Nonpharmacological Interventions for Pediatric Migraine: A Network Meta-analysis

This systematic review and NMA is registered with PROSPERO (CRD42019146666).

We conducted a systematic review and NMA in accordance with the Preferred Reporting Items for Systematic Reviews and Meta-analysis (PRISMA) statement.^18,19  We searched Medline, Cochrane, Embase, and PsycINFO from inception until August 5, 2019. Furthermore, additional trials were identified from an existing systematic review of migraine treatments.²⁰  For search terms, see Supplemental Information 1. In total, the search led to 9012 articles (Supplemental Fig 3). Notably, the search also identified pharmacological studies; these results have been published elsewhere.⁴  The screening and selection processes were conducted independently by 5 coauthors (C.L., H.K., J.K., J.B., and T.L.L. in pairs of 2).

Randomized controlled trials (RCTs) of nonpharmacological interventions for children and adolescents <18 years were included in this study. Participants had to have a diagnosis of episodic migraine (with or without aura) according to the International Headache Society (IHS) criteria, or criteria for migraine diagnosis had to be in close agreement with the IHS classification. Trials had to specifically state that they were focusing on pediatric migraine but were not required to specify the exact diagnosis of migraine to be included. Eligible trial designs included RCTs that make head-to-head comparisons of at least 2 nonpharmacological interventions as well as RCTs that compare at least 1 nonpharmacological intervention with a control group. To be included, trials had to report at least 1 migraine-related outcome. Crossover studies were only included if we were able to extract the results of the first period separately. Studies in which migraine was associated with other neurologic disorders as well as studies on menstrual migraine were excluded.

All eligible data were extracted in duplicate (C.L., H.K., J.B., J.K., and T.L.L. in pairs of 2) on a standardized form. We resolved disagreements through consensus and, if indicated, consultation with a third reviewer. For continuous outcomes, means and SDs were extracted. If SDs were not reported, we calculated them from SEs, confidence intervals (CIs), or other measures.^21,22  In cases where we were not able to calculate SDs, we imputed them with the help of SDs reported for the same outcome measure.²³  If the sample size was missing in the table of analysis, we used the sample size of the baseline data. In cases where the continuous outcome data were not reported, we extracted the number of patients who fulfilled the response criterion as defined by the authors of the included study.

We defined the primary efficacy outcomes in line with the recent guidelines of the IHS for children and adolescents with migraine.²⁴  We created a hierarchy of measures and chose the highest available priority in each individual study. In descending order, the primary efficacy outcome measures were defined as (1) number of headache days per month, (2) the number of migraine days per month, (3) frequency of headache attacks (means and SDs), (4) frequency of migraine attacks (means and SDs), or (5) headache index and activity. If no information on these primary efficacy outcomes were available, the proportion of responders was used instead. Preferably, we defined responders as patients with at least 50% reduction in the number of headache days. If these data were not reported, we used (in descending order of preference) patients (1) with at least a 50% reduction in the number of migraine days, (2) with at least a 50% reduction in frequency of headache attacks, (3) with at least 50% reduction in frequency of migraine attacks, (4) with at least a 50% reduction in headache index, or the global assessment of improvement by patients and physicians.

We defined different time periods to reduce between-study heterogeneity and to increase the comparability between studies: 8 weeks or 2 months after randomization (post), 3 to 4 months after randomization (follow-up [FU] 1), 5 to 6 months after randomization (FU 2), and >6 months after randomization (FU 3). For the main analysis, we considered outcomes reported between 3 and 4 months after randomization. If no data were available for that time period, outcomes at 8 weeks or 2 months after randomization were applied. For the long-term analysis, we considered all reported outcomes from FU 3, FU 2, and FU 1 with a priority for longer follow-up.

We assessed the quality of the included studies using the Cochrane risk of bias tool for RCTs.²⁵  Two reviewers rated each study, with conflicts resolved through consensus or, if necessary, consultation with a third reviewer.

For our primary efficacy outcomes (ie, continuous outcome data), we calculated the effect sizes of the interventions applying the standardized mean difference (SMD). The magnitude of the SMDs was interpreted as small, moderate or large, with 0.20, 0.50, and 0.80 SD units, respectively.²⁶  For our secondary efficacy outcomes (ie, categorical outcome data), we calculated odds ratios as effect sizes between groups²²  and transformed them into SMDs in line with the recommendations in the Cochrane Handbook of Systematic Reviews.²⁷  We decided to primarily calculate with continuous outcome data, because dichotomizing continuous scores into categorical scores is associated with a loss of information, reduced power, and leading to an artificial boundary.²⁸  We decided to apply random-effects models rather than fixed-effects models because the included studies were assumed to be heterogeneous.²⁹ 

We conducted NMAs using R package “netmeta,”³⁰  which applies a frequentist method based on a graph-theoretical approach.³¹  With regard to the nodes in the network, we applied 2 different approaches (ie, lumping versus splitting approach). Applying the lumping approach, we formed broad classifications of interventions with similar components allocated into groups. For this broad classification, we modeled interventions as “class-effects,” assuming interventions to be similar within 1 class. For the splitting approach, we differentiated between all the interventions and plotted networks accordingly. We decided to rank the included interventions, using P scores that are the frequentist analog of the surface under the cumulative ranking curve³²  and can be similarly interpreted. P scores (range: 0–1) represent the extent of certainty that a treatment is better than another, averaged over all competing treatments. For all treatment comparisons in a NMA, we assumed a common between-study heterogeneity. Different statistics were used to quantify heterogeneity: the (within design) Q statistic,³³  the between-study variance τ², and the heterogeneity statistic I².³⁴  The I² value can be interpreted as follows: 0% to 40%: might not be important; 30% to 60%: may represent moderate heterogeneity; 50% to 90%: may represent substantial heterogeneity; 75% to 100%: represents considerable heterogeneity.³⁵  We calculated the agreement (ie, consistency) between direct and indirect treatment effects, with local (ie, separating direct from indirect evidence)³⁶  and global (ie, design-by-treatment interaction test)³⁷  statistical approaches.

The certainty of evidence for the network estimates of the efficacy outcomes was evaluated by using the Grading of Recommendations Assessment, Development, and Evaluation (GRADE) ratings,³⁸  which were conducted in CINeMA (Confidence in Network Meta-Analysis).³⁹  In GRADE, the quality of a body of evidence is defined as the study limitations, imprecision, inconsistency, indirectness and publication bias.³⁸  Prediction intervals were calculated that consider between-study heterogeneity and estimate what true treatment effects can be expected in future studies under similar settings.⁴⁰  To date, no standardized methodology to assess across-studies bias (publication bias) in NMAs exists. Therefore, a comparison-adjusted funnel plot and the Egger test for funnel plot asymmetry were examined.⁴¹ 

In total, 14 RCTs met our inclusion criteria, but we had to exclude 2 studies because they did not connect with the other studies in the network^42,43  (see Supplemental Table 2). Overall, 12 RCTs (comprising 576 patients) conducted between 1986 and 2019 and comparing various interventions (ie, relaxation stress management, relaxation education, relaxation, biofeedback, biofeedback stress management, biofeedback relaxation education, transcendental meditation, autogenic feedback, autogenic training, psychological treatments, progressive muscle relaxation, self-administered psychological treatments, education, and hypnotherapy) with different control groups (ie, psychological placebo, sham biofeedback, and waiting list) could be included.^44–55  The characteristics of the 12 studies included in the NMA are presented in Table 1. For one of the included studies, authors provided us the summary data for the subsample of pediatric migraine: results were only reported across different forms of primary headaches in the published article.⁵³  Researchers in 1 study reported only categorical data⁵² ; those in another study reported continuous data insufficiently and categorical data had to be used.⁴⁵  In both cases, odds ratios were transformed into SMDs. A list of outcome measure that were analyzed for the individual trials can be found in the Supplemental Table 3.

In total, the mean age was 12.01 years (SD 2.1) and 353 (61%) of the sample population were female. In 6 studies, researchers used the IHS criteria (4 used the first edition,^44,47,49,52  2 used the second edition^46,53 ); authors of the remaining 6 studies used similar, albeit not completely analogous, diagnostic criteria (ie, they merged the ICHD-I and ICHD-II criterion C and D symptoms).^{45,48,50,51,54,55}  The median duration of the nonpharmacological intervention was 6 weeks (range: 4–12 weeks). Furthermore, 2 studies (17%) were multicenter studies. Six (50%) of the included trials recruited children and adolescents from the United States, 3 (25%) from Europe, and 3 (25%) from Canada. Details on the interventions (Supplemental Table 2) and raw data of included studies (Supplemental Table 3) can be found in the Supplemental Information.

First, we clustered the nonpharmacological interventions into broad classes. For example, biofeedback, biofeedback stress management, biofeedback relaxation education, and autogenic feedback were taken together and modeled in the “biofeedback” node (see Supplemental Information 3 for details). This resulted in the following intervention nodes: biofeedback, relaxation, psychological treatment, education, and self-administered psychological treatments. The control group nodes comprised psychological placebo, sham biofeedback, and waiting list. Two studies had to be excluded because the interventions could only be assigned to the same intervention node: researchers in 1 of the studies⁴⁴  examined 2 forms of biofeedback, the other study⁵³  was focused on 3 different forms of relaxation.

Figure 1A shows the network of all comparisons for short-term efficacy for the broadly defined intervention nodes. Self-administered treatments (SMD: 1.44; 95% CI, 0.26 to 2.62), biofeedback (SMD: 1.41; 95% CI, 0.64 to 2.17), relaxation (SMD: 1.38; 95% CI, 0.61 to 2.14), psychological treatments (SMD: 1.36; 95% CI, 0.15 to 2.57), and psychological placebos (SMD: 1.17; 95% CI, 0.06 to 2.27) were significantly more effective than the waiting list (see Fig 2A for forest plot). Head-to-head comparisons of all included nonpharmacological treatments can be found in the league table (see Supplemental Table 4).

Figure 1B shows the network of all comparisons for long-term efficacy applying a broad classification rule for the nodes. Self-administered treatments (SMD: 1.40; 95% CI, 0.28 to 2.52), relaxation (SMD: 1.35; 95% CI, 0.60 to 2.09), psychological treatments (SMD: 1.33; 95% CI, 0.18 to 2.47), biofeedback (SMD: 1.21; 95% CI, 0.47 to 1.94), and psychological placebos (SMD: 1.14; 95% CI, 0.09 to 2.19) revealed significantly higher effects than the waiting list (see Fig 2B for forest plot). Head-to-head comparisons of all included nonpharmacological treatments are displayed in the league table (see Supplemental Table 5).

In all 12 studies, researchers provided sufficient data in the prespecified time periods to be included in the splitting approach for both the short-term and the long-term efficacy analyses.

Figure 1C shows the network of all comparisons for short-term efficacy. No nonpharmacological intervention was significantly more effective than the waiting list, which was the reference group. The nonsignificant SMDs ranged from −0.20 (95% CI, −3.20 to 2.79 for hypnotherapy) to 2.50 (95% CI, −0.75 to 5.75 for relaxation stress management) (see Fig 2C for details). There were no significant differences between the included nonpharmacological interventions (see Supplemental Table 6 for details). Although the relaxation stress management appeared to have the largest P score (P = .81) with respect to short-term efficacy outcomes (see Fig 2C), it was only examined in 1 trial with a sample size of 15 patients per arm.⁴⁷  The prediction intervals for all comparisons showed nonsignificant effects and included both clinically beneficial and detrimental effects.

Three studies did not report long-term efficacy for the control groups.^48,50,51  For these studies, we included the last complete data set (ie, in all cases FU 1). Additionally, 5 studies only reported FU 1 and not FU 2 or FU 3.^{43,46,49,52,54}  For the remaining 4 studies, FU 2 or FU 3 served as long-term outcomes. Figure 1D shows the network of all comparisons for efficacy in the long-term.

All nonpharmacological interventions revealed nonsignificant SMDs, ranging from 0.03 (95% CI, −2.41 to 2.47 for hypnotherapy) to 2.50 (95% CI, −0.26 to 5.26 for relaxation stress management) (see Fig 2D). Additionally, none of the included nonpharmacological interventions did differ significantly from one another (see Supplemental Table 7 for details). Similarly, the 95% prediction intervals for all comparisons included the null value and contained both clinically beneficial and detrimental effects.

The certainty of evidence for the network estimates of the short- and long-term efficacy outcomes was examined by using GRADE.³⁸  The results for study limitations (within study bias), publication bias (across-studies bias), indirectness, imprecision, heterogeneity, and incoherence can be found in the supplement (Supplemental Information 4–7, Supplemental Figs 4 and 5). All certainty of evidence analyses are based on the large networks with finer-grained nodes of the individual interventions (Supplemental Information 4–7, Supplemental Figs 4 and 85).

None of the included studies reported safety or acceptability outcomes. Hence, we were unable to conduct these analyses.

The detailed PRISMA for NMA can be found in the Supplemental Information 8.

We conducted the first NMA on the efficacy of nonpharmacological interventions for pediatric migraine and included 12 studies with a total of 576 patients. Interestingly, our NMA revealed different findings depending on the structure of the nodes in the network. In a first step, we lumped the interventions into broader classes. Significant short- and long-term effects were found for most nonpharmacological interventions (ie, relaxation, biofeedback, psychological treatments, and self-administered psychological treatments) as well as for 1 control group (ie, psychological placebo) when compared with the waiting list. In terms of our second aim (ie, to systematically compare the different nonpharmacological treatment options relative to each other), the included interventions did not significantly differ from one another. In a second step, we split the various published interventions into individual nodes. Here, in the short- and long-term analyses, none of the included interventions were significantly more effective than the waiting list, which was the control group that most interventions were compared with and that connected 2 otherwise unconnected networks. Also, none of the interventions differed significantly from each other in the head-to-head comparisons.

There are several reasons why we conducted 2 analyses that apply different strategies for the formation of the nodes. As stated in a recent literature review, there is currently no consensual method to support the node-making process in NMA.⁵⁶  One reason for this is that the descriptions of nonpharmacological interventions in RCTs often lack essential information.⁵⁷  Generally, the lumping versus splitting approach involves finding a compromise between clinical and statistical considerations. The lumping approach, ie, our broad classification, has the statistical advantage of increased power and allowing for a more accurate estimation of intervention effect sizes, especially when grouping interventions with similar components together.⁵⁸  The splitting approach, ie, our individual nodes, has the advantage of enhancing clinical interpretability and utility. This is because the individual interventions that have been taken together in the lumping approach share similar treatment components (that justify the lumping process); however, they are not clinically interchangeable.⁵⁹  For example, in our analyses, we combined several treatment arms into the node “relaxation” for the lumping approach. These individual interventions apply a variety of approaches linked to relaxation (eg, progressive muscle relaxation, autogenic training, hypnotherapy, and transcendental meditation). Hence, although the splitting approach compares all available individual interventions with each other, the lumping approach gives us an estimation of the effects of different types of interventions available for pediatric migraine. Both types of node-making were based on expert consensus in our group of authors that includes researchers, clinicians, and statisticians, which is in line with recommendations.⁵⁶ 

The difference in results between the 2 types of analyses (ie, lumping approach versus splitting approach) is noteworthy. Compared with traditional meta-analysis, the indirect comparisons that the NMA considers influence the respective effect sizes of the included interventions. The advantage of a NMA is that different interventions can be examined separately and relative to each other.⁶⁰  Although the more detailed analysis represent the actual breadth of published studies and displays the actual types of studies that have been conducted, the smaller amount of studies in each node and the resulting lack of power led to a lack of significance, mostly because of large confidence and prediction intervals.

When compared with previous reviews and meta-analyses in the same area of research,^8,9,61  our findings are comparable to some extent: researchers in other studies found considerably large, positive, and significant effect sizes for pain frequency at posttreatment of some nonpharmacological interventions, such as relaxation-based interventions, biofeedback, and CBT. Although the inclusion criteria differed substantially from previous reviews in that we exclusively focused on pediatric migraine and excluded other types of headaches, our analyses with the broader intervention nodes found similar effect sizes for relaxation, biofeedback, psychological treatments, and self-administered psychological treatments. Interestingly, these effects were also maintained in the long-term. This is in contrast to our previous analysis of prophylactic pharmacologic interventions in pediatric migraine, where we found effects in the short- but not the long-term.⁴  One reason for this might be an effect of training: biofeedback, for example, works through the control of otherwise involuntary physiologic responses, such as skin temperature, blood volume pulse, and brain activity.⁶²  Previous studies in tension-type headache and migraine also reported a durable effect of biofeedback and relaxation trainings.^63,64  In the short- and in the long-term analyses, self-administered treatments resulted in the largest P score with a value of 0.68 and 0.70, respectively. The P score is interpreted analogously to surface under the cumulative ranking curve in the Bayesian framework; a value of 0.68 means that 68% of competitor interventions are worse than the target intervention.⁶⁵  Notably, researchers of both studies that examined self-administered treatments^45,51  concluded that self-control of migraine may be a main factor in the effectiveness of interventions for pediatric migraine. Of note, in one of the studies, the self-administered treatment (called “own best efforts”) was designed as a control condition.⁵¹  Patients had 1 single session to discuss the use of the headache diary. In the other study, patients took part in an 8-week home-based treatment program focusing on cognitive and behavioral stress coping and relaxation strategies.⁴⁵ 

Interestingly, psychological placebos were significantly effective interventions when compared with waiting list controls in the short- and long-term. In the included studies, the psychological placebo for example consisted of 6 individual, 1-hour weekly sessions in which children were taught to recognize and label their emotions, relate them to their life situation, and discuss their feelings daily with a friend or parent.⁵¹  In the second study with a psychological placebo,⁴⁵  participants were given a list of common triggers for migraine, such as different foods, met with a therapist once to become aware of and avoid triggers, and were taught brainstorming skills to deal with stressful situations. After that, participants were contacted weekly by the therapist by phone. The finding of significant effects for psychological placebos is not surprising, given that researchers have shown psychological placebos to be effective in other settings,^66,67  which can in part be explained by various components of the placebo effect (such as a supportive patient–practitioner relationship and a therapeutic ritual⁶⁸ ), which are present even in these control conditions.

The more detailed analyses in which the individual published interventions comprised 17 nodes could not confirm those significant effects found when combining the studies into 8 broader nodes. Various reasons why this might be the case come to mind. The individual nodes were composed of predominantly small studies, date back up to 3 decades, and are mainly single-center. Some of the comparisons in our network consist of only 1 indirect comparison (eg, relaxation stress management versus waiting list, n = 15). Therefore, some effects are potentially due to the so-called small study effect, a bias that describes how smaller studies reveal different treatment effects than large ones.^41,69,70  Potential causes for the small study effect include selective outcome reporting,^71–73  clinical heterogeneity between patients in large and small trials (eg, smaller trials tend to include a more homogeneous sample of patients or include patients at higher risk), publication bias, and selective analysis reporting.⁷⁴  In conducting 2 different analyses (ie, the lumping approach versus the splitting approach), we tried to eliminate the small study effect, because broader nodes increase the number of participants per node. In addition, the apparent small study effect is often actually due to differences in quality, patient inclusion criteria, baseline severity, and definition of outcome between small and large trials.⁴¹  With regard to the detection of the small study effect, an asymmetric funnel plot implies differences between the estimated derived from large and small trials.⁷⁵  In the case of the presented NMAs, the funnel plots were nonsignificant for the short- and the long-term efficacy (see Supplemental Figs 4 and 5).

Overall, and in line with previous analyses, some of the effect sizes were considerably large in both types of analyses (ie, lumping and splitting approaches), with SMDs up to SMD = 2.50 for relaxation stress management and SMD = 1.81 for biofeedback stress management in the short- and long-term, pointing to a potentially clinically meaningful effect in some patients. Such large effect sizes are somewhat unexpected, especially when compared with prophylactic pharmacologic interventions with SMDs typically <1.0,^4,76  but in line with a meta-analysis that focused on biofeedback for migraine only (and no other type of headache).⁵³  This might point to the potential of these nonpharmacological interventions in children and adolescents. Notably, these included both beneficial and detrimental effects and suggest that interindividual differences play an important role: one subgroup of patients for whom nonpharmacological interventions lead to substantial pain relief versus a subgroup of patients who will not respond to these interventions or even experience a worsening of symptoms. Our results indicate that these differential reactions to the same interventions might exist, which is in line with the precision medicine approach;⁷⁷  however, our findings do not inform about the characteristics of these subgroups.

Noteworthy, none of the studies included in our NMA reported safety or acceptability outcomes. This is concerning, given that nonpharmacological interventions can lead to negative consequences, such as side effects, nonimprovement of symptoms, or symptom deterioration.^78,79  However, to date, negative consequences of nonpharmacological interventions, especially psychotherapy, are underreported and not adequately explored.⁸⁰ 

Our analysis has some limitations: first, we could only include a small amount of studies examining nonpharmacological interventions for pediatric migraine. This is in contrast to previous analyses,⁸  because we decided to specifically focus on migraine to increase the clinical usefulness of our results. However, an NMA uniquely allows for the formation of a network of intervention of any set of studies that links 3 or more interventions via direct comparisons, which then results in multiple ways to assess indirect comparisons between the interventions. All direct and indirect evidence can then be exploited; this simultaneous comparison is suggested to yield more precise estimates of the relative intervention effects than any single direct or indirect estimate.⁸¹  Conclusively, indirect evidence, when combined with direct evidence, increases the power and precision of treatment effects.⁸²  Second, the included studies showed considerable statistical heterogeneity, indicating that patients and trials differed substantially. With the small and heterogeneous set of studies, the definition of nodes (ie, classes of interventions) was challenging. Merging different interventions (ie, lumping) has shown to increase heterogeneity within nodes, because similar interventions might not have the same treatment effect. Splitting treatments, in contrast, leads to decreased power.⁸³  We tried to find a compromise between lumping and splitting by conducting 2 analyses with different sizes of nodes. A statistical alternative would have been to conduct several comparison-specific pairwise meta-analyses. However, in contrast to meta-analyses, NMAs can easily incorporate multiarm studies and evaluate disagreements between different sources of evidence. Third, none of the studies reported any safety or acceptability outcomes. Therefore, we were not able to evaluate the risk profile of these interventions and to make a statement about the risk-benefit balance. Fourth, the majority of our comparisons in the long-term analysis were based on FU 1 (ie, 3–4 months after randomization), because no later time points were reported. Moreover, 3 studies did report FU 2 or FU 3, but not for their respective control groups. It is therefore impossible to draw final conclusions on the maintenance of the effect. Fifth, because of limited reporting of follow-up assessment in the included studies, the applied time periods in the short- and long-term analyses did overlap in some cases. Sixth, researchers in 2 studies analyzed pediatric migraine in combination with tension-type headache⁴⁹  and vascular headache.⁵⁰  For these studies, the change of migraine headache cannot be clearly distinguished from the change of other types of pediatric headache. Seventh, half of the studies used similar, albeit not completely analogous, diagnostic criteria for migraine compared with the other half of the studies.^{45,48,50,51,54,55}  We were not able to conduct an additional sensitivity analysis because the exclusion of these studies resulted in 2 separate subnetworks. Finally, 2 studies did not connect with the network and therefore had to be excluded. Hence, the efficacy of acupuncture and music therapy for this specific age group could not be evaluated.

Because none of the studies included in this NMA provided safety or acceptability outcomes, it was impossible to compare the interventions in this regard. We therefore highly recommend including measures of safety and acceptability in every trial, independent of the type of intervention (pharmacological and nonpharmacological). This is also in line with recommendations on outcome measures for pediatric pain trials such as PedIMMPACT (Pediatric Initiative on Methods, Measurement, and Pain Assessment in Clinical Trials).⁸⁴  Along with the idea that uncertainty in high-quality systematic reviews and NMAs indicates that research has yet to answer the primary question,⁸⁵  our findings reveal that there are significant research gaps in the area of pediatric migraine. This is mainly due to the lack of data, a problem that is well-known across pediatric pain research.⁸⁶ 

Future researchers should control for natural course of pediatric migraine, and, preferably in studies with more participants and study sites, further evaluate the safety and efficacy of those interventions with large effect sizes in our NMA. Furthermore, to correspond with recent guidelines of the IHS for pediatric migraine,²⁴  future RCTs should include the number of headache days as their primary outcome, which was not the case for the included studies. This is because the reporting of headache days allows the use of relatively simple trial diaries compared with the reporting of migraine days.²⁴  Finally, and importantly, we urge future NMAs to report the node-making process in detail, especially for nonpharmacological treatments that are usually complex and heterogeneous.⁵⁶ 

Clinically, our results reveal that relaxation, biofeedback, psychological treatments, and self-administered psychological treatments are effective interventions for pediatric migraine. When analyzed in broad nodes and lumped on the basis of similarity of treatment components, these interventions revealed large and presumably clinically meaningful effect sizes for some patients. The more detailed analysis (ie, splitting approach), however, suggested that some of the effects have to be considered carefully because they are based on small studies. Moreover, because the CIs were considerably large for the individual treatment nodes, it remains important to find strategies on how to best identify those patients who profit most from individual nonpharmacologic interventions, in line with of the goals of precision medicine.⁷⁷  Statistically, our results highlight that the decision about the formation of the nodes (ie, the lumping versus splitting approach) in an NMA has a strong impact on the significance and interpretability of the findings. We encourage the reader to weigh the clinical and statistical considerations that are associated with the different formations of the nodes.

CBT

cognitive behavioral therapy

CI

confidence interval

FU

follow-up

GRADE

Grading of Recommendations Assessment, Development, and Evaluation

ICHD

International Classification of Headache Disorders

IHS

International Headache Society

NMA

network meta-analysis

PRISMA

Preferred Reporting Items for Systematic Reviews and Meta-analysis

RCT

randomized controlled trial

SMD

standardized mean difference