Craniosacral therapy for chronic pain: a systematic review and meta-analysis of randomized controlled trials

Studies were eligible if they were published as: either full-texts or abstracts of randomized controlled trials (RCTs) or randomized crossover trials that included adult patients with a chronic, non-malignant pain condition of any cause, duration, or intensity. Studies had to examine a type of CST regardless of length or content. Eligible control interventions were active or inactive comparators such as: treatment as usual, waiting list, sham, pharmacological therapies, or non-pharmacological comparators. To be included, studies had to report at least one primary or secondary outcome assessed at the end of the intervention period or at a follow-up point closest to six months after randomization. Pain intensity and functional disability were defined as primary outcomes. Secondary outcomes included physical quality of life, mental quality of life, global improvement, and safety [27]. If a study reported on more than one instrument assessing the same outcome, disease-specific instruments were preferred over generic ones, multi-item over single-item ones, and clinician-rated over patient-rated ones. Safety was operationalized as the number of adverse events (AE) or study withdrawals due to AEs. AEs were defined as any untoward medical occurrence in a patient, which did not have to have a defined causal relationship with the study treatment. Cases of any untoward medical occurrence that, at any dose, has resulted in death, was life-threatening, required inpatient hospitalization, or caused persistent or significant disability were rated as serious AEs [28].

Studies were excluded if they were non-randomized trials, included samples of children or adolescents, or tested interventions that were not defined as CST by the trial authors (for example specific techniques related to cranial osteopathy).

We searched PubMed, PsycInfo, Central Trials, Cinahl, and Scopus from inception to August 2018 by browsing titles, abstracts, and keywords using the search terms “craniosacral” or “cranio sacral”. No language restrictions were applied. We manually searched reference lists of previous studies and reviews, PhD and DO theses, and websites of international craniosacral associations to retrieve additional articles. For ongoing and unpublished studies, we searched international trial registries of the NIC and WHO and conference proceedings. Two reviewers (HH and HC) independently screened titles and abstracts of those studies and assessed the remaining full-texts for eligibility. Any disagreements were rechecked with a third reviewer (RL) until consensus was achieved.

Two reviewers (RL and HC) independently extracted data from the eligible studies including: their origin, the studied pain condition, the sample size, the mean age of the patients, the percentage of included women, the type, content and lengths of the experimental and control intervention, the outcomes and assessment points included in the meta-analysis, reported AEs, and sources of funding. Discrepancies were rechecked with a third reviewer (HH) until consensus was achieved.

Again, two reviewers (RL and TS) independently assessed the risk of: selection, performance, detection, attrition, reporting, and other bias using the Cochrane risk of bias tool [26]. Each domain was judged as either, ‘low risk of bias’ if all requirements were adequately fulfilled, ‘high risk of bias’ if the requirements were not adequately fulfilled, and as ‘unclear risk of bias’ if insufficient data for a judgment was provided. Divergent judgments were rechecked with a third reviewer (HC) until consensus was achieved.

The electronic database search revealed 540 articles (Fig. 1). Two additional articles were retrieved from the manual search. After removing duplicates and excluding articles by screening titles and abstracts, 12 full-text articles were assessed for eligibility. Two further articles [32, 33] had to be excluded as they did not report sufficient data for meta-analysis. Another article was only published as a study protocol [34] and a conference proceeding [35] but detailed data was provided by email. Thus, a final sample of 10 RCTs published between 1999 and 2016 that included 681 patients were eligible for meta-analysis [35‐44].

The characteristics of the included RCTs are presented in Table 1. The RCTs were conducted in: the US [35, 42, 44], Spain [38, 39, 43], Germany [41], Iceland [36], Poland [37], and Sweden [40]. The trials included patients suffering from: tension-type headache [41], migraine [35, 36], low back pain [37, 39], neck pain [41], fibromyalgia [38, 43], pelvic girdle pain [40], and lateral epicondylitis [44]. Sample sizes ranged from 20 to 123 with a median N of 62 and a median of 90% of women. The median age of the total sample was 43.4 years with a range from 30.6 to 52.5 years. Studies provided 1 to 50 CST treatments with a median number of 7 treatments within a maximum of 25 weeks. While two studies used a single CST technique [42, 44], the others implemented a more comprehensive, semi-standardized treatment protocol [35‐41, 43]. Control conditions included: treatment as usual [40], no treatment [42], wait list [36], non-manual sham procedures (disconnected devices) [35, 38, 43], manual sham [41, 44], and active manual treatments such as trigger point therapy [37] and soft tissue massage [39]. No study compared CST to an active drug treatment.

Pain intensity was mostly measured using Numeric Rating Scales (NRS) and Visual Analogue Scales (VAS) [39‐42, 44]. One study reported VAS scores as medians only [40]. However, upon request, trial authors provided means and SDs of the morning and evening pain ratings, which were combined to an average pain score. Two additional studies also assessed VAS/NRS data but did not report related SDs [43] or provided incomplete outcome data comprising of only 72% of the sample [35]. Thus, we had to include alternative measurements taking complete data from the Bodily Pain subscale of the 36-Item Short Form Health Survey (SF-36) and from a pain diary assessing hours of severe headache per day. One study, moreover, used the Intensity of Pain subscale of the Laitinen Pain Indicator Questionnaire (LPIQ) [37]. Functional disability was measured using the Headache Impact Test (HIT-6) [36], the Limitation of Activity subscale of the LPIQ [37], the Roland Morris Disability Questionnaire (RMQ) [39], the Oswestry Disability Index (ODI) [40], the Neck Disability Index (NDI) [41], the Migraine Disability Assessment Score (MIDAS) [35], the Physical Function subscale of the SF-36 [43], and the Patient Specific Functional Scale (PSFS) [44]. Physical and mental quality of life were measured by sub- and component-scores of the SF-12 and SF-36 [41, 43], In addition, one study measured physical quality of life using the European Quality of Life Measure (EQ. 5D) and reported median changes [40]. Upon request, the trial authors provided means and SDs, which led us to calculate an additional meta-analysis although it included only this RCT. Global improvement was assessed by the Patient Global Impression of Improvement Scale (PGII) [41] and the Clinical Global Impression of Improvement Scale (CGII) [38].

The risk of bias assessments are summarized in Figs. 2 and 3. Risk of selection bias was assessed as low in 60% of the included studies [35, 37, 39‐41, 44]. Two further trials reported adequate random sequence generation but did not provide information about allocation concealment [38, 43]. Two trials [41, 44] ensured blinding of participants. However, the overall risk of performance bias was unclear or high for all but one of the trials, as the therapists could not be blinded to treatment allocation or this information was missing. We assessed one of the RCTs [41] as having low risk of performance bias, although the therapists were not described as being blinded, as secondary analyses had shown that the quality of the alliance to the assigned therapists did not systematically affect study outcomes [45]. Adequate blinding of outcome assessors was reported by 40% of the studies [38, 39, 41, 44], whereas 60% did not provide sufficient information to assess the risk of detection bias. The risk of attrition bias was evaluated as low in 90% of the studies [35, 36, 38‐44], the risk of selective reporting as low in 40% [39‐41, 43]. The risk of other bias was assessed as unclear in 90% of the RCTs because of missing alpha-level adjustment [35, 38‐40] or information about sources of funding [36, 37, 42‐44]. The other studies reported having received no funding [38, 39], university funding [41], or government research grants [35, 40]. One of the trials also reported partial funding from CST associations for the publication fee [41].

Although funnel plots could not be created, the risk of publication bias is likely to be low. Searches of trial registries and conference proceedings revealed only one unpublished study [35], which could be included, as the trial authors provided all relevant data upon request. Manual searches of non-peer reviewed literature revealed two further RCTs [32, 33]. One of these [32] only reported rates of response for those whose quality of life improved but did not define improvement, the other RCT [33] did not report the sample sizes for each study group. By dividing the total N by 2, the calculated between-group effect sizes appeared unexpectedly high in favor of CST. Thus, the exclusion of those two trials will most probably not raise the risk of publication bias.

By excluding studies with an unclear or high risk of the respective bias from the comparisons to treatment as usual, CST effects on pain intensity post intervention were found to be robust only against the risk of attrition bias, while the effects on functional disability and physical quality of life were found to be robust against the risk of selection, attrition, and reporting bias.

In comparison to manual and non-manual sham treatments, CST effects on pain intensity and functional disability post intervention as well as six months after randomization were still found to be significant even if the respective studies with unclear or high risk of selection, performance, detection, attrition, reporting, and other source of bias were excluded. The effects of CST on physical and mental quality of life in comparison to sham post intervention were found to be robust only against the risk of attrition and reporting bias. The significant follow-up effect on physical quality of life were robust against all risk of bias dimensions. This is also true for the post intervention and follow-up analyses on global improvement.

Sensitivity analyses of the comparisons to active manual controls revealed robust CST effects on pain intensity and functional disability post intervention against the risk of selection, detection, attrition, and reporting bias.

However, most of the sensitivity analyses included only one remaining RCT that had a low risk of the respective bias, with the exception of the analyses of pain intensity and functional disability in comparison to sham post intervention. These meta-analyses included always 2 to 3 of the 4 initially analyzed RCTs. Detailed analyses can be found in the Additional file 1.

Five RCTs [35‐37, 42, 44] provided no information about AEs. Two RCTs stated no withdrawal due to AEs [38, 39], while another reported no AEs at all [43]. The two remaining RCTs found 5 and 7 minor AEs in the CST group in comparison to 6 and 9 minor AEs in the groups receiving treatment as usual [40] and manual sham [41]. Minor AEs during or subsequent to the CST treatment included increased intensity of pain, headache, shivering, drowsiness, tiredness, and strong emotional reactions such as weeping. No serious adverse events were reported [40, 41].

The systematic search revealed 10 RCTs investigating the efficacy and effectiveness of CST in pain patients with different chronic diagnoses. In comparison to treatment as usual, this meta-analysis found significant small to medium size pooled effects of CST directly after the end of the intervention for: pain intensity, functional disability, and physical quality of life, which was however based mainly on one RCT in patients with pelvic girdle pain. The effects on pain intensity were not robust against all, but one risk of bias domain; those on functional disability and physical quality were not robust against the risk of performance, detection and other bias. In comparison to manual and non-manual sham controls, CST resulted in significantly greater pooled effects of a medium to large size directly after the end of the intervention as well as six months after randomization for pain intensity, functional disability, physical quality of life, and global improvement. Effects tended to be higher in comparisons of studies with blinded patients as well as patients with neck pain or lateral epicondylitis compared to those with fibromyalgia or migraine. Six months after randomization, mental quality of life was no longer found to be significantly different to sham. All analyses towards sham were robust against all risk of bias domains, except for the effects of CST on physical and mental quality of life post intervention that were found to be robust only against the risk of attrition and reporting bias. In comparison to another active manual control, post-intervention data were available for meta-analysis of the effects on pain intensity and functional disability in patients suffering from low back pain. Both comparisons revealed significantly greater medium effect sizes in favor of CST and were robust against the risk of selection, detection, attrition, and reporting bias. No serious AEs were reported. Minor AEs were equally distributed between the groups, while patients receiving CST tended to report less AEs than those randomized to the treatment as usual or manual sham group. In general, however, the included RCTs did not sufficiently report adverse events.

In comparison to prior systematic reviews that included observational studies and RCTs [20], mixed cranial osteopathic and CST techniques [22], and healthy and clinical participants [24], this analysis focused on RCTs investigating CST in patients with chronic pain diagnoses. By searching published as well as unpublished studies, we were able to include one additional RCT that showed less positive results and was missed by the previous reviews [35]. Thus, we performed the first meta-analysis of CST trials that revealed no statistical heterogeneity except for one follow-up analysis; although it contained some clinical heterogeneity regarding the length of the CST interventions and the pain diagnoses of the patients. A further important issue for research and clinical practice are safety analyses that are not part of many previous reviews of CST [22, 24, 46].

The first limitation is the small number of studies included in the meta-analysis. Conclusions drawn, especially those from analyses that included only 2 RCTs, remain preliminary [26]. We used Hedges’ correction for small samples and found no statistical heterogeneity in almost all meta-analyses, but adding a few more studies may change the significance of the results. Additionally, the large effect on global improvement may be overestimated, as retrospective data tend to be more vulnerable to recall biases [47]. A second limitation is the often unclear risk of bias profile of the included RCTs. Many RCTs did not report allocation concealment, blinding of outcome assessment, and alternative methods of decreasing the risk of performance bias. Risk of bias assessment may be influenced by the fact that four of the review authors (HH, RL, GD, and HC) conducted one of the included RCTs. However, a fifth review author (TS) independently assessed the risk of bias of the RCTs. As a result, we do not substantially deviate from the risk of bias assessment performed by previous reviews [20, 22]. The third limitation is a lack of subgroup analyses. We were neither able to derive conclusions about CST efficacy or effectiveness for special pain diagnoses, nor for the requisite number of treatment sessions. The fourth limitation is the focus on patient-reported outcomes, which are more vulnerable to the risk of detection bias. A fact that reduces the reliability of specific CST effects [22]. However, two of the included RCTs [41, 44] blinded patients to group allocation effectively; and three [39, 41, 44] used additional objective measures of pain and function, which in part led to short-term effects comparable to those assessed with self-reported measures. Another point that argues against specific CST effects is the mostly unclear or high risk of performance bias due to the lack of blinding therapists to group allocation. This issue was only controlled within one sham-controlled RCT [41] that showed that the quality of therapeutic alliance, rated by the blinded patients, did not significantly influence patient-reported outcomes [45]. Additionally, the light-touch sham control group used was credible to patients. Analyses confirmed that both expectation and credibility ratings were no significant predictors of group allocation [45]. In contrast, other control groups used in the analyzed RCTs did not achieve comparable levels of expectation or credibility compared to CST [48]. Besides, results gained from waiting list and comparative effectiveness trials should be interpreted with restraint as none of the RCTs controlled for patient expectations. Thus, placebo effects on pain cannot be excluded, although they were calculated as ranging just between a SMD of − 0.35 and − 0.16 [49].

Further clinical trials on CST are required. Authors should ensure rigorous methodology and reporting [50] as well as adequate controls for nonspecific therapy and therapist effects in order to reduce the risk of performance and detection bias. Even though therapists could not be blinded, controlling for attention effects by e.g. asking the patients about their perception of the therapeutic alliance [51] would be feasible. In waiting list or comparative effectiveness trials, where patients could not be blinded, patients’ expectations should be operationalized as a covariate and included in statistical analyses. In general, more adequate statistics (including intention-to-treat analyses as well as alpha-level adjustment for multiple testing) would ensure a low risk of attrition bias and other sources of bias. Increased attention should also be drawn to the adequate assessment and reporting of AEs and reasons for drop-out.

The summarized evidence suggests robust short-term efficacy and comparative effectiveness of CST on pain intensity and functional disability. Longer-term effects seem plausible as well. According to this meta-analysis, CST was not associated with serious adverse events. However, clinicians should be aware of the potential risks of forcibly applied spinal CST techniques, which ca be associated with serious AEs, particularly in patients with preexisting pathologies of the spine [52]. Nonetheless, CST seem to be as safe as other conventional or commentary manual treatments [52] and might provide a novel treatment option in cases where standard treatments have failed to cause symptom alleviation. Recommendations for specific pain conditions cannot be given.