CONTEXT: Migraine is a common problem in children and adolescents, but few satisfactory prophylactic treatments exist.
OBJECTIVE: Our goal was to investigate the pooled evidence for the effectiveness of using biofeedback to reduce childhood migraine.
DATA SOURCES: A systematic search was conducted across the databases Medline, Embase, CENTRAL, CINAHL, and PsychINFO.
STUDY SELECTION: Prospective, randomized controlled trials of biofeedback for migraine among children and adolescents were located in the search.
DATA EXTRACTION: Data on reduction of mean attack frequency and a series of secondary outcomes, including adverse events, were extracted. Risk of bias was also assessed.
RESULTS: Forest plots were created by using a fixed effects model, and mean differences were reported. Five studies with a total of 137 participants met the inclusion criteria. Biofeedback reduced migraine frequency (mean difference, –1.97 [95% confidence interval (CI), –2.72 to –1.21]; P < .00001), attack duration (mean difference, –3.94 [95% CI, –5.57 to –2.31]; P < .00001), and headache intensity (mean difference, –1.77 [95% CI, –2.42 to –1.11]; P < .00001) compared with a waiting-list control. Biofeedback demonstrated no adjuvant effect when combined with other behavioral treatment; neither did it have significant advantages over active treatment. Only 40% of bias judgments were deemed as “low” risk.
LIMITATIONS: Methodologic issues hampered the meta-analyses. Only a few studies were possible to include, and they suffered from incomplete reporting of data and risk of bias.
CONCLUSIONS: Biofeedback seems to be an effective intervention for pediatric migraine, but in light of the limitations, further investigation is needed to increase our confidence in the estimate.
- IHS —
- International Headache Society
- CI —
- confidence interval
- OR —
- odds ratio
Migraine represents a serious problem among children and adolescents. A review of 64 studies estimated the 1-year prevalence of childhood migraine to be 9.1%.1 This figure is probably an underestimation, however, due to the common practices of using restrictive screening questions and neglecting probable migraine. A recent study reported a 36% one-year prevalence of all migraine among adolescents.2 For patients, this finding means troublesome symptoms and often a considerable degree of disability with time lost from school, friends, and other activities.2,3 From a societal perspective, migraine leads to substantial indirect costs from lost productivity and direct costs for health care.4
Despite migraine’s high prevalence and morbidity, relatively few prophylactic drugs have been proven effective among children and adolescents, and they are all associated with a risk of adverse effects.5 Nonpharmacologic treatment (eg, biofeedback) is therefore an attractive alternative. In biofeedback, patients learn to voluntarily modify their bodily reactions through feedback-mediated awareness of physiologic parameters.6 Biofeedback reduces cortical excitability and affects resonance and oscillations of essential feedback loops in the central nervous system.7,8 The most frequently used modalities in biofeedback treatment are peripheral skin temperature, blood-volume-pulse, and electromyography.
Many systematic reviews have reported a favorable effect of behavioral treatments for pain conditions,9⇓⇓⇓⇓–14 but they vary greatly in how they applied meta-analytic methodology. Unfortunately, most of these studies9,10,12⇓–14 have merged different types of psychological treatment and pain conditions, including tension-type headache and migraine. This approach does not allow us to claim that biofeedback is effective as a migraine prophylactic. Only Nestoriuc and Martin11 have considered migraine separate from other headache disorders and biofeedback separate from other psychological treatment. However, their study was restricted to adults.
To fill in this gap of knowledge, we present here the results of a systematic review with a meta-analysis of the effect of biofeedback treatment in pediatric migraine. The objectives were as follows: (1) to assess the efficacy of biofeedback on primary attack frequency in children and adolescents with migraine; (2) to assess the efficacy on secondary end points (eg, attack duration, headache intensity, quality of life, disability, acute medication use); (3) to investigate any potential adverse events associated with the treatment; and (4) to conduct a risk of bias assessment of the included studies.
Criteria for Considering Studies for This Review
Types of Studies
Included studies were required to be prospective, randomized controlled trials investigating biofeedback as a prophylactic treatment of episodic migraine in children or adolescents. Studies were included only if they were randomized or pseudo-randomized. Due to the low number of studies expected to meet these criteria, no lower limit for number of participants was set.
Types of Participants
Participants were children and adolescents up to the age of 18 years experiencing episodic migraine. The use of a specific set of diagnostic criteria (eg, International Headache Society [IHS] Classification Committee 15 or International Classification of Headache Disorders–II 16) was not required, but the diagnosis had to be based on at least some of the distinctive migraine features defined by the IHS: unilateral location, pulsating character, moderate to severe intensity, physical aggravation, accompanying nausea or photophobia and phonophobia, and aura.17
Types of Interventions
Studies were eligible if at least 1 arm represented biofeedback treatment. All modalities of biofeedback were included. Studies were considered eligible when some degree of behavioral treatment was delivered together with biofeedback during the same session, or when biofeedback was the only difference between the intervention group and the comparison group. Eligible comparison groups were active treatment with documented effectiveness; nonpharmacologic therapies with documented effectiveness; waiting-list control; or treatment as usual.
Types of Outcome Measures
Migraine frequency was chosen as the primary outcome of interest.18 Secondary outcomes prespecified to be extracted were: responder rate ≥50%, headache intensity, attack duration, disability, quality of life, doses of acute medication, and adverse events. We also aimed to assess effect sizes according to sex in the included studies.
Search Methods for Identification of Studies
A medical librarian performed the literature search.19 The searched databases were Medline, Embase, CENTRAL, CINAHL, and PsychINFO. The search was updated on November 23, 2015, and involved a combination of thesaurus and free-text terms optimized to cover randomized controlled trial studies in which patients aged <18 years had received biofeedback treatment as a prophylaxis for migraine. (Supplemental Information presents the complete search strategy for all databases searched.) The literature lists of all reviews encountered on the subject were hand-searched to capture potentially relevant studies not detected in the electronic search.
Data Collection and Analysis
Two authors independently screened the results from the literature search to identify eligible studies. In cases in which articles could not be excluded based on information in the title and abstract, full-text articles were obtained and screened. The remaining studies were included in this review. Disagreements were resolved through discussion, and near-eligible studies are referenced in this review with reasons for exclusion.
Data Extraction and Management
Characteristics of each included study were summarized, including: study design and methods; participants’ demographic characteristics and criteria for migraine diagnosis; characteristics of intervention arms; outcomes with method of data collection; and units of measurement. Information on the biofeedback treatment, including type of instrument, modality, setting, and circumstances, was extracted. Any treatment additional to biofeedback was reviewed. Raw outcome data were extracted from the studies for meta-analysis. We primarily sought N values, means, and SDs. In such cases where this information could not be obtained directly from the article, the data were calculated in-house from the information provided in the article. Headache diary outcomes are usually reported over different time periods, and we therefore attempted to standardize the unit of time over which outcomes were measured. Outcome data were assessed at the end of treatment and follow-up. End of treatment was considered as the last weeks of treatment when outcomes were assessed, or the first weeks immediately after treatment if outcome assessment was posttreatment. Follow-up was considered to be 3 to 12 months after completed treatment; in cases in which >1 follow-up time point was reported, the last time point was used. Two authors extracted data and reconciled their findings.
Review Manager software (RevMan 5.3; The Nordic Cochrane Centre, The Cochrane Collaboration, Copenhagen, Denmark) was used for synthesis of meta-analyses and construction of figures. Raw data from the included studies were entered into the software. In cases in which the means and variances of groups were not sufficiently reported, we attempted to calculate the necessary data from the data reported (eg, test statistics, error bars in graphs) whenever possible. Scales for outcome assessments were converted to be equivalent. For continuous outcomes, the summary mean differences with 95% confidence intervals (CIs) were calculated, using an inverse variance fixed effects model. For dichotomous outcomes, the summary odds ratios (ORs) with 95% CIs with a fixed effects model were calculated. Because of the low number of participants in each meta-analysis, the Mantel-Haenszel method was used for calculating dichotomous outcomes. We also calculated the number-needed-to-treat-to-benefit based on an assumed control risk, calculated from the responder rate in the control groups. Statistical heterogeneity was also calculated for each meta-analysis to evaluate the variability of intervention effects across the included studies.
Risk of Bias Assessment in Included Studies
Four categories of bias were considered: (1) selection bias, with regard to random sequence generation and allocation concealment; (2) detection bias, with regard to blinding of outcome assessors; (3) attrition bias, which is selective occurrence and biased handling of protocol deviations and losses to follow-up; and (4) reporting bias, determined by differences between prespecified measures and reported outcomes. Other potential biases (eg, biased study design or claim of fraud) were to be reported if encountered. Performance bias was not assessed due to the difficulty of blinding participants and personnel when delivering biofeedback treatment. Each bias was graded as being of “low,” “high,” or “unclear” risk. The latter was chosen when the information in the article was insufficient to determine the risk. Two authors performed the assessment independently, and discrepancies were thereafter resolved by discussion and referral with a third author.
Figure 1 presents a flow diagram of the process for study selection. The electronic search yielded 908 records. After removing duplicates, 639 records remained, and 581 of these were excluded through screening of titles and abstracts. The full-text files of the 58 remaining records were then retrieved and read. Eleven of these studies, and a single study identified through the hand-search20 (ie, a total of 12 studies), qualified for description in the review. Five of these studies21⇓⇓⇓–25 met all the eligibility criteria and are included in data synthesis. The remaining 7 studies20,26⇓⇓⇓⇓–31 are listed with their reason for exclusion in Table 1. Characteristics of the studies included in the summary are found in Table 2. Detailed information may be accessed in Supplemental Tables 3 through 7.
Risk of Bias
Of the 30 risk of bias items scored for the 5 studies, 12 (40%) were low, 15 (50%) were unclear, and 3 (10%) were high. The 3 bias items scored as high were limited to 2 studies.23,24 Figure 2 provides an overview of the risk of bias assessment. One24 of the 5 included studies described an adequate random sequence generation, earning a low risk of bias; the other 4 studies21⇓–23,25 lacked description and were assigned unclear risk of bias. For allocation concealment, none of the studies provided sufficient information to ascertain the true risk of bias and, subsequently, all were assigned an unclear risk of bias. For the blinding of outcome assessment, Scharff et al24 was judged to suffer from a high risk of detection bias because all evaluations, treatment, and follow-up sessions were conducted by a single investigator. The 4 remaining studies21⇓–23,25 were assigned an unclear risk of bias status due to insufficient information. Only 2 of the included studies reported when there were significant differences between completers and noncompleters.22,24 Fentress et al25 evaluated 35 patients to obtain a final sample of 18 participants. These 18 were also analyzed, thus giving the study a low risk of bias. Labbé and Williamson21 reported dropouts only at follow-up, a time point not included in our analyses, thus giving the study an unclear risk of bias. Labbé22 recruited 46 participants, but only 30 completed the study. The study reported no significant differences between completers and dropouts, but no information is given on how the dropouts were treated in the analyses, resulting in an unclear risk of bias for the study. In the study by Sartory et al,23 16 children could not be contacted at follow-up. Only children with complete data sets are included in the table of means that was used for the meta-analyses, resulting in our analyses being conducted with a substantial departure of participants from the intervention to which they were assigned at randomization. This approach qualifies for a high risk of bias status. Scharff et al24 reported 2 dropouts after randomization but before initiation of treatment. No significant differences were found between dropouts and participants with regard to age, psychological measures, or headache characteristics, thus giving the study a low risk of bias. Four of 5 studies21⇓–23,25 reported results of all preplanned outcomes and were assigned a low risk of bias for selective reporting. Scharff et al was the only study to not report data fully, and it was therefore classified as high risk of bias for selective reporting. The study also did not report data sufficient for assessment of depression and anxiety outcomes at posttreatment. No other bias was encountered in the studies.
Four of the 5 included studies reported outcomes over a 1-week time period.21⇓–23,25 Data from the final study24 were converted to fit this approach. Ordinal scales used for outcome assessment were converted to be equal. One study24 did not report means and measures of spread as numbers. These data were therefore derived by hand from error bars in the graphs. Two studies21,22 did not report measures of spread, only F-statistics for the analysis of variance analyses. To estimate the SD, we calculated the between-group variance of the groups and phases included in the analysis of variance assessments, and thereby estimated a within-group variance. One study25 used nonparametric methods in their analyses. Consequently, no continuous outcomes from this study could be used in the meta-analyses. No investigations of differences in treatment efficacy between girls and boys could be performed because none of the included studies reported outcomes according to sex.
Results of Analyses
In cases in which only 1 study could be entered into a comparison, we chose to present a forest plot for our primary outcome measurement for ease of interpretation.
Biofeedback Versus Waiting-List Control
Four studies, with a total of 84 participants, qualified for comparisons of biofeedback versus waiting-list control.21,22,24,25 In all 4 studies, hand-warming biofeedback, with an additional behavioral therapy delivered during the same sessions (Supplemental Tables 3–7), was compared with a waiting-list control.
Data from 3 trials21,22,24 (72 participants) showed that biofeedback significantly (z = 5.10; P < .00001) reduced the frequency of migraine attacks at the end of treatment compared with waiting-list control (Fig 3). The mean difference between interventions was –1.97 (95% CI, –2.72 to –1.21) attacks per week. Only 1 study22 compared biofeedback and waiting-list control at posttreatment follow-up. The study reported significant differences for headache frequency and duration across time for all subjects at the 6-month follow-up.
Data from 4 studies21,22,24,25 (84 participants) of biofeedback versus waiting-list control were included in an analysis to enumerate the responder rate. The definition of responder rate varied between all of these studies (Supplemental Tables 3–5, and 7). Participants treated with biofeedback revealed a significantly higher (z score = 4.57; P < .00001) proportion of responders to treatment at the end of treatment compared with waiting-list control (OR, 27.71 [95% CI, 6.66 to 115.35]) (Fig 4). The number-needed-to-treat-to-benefit was 2.
Two studies21,22 (48 participants) underwent meta-analysis to assess whether biofeedback reduced the duration of migraine attacks compared with waiting-list control at the end of treatment (Supplemental Tables 4 and 5). The analysis revealed a mean difference in pain intensity after biofeedback versus waiting-list control of –3.94 (95% CI, –5.57 to –2.31), which was significant (z score = 4.75; P < .00001) (Fig 5). The 1 study assessing the outcome at posttreatment follow-up reported maintained improvement for the biofeedback group.22
Data from 2 studies21,24 (52 participants) were included in a meta-analysis to investigate if biofeedback improved headache intensity compared with waiting-list control (Supplemental Tables 4 and 7). The analysis showed a mean difference in headache duration after biofeedback versus waiting-list control of –1.77 (95% CI, –2.42 to –1.11), which was significant (z score = 5.30; P < .00001) (Fig 6). None of the included studies assessed headache intensity at posttreatment follow-up for this comparison.
The secondary outcomes of interest (disability, quality of life, and adverse events) were not assessed by any of the studies comparing biofeedback with a waiting-list control (Supplemental Tables 3–5 and 7). Only 1 study comparing biofeedback with a waiting-list control assessed the outcome doses of acute medication, and it reported a significant reduction over time for medication consumption in both the biofeedback and waiting-list control group. However, no significant difference between the groups at end of treatment and follow-up was reported21 (Supplemental Table 4).
Adjuvant Effect of Biofeedback
Two of the eligible studies22,25 had biofeedback as the only difference between 2 treatment arms, allowing for a meta-analysis of its adjuvant effect. Only 1 of these studies22 (20 participants) reported sufficient data to analyze continuous outcomes. This trial displayed no significant effects, either for migraine frequency (mean difference, –0.40 [95% CI, –1.64 to 0.84]; z score = 0.63; P = .53) (Fig 7) or attack duration (mean difference, –0.36 [95% CI, –2.80 to 2.08]; z score = 0.29; P = .77), when comparing biofeedback plus autogenic training versus autogenic training only. Both studies22,25 (32 participants) reported the proportion of responders to treatment, and a meta-analysis showed no significant effect (OR, 1.79 [95% CI, 0.21 to 15.55]; z score = 0.53; P = .60) (Fig 8) for biofeedback as adjuvant treatment in this regard.
Biofeedback Versus Active Treatment
One study23 compared biofeedback with active control groups. Data were reported for 27 of the original 43 included participants. No significant differences were found in migraine frequency when comparing biofeedback versus progressive relaxation, nor when comparing biofeedback versus propranolol at the end of treatment or at follow-up (Fig 9). Moreover, the study reported no significant group differences for the outcomes headache intensity, attack duration, and analgesic intake. Conversely, nonparametric, pre–post within-group analyses revealed significant improvement in migraine frequency and intensity for the relaxation group, and significant improvement with regard to migraine frequency, duration, and mood for the biofeedback group. Neither the relaxation group nor the metoprolol group differed significantly from the biofeedback group with regard to responder rate at posttreatment. The study did not assess the outcomes of disability, quality of life, or adverse events.
Biofeedback Versus “Sham-Biofeedback”
One study24 (23 participants) compared hand-warming biofeedback versus hand-cooling biofeedback. No significant between-group benefit was found for migraine frequency at the end of treatment or follow-up (Fig 10). However, the proportion of responders to treatment was significantly higher in the hand-warming group (7 of 13 vs 1 of 10; OR, 10.50 [95% CI, 1.02 to 108.58]; z score = 1.97; P = .049).
The present systematic review is the first to attempt to estimate the pooled intervention effect for biofeedback treatment among children and adolescents with migraine. We primarily set out to assess its impact on headache frequency but also several secondary outcomes defined by IHS.32 The most robust finding of the review is that biofeedback can reduce the frequency of migraine compared with a waiting-list control (Fig 3). Biofeedback also seems to reduce attack duration and headache intensity compared with waiting-list controls. However, some prespecified outcomes could not undergo meta-analysis due to the low number of studies reporting these data.
An adverse event is an outcome that is often neglected; through this review, we had hoped to learn some of its association to biofeedback. The lack of attention to the adverse events outcome became even more apparent upon learning that none of the included studies addressed this result.
A low risk of bias was found in 40% of the scores, the remaining being deemed unclear or high. This finding decreases the confidence in our estimates. There was a substantial lack of description of the randomization process, in which 4 of 5 random sequence generation judgments, and all judgments for allocation concealment, were scored unclear. Because blinding is not possible when delivering biofeedback, this risk of bias has not been assessed. Consequently, there is the possibility of a contribution by a placebo effect in the intervention group.
Three of the studies21,22,24 (Supplemental Tables 4, 5, and 7) used peripheral skin temperature, 1 study25 (Supplemental Table 3) used electromyography, and 1 study23 (Supplemental Table 6) used vasomotor tone for biofeedback. The 2 former techniques are based on the fact that increased peripheral skin temperature and decreased muscle tension are associated with a higher parasympathetic tone and a higher degree of relaxation, which in turn is assumed to lead to less migraine. The vasomotor feedback is suggested to have associations with changes in intracranial blood flow similar to those occurring in electromyography or peripheral skin temperature feedback,33 although its physiologic basis is not fully understood.
A major limitation of this study is the heterogeneity of the interventions. This raises the question of what part of the observed package effect may be attributed to the biofeedback. In the comparison of biofeedback with waiting-list control, we grouped together the somewhat heterogeneous intervention packages (Supplemental Tables 3–7), assuming that the analyses might provide information on the intervention effect of biofeedback among children with migraine. This assumption was further investigated in the analyses of the adjuvant effect of biofeedback.
Biofeedback is regarded as a complete treatment package, not just feedback from a computer.6,34 Indeed, the characteristics of included studies revealed a broad composition of treatment packages (Supplemental Tables 3–7). Biofeedback as an adjuvant does not seem to increase the effect of other behavioral treatment. Some might use this finding to conclude that biofeedback per se produces no effect, but instead the effect may be attributed to other components of the treatment packages. However, considering the small sample size, the adjuvant analysis is likely to lack sufficient statistical power to exclude the possibility that some differences may exist. The small number of participants eligible to be included warrants further research. In addition, it is possible that biofeedback as a supplement to relaxation therapies would provide no additional effect because the patient has received the maximum effect from the other relaxation strategies.
According to the publications we found, biofeedback has a greater responder rate compared with waiting-list controls, with a number-needed-to-treat-to-benefit of 2 (Fig 4). However, this information should be treated with caution, given that only 1 study25 used the responder rate as defined by IHS.18,32 Three studies21,22,24 defined responder rate as a 50% reduction in the average headache intensity, whereas the final study23 used a 50% reduction in an index derived by multiplying headache frequency by intensity. Despite these differences, we chose to perform a meta-analysis of these outcomes.
Another limitation of the present review is the fact that children and adolescents were regarded as 1 group. Biological and psychological differences between these age groups could hamper interpretation of the results. The included studies only provided age means, and never medians, making it impossible to perform separate subgroup analyses of young children and adolescents as defined by (for example) the Adolescent Health Committee.35 We may therefore only be certain that the intervention effect is of value for patients aged <18 years.
Our findings are in accordance with the well-established use of behavioral treatment as migraine prophylaxis36 and with recommendations of biofeedback treatment of migraine in guidelines.37 Another meta-analysis from 2007 that investigated biofeedback as prophylactic treatment of adults with migraine concluded with a medium effect size.11 These results, together with our findings, show that biofeedback has a place in the treatment of migraine regardless of age group.
A major strength of the present review is the fact that it analyzed biofeedback separately from other psychological treatments, and migraine separately from other headache diagnoses. We also present systematic descriptions of all included studies (Supplemental Tables 3–7) because it serves to enlighten the diversity of treatment compositions and differences in outcome definitions. Further strengthening this review, a comprehensive literature search strategy was used to locate all potentially eligible studies. In addition, we were able to estimate continuous data from the sparse data reported in many of the included studies and to then use this information in the analyses. These are data that are not readily available from the articles. We recommend that investigators thoroughly report the number of participants, means, and measures of spread, to ease interpretation and comparison, as well as allow for future meta-analyses. Based on the positive effectiveness findings and seemingly high tolerability, we recommend biofeedback as prophylactic treatment of childhood migraine.
There was a wide range in the number of treatment sessions, raising questions regarding the importance of treatment dose. Another review of psychological treatment of headaches concluded that higher treatment dose leads to better pain scores posttreatment.38 The studies included in this review delivered biofeedback in a clinic, which is time-consuming for the patient and hampers the widespread delivery of treatment, despite its positive results in treating headache. This finding has led to the emergence of less time-consuming approaches, such as prudent limited office treatment and Internet-based delivery.14,39,40 These approaches are obviously promising and warrant further research.
Another question is whether part of the positive effect of biofeedback treatment packages should be attributed to nonspecific effects, such as effects of attention, suggestion, and expectation. In an attempt to investigate this topic, 1 of the included studies24 compared hand-warming biofeedback, traditionally assumed to be effective, versus “sham biofeedback,” consisting of hand-cooling biofeedback. The study was unable to demonstrate any differences between the groups at the end of treatment and follow-up, supporting the idea that nonspecific effects are partially responsible. Again, one should bear in mind the fact that the small number of participants might lack the statistical power to detect a difference.
Biofeedback delivered together with relaxation therapy or autogenic training seems to be effective in reducing the frequency of migraine in the pediatric population. In addition, the apparent lack of adverse advents should qualify biofeedback as an attractive treatment alternative for pediatric migraine. Despite the positive findings, the number of identified studies and participants was small, and a series of methodologic issues hampered proper meta-analyses. Therefore, continued research is warranted.
The authors thank Øyvind Salvesen at the Unit for Applied Clinical Research, Norwegian University of Science and Technology, for valuable statistical advice.
- Accepted May 25, 2016.
- Address correspondence to Anker Stubberud, Department of Neuroscience, NTNU Norwegian University of Science and Technology, Norway. E-mail: firstname.lastname@example.org
FINANCIAL DISCLOSURE: The authors have indicated they have no financial relationships relevant to this article to disclose.
FUNDING: Funding for this project was provided by the Medical Student Research Programme at the NTNU Norwegian University for Science and Technology (project number: 70367015).
POTENTIAL CONFLICT OF INTEREST: The authors have indicated they have no potential conflicts of interest to disclose.
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- Copyright © 2016 by the American Academy of Pediatrics