study design
This case report aims to describe the effects of craniosacral therapy and acupuncture in a patient with chronic migraine.
A 33-year-old man with chronic migraine was treated with 20 sessions of craniosacral therapy and acupuncture for 8 weeks. The number of migraine and headache days were monitored every month. The pain intensity of headache was measured on the visual analog scale (VAS). Korean Headache Impact Test-6 (HIT-6) and Migraine Specific Quality of Life (MSQoL) were also used.
The number of headache days per month reduced from 28 to 7 after 8 weeks of treatment and to 3 after 3 months of treatment. The pain intensity of headache based on VAS reduced from 7.5 to 3 after 8 weeks and further to < 1 after 3 months of treatment. Furthermore, the patient’s HIT-6 and MSQoL scores improved during the treatment period, which was maintained or further improved at the 3 month follow-up. No side effects were observed during or after the treatment.
The authors concluded that this case indicates that craniosacral therapy and acupuncture could be effective treatments for chronic
migraine. Further studies are required to validate the efficacy of craniosacral therapy for chronic migraine.
So, was the treatment period 8 weeks long or was it 3 months?
No, I am not discussing this article merely for making a fairly petty point. The reason I mention it is diffteren. I think it is time to discuss the relevance of case reports.
What is the purpose of a case report in medicine/healthcare. Here is the abstract of an article entitled “The Importance of Writing and Publishing Case Reports During Medical Training“:
Case reports are valuable resources of unusual information that may lead to new research and advances in clinical practice. Many journals and medical databases recognize the time-honored importance of case reports as a valuable source of new ideas and information in clinical medicine. There are published editorials available on the continued importance of open-access case reports in our modern information-flowing world. Writing case reports is an academic duty with an artistic element.
An article in the BMJ is, I think, more informative:
It is common practice in medicine that when we come across an interesting case with an unusual presentation or a surprise twist, we must tell the rest of the medical world. This is how we continue our lifelong learning and aid faster diagnosis and treatment for patients.
It usually falls to the junior to write up the case, so here are a few simple tips to get you started.
First steps
Begin by sitting down with your medical team to discuss the interesting aspects of the case and the learning points to highlight. Ideally, a registrar or middle grade will mentor you and give you guidance. Another junior doctor or medical student may also be keen to be involved. Allocate jobs to split the workload, set a deadline and work timeframe, and discuss the order in which the authors will be listed. All listed authors should contribute substantially, with the person doing most of the work put first and the guarantor (usually the most senior team member) at the end.
Getting consent
Gain permission and written consent to write up the case from the patient or parents, if your patient is a child, and keep a copy because you will need it later for submission to journals.
Information gathering
Gather all the information from the medical notes and the hospital’s electronic systems, including copies of blood results and imaging, as medical notes often disappear when the patient is discharged and are notoriously difficult to find again. Remember to anonymise the data according to your local hospital policy.
Writing up
Write up the case emphasising the interesting points of the presentation, investigations leading to diagnosis, and management of the disease/pathology. Get input on the case from all members of the team, highlighting their involvement. Also include the prognosis of the patient, if known, as the reader will want to know the outcome.
Coming up with a title
Discuss a title with your supervisor and other members of the team, as this provides the focus for your article. The title should be concise and interesting but should also enable people to find it in medical literature search engines. Also think about how you will present your case study—for example, a poster presentation or scientific paper—and consider potential journals or conferences, as you may need to write in a particular style or format.
Background research
Research the disease/pathology that is the focus of your article and write a background paragraph or two, highlighting the relevance of your case report in relation to this. If you are struggling, seek the opinion of a specialist who may know of relevant articles or texts. Another good resource is your hospital library, where staff are often more than happy to help with literature searches.
How your case is different
Move on to explore how the case presented differently to the admitting team. Alternatively, if your report is focused on management, explore the difficulties the team came across and alternative options for treatment.
Conclusion
Finish by explaining why your case report adds to the medical literature and highlight any learning points.
Writing an abstract
The abstract should be no longer than 100-200 words and should highlight all your key points concisely. This can be harder than writing the full article and needs special care as it will be used to judge whether your case is accepted for presentation or publication.
What next
Discuss with your supervisor or team about options for presenting or publishing your case report. At the very least, you should present your article locally within a departmental or team meeting or at a hospital grand round. Well done!
Both papers agree that case reports can be important. They may provide valuable resources of unusual information that may lead to new research and advances in clinical practice and should offer an interesting case with an unusual presentation or a surprise twist.
I agree!
But perhaps it is more constructive to consider what a case report cannot do.
It cannot provide evidence about the effectiveness of a therapy. To publish something like:
- I had a patient with the common condition xy;
- I treated her with therapy yz;
- this was followed by patient feeling better;
is totally bonkers – even more so if the outcome was subjective and the therapy consisted of more than one intervention, as in the article above. We have no means of telling whether it was treatment A, or treatment B, or a placebo effect, or the regression towards the mean, or the natural history of the condition that caused the outcome. The authors might just as well just have reported:
WE RECENTLY TREATED A PATIENT WHO GOT BETTER
full stop.
Sadly – and this is the reason why I spend some time on this subject – this sort of thing happens very often in the realm of SCAM.
Case reports are particularly valuable if they enable and stimulate others to do more research on a defined and under-researched issue (e.g. an adverse effect of a therapy). Case reports like the one above do not do this. They are a waste of space and tend to be abused as some sort of indication that the treatments in question might be valuable.
This systematic review and meta-analysis was aimed at analyzing the effectiveness of craniosacral therapy in improving pain and disability among patients with headache disorders.
PubMed, Physiotherapy Evidence Database, Scopus, Cochrane Library, Web of Science, and Osteopathic Medicine Digital Library databases were searched in March 2023. Two independent reviewers searched the databases and extracted data from randomized clinical trials comparing craniosacral therapy with control or sham interventions. The same reviewers assessed the methodological quality and the risk of bias using the PEDro scale and the Cochrane Collaboration tool, respectively. Grading of recommendations, assessment, development, and evaluations was used to rate the certainty of the evidence. Meta-analyses were conducted using random effects models using RevMan 5.4 software.
The searches retrieved 735 papers, and 4 studies were finally included. The craniosacral therapy provided statistically significant but clinically unimportant change on pain intensity (Mean difference = –1.10; 95% CI: –1.85, –0.35; I2: 44%), and no change on disability or headache effect (Standardized Mean Difference = –0.34; 95% CI –0.70, 0.01; I2: 26%). The certainty of the evidence was downgraded to very low.
The authors concluded that very low certainty of evidence suggests that craniosacral therapy produces clinically unimportant effects on pain intensity, whereas no significant effects were observed in disability or headache effect.
I find it strange that researchers seem so frequently unable to formulate their conclusions clearly. Is it political correctness? Or are they somehow favorably inclined (i.e. biased) towards the treatment that they pretend to critically evaluate?
Let’s look at the facts related to this review:
- Craniosacral therapy (CST) is utterly implausible.
- Only 4 RCTs were found.
- They were of poor quality.
- They were published mostly by people who want to promote CST.
- Therefore the overall statistically significant effect is most likely a false-positive result.
- This means that the conclusion should be much more straight forward.
I suggest something along the following lines:
A critical evaluation of the existing RCTs failed to find convincing evidence that CST is an effective treatment for headache disorders.
This randomised, double blind controlled trial compared the efficacy of curcumin versus omeprazole in improving patient reported outcomes in people with dyspepsia.
The interventions were:
- curcumin alone (C),
- omeprazole alone (O),
- curcumin plus omeprazole (C+O).
Patients in the combination group received two capsules of 250 mg curcumin, four times daily, and one capsule of 20 mg omeprazole once daily for 28 days.
Main outcome measure was unctional dyspepsia symptoms on days 28 and 56, assessed using the Severity of Dyspepsia Assessment (SODA) score. Secondary outcomes were the occurrence of adverse events and serious adverse events.
A total of 206 patients were enrolled in the study and randomly assigned to one of the three groups; 151 patients completed the study. Demographic data (age 49.7±11.9 years; women 73.4%), clinical characteristics and baseline dyspepsia scores were comparable between the three groups. Significant improvements were observed in SODA scores on day 28 in the pain (−4.83, –5.46 and −6.22), non-pain (−2.22, –2.32 and −2.31) and satisfaction (0.39, 0.79 and 0.60) categories for the C+O, C, and O groups, respectively. These improvements were enhanced on day 56 in the pain (−7.19, –8.07 and −8.85), non-pain (−4.09, –4.12 and −3.71) and satisfaction (0.78, 1.07, and 0.81) categories in the C+O, C, and O groups, respectively. No significant differences were observed among the three groups and no serious adverse events occurred.
The authors concluded that curcumin and omeprazole had comparable efficacy for functional dyspepsia with no obvious synergistic effect.
This study, which was funded by the Thai Traditional and Alternative Medicine Fund, has been picked up by the press and is being lauded as a solid proof of efficacy. Its authors too are not half proud of their splendid trial:
This multicentre randomised controlled trial provides highly reliable evidence for the treatment of functional dyspepsia. PPIs, widely used and approved for over-the-counter use, were compared with curcumin, a popular herbal remedy. The study design, including double blind randomisation, minimised biases. Participants met strict criteria, underwent endoscopy and were tested for H pylori infection. Furthermore, we implemented measures to minimise biases by ensuring that the individuals administering the drugs, participants receiving the drugs and individuals conducting the assessment remained blinded to the type of medications administered to the participants. The trial was carried out in hospitals, and certified individuals used standardised questionnaires for assessments. Statistical methods were appropriate and followed accepted principles.
Two follow-up appointments were scheduled, and blood tests showed no abnormal symptoms or liver function abnormalities. However, participants with high body mass index indicated a trend towards liver function impairment in the curcumin group, suggesting the need for larger studies. Some participants did not provide follow-up information, which is a study weakness. However, the number of participants who provided this information was sufficient for statistical analysis and the majority of the participants attended the follow-up visit. Therefore, it can be deduced from the results that even if the number of participants followed after drug administration increased, the study findings would not be significantly different. Another limitation of this study was the absence of long term follow-up data for all patients after treatment. This is a question that will require further investigation.
The strength of the study lies in its relevance to daily clinical practice, providing additional drug options in addition to PPIs alone, without added side effects. The study was unbiased, partially funded by government organisations and the first well designed trial comparing curcumin with PPI for functional dyspepsia, with confirmation through endoscopy and ruling out H pylori infection. Limitations of this study included the small number of patients who were lost to follow-up and the lack of long term follow-up data.
However, I am far less impressed.
Why?
Curcumin is bright yellow and has a very distinct taste/smell. Even though curumin was given in capsules, patients can easily tell what they are taking. I therefore doubt that they were adequately blinded. In fact, the authors seem to agree when they state the following:
We observed that despite improvements in pain and non-pain scores, there was no significant improvement in the SODA satisfaction scores in the O and C+O groups (table 3). A possible explanation for this observation could be related to the taste and/or smell of curcumin, which might have caused reduced pleasantness for the participants while ingesting it. This potential discomfort could offset the improvements in pain and non-pain symptoms, leading to the non-significant change in satisfaction score. Further studies may be needed to explore this hypothesis as well as to improve the palatability of curcumin.
Sadly, the success of blinding (which under such circumstances should always be tested) was not reported and probably not even quantified. If many patients were de-blinded, it seems inevitable that their expectation influenced the results. In other words, the much-lauded effect of curcumin might just be due to placebo and curcumin might be entirely useless. Or, to put it bluntly, the trial was not nearly as good as many made it out to be.
PS
Sad to see that the reviewers of a reputable journal failed to pick up on this significant flaw.
The aim of this systematic review was to update the current level of evidence for spinal manipulation in influencing various biochemical markers in healthy and/or symptomatic population.
Various databases were searched (inception till May 2023) and fifteen trials (737 participants) that met the inclusion criteria were included in the review. Two authors independently screened, extracted and assessed the risk of bias in included studies. Outcome measure data were synthesized using standard mean differences and meta-analysis for the primary outcome (biochemical markers). The Grading of Recommendations, Assessment, Development and Evaluation (GRADE) was used for assessing the quality of the body of evidence for each outcome of interest.
There was low-quality evidence that spinal manipulation influenced various biochemical markers (not pooled). There was low-quality evidence of significant difference that spinal manipulation is better (SMD -0.42, 95% CI – 0.74 to -0.1) than control in eliciting changes in cortisol levels immediately after intervention. Low-quality evidence further indicated (not pooled) that spinal manipulation can influence inflammatory markers such as interleukins levels post-intervention. There was also very low-quality evidence that spinal manipulation does not influence substance-P, neurotensin, oxytocin, orexin-A, testosterone and epinephrine/nor-epinephrine.
The authors concluded that spinal manipulation may influence inflammatory and cortisol post-intervention. However, the wider prediction intervals in most outcome measures point to the need for future research to clarify and establish the clinical relevance of these changes.
The majority of the studies were of low or very low quality. This means that the collective evidence is less than reliable. In turn, this means, I think, that the conclusions are misleading. A more honest conclusion would be this:
There is no reliable evidence that spinal manipulation influences inflammatory and cortisol levels.
As for the clinical relevance, I would like to point out that it would not be surprising if chiropractors could one day convincingly show that spinal manipulation do influence various biochemical markers. Many things do! If you fall down a staircase, for instance, plenty of biochemical markers will be affected. This, however, does not mean that throwing our patients down the stairs is of therapeutic value.
This study aimed to compare the effects of cognitive functional therapy (CFT) and movement system impairment (MSI)-based treatment on pain intensity, disability, Kinesiophobia, and gait kinetics in patients with chronic non-specific low back pain (CNSLBP).
In a single-blind randomized clinical trial, the researchers randomly assigned 91 patients with CNSLBP into CFT (n = 45) and MSI-based treatment (n = 46) groups. An 8-week training intervention was given to both groups. The researchers measured the primary outcome, which was pain intensity (Numeric rating scale), and the secondary outcomes, including disability (Oswestry disability index), Kinesiophobia (Tampa Kinesiophobia Scale), and vertical ground reaction force (VGRF) parameters at self-selected and faster speed (Force distributor treadmill). They evaluated patients at baseline, at the end of the 8-week intervention (post-treatment), and six months after the first treatment. Mixed-model ANOVA was used to evaluate the effects of the interaction between time (baseline vs. post-treatment vs. six-month follow-up) and group (CFT vs. MSI-based treatment) on each measure.
CFT showed superiority over MSI-based treatment in reducing pain intensity (P < 0.001, Effect size (ES) = 2.41), ODI (P < 0.001, ES = 2.15), and Kinesiophobia (P < 0.001, ES = 2.47) at eight weeks. The CFT also produced greater improvement in VGRF parameters, at both self-selected (FPF[P < 0.001, ES = 3], SPF[P < 0.001, ES = 0.5], MSF[P < 0.001, ES = 0.67], WAR[P < 0.001, ES = 1.53], POR[P < 0.001, ES = 0.8]), and faster speed, FPF(P < 0.001, ES = 1.33, MSF(P < 0.001, ES = 0.57), WAR(P < 0.001, ES = 0.67), POR(P < 0.001, ES = 2.91)] than the MSI, except SPF(P < 0.001, ES = 0.0) at eight weeks.
The authors concluded that this study suggests that the CFT is associated with better results in clinical and cognitive characteristics than the MSI-based treatment for CNSLBP, and the researchers maintained the treatment effects at six-month follow-up. Also, This study achieved better improvements in gait kinetics in CFT. CTF seems to be an appropriate and applicable treatment in clinical setting.
To understand this study, we need to know what CFT and MSI exactly entailed. Here is the information that the authors provide:
Movement system impairment-based treatment
The movement system impairment-based treatment group received 11 sessions of MSI-based treatment over the 8 weeks for 60 min per session with a supervision of a native speaker experienced (above 5 years) physical therapist with the knowledge of MSI-based treatment. The researchers designed the MSI-based treatment uniquely for each patient based on the interview, clinical examination, and questionnaires, just like they did with the CFT intervention. First, they administered standardized tests to characterize changes in the patient’s low back pain symptoms, and then they modified the treatment to make it more specific based on the participant’s individual symptoms. Depending on the participant’s direction-specific low back pain classification, they performed the intervention following one of the five MSI subgroups namely [1] rotation, [2] extension, [3] flexion, [4] rotation with extension, and [5] rotation with flexion. Finally, Patients treated using the standardized MSI protocol as follows: [1] education regarding normal postures and movements such as sitting, walking, bending, standing, and lying down; [2] education regarding exercises to perform trunk movements as painlessly as possible; and [3] prescription of functional exercises to improve trunk movement [32].
Cognitive functional therapy
Cognitive functional therapy was prescribed for each patient in CFT group based the CFT protocol conducted by O’Sullivan et al. (2015). Patients received supervised 12 sessions of training over the 8-week period with 60 min per session provided with another physical therapist who had been trained in CFT treatment. In this protocol, a physical therapist with more than 5 years of experience conducted an interview and physical examination of the patients to determine their own unique training programs, considering modifiable cognitive, biopsychosocial, functional, and lifestyle behavior factors. The intervention consists of the following 3 main stages: [1] making sense of pain that is completely reflective, where physical therapist could use the context of the patient’s own story to provide a new understanding of their condition and question their old beliefs [2] exposure with control which is designed to normalize maladaptive or provocative movement and posture related to activities of daily living that is integrated into each patient’s functional impairments, including teaching how to relax trunk muscles, how to have normal body posture while sitting, lying, bending, lifting, moving, and standing, and how to avoid pain behaviors, which aims to break poor postural habits; and [3] lifestyle change which is investigating the influence of unhealthy lifestyles in the patient’s pain context. Assessing the individual’s body mass, nutrition, quality of sleep, levels of physical activity or sedentary lifestyle, smoking, and other factors via video calls. Identifying such lifestyle factors helped us to individually advise and design exercise programs, rebuild self-confidence and self-efficacy, promote changes in lifestyle, and design coping strategies.
I must admit that I am not fully convinced.
Firstly, the study was not large and we need – as the authors state – more evidence. Secondly, I am not sure that the results show CFT to be more effective that MSI. They might merely indicate 1) that the bulk of the improvement is due to non-specific effects (e.g. reression towards the mean, natural history of the condition, placebo) and 2) that CFT is less harmful than MSI.
My conclusion:
we need not just more but better evidence.
This study aimed to compare the effectiveness of three distinct interventions – Yoga, Naturopathy, and Conventional medical management – in alleviating pain, reducing disability, enhancing spinal mobility, and improving the quality of life in individuals with low back pain. Ninety participants were recruited and randomly divided into three groups.
- The first group (group 1) received Yoga,
- the second group (group 2) received Naturopathy treatments,
- the third group served as the control and received conventional medications.
Visual Analogue Scale (VAS) scores, Oswestry Disability Index (ODI), Flexion Test-Finger to Floor Test (FTFT) results, and Quality of Life (QOL) were assessed at baseline and after a 10-day intervention period for all groups.
Overall comparisons between the groups, utilizing ANOVA, revealed marked differences in pain severity, disability index, daily functional capacity, and Quality of Life (QoL) improvements following respective interventions. Substantial improvements were also noted within the yoga and naturopathic medicine groups across multiple variables.
The authors concluded that the results of this comparative analysis emphasize the effectiveness of Yoga, Naturopathy, and Conventional Medical Treatment in managing low back pain. All three interventions demonstrated significant improvements in pain intensity, disability, spinal mobility, and quality of life. This study contributes valuable insights into the diverse therapeutic approaches for low back pain management, highlighting the potential of holistic and alternative treatments to enhance patients’ well-being.
__________________
This is a remarkably poor study. Its flaws are too numerous to account for them all here. Let me focus on just a three that stand out.
- All we learn about the 3 treatment regimen is this (and it clearly not enough to do an independent replication of this trial):
Yoga Group:
Participants in the Yoga Group underwent a specifically designed integrated approach of Yoga therapy (IAYT) for back pain, incorporating relaxation techniques, spinal movements, breathing exercises, pranayama, and deep relaxation techniques. The intervention was conducted by qualified yoga instructors at SDM College of Naturopathy and Yogic Sciences.
Naturopathy Group:
Participants in the Naturopathy Group received neutral spinal baths and partial massages. The spinal bath was administered at Government Yoga & Nature Cure Out Patient Center, Puttur, and massages were performed by trained naturopathy therapists.
Conventional Medicine Group:
Participants in the Conventional Medicine Group received standard medical treatments for low back pain as recommended by orthopedic physicians from S.D.M Medical College, Dharward
- As an equivalence trial, the sample size of this study is far too small. This means that its findings are most likely caused by coincidence and not by the interventions applied.
- There was no attempt of blinding the patients. Therefore, the results – if they were otherwise trustworthy – would be dominated by expectations and not by the effects of the treatments.
Altogether, this study is, I think, a good example for the fact that
poor research often is worse than no research at all.
Women experience more problems in their sexual functioning after childbirth. Due to the high prevalence of sexual problems during the lactation period, the World Health Organization suggests that measures are needed to improve women’s sexual functioning during breastfeeding. This study investigated the effect of auricular acupressure on sexual functioning among lactating women.
A randomized, sham-controlled trial was conducted between October 2019 to March 2020 in urban comprehensive health centers of Qazvin, Iran. Seventy-six women who had been lactating between six months and one year postpartum were randomly assigned to auricular acupressure group (n=38) or sham control group (n=38) using a balanced block randomization method. The intervention group received ear acupressure in 10 sessions (at four-day intervals) and control group received the sham intervention at the same intervals. Sexual functioning was the primary outcome of the study (assessed using the Female Sexual Function Index) before and at three time points post-intervention (immediately after, one month after, and two months after). The secondary outcome was sexual quality of life assessed using Sexual Quality of Life-Female Version.
Auricular acupressure had a large effect on female sexual functioning at all three post-intervention time points:
- immediately after the intervention (adjusted mean difference [95% CI]: 8.37 [6.27; 10.46] with Cohen’s d [95% CI]: 1.81[1.28; 2.34]),
- one month after the intervention (adjusted mean difference [95% CI]: 8.44 [6.41; 10.48] with Cohen’s d [95% CI]: 2.01 [1.46; 2.56]),
- two months after the intervention (adjusted mean difference [95% CI]: 7.43 [5.12; 9.71] with Cohen’s d [95% CI]: 1.57 [1.06; 2.08]).
Acupressure significantly increased participants’ sexual quality of life on the Sexual Quality of Life-Female scale by 13.73 points in the intervention group compared to the control group (p<0.001). The effect size of intervention for female sexual quality was large (adjusted Cohen’s d [95% CI]: 1.09 [0.58; 1.59]). Weekly frequency of sexual intercourse in the intervention group significantly increased compared to sham control group (p<0.001). These changes were clinically significant for sexual functioning and sexual quality of life.
The authors concluded that auricular acupressure was effective in increasing quality of sexual life and sexual functioning among lactating women. Although further research is needed to confirm the efficacy of auricular acupressure, based on the present study’s findings, the use of auricular acupressure by women’s healthcare providers after childbirth is recommended.
One possible explanation for this result is that the study was de-blinded; the sham treatment might not have been distinguished from the verum, or the verbal and/or non-verbal communications between the therapist and the patients contributed to a de-blinding effect. As the sucess of blinding was not reported and probably not even tested, we cannot know. The authors explain that auricular acupressure might improve both endocrine function (increased sex hormones including androgens and estrogens) and its physiological consequences (e.g., vaginal dryness, and vaginal epithelial atrophy), as well as reducing fatigue and insomnia problems (which might increase sexual desire).
Personally, I find this VERY hard to believe. Auricular acupressure or auriculotherapy, as it is also called, was invented by Paul Nogier in the 1950s. Its assumptions are not in line with our knowledge of anatomy and physiology. The different maps used by proponents of auriculotherapy show embarrassing disagreements. The therapy is being promoted as a treatment for many conditions. However, the clinical evidence that it might be effective is weak, not least because many of the clinical trials are of low quality and thus unreliable. One of the first rigorous tests of auriculotherapy was published in 1984 by one of the most prominent researchers of pain, R. Melzack. Here is the abstract[2]:
Enthusiastic reports of the effectiveness of electrical stimulation of the outer ear for the relief of pain (“auriculotherapy”) have led to increasing use of the procedure. In the present study, auriculotherapy was evaluated in 36 patients suffering from chronic pain, using a controlled crossover design. The first experiment compared the effects of stimulation of designated auriculotherapy points, and of control points unrelated to the painful area. A second experiment compared stimulation of designated points with a no-stimulation placebo control. Pain-relief scores obtained with the McGill Pain Questionnaire failed to show any differences in either experiment. It is concluded that auriculotherapy is not an effective therapeutic procedure for chronic pain.
Today we have an abundance of clinical trials of this therapy. Their results are by no means uniform. It is therefore best not to rely on single studies but on systematic reviews that include the evidence from all reliable trials. Our review concluded that “because of the paucity and of the poor quality of the data, the evidence for the effectiveness of auricular therapy for the symptomatic treatment of insomnia is limited. Further, rigorously designed trials are warranted to confirm these results.”[3] Other, less rigorous reviews arrive at more positive conclusions; due to the often poor quality of the primary studies, they should, however, be interpreted with great caution.[4]
The most frequently reported adverse events of auriculotherapy include local skin irritation and discomfort, mild tenderness or pain, and dizziness. Most of these events were transient, mild, and tolerable, and no serious adverse events were identified.[5]
In view of all this, I think that we need much more and much better evidence for auricular acupressure to be recommended for ANY condition.
[1] Wirz-Ridolfi A. The History of Ear Acupuncture and Ear Cartography: Why Precise Mapping of Auricular Points Is Important. Med Acupunct. 2019 Jun 1;31(3):145-156. doi: 10.1089/acu.2019.1349.
[2] Melzack, R., & Katz, J. (1984). Auriculotherapy fails to relieve chronic pain. A controlled crossover study. JAMA, 251(8), 1041–1043.
[3] Lee MS, Shin BC, Suen LK, Park TY, Ernst E (2008) Auricular acupuncture for insomnia: a systematic review. Int J Clin Pract 62(11):1744–1752.
[4] Usichenko, T. I., Hua, K., Cummings, M., Nowak, A., Hahnenkamp, K., Brinkhaus, B., & Dietzel, J. (2022). Auricular stimulation for preoperative anxiety – A systematic review and meta-analysis of randomized controlled clinical trials. Journal of clinical anesthesia, 76, 110581.
[5] Tan JY, Molassiotis A, Wang T, Suen LK (2014) Adverse events of auricular therapy: a systematic review. Evid Based Complement Alternat Med 2014:506758
A ‘pragmatic, superiority, open-label, randomised controlled trial’ of sleep restriction therapy versus sleep hygiene has just been published in THE LANCET. Adults with insomnia disorder were recruited from 35 general practices across England and randomly assigned (1:1) using a web-based randomisation programme to either four sessions of nurse-delivered sleep restriction therapy plus a sleep hygiene booklet or a sleep hygiene booklet only. There was no restriction on usual care for either group. Outcomes were assessed at 3 months, 6 months, and 12 months. The primary endpoint was self-reported insomnia severity at 6 months measured with the insomnia severity index (ISI). The primary analysis included participants according to their allocated group and who contributed at least one outcome measurement. Cost-effectiveness was evaluated from the UK National Health Service and personal social services perspective and expressed in terms of incremental cost per quality-adjusted life year (QALY) gained. The trial was prospectively registered (ISRCTN42499563).
Between Aug 29, 2018, and March 23, 2020 the researchers randomly assigned 642 participants to sleep restriction therapy (n=321) or sleep hygiene (n=321). Mean age was 55·4 years (range 19–88), with 489 (76·2%) participants being female and 153 (23·8%) being male. 580 (90·3%) participants provided data for at least one outcome measurement. At 6 months, mean ISI score was 10·9 (SD 5·5) for sleep restriction therapy and 13·9 (5·2) for sleep hygiene (adjusted mean difference –3·05, 95% CI –3·83 to –2·28; p<0·0001; Cohen’s d –0·74), indicating that participants in the sleep restriction therapy group reported lower insomnia severity than the sleep hygiene group. The incremental cost per QALY gained was £2076, giving a 95·3% probability that treatment was cost-effective at a cost-effectiveness threshold of £20 000. Eight participants in each group had serious adverse events, none of which were judged to be related to intervention.
The authors concluded that brief nurse-delivered sleep restriction therapy in primary care reduces insomnia symptoms, is likely to be cost-effective, and has the potential to be widely implemented as a first-line treatment for insomnia disorder.
I am frankly amazed that this paper was published in a top journal, like THE LANCET. Let me explain why:
The verum treatment was delivered over four consecutive weeks, involving one brief session per week (two in-person sessions and two sessions over the phone). Session 1 introduced the rationale for sleep restriction therapy alongside a review of sleep diaries, helped participants to select bed and rise times, advised on management of daytime sleepiness (including implications for driving), and discussed barriers to and facilitators of implementation. Session 2, session 3, and session 4 involved reviewing progress, discussion of difficulties with implementation, and titration of the sleep schedule according to a sleep efficiency algorithm.
This means that the verum group received fairly extensive attention, while the control group did not. In other words, a host of non-specific effects are likely to have significantly influenced or even entirely determined the outcome. Despite this rather obvious limitation, the authors fail to discuss any of it. On the contrary, that claim that “we did a definitive test of whether brief sleep restriction therapy delivered in primary care is clinically effective and cost-effective.” This is, in my view, highly misleading and unworthy of THE LANCET. I suggest the conclusions of this trial should be re-formulated as follows:
The brief nurse-delivered sleep restriction, or the additional attention provided exclusively to the patients in the verum group, or a placebo-effect or some other non-specific effect reduced insomnia symptoms.
Alternatively, one could just conclude from this study that poor science can make it even into the best medical journals – a problem only too well known in the realm of so-called alternative medicine (SCAM).
This systematic review evaluated all available randomized controlled trials (RCTs) investigating the clinical effects of hydrotherapy according to Kneipp which is characterized by cold water applications. All RCTs on therapy and prevention with Kneipp hydrotherapy were included. Study participants were patients and healthy volunteers of all age groups. MEDLINE (via PubMed), Scopus, Central, CAMbase, and opengrey.eu were systematically searched through April 2021 without language restrictions and updated by searching PubMed until April 6th 2023. The risk of bias was assessed using the Cochrane tool version 1.
Twenty RCTs (N=4247) were included. Due to the high heterogeneity of the RCTs, no meta-analysis was performed. The risk of bias was rated as unclear in most of the domains. Of 132 comparisons, 46 showed significant positive effects in favor of hydrotherapy on chronic venous insufficiency, menopausal symptoms, fever, cognition, emotional function, and sickness absenteeism. However, 81 comparisons showed no differences between groups, and 5 were in favor of the respective control group. Only half of the studies reported safety issues.
The authors concluded that although RCTs on Kneipp hydrotherapy seem to show positive effects in some conditions and outcomes, it remains difficult to ascertain treatment effects due to the high risk of bias and heterogeneity of most of the considered studies. Further high-quality RCTs on Kneipp hydrotherapy are urgently warranted.
This is certainly the best review of the subject so far. It makes it very clear that the evidence for Kneipp hydrotherapy is weak, mostly because of the many flaws in the primary studies. One needs to add, I think, that 20 RCTs are an absurdly small amount considering that many indications this type of therapy is advocated for – many enthusiasts even consider it a panacea.
It follows, I fear, that Kneipp hydrotherapy is almost entirely not evidence-based. This should be bad news for the numerous institutions and Spa towns (mostly in Germany) that live on employing this treatment and telling patients that it is effective. They usually claim that experience shows this to be true. But this was the mantra of medicine ~100 years ago. Since then, we have learned that experience is a very poor guide that regularly leads us up the garden path.
Kneippians will counter that clinical trials are difficult to conduct and expensive to finance. Both arguments are of course true but, considering that an entire industry lives on telling patients something that essentially amounts to a lie (i.e. the claim that it works), it surely is obligatory to overcome these obstacles.
Cervical artery dissection (CeAD), which includes both vertebral artery dissection (VAD) and carotid artery dissection (CAD), is the most serious safety concern associated with cervical spinal manipulation (CSM). This study evaluated the association between CSM and CeAD among US adults.
Through analysis of health claims data, the researchers employed a case-control study with matched controls, a case-control design in which controls were diagnosed with ischemic stroke, and a case-crossover design in which recent exposures were compared to exposures in the same case that occurred 6-7 months earlier. The researchers evaluated the association between CeAD and the 3-level exposure, CSM versus office visit for medical evaluation and management (E&M) versus neither, with E&M set as the referent group.
2337 VAD cases and 2916 CAD cases were identified. Compared to population controls, VAD cases were 0.17 (95% CI 0.09 to 0.32) times as likely to have received CSM in the previous week as compared to E&M. In other words, E&M was about 5 times more likely than CSM in the previous week in cases, relative to controls. CSM was 2.53 (95% CI 1.71 to 3.68) times as likely as E&M in the previous week among individuals with VAD than among individuals experiencing a stroke without CeAD. In the case-crossover study, CSM was 0.38 (95% CI 0.15 to 0.91) times as likely as E&M in the week before a VAD, relative to 6 months earlier. In other words, E&M was approximately 3 times more likely than CSM in the previous week in cases, relative to controls. Results for the 14-day and 30-day timeframes were similar to those at one week.
The authors concluded that, among privately insured US adults, the overall risk of CeAD is very low. Prior receipt of CSM was more likely than E&M among VAD patients as compared to stroke patients. However, for CAD patients as compared to stroke patients, as well as for both VAD and CAD patients in comparison with population controls and in case-crossover analysis, prior receipt of E&M was more likely than CSM.
What seems fairly clear from this and a previous similar analysis by the same authors is, I think, this: retrospective studies of this type can unfortunately not provide us with much reliable information about the risks of spinal manipulation. The reasons for this are manyfold, e.g.: less than exact classifications in patients’ records, or the fact that multiple types of spinal manipulations exist of which only some might be dangerous.
