit electrical potentials. The patient is asked to activate or lessen the activity of the muscle(s). The instrumentation converts the potentials into visual or audio information for the patient and the therapist. It is usually used to augment desired muscle action or to decrease unwanted muscle activity. There is no standardized approach. The question was focused on functional outcomes and the comparison with conventional therapy in order to provide information relevant to clinical decision making. For the purposes of this study, functional outcomes was defined as outcomes related to movement as opposed to physiological variables.

Rationale for This Overview

The investigation of EMG biofeedback therapy for patients following stroke has progressed from case studies to case series to comparison group studies. Interspersed with these studies, literature reviews have been published. A systematic search for reviews of EMG biofeedback for patients following stroke was done from 1981 forward. Six relevant review articles were located. To evaluate these reviews, the criteria developed by Oxman and Guyatt[2] were applied. The results are summarized in Table 1.

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Wolf[3] reviewed biofeedback studies using validity criteria. He concluded that the majority of studies supported the use of EMG biofeedback in addition to exercise. Ince et al[4] primarily discussed early case studies in their review. The authors concluded that the early studies demonstrated that EMG biofeedback is superior to "physical therapy" and that the later comparison studies have not concurred with this finding. The possibility of Type II error in the comparison studies was not discussed. In a position paper, Mar-Zuk[5] summarized the methodologic difficulties in assessing the efficacy of EMG biofeedback. Studies were reported but not appraised, nor was the rationale for their inclusion explained. The possibility of Type II error was not discussed for the control studies with nonsignificant findings. Marcer[6] critically appraised the methodology and analysis of EMG biofeedback trials. He concluded that all trials demonstrated clinically significant gains in patients with chronic conditions who would be least likely to improve but that the methodology was inadequate for demonstrating a specific effect of biofeedback.

De Weerdt and Harrison[7] conducted an extensive review with critical appraisal of the included studies. Selected validity criteria for the studies were assessed, and they concluded that the evidence was insufficient to answer the question of efficacy. They noted that in the more scientifically rigorous studies, the small sample sizes increased the risk of Type II error. In a review by Ince et al,[8] no studies were found to be definitive due to various problems with study design, presentation, and analysis. The authors suggested that future research should concentrate on functional activities in more basic well-controlled studies.

Among the review papers, some consistencies were evident. Generally, it was concluded that the early uncontrolled studies supported the finding of efficacy and that the later group studies did not. In none of the reviews were selection criteria provided or a quantitative analysis conducted. The possibility of Type II error also was not evaluated. We therefore conducted a systematic research overview and meta-analysis. With respect to Type Il error, meta-analysis is useful when individual sample sizes are too small to detect a statistically significant effect.

Methods

Identification of Relevant Studies

Because the first controlled study identified by De Weerdt and Harrison[7] was published in 1976, we confined our search to the period 1976 to 1992. MEDLINE was searched using the key words "electromyography," "biofeedback," and "cerebrovascular disorders." The key words "biofeedback" and "cerebral vascular accident" were used to search the CINAHL database. The Dissertation Abstracts International database was explored using the search words "electromyography" and "biofeedback." EXCERPTA MEDICA was reviewed manually, and a follow-up of key references was done via SCISEARCH. In an attempt to identify any unpublished studies, the authors of relevant articles were contacted by mail. The search was limited to English-language publications.

Each investigator reviewed all located references (titles and abstracts, if available) independently for relevance using four criteria. The reference lists within these reports and review articles were also evaluated in the same way. Any study deemed to be relevant by either author was included at this stage.

Selection of Studies

Relevant studies were assessed independently by each author for the following selection criteria:

1. Population: Adults poststroke.

2. Intervention: Treatment group-EMG

biofeedback alone or with

conventional physical therapy;

control group-conventional physical

therapy (exclusion of feedback

devices or functional electrical

stimulation).

3. Outcomes: Any functional measure

of the upper extremity, including

upper-extremity function testing,

stage of motor recovery, range of

motion, and muscle strength.

4. Methodology: Randomized control

trials with blinded outcome

assessment.

Interobserver reliability of these criteria was determined using the weighted Kappa statistic. Disagreements were resolved by consensus. Bias was minimized by the fact that one investigator does not treat patients who have had strokes and had no previous knowledge of the literature.

Validity Assessment of the Selected Studies

To judge the degree of confidence that can be placed on the conclusions and to identify possible explanations for differences in study results, the selected studies were evaluated using nine methodologic indicators:

1. Follow-up of 95% (excluding

deaths).

2. Treatment and control group comparability

(within 10% for age, time

poststroke, receptive communication,

sensation, and baseline measures

of outcome variables).

3. Provision of equal time and attention

to both groups.

4. Random allocation of therapists to

patients.

5. Monitoring of treatment protocols

to prevent bias.

6. Provision of placebo biofeedback

to the control group.

7. Avoidance of contamination and

cointervention.

8. Use of reliable and valid outcome

measures.

9. Analysis of withdrawals in the

group to which they were randomly

allocated.

Both investigators independently applied these criteria, and the interobserver agreement for each criterion was determined using the Kappa statistic. Disagreements were resolved by discussion.

Data Extraction

Information was abstracted from each study regarding the patients and facilities, the interventions, the sample size, the number of dropouts, and the results. Authors of the studies were contacted to obtain missing information.

Data Analysis

The goal of the data analysis was to integrate the results of the studies to obtain a representative estimate of the magnitude of the effect of EMG biofeedback and to explore the influence of mediating factors. In order to compare studies and combine the results of studies, several options exist. If the data are normally distributed, an effect size (difference between the means divided by the pooled standard deviation) can be calculated for each study.[9] Alternatively, an odds ratio[10] can be calculated if the data are available and if a reasonable cutoff point for success and failure can be defined.

The odds ratio is formed from nominal data (eg, improved versus not improved, EMG biofeedback versus conventional therapy). It estimates the strength of association between the treatment condition and the response to treatment. If the odds ratio is greater than 1.00, this indicates a more favorable response to EMG biofeedback than to conventional therapy. For example, the patients are "x" times more likely to improve. Although dichotomizing the data results in a loss of information, such dichotomization is a valuable alternative when data cannot be analyzed with parametric statistics. It also simplifies the results and conclusions to a clinical level when differences in measurement points lack clear meaning.

Plots of the data revealed that some distributions were highly skewed. We therefore decided to use odds ratios to describe each study and to combine the results, Because some of the outcome measures were imbalanced at baseline, the change score (post-treatment score minus pretreatment score) was used, Before any analyses were performed, improvement versus no improvement was selected as the cutoff point for success or failure. Analyses were done using the OR2x2xK program[11] to obtain the individual odds ratios and their 95% confidence intervals and the Mantel-Haenszel common odds ratios and their 95% confidence intervals (Cornfield method).[12,13] To test for homogeneity of the odds ratios, the Breslow-Day method[12,13] Was selected.

To obtain an indication of the magnitude of the effect and its clinical significance, the odds ratios were used to estimate the proportion of failures (no improvement) expected in the treatment group (P) . Using the proportion of failures in the control group from representative studies Pc), the number needed to treat to prevent a failure was calculated from the equation 1/[P.sub.c]-[P.sub.t].[14] An example of an odds ratio calculation and number needed to treat is provided in the Appendix.

To obtain a more sensitive indication of statistical significance, a Mann-Whitney U Test (Minitab 8.2) was done for each study. The one-tailed probability values were then combined using the Stouffer method[5] on Meta-analysis Programs, Version 5.1.[16]

These analyses were done for two outcome constructs: upper-extremity function and upper-extremity impairment. Outcomes measuring upper-extremity function and stage of motor recovery as delineated by Brunnstrom[17] were used to define the function construct. Impairment outcome measures were deemed to represent the impairment construct, Impairments were those outcomes that are substrates used to form movements such as muscle strength or range of motion. In cases where two outcomes were present from one study for a construct, the outcomes were combined to provide one input into the common odds ratio. For the combination of probability values, one outcome was randomly selected to represent that study in the meta-analysis.

A Priori Hypotheses Regarding Sources of Hoterogeneity

Before analyzing the results, we constructed a list of possible sources of heterogeneity. We hypothesized that differences in odds ratios may be due to the methodology, which included treatment monitoring versus no monitoring; treatment consisting of biofeedback combined with conventional therapy versus biofeedback alone; placebo feedback in the control maneuver versus no placebo; and acute (<6 months) versus chronic conditions. If significant heterogeneity was found, sensitivity analyses based on these hypotheses were planned. Sensitivity analyses divide the studies into two or more groups based on a factor (eg, acute studies and chronic studies). The groups are then analyzed separately to determine whether grouping has resulted in homogeneity and differences in the results.

Results

Selected Studies

Eighty-eight studies were identified as being relevant, and 8 of those studies[18-25] met the selection criteria. The interobserver agreement for applying the selection criteria to the relevant articles was .96 (weighted Kappa). The selected studies were all identified within the database searches. The responses from letters to authors yielded 8 studies; however, these studies did not meet our inclusion criteria. There was no additional return from the search through reference lists. Two of the 8 studies were subsequently excluded. In one instance,[24] contact with an author indicated that outcome evaluation was not blinded for all subjects. In this study, range of motion was the only functional outcome assessed. A study by John[25] was initially selected; however, information from the author revealed that this study was confined to lower-extremity training. The remaining 6 studies are summarized in Table 2.

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Study Quality

The methodological evaluation of each study is presented in Table 3 according to the nine validity criteria. Interobserver agreement ranged between .00 and .86 as measured by weighted Kappa and Kappa. Baseline imbalance for the outcome measures occurred in four of the studies.[18,20,21,23] Imbalance in prognostic variables was present in two of the studies.[21,23] The only studies in which monitoring of the treatment protocols was reported were those of Basmajian and colleagues.[19,21] Cointervention was present in one study,[19] in which emphasis on home practice was given to the experimental group and not the control group.

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Study Description

Essential information was not obtainable for the study by Hurd et al.[22] In this study, the results reported were probability values for combined upper- and lower-extremity measures of EMG output and range of motion. One publication (Smith[23]) contained the raw data, and the investigators in four of the studies (Crow et al,[18] Prevo et al,[20] and Basmajian and colleagues[19,21]) provided us with their data. Sufficient information, therefore, was available from five studies for analysis of the outcome results.

Crow et al[18] used EMG biofeedback to normalize muscle tone, gain active movement, and then aim for functional goals. This treatment was incorporated with regular ward physical therapy. The control group treatment consisted of therapy directed at the same goals. Outcomes were assessed with the Action Research Ann Test[26] and the Brunnstrom-Fugl-Meyer Test.[27]

Basmajian et al,[19] in 1987, incorporated EMG biofeedback with a cognitive behavioral approach. Feedback was used to train muscle recruitment and inhibition within the skill acquisition phase. The control treatment adhered to the neurodevelopmental treatment (NDI) approach. The Upper-Extremity Function Test[28] (UEFT) and the finger oscillation test29 were the outcome measures. In 1982, Basmajian et al[21] applied EMG biofeedback for both muscle recruitment and inhibition. This feedback was combined with the same treatment as the control group received, which was based on NDT principles. The primary outcome measure was the UEFF, and complete data were also available for grip strength (in millimeters of mercury) and pinch strength (in pounds).

Smith[23] also applied EMG biofeedback for both recruitment of weak muscles and inhibition of hypertonic muscles. Bobath and Brunnstrom techniques were used for the control group. Several outcomes were measured; however, the only blinded evaluation was for Brunnstrom stage of motor recovery.

Prevo et al[20] used EMG biofeedback to both increase muscle activity and decrease reciprocal activity and motor irradiation. The control group received NDT and functional training. Outcome measures included EMG activity, muscle force, synergy patterns, and arm and hand function. Raw data for elbow flexion force and synergy patterns were provided by the authors.

Overall, these five studies[18-21,23] Were consistent in using EMG biofeedback to both increase and decrease muscle activity. As shown in Table 2, patients varied in time poststroke from 2 weeks to 8 years. The studies are fairly consistent in the frequency and duration of treatment.

Analyses

Odds ratios for improvement versus no improvement and their confidence intervals for the five studies[18-21,23] are presented in Tables 4 and 5. An odds ratio above 1.00 represents a difference in favor of biofeedback, and an odds ratio below 1.00 indicates superiority of conventional therapy. Figures 1 and 2 are graphical presentations of the results. None of the odds ratios were statistically significant. The one-tailed probability values are also given in Tables 4 and 5. None of the two-tailed Mann-Whitney tests were significant at the .05 level.

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The meta-analysis results for the function and impairment constructs are also summarized in Tables 4 and 5. For both constructs, the statistical tests of association were not significant (P>.05). The meta-analyses for probabilities were also not significant. Functional outcome measures included the UEFT, the Action Research Arm Test, and Brunnstrom staging. The common odds ratio was 2.16 (0.82-5.79). Given the proportion of responders in the control group (0.21) in the study by Basmajian et al,[21] the number of patients needed to treat with biofeedback to prevent one nonresponder is 10.

Grip strength, elbow flexion force, and finger oscillation formed the impairment construct, and the common odds ratio was 1.29 (range=0.43-3.99). Using the proportion of nonresponders (0.26) for grip strength,[18] the number of patients needed to treat would be 22.

The tests for homogeneity for each meta-analysis were not significant, indicating that the variability in odds ratios among the studies was not greater than what was expected by chance. With a small number of studies, however, the power of this test is low.[14] We therefore performed sensitivity analyses as per the a priori hypotheses. The results of these analyses are presented in Table 6. None were statistically significant. The study by Basmajian et al[19] was classified as an acute study because only 3 of the 29 patients were more than 6 months poststroke. For the functional outcomes, the common odds ratio for the studies with patients less than 6 months poststroke was 2.9.

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To determine the magnitude of response for these subgroups (sensitivity analyses), the number of patients needed to treat was calculated as shown in the Appendix. The study by Crow et al,18 in which patients were less than 8 weeks poststroke, was used to estimate the proportion of patients whose functional status did not change with conventional therapy (0.70). Given this estimate, the number of patients needed to treat with biofeedback to prevent one nonresponder is four. For the studies in which biofeedback was combined with conventional therapy, the odds ratio was 2.5 and the number of patients needed to treat is nine, given a nonresponder proportion of 0.21. For the impairment outcome in patients with long-standing stroke,[20] the number needed to treat is seven for elbow flexion force. One study[21] measured hand impairments and combined conventional therapy with biofeedback. In this study, the estimated number of patients needed to treat is eight to prevent a nonresponder for grip strength.

Discussion

A number of methodologic issues exist when conducting meta-analyses. These issues include agreement on the predefined criteria, statistical analysis, and the nature of the variables that are being pooled in the analysis. Agreement on the selection criteria was high, but interobserver agreement for the validity criteria ranged from poor to good. Disagreement primarily occurred where judgment was required to decide whether a criterion was not met or was possibly done but not reported. To resolve this problem, we decided to score these criteria as possibly achieved. The disagreements we noted point out the importance of having more than one evaluator assess the internal validity of studies that are included in a research overview.

A common criticism of meta-analysis is that studies are combined in which different populations, interventions, and outcomes are represented. Because efficacy may be related to these characteristics, combining all trials may underestimate or overestimate the intervention effect for certain groups. Among the studies, the biofeedback protocols we considered were similar for duration and frequency. There were differences in the control treatments; however, randomized trials comparing different forms of conventional physical therapy have not demonstrated any clinically important differences.[30,31]

For the upper-extremity function meta-analysis, the outcomes of upper-extremity function testing were combined with those of Brunnstrom staging. We believe this approach is justified based on the study of De Weerdt et al,[32] in which a correlation of .91 was found between the Action Research Arm Test and the Brunnstrom-Fugl-Meyer evaluation. Furthermore, the Action Research Arm Test was developed directly from the UEFT,[26] thus making these two tests comparable. The measurements that formed the impairment construct are not directly comparable. Two represent force measurements, and one is a coordination measure. The results shown in Table 5 suggest that EMG biofeedback may be more effective for strengthening than coordination.

The nature of the data distributions determined the choice of statistical analysis. Because effect sizes based on standard deviation units would not be meaningful for highly skewed data, a nonparametric measure was chosen. The choice of improvement versus no improvement as a cutoff point has clinical relevance, although it is not ideal because it disregards the amount of change that occurred. Choosing clinically important values is difficult because conceptualizing the performance of ordinal measures is a challenge (when ordinal scores are added, similar resulting scores do not imply the same amount of change). In the future, those who develop measures should consider techniques that yield interval scales and surveys to determine clinically significant differences.

To assess the degree of confidence one can have in the conclusions, it is necessary to examine the validity of the studies. All of the included studies were randomized trials with blinded outcome assessment. The outcomes were measured using methods of known reliability, or reliability was determined before the study. The sensitivity analyses probing the effects of placebo in the control group and treatment monitoring indicate that these factors do not have a significant impact.

In two studies, there were baseline imbalances for prognostic factors. In the 1982 study by Basmajian et al,[21] the duration poststroke for the control group was less than in the treatment group. The potential effect of this difference is to bias the results against the biofeedback group. Basmajian and colleagues' analysis of covariance to adjust for pretest means, however, did not substantiate this effect. In Smith's[23] study of patients with long-standing stroke, baseline imbalance for age and duration of stroke may have biased the results against the biofeedback treatment. Whether time poststroke is a prognostic indicator in patients greater than 1 year poststroke, however, is unclear. Basmajian et al[19] identified duration as a predictor of functional outcome in patients less than 1 year poststroke. Contrary to this finding, in a cohort study, Wolf et al[33] found that age, gender, duration of stroke, and number of training sessions did not predict biofeedback outcomes.

The purpose of this overview was to obtain an estimate of the effect of EMG biofeedback compared with conventional therapy in order to guide clinical decision making. Generalization of the findings is limited to biofeedback training using recruitment and inhibition strategies for the upper extremity. Because all of the analyses were statistically nonsignificant, the studies to date do not conclusively demonstrate that EMG bio-feedback is superior to conventional therapy. Although there is a possibility of Type II error, we are unaware of any method to calculate power for a meta-analysis to confirm the presence of Type II error. Overall, the size of the effect, as indicated by the number of patients needed to treat, is small. This interpretation is limited because it assumes that change versus no change is the only outcome of interest without consideration of the magnitude of improvement. Two factors, however, support the conclusion of a small effect. One is that the results of the meta-analyses for probability values (based on the Mann-Whitney test, which uses the magnitudes of the data) were greater than those of the significance tests for the common odds ratios. This finding indicates that the odds ratio analyses were anticonservative (more in favor of biofeedback than warranted by the magnitude of the change scores). A second factor is that a post hoc parametric meta-analysis of the functional data for those who did change showed an effect size of -0.02 standard deviation. This value corresponds to one point on the UEFT in favor of conventional therapy and suggests that those patients who respond to treatment do equally well in either group. Our findings should not be extrapolated, however, to other forms of biofeedback (eg, positional) or to the lower extremity.

The sensitivity analysis of studies that examined patients who were less than 6 months poststroke suggests that EMG biofeedback may be worthwhile in this group. The sensitivity analyses should be viewed as exploratory because the factors are confounded within the studies and because there was multiple significance testing on each construct. All of the sensitivity analyses had wide and overlapping confidence intervals, which precluded any definitive conclusions. The seemingly anomalous finding of an odds ratio of 2.7 for impairment in the chronic subgroup occurred because this finding represented one study[20] with a sample size of 17. There was one nonresponder in the experimental group, and there were two nonresponders in the control group.

How do these results compare with the conclusions of the individual studies? With respect to functional outcomes, two of the selected studies concluded that biofeedback was superior to conventional therapy. Smith[23] reached this conclusion based on the differences between groups; however, a statistical analysis was not done. Crow et al[18] based their conclusions on posttreatment scores without adjustment for baseline differences. In their study, one-tailed tests were significant for the Action Research Arm Test and the Brunnstrom-Fugl-Meyer Test, although the authors did not comment on the clinical importance of the differences. A follow-up done 6 weeks later showed no statistically significant differences. Basmajian et al[19] also performed follow-up measures at 9 months and found no statistically significant difference between the groups. In this study, the mean UEFT scores were higher for the conventional group at both posttest and follow-up.

In view of the findings, further research needs to be done. Motor learning research in nondisabled subjects indicates that constant, precise feedback is inferior to less frequent, delayed or bandwidth feedback.[34] This is compelling evidence that the scheduling of EMG biofeedback training needs to be studied in patient populations. Another area for study at a basic level is the relative effectiveness of biofeedback (motor unit potentials) compared with overt feedback or knowledge of results. Interestingly, two studies that compared simulated feedback with actual feedback concluded that biofeedback was nonspecific.[22,35] Once these issues are sorted out, clinical studies that examine functional outcomes in homogeneous groups would be appropriate. Our findings suggest that studies should evaluate acute and chronic groups separately. For clinical studies, measures need to be selected or developed such that the clinical importance of differences can be readily evaluated.

Conclusions

The purpose of this overview and meta-analysis was to determine whether there is conclusive evidence regarding the use of EMG biofeedback for improving upper-extremity function in adults who have had a stroke. Evidence was sought that compared EMG feedback alone or combined with conventional therapy with conventional treatment. Despite examining a group of rigorous studies using techniques that incorporate the total number of subjects, statistically significant differences were not found, The estimated size of the effect was small; therefore, we recommend that therapists consider factors such as cost, ease of application, and patient preference when deciding between the two forms of treatment. Therapists may wish to reserve this technique for those patients who do not respond to conventional therapy.

Acknowledgments

We thank the investigators, who responded to our requests for information. In particular, we thank Dr N Lincoln, Professor Carolyn Gowland, Ms Janina John, and Dr A Prevo for graciously providing us with their data.

References

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Physiotherapy. 1986;72:108-118. [8] Ince LP, Leon MS, Christidis D. EMG biofeedback with the upper extremity: a critical review of experimental foundation of clinical treatment with the disabled. Rehabilitation Psychology. 1987;32:77-91. [9] Hedges LV, Olkin I. Statistical Methods for Meta-Analysis. Orlando, Fla: Academic Press Inc; 1985. [10] Boissel JP, Blanchard J, Panak E, et al. Considerations for the meta-analysis of randomized clinical trials: summary of a panel discussion. Controlled Clin Trials. 1989;10:254-281. [11] Julian JA. OR2X2XK Version 1.0. Hamilton, Ontario, Canada: McMaster University; 1988. [12] Julian JA, Guide to OR2X2XK, Version 1,0. Hamilton, Ontario, Canada: McMaster University; 1988. [13] Oxman AD. Meta-analysis in primary care: theory and practice. In: Tudiver F, Bass MJ, Dunn EV, et al, eds. Assessing Interventions Traditional and Innovative Methods. Newbury Park, Calif: Sage Publications Inc; 1992:191-207. [14] L'Abbe KA, Detsky AS, O'Rourke K. Meta-analysis in clinical research. Ann Intern Med. 1987;107:224-233. [15] Rosenthal R. Meta-analytical Procedures for Social Research. Newbury Park, Calif: Sage Publications Inc; 1984. [16] Schwarzer R. Meta-analysis Programs, Version 5.1. Berlin, Federal Republic of Germany: Free University of Berlin; 1989. [17] Brunnstrom S. Movement Therapy in Hemiplegia. New York, NY: Harper & Row; 1970, [18] Crow JL, Lincoln NB, Nouri FM, De Weerdt WJG. The effectiveness of EMG biofeedback in the treatment of arm function after stroke. Int Disabil Studies. 1989;11:155-160. [19] Basmajian JV, Gowland CA, Finlayson AJ, et al. Stroke treatment: comparison of integrated behavioral-physical therapy vs traditional physical therapy programs. Arch Phys Med Rehabil. 1987;68:267-272. [20] Prevo AJH, Visser SL, Vogelaar TW. Effect of EMG feedback on paretic muscles and abnormal co-contraction in the hemiplegic arm, compared with conventional physical therapy. Scand J Rehabil Med. 1982;14:121-131. [21] Basmajian JV, Gowland CA, Brandstater ME, et al. EMG feedback treatment of upper limb in hemiplegic stroke patients: a pilot study. Arch Phys Med Rehabil 1982;63:613-616. [22] Hurd WW, Pegram V, Nepomuceno C. Comparison of actual and simulated EMG biofeedback in the treatment of hemiplegic patients Am J Phys Med. 1980;59:73-82. [23] Smith KN. Biofeedback in strokes. Australian Journal of Physiotherapy. 1979;25:155-161. [24] Mroczek N, Halpern D, McHugh R. Electromyographic feedback and physical therapy for neuromuscular retraining in hemiplegia. Arch Phys Med Rehabil. 1978;59:258-267. [25] John J. Failure of electrical myofeedback to augment the effects of physiotherapy in stroke. Int J Rehabil Res. 1986;9:35-45. [26] Lyle RC. A performance test for assessment of upper limb function in physical rehabilitation treatment and research. Int J Rehabil Res. 1981;4:483-492. [27] Fug]-Meyer AR, Jaasko L, Leymann I, et al. The post-stroke hemiplegic patient, I: a method for evaluation of physical performance. Scand J Rehabil Med. 1975;7:13-31. [28] Carroll D. Quantitative test of upper extremity function. J Chronic Dis. 1965; 18:479-491. [29] Reitan RM, Davison LA Clinical Neuropsychology: Current Status and Applications Washington, DC: Winston; 1974. [30] Wagenaar RC, Meijer OG, van Wieringen PCW, et al. The functional recovery of stroke: a comparison between neuro-developmental treatment and the Brunnstrom method. Scand J Rehabil Med. 1990;22:1-8. [31] Ernst E. A review of stroke rehabilitation and physiotherapy. Stroke. 1990;21:1081-1085. [32] De Weerdt WJG, Harrison MA. Measuring recovery of arm-hand function in stroke patients: a comparison of the Brunnstrom-Fugl-Meyer test and Action Research Arm Test. Physiotherapy Canada. 1985;37:65-70. [33] Wolf SL, Baker MP, Kelly JL. EMG biofeedback in stroke: effect of patient characteristics. Arch Phys Med Rehabil. 1979;60:96-102. [34] Winstein CJ. Knowledge of results and motor learning: implications for physical therapy. Phys Ther. 1991;71:140-149. [35] Lee KH, Hill E, Johnston R, Smichorowski T. Myofeedback for muscle retraining in hemiplegic patients. Arch Phys Med Rehabil. 1976; 57:588-591. Appendix. Example of Odds Ratio Calculation and Number of Patients Needed to Treat The odds ratio is calculated from a 2x2 table. The following are some sample data:

Treatment group change scores for each subject:

-1, 0, 0, 0, 2, 2, 4, 4, 5, 6; 10, 15

Control group change scores for each subject:

-1, -1, 0, 0, 0, 0, 0, 3, 3. 4, 8. 19 For a given cutoff point, counts are placed in the table. In the example below, the cutoff point

is improved versus not improved. From the data above, the following table is constructed:

                                             Improved  Not improved
Treatment group                              8 (a)     4 (b)
Control group                                5 (c)     7 (d)

The odds ratio is calculated as: (a)(d)/(b)(c)=2.8 To determine the number of patients needed to treat to prevent a nonresponder, the following

equation is used: n=1/proportion control-proportion treatment In this example, the proportion of nonresponders in the control group is 7/12=0.58 If one believes that the best estimate of the odds ratio is, for example, 2.2, and because we

know the number in cell d is 0.58 or 58 of 100 cases, the corresponding proportion of

nonresponders in the treatment group can be calculated in the following way:

                                         Improved  Not improved
Treatment group                           (a)      (b)
Control group                             42       58

There are two unknowns and two equations: 58 (a)/42 (b) = 2.2 and a+b = 100 Solving for both: a=61.4 b=38.6 Therefore, the proportion of nonresponders in the treatment group is 0.386. Substituting this

into the equation above for n: The number needed to treat=1/(0.58-0.386)=5.

Invited Commentary

In providing a meta-analysis of the efficacy of electromyographic (EMG) biofeedback compared with conventional physical therapy, Moreland and Thomson have laid a framework from which physical therapy students and clinicians can benefit. The critical criteria that form the basis for selection of studies and the validity criteria against which these studies are assessed are exceptionally stringent. As such, readers should consider these criteria as they evaluate the merits of any clinical content.

Through their independent analyses of available literature, the authors were able to identify six articles from over 124 articles on this topic that span the time frame (1976-1992) of their search. The fact that only a few articles met their criteria would logically imply that either their criteria are too strict or the quality of past work in this area is inadequate. The latter possibility seems unlikely because (1) there have already been several reviews on this subject in which the relative strengths and weaknesses of EMG biofeedback applications to patients with stroke have been analyzed; (2) in the United States, several current procedural terminology codes exist in rehabilitation for reimbursement of this approach, a circumstance that could never have occurred without substantive evidence of its potential efficacy a point well supported by Moreland and Thomson); and (3) on a comparative basis, the shear number of clinical studies (as opposed to case reports or anecdotal commentaries) that have examined this approach as a neuromuscular reeducation tool in the treatment of patients with neurological problems so far outweighs those of other approaches as to make this treatment an inviting target for dissection and analysis. Therefore, one must conclude that the criteria for selection of studies and the validity assessment of selected studies are remarkably strict. In fact, I would conjecture that few studies in rehabilitation have been subjected to this degree of vigorous analysis. In light of this fact and my inherent bias on this subject, as one who has researched it for 19 years, the favorable common odds ratio for biofeedback, even in the absence of statistically significant differences between biofeedback and conventional therapy, is surprisingly comforting.

A recent meta-analysis on this subject by Schleenbaker and Mainous[1] was probably unavailable to the authors. Schleenbaker and Mainous computed a size effect for each of eight studies that met their criteria, which ostensibly were similar to those used by Moreland and Thomson, with three exceptions. First, Schleenbaker and Mainous examined EMG biofeedback studies without attempting to compare this treatment approach with any other. Second, they included studies that addressed treatment of both the upper and lower extremities. Last, they did not include the criterion that studies be evaluated blindly. Schleenbaker and Mainous computed an average effect size of 0.81, with a 95% confidence interval for the effect size at 0.5 to 1.12, and concluded that this approach is an effective tool for neuromuscular reeducation among patients who have sustained a stroke.

Moreland and Thomson used an odds ratio to describe each study and to combine results because of the apparent skewness of data distribution. Because of the difference in procedures for evaluating the meta-analysis between these two reviews, one must assume that Schleenbaker and Mainous[1] did not feel their data sets were too skewed. This supposition is remarkable because both groups included two of the same articles in their meta-analysis. One can deduce that the skewness in Moreland and Thomson's data set is due more to the inclusion of blinded studies than to limiting the review to upper-extremity treatment. One must wonder why the authors felt that this inclusion criterion was important, particularly among studies that, by design, necessitate intense evaluator-subject interaction. In fact, despite the well-intended attributes of the evaluators, I have neither engaged in nor seen a clinical study of this nature that was truly "blind." Inevitably, one or more subjects have intentionally or inadvertently revealed their treatment groups to the evaluators. I suspect that, given the inclusion criteria used by Moreland and Thomson, an odds ratio analysis would almost always be the computation of choice, irrespective of the treatment variables. One must ask the obvious teleological question of whether, by incorporating these stringent inclusion criteria, the skewness that would result from the data set, necessitating the exclusive use of odds ratio calculations, is not, in itself, a bias. Furthermore, one could challenge the degree of complexity and rater comprehension of the study evaluation criteria, because the interobserver (the authors') agreement on these criteria across studies ranged from .00 to .86 (weighted Kappa score).

A few specific points require clarification. I would caution the authors about placing much credence on the deductions made by Marcer.[2] Several of the studies he cited, as well as subsequent work, have included control groups and have addressed important specificity of treatment issues that we have recognized previously.[3] The authors note that only Basmajian and colleagues[4,5] reported monitoring of treatment protocols, yet their Table 3 indicates that Prevo et al[6] did as well. The authors also state that although all the odds ratios for functional (Tab. 4) and impairment (Tab. 5) outcomes favor EMG biofeedback, none of the studies achieved statistically significant ratios. This statement is in conflict with the probability value for the Action Research Arm Test in the study by Crow et al[7] and warrants explanation.

In citing Winstein's study,[8] the authors correctly surmise the importance of periodic rather than continuous feedback and suggest that this consideration be incorporated in future studies. This notion should be applauded. On the other hand, anyone using EMG biofeedback to treat patients who have sustained a stroke recognizes that this concern is probably overemphasized. We[9] have commented that these patients wean themselves from continuous feedback as they attend progressively to the change in actual limb segmental movement. Furthermore, any good inherent clinical test for the incorporation of kinesthetic awareness during or subsequent to EMG biofeedback treatment must require elimination of feedback as the clinician monitors the patient's ability to first achieve a certain level of EMG output and second to tell the clinician when that level is reached.

I am somewhat concerned about Moreland and Thomson's discussion on prognostic indicators. In light of the need for such important data, we[10] painstakingly attempted to answer this question through a clinical trial that included a control group, blinded evaluations, and an analysis of multiple physiological and functional measures. We were able to ascertain the neuromuscular characteristics of those patients with chronic stroke who achieved complete functional use of their upper extremities as well as the profile of those patients who simply improved. Patients with longstanding stroke and possessing those characteristics formed the basis for novel EMG biofeedback interventions,[11] which also improved quantified, functional capability.

Perhaps most distressing in the presentation of this study is the authors' assumption that a comparison between EMG biofeedback and conventional physical therapy for patients with chronic stroke is necessary and their implicit statement that there is a cost factor in use of EMG biofeedback that might mitigate against its preferential use. Perhaps the time has come to lay to rest the notion of comparing treatments and realize the intent to which EMG biofeedback has evolved--the integration of EMG monitoring within treatment, a concept promoted some time ago.[12] Ironically, two of the articles[5,6] cited by Moreland and Thomson were the first to remotely suggest this integrative approach.

The authors should be reminded about their conclusion. Although one can say that EMG biofeedback was not superior to conventional therapy in terms of the outcomes and criteria used by the authors, the reverse is also true; conventional therapy is not superior to EMG biofeedback in the treatment of these patients. Do these two sides of the same coin imply exclusivity? Of course not. Rather, we should assess the value of any on-line physiological monitoring to guide treatment. In point of fact, one can easily make the argument that failure to allow spontaneous interpretation of physiological events (EMG, motion, force) to guide treatment decisions and patient instruction leads to cost ineffectiveness. By denying ourselves and our patients maximal (and appropriate) information, we may be prolonging treatment and hence elevating costs. To believe that costs are measured in equipment purchases rather than efficiency of time utilization is simply incompatible with contemporary health care trends in the United States. Ultimately, the availability of monitoring equipment that allows treatment and quantification should find its place within treatment rather than segregated from it. Steven L Wolf, PhD, PT, FAPTA Professor and Director of Research Department of Rehabilitation

Medicine Professor of Geriatrics Department of Medicine Associate Professor Department of Anatomy and Cell

Biology Emory University School of Medicine 1441 Clifton Rd NE Atlanta, GA 30322

References

[1] Schleenbaker RE, Mainous AG III. Electromyographic biofeedback for neuromuscular reeducation in the hemiplegic stroke patient: a meta-analysis. Arch Phys Med Rehabil. 1993;74: 1301-1304. [2] Marcer PM. In: Biofeedback and Related Therapies in Clinical Practice, London, England: Croom Helm Ltd; 1986:145-159. [3] Wolf SL. Electromyographic biofeedback applications to stroke patients: a critical review. Phys Ther. 1983;63:1448-1455. [4] Basmajian JV, Gowland CA, Brandstater ME, et al. EMG feedback treatment of upper limb in hemiplegic stroke patients: a pilot study. Arch Phys Med Rehabil. 1982;63:613-616. [5] Basmajian JV, Gowland CA, Finlayson AJ, et al. Stroke treatment: comparison of integrated behavior-physical therapy vs traditional physical therapy programs. Arch Phys Med Rehabil. 1987;68:267-272. [6] Prevo AJH, Visser SL, Vogelaar TW. Effect of EMG feedback on paretic muscles and abnormal co-contraction in the hemiplegic arm, compared with conventional physical therapy. Scand J Rehabil Med, 1982;14:121-131. [7] Crow JL, Lincoln NB, Nouri FM, DeWeerdt W. The effectiveness of EMG biofeedback in the treatment of arm function after stroke. Int Disabil Studies. 1989;11:155-160. [8] Winstein CJ. Knowledge of results and motor learning: implications for physical therapy. Phys Ther. 1991;71:140-149. [9] LeCraw DE, Wolf SL. Electromyographic biofeedback (EMGBF) for neuromuscular relaxation and re-education. In: Gersh MR, ed. Electrotherapy in Rehabilitation. Philadelphia, Pa: FA Davis Co; 1992:292-325. [10] Wolf SL, Binder-Macleod SA. Electromyographic biofeedback applications to the hemiplegic patient: changes in upper extremity neuromuscular and functional status, Phys Ther. 1983;63:1393-1403. [11] Wolf SL, LeCraw DE, Barton LA. Comparison of motor copy and targeted biofeedback training techniques for restitution of upper extremity function among patients with neurologic disorders. Phys Ther. 1989;69:719-735. [12] Wolf SL, Edwards DI, Shutter IA. Concurrent assessment of muscle activity (CAMA): a procedural approach to assess treatment goals. Phys Ther. 1986;66:218-224.

Author Response

We would like to thank Dr Wolf for his thoughtful comments on our article. He has raised several points related to this research to which we would like to respond.

The first point was the stringency of the criteria related to the purpose of our overview. This purpose was to answer the clinical question of whether biofeedback alone or in addition to conventional therapy was more efficacious than conventional therapy alone, To answer this question, it is important to look for answers from studies that have high internal validity, regardless of the volume of studies that exist. We chose to examine indicators (validity criteria) that would provide information on potential biases within the studies. Given this, we do not feel the criteria were too stringent, and we believe that the quality of much of the past work was not adequate for our purposes. Although few areas in rehabilitation have been subjected to vigorous analysis, we suggest that it is part of the evolution of our science to do so. It is important that valid information is sought and appropriate research questions defined and answered with rigorous methodology. The cost-effectiveness of making policy or treatment decisions based on methodologically weak studies is questionable. These studies are very useful, however, for building evidence and theory in an area of research.

With respect to the meta-analysis by Schleenbaker and Mainous,[1] we find it surprising that they did not specify that a treatment comparison group be used. Even in patients with longstanding stroke, improvement occurs with traditional therapy, as demonstrated in the studies by Smith[2] and Prevo et al.[3] In addition, Schleenbaker and Mainous did not indicate whether they obtained the raw data from the authors of articles in order to determine the nature of the data distributions, that is, whether the data were skewed or normally distributed. In our study, we used change scores, and the skewness of the data was due to the large number of no-change or small-change results. The meta-analysis by Schleenbaker and Mainous is also missing a number of elements that Oxman and Guyatt[4] have put forth as critical appraisal criteria for a research overview. It is difficult to know whether bias was avoided in selecting the studies, and internal validity criteria were not assessed. For example studies with a large loss to follow-up may have biased results. Group comparability at outset is also a source of bias that should be checked. We also believe that blinded outcome assessment is an important methodological feature. If nonblinded studies are used in a meta-analysis, it may be wise to do a sensitivity analysis on this factor.

Although our interrater agreement was low for some of the validity criteria, investigation of the reasons revealed that low agreement occurred for those criteria in which it was uncertain whether the criterion was done but not reported, or not done. We updated our validity criteria table as information from the authors became available. For example, the information that the treatments were monitored in the study by Prevo et al[3] came from our correspondence with Dr Prevo.

Although the probability value reported for the Action Research Arm Test in the study by Crow et al[5] was .05, this is a one-tailed value that was computed for the purposes of the probability value meta-analysis. It would not be significant on a two-tailed test, which would be the appropriate test when comparing two therapies that are already in use.

Although patients are usually weaned over time from feedback, as Dr Wolf pointed out, we believe there is still merit to investigating whether periodic feedback at the outset would be more effective than constant feedback for motor learning because this represents a different technique from weaning.

Dr Wolf points out electromyographic biofeedback has evolved such that it is now integrated into treatment as a monitoring device. This method of monitoring in itself needs to be studied for cost-effectiveness. For example, is feedback of covert (electromyographic) responses more beneficial than feedback of overt responses such as range of motion? Our knowledge of the mechanisms of motor learning would be expanded by such studies.

There were two comments of which we do not understand the intent. The first is the issue of prognostic indicators, and the second is why it is distressing to compare treatments in patients with long-standing stroke because it has been demonstrated that they improve with traditional therapy.[2.3]

Once again, we would like to thank Dr Wolf for his comments, and we appreciate the opportunity to respond to them. Julie Moreland, BHSc (PT) Mary Ann Thomson, BHSc (PT)

References

[1] Schleenbaker RE, Mainous AG III. Electromyographic biofeedback for neuromuscular reeducation in the hemiplegic stroke patient: a meta-analysis. Arch Phys Med Rehabil. 1993; 74:1301-1304. [2] Smith KN. Biofeedback in strokes. Australian Journal of Phsyiotherapy. 1979;25:155-161. [3] Prevo AJH, Visser SL, Vogelaar TW. Effect of EMG feedback on paretic muscles and abnormal co-contraction in the hemiplegic arm compared with conventional physical therapy. Scand J Rehabil Med. 1982;14:121-131. [4] Oxman AD, Guyatt GH. Guidelines for reading literature reviews. Can Med Assoc J. 1988; 138:697-703. [5] Crow JL, Lincoln NB, Nouri FM, DeWeerdt WJG. The effectiveness of EMG biofeedback in the treatment of arm function after stroke. Int Disabil Studies, 1989;11:155-160.

J Moreland, BHSc(PT), is Research Coordinator, St Joseph's Hospital, and Clinical Lecturer, School of Occupational Therapy and Physiotherapy, McMaster University, Hamilton, Ontario, Canada. Address correspondence to Ms Moreland at Physiotherapy Department, St Joseph's Hospital, 50 Charlton Ave E, Hamilton, Ontario, Canada L8N 4A6.

MA Thomson, BHSC(PT), is Education Manager, Chedoke-Mcmaster Hospitals, and Clinical Lecturer, School of Occupational Therapy and Physiotherapy, McMaster University,

This research was supported by a grant from the Hamilton District of the Ontario Physiotherapy Association.

This overview was presented in part at the Canadian Physiotherapy Association Congress, June 1992.

This article was submitted April 19, 1993, and was accepted December 7, 1993.