study design

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This double-blind, randomized study assessed the effectiveness of physiotherapy instrument mobilization (PIM) in patients with low back pain (LBP) and compared it with the effectiveness of manual mobilization.

Thirty-two participants with LBP were randomly assigned to one of two groups:

  • The PIM group received lumbar mobilization using an activator instrument, stabilization exercises, and education.
  • The manual group received lumbar mobilization using a pisiform grip, stabilization exercises, and education.

Both groups had 4 treatment sessions over 2-3 weeks. The following outcomes were measured before the intervention, and after the first and fourth sessions:

  • Numeric Pain Rating Scale (NPRS),
  • Oswestry Disability Index (ODI) scale,
  • Pressure pain threshold (PPT),
  • lumbar spine range of motion (ROM),
  • lumbar multifidus muscle activation.

There were no differences between the PIM and manual groups in any outcome measures. However, over the period of study, there were improvements in both groups in NPRS (PIM: 3.23, Manual: 3.64 points), ODI (PIM: 17.34%, Manual: 14.23%), PPT (PIM: ⩽ 1.25, Manual: ⩽ 0.85 kg.cm2), lumbar spine ROM (PIM: ⩽ 9.49∘, Manual: ⩽ 0.88∘), and/or lumbar multifidus muscle activation (percentage thickness change: PIM: ⩽ 4.71, Manual: ⩽ 4.74 cm; activation ratio: PIM: ⩽ 1.17, Manual: ⩽ 1.15 cm).

The authors concluded that both methods of lumbar spine mobilization demonstrated comparable improvements in pain and disability in patients with LBP, with neither method exhibiting superiority over the other.

If this conclusion is meant to tell us that both treatments were equally effective, I beg to differ. The improvements documented here are consistent with improvements caused by the natural history of the condition, regression towards the mean, and placebo effects. The data do not prove that they are due to the treatments. On the contrary, they seem to imply that patients get better no matter what therapy is used. Thus, I feel that the results are entirely in keeping with the hypothesis that spinal mobilization is a placebo treatment.

So, allow me to re-phrase the authors’ conclusion as follows:

Lumbar mobilizations do not seem to have specific therapeutic effects and might therefore be considered to be ineffective for LBP.

Acupuncture is emerging as a potential therapy for relieving pain, but the effectiveness of acupuncture for relieving low back and/or pelvic pain (LBPP) during pregnancy remains controversial. This meta-analysis aimed to investigate the effects of acupuncture on pain, functional status, and quality of life for women with LBPP pain during pregnancy.

The authors included all RCTs evaluating the effects of acupuncture on LBPP during pregnancy. Data extraction and study quality assessments were independently performed by three reviewers. The mean differences (MDs) with 95% CIs for pooled data were calculated. The primary outcomes were pain, functional status, and quality of life. The secondary outcomes were overall effects (a questionnaire at a post-treatment visit within a week after the last treatment to determine the number of people who received good or excellent help), analgesic consumption, Apgar scores >7 at 5 min, adverse events, gestational age at birth, induction of labor and mode of birth.

Ten studies, reporting on a total of 1040 women, were included. Overall, acupuncture

  • relieved pain during pregnancy (MD=1.70, 95% CI: (0.95 to 2.45), p<0.00001, I2=90%),
  • improved functional status (MD=12.44, 95% CI: (3.32 to 21.55), p=0.007, I2=94%),
  • improved quality of life (MD=−8.89, 95% CI: (−11.90 to –5.88), p<0.00001, I2 = 57%).

There was a significant difference in overall effects (OR=0.13, 95% CI: (0.07 to 0.23), p<0.00001, I2 = 7%). However, there was no significant difference in analgesic consumption during the study period (OR=2.49, 95% CI: (0.08 to 80.25), p=0.61, I2=61%) and Apgar scores of newborns (OR=1.02, 95% CI: (0.37 to 2.83), p=0.97, I2 = 0%). Preterm birth from acupuncture during the study period was reported in two studies. Although preterm contractions were reported in two studies, all infants were in good health at birth. In terms of gestational age at birth, induction of labor, and mode of birth, only one study reported the gestational age at birth (mean gestation 40 weeks).

The authors concluded that acupuncture significantly improved pain, functional status and quality of life in women with LBPP during the pregnancy. Additionally, acupuncture had no observable severe adverse influences on the newborns. More large-scale and well-designed RCTs are still needed to further confirm these results.

What should we make of this paper?

In case you are in a hurry: NOT A LOT!

In case you need more, here are a few points:

  • many trials were of poor quality;
  • there was evidence of publication bias;
  • there was considerable heterogeneity within the studies.

The most important issue is one studiously avoided in the paper: the treatment of the control groups. One has to dig deep into this paper to find that the control groups could be treated with “other treatments, no intervention, and placebo acupuncture”. Trials comparing acupuncture combined plus other treatments with other treatments were also considered to be eligible. In other words, the analyses included studies that compared acupuncture to no treatment at all as well as studies that followed the infamous ‘A+Bversus B’ design. Seven studies used no intervention or standard of care in the control group thus not controlling for placebo effects.

Nobody can thus be in the slightest surprised that the overall result of the meta-analysis was positive – false positive, that is! And the worst is that this glaring limitation was not discussed as a feature that prevents firm conclusions.

Dishonest researchers?

Biased reviewers?

Incompetent editors?

Truly unbelievable!!!

In consideration of these points, let me rephrase the conclusions:

The well-documented placebo (and other non-specific) effects of aacupuncture improved pain, functional status and quality of life in women with LBPP during the pregnancy. Unsurprisingly, acupuncture had no observable severe adverse influences on the newborns. More large-scale and well-designed RCTs are not needed to further confirm these results.


I find it exasperating to see that more and more (formerly) reputable journals are misleading us with such rubbish!!!

The aim of this evaluator-blinded randomized clinical trial was to determine if manual therapy added to a therapeutic exercise program produced greater improvements than a sham manual therapy added to the same exercise program in patients with non-specific shoulder pain.

Forty-five subjects were randomly allocated into one of three groups:

  • manual therapy (glenohumeral mobilization technique and rib-cage technique);
  • thoracic sham manual therapy (glenohumeral mobilization technique and rib-cage sham technique);
  • sham manual therapy (sham glenohumeral mobilization technique and rib-cage sham technique).

All groups also received a therapeutic exercise program. Pain intensity, disability, and pain-free active shoulder range of motion were measured post-treatment and at 4-week and 12-week follow-ups. Mixed-model analyses of variance and post hoc pairwise comparisons with Bonferroni corrections were constructed for the analysis of the outcome measures.

All groups reported improved pain intensity, disability, and pain-free active shoulder range of motion. However, there were no between-group differences in these outcome measures.

The authors concluded that the addition of the manual therapy techniques applied in the present study to a therapeutic exercise protocol did not seem to add benefits to the management of subjects with non-specific shoulder pain.

What does that mean?

I think it means that the improvements observed in this study were due to 1) exercise and 2) a range of non-specific effects, and that they were not due to the manual techniques tested.

I cannot say that I find this enormously surprising. But I would also find it unsurprising if fans of these methods would claim that the results show that the physios applied the techniques not correctly.

In any case, I feel this is an interesting study, not least because of its use of sham therapy. But I somehow doubt that the patients were unable to distinguish sham from verum. If so, the study was not patient-blind which obviously is difficult to achieve with manual treatments.

The aim of this study was to evaluate the effectiveness of craniosacral therapy on different features in migraine patients.

Fifty individuals with migraine were randomly divided into two groups (n = 25 per group):

  • craniosacral therapy group (CTG),
  • sham control group (SCG).

The interventions were carried out with the patient in the supine position. The CTG received a manual therapy treatment focused on the craniosacral region including five techniques, and the SCG received a hands-on placebo intervention. After the intervention, individuals remained supine with a neutral neck and head position for 10 min, to relax and diminish tension after treatment. The techniques were executed by the same experienced physiotherapist in both groups.

The analyzed variables were pain, migraine severity, and frequency of episodes, functional, emotional, and overall disability, medication intake, and self-reported perceived changes, at baseline, after a 4-week intervention, and at an 8-week follow-up.

After the intervention, the CTG significantly reduced pain (p = 0.01), frequency of episodes (p = 0.001), functional (p = 0.001) and overall disability (p = 0.02), and medication intake (p = 0.01), as well as led to a significantly higher self-reported perception of change (p = 0.01), when compared to SCG. The results were maintained at follow-up evaluation in all variables.

The authors concluded that a protocol based on craniosacral therapy is effective in improving pain, frequency of episodes, functional and overall disability, and medication intake in migraineurs. This protocol may be considered as a therapeutic approach in migraine patients.

Sorry, but I disagree!

And I have several reasons for it:

  • The study was far too small for such strong conclusions.
  • For considering any treatment as a therapeutic approach in migraine patients, we would need at least one independent replication.
  • There is no plausible rationale for craniosacral therapy to work for migraine.
  • The blinding of patients was not checked, and it is likely that some patients knew what group they belonged to.
  • There could have been a considerable influence of the non-blinded therapists on the outcomes.
  • There was a near-total absence of a placebo response in the control group.

Altogether, the findings seem far too good to be true.



Shiatsu is a Japanese form of so-called alternative medicine (SCAM) derived from Traditional Chinese Medicine using deep pressure on the paths of the postulated acupuncture meridians. Clinical observations on this topic are said to be encouraging, especially for the treatment of sleep and conduct disorders, but there is a lack of empirical data.

The objective of this study was to examine the possible therapeutic effects of shiatsu in a clinical population of children treated in child and adolescent psychiatry. It was designed as a qualitative descriptive and non-interventional study, conducted on children treated in day-care hospital units and outpatient clinical settings. Shiatsu was administered, at least during 3 sessions, to children with an autism spectrum disorder or other disorders according to ICD-11 criteria (such as conduct disorders with impulsivity or attention deficit).

The evaluation was performed by two independent researchers (a child psychiatrist and a psychologist who were not the caregivers) based on direct observation of children during the shiatsu sessions, combined with semi-structured non-inductive interviews with their parents, and data collected from focus groups conducted with the children’s caregivers. A phenomenological interpretive analysis (IPA) approach with Nvivo coding software was used to analyze the data.

Based on semi-structured interviews with 13 parents cross-referenced with data from 2 focus groups and direct observations of 7 children during 2 full shiatsu sessions for each observation, the results show that shiatsu has positive effects on

  • internal tension (a relief effect, notably on aggressive behaviors directed against others or self),
  • sleep (including improvement of sleep quality),
  • social interaction,
  • attention,
  • verbalization of affects and traumatic memories of early childhood,
  • perception of bodily limits.

As these children had several other treatments as well, it cannot be proved that the positive effects observed in this study are related specifically to shiatsu practice. Shiatsu may participate and facilitate the effects of other treatments. It is noteworthy that most of the children came willingly to the shiatsu sessions, ask their parents to repeat the shiatsu sessions at home, and indicate to the practitioner, from one session to the next, their elective body points where they wish to receive the application of shiatsu.

The authors concluded that the findings suggest therapeutic benefits of shiatsu, especially on externalize violence with a relief of aggressive behavior directed against others or self (knowing, moreover, that internal tension, sleep disorders and non-verbalization of affects or traumatic memories, all improved by shiatsu, are also all risk factors for externalize violence). These results highlight, therefore, the need to develop a daily practice of shiatsu in child and adolescent psychiatry. Further research is required to clarify the effects of shiatsu and ascertain better its underlying mechanisms based on this exploratory pilot study.

I do appreciate that, with a treatment that has not been submitted to many controlled clinical trials, researchers feel that they have to start from scratch, e.g. simple observations. However, they also must realize that their observations do not lend themselves to firm conclusions about the effects of the treatment. In the present case, the researchers do seem to be aware of this caveat but nevertheless make statements that go way beyond of what is warranted:

  • the results show that shiatsu has positive effects on …
  • Shiatsu may participate and facilitate the effects of other treatments
  • the findings suggest therapeutic benefits of shiatsu, especially on externalize violence
  • These results highlight, therefore, the need to develop a daily practice of shiatsu in child and adolescent psychiatry

I fear that these statements are not merely exaggerated but suspect they are also untrue. Testing them in properly controlled clinical trials would show whether my suspicion is correct. Meanwhile, I would like to remind

  • researchers,
  • reviewers,
  • and journal editors

of their duty to be truthful and not mislead the public.


This study aimed to evaluate the number of craniosacral therapy sessions that can be helpful to obtain a resolution of the symptoms of infantile colic and to observe if there are any differences in the evolution obtained by the groups that received a different number of Craniosacral Therapy sessions at 24 days of treatment, compared with the control group which did not received any treatment.

Fifty-eight infants with colic were randomized into two groups:

  • 29 babies in the control group received no treatment;
  • babies in the experimental group received 1-3 sessions of craniosacral therapy (CST) until symptoms were resolved.

Evaluations were performed until day 24 of the study. Crying hours served as the primary outcome measure. The secondary outcome measures were the hours of sleep and the severity, measured by an Infantile Colic Severity Questionnaire (ICSQ).

Statistically significant differences were observed in favor of the experimental group compared to the control group on day 24 in all outcome measures:

  • crying hours (mean difference = 2.94, at 95 %CI = 2.30-3.58; p < 0.001);
  • hours of sleep (mean difference = 2.80; at 95 %CI = – 3.85 to – 1.73; p < 0.001);
  • colic severity (mean difference = 17.24; at 95 %CI = 14.42-20.05; p < 0.001).

Also, the differences between the groups ≤ 2 CST sessions (n = 19), 3 CST sessions (n = 10), and control (n = 25) were statistically significant on day 24 of the treatment for crying, sleep and colic severity outcomes (p < 0.001).

The authors concluded that babies with infantile colic may obtain a complete resolution of symptoms on day 24 by receiving 2 or 3 CST sessions compared to the control group, which did not receive any treatment.

Why do SCAM researchers so often have no problem leaving the control group of patients in clinical trials without any treatment at all, while shying away from administering a placebo? Is it because they enjoy being the laughingstock of the science community? Probably not.

I suspect the reason might be that often they know that their treatments are placebos and that their trials would otherwise generate negative findings. Whatever the reasons, this new study demonstrates three things many of us already knew:

  1. Colic in babies always resolves on its own but can be helped by a placebo response (e.g. via the non-blinded parents), by holding the infant, and by paying attention to the child.
  2. Flawed trials lend themselves to drawing the wrong conclusions.
  3. Craniosacral therapy is not biologically plausible and most likely not effective beyond placebo.

Guest post by Norbert Aust and Viktor Weisshäupl

Readers of this blog may remember the recent study of Frass et al. about the adjunct homeopathic treatment of patients suffering from non-small cell lung cancer (here). It was published in 2020 by the ‘Oncologist’, a respectable journal, and came to stunning results about to the effectiveness of homeopathy.

In our analysis, however, we found strong indications for duplicity: important study parameters like exclusion criteria or observation time were modified post hoc, and data showed characteristics that occur when unwanted data sets get removed.

We, that is the German Informationsnetzwerk Homöopathie and the Austrian ‘Initiative für wissenschaftliche Medizin’, had informed the Medical University Vienna about our findings – and the research director then asked the Austrian Agency for Scientific Integrity (OeAWI) to review the paper. The analysis took some time and included not only the paper and publicly available information but also the original data. In the end, OeAWI corroborated our findings: The results are not based on sound research but on modified or falsified data.

Here is their conclusion in full:

The committee concludes that there are numerous breaches of scientific integrity in the Study, as reported in the Publication. Several of the results can only be explained by data manipulation or falsification. The Publication is not a fair representation of the Study. The committee cannot for all the findings attribute the wrongdoings and incorrect representation to a single individual. However following our experience it is highly unlikely that the principal investigator and lead author, but also the co-authors were unaware of the discrepancies between the protocols and the Publication, for which they bear responsibility. (original English wording)

Profil, the leading news magazine of Austria reported in its issue of October 24, 2022, pp 58-61 (in German). There the lead author, Prof. M. Frass, a member of Edzard’s alternative medicine hall of fame, was asked for his comments. Here is his concluding statement:

All the allegations are known to us and completely incomprehensible, we can refute all of them. Our work was performed observing all scientific standards. The allegation of breaching scientific integrity is completely unwarranted. To us, it is evident that not all documents were included in the analysis of our study. Therefore we requested insight into the records to learn about the basis for the final statement.

(Die Vorwürfe sind uns alle bekannt und absolut unverständlich, alle können wir entkräften. Unsere Arbeit wurde unter Einhaltung aller wissenschaftlichen Standards durchgeführt. Der Vorhalt von Verstößen gegen die wissenschaftliche Intergrität enbehrt jeder Grundlage. Für uns zeigt sich offenkundig, dass bei der Begutachtung unserer Studie nicht alle Unterlagen miteinbezogen wurden. Aus diesem Grunde haben wir um Akteneinsicht gebeten, um die Grundlagen für das Final Statment kennenzulernen.)

The OeAWI together with the Medical University Vienna asked the ‘Oncologist’ for a retraction of this paper – which has not occurred as yet.

Aging often contributes to a decrease in physical activity. As age advances, a decrease in muscle mass, muscle strength, and flexibility can impair physical function. One obvious way to prevent these developments might be regular physical exercise.

This open-label, randomized trial was intended to evaluate the effects of an integrated yoga module in improving the flexibility, muscle strength, and quality of life (QOL) of older adults. Participants were 96 older adults, aged 60-75 years (64.1 ± 3.95 years). The program was a three-month, yoga-based lifestyle intervention. The participants were randomly allocated to the intervention group (n = 48) or to a waitlisted control group (n = 48). The intervention group underwent three one-hour sessions of yoga weekly, with each session including loosening exercises, asanas, pranayama, and meditation spanning.

At baseline and post-intervention, the following assessments were made:

  • spinal flexibility using a sit-and-reach test,
  • back and leg strength using a back leg dynamometer,
  • handgrip strength (HGS) and endurance (HGE) using a hand-grip dynamometer,
  • Older People’s Quality of Life (OPQOL) questionnaire.

Analysis was performed employing Wilcoxon’s Sign Rank tests and Mann-Whitney Tests, using an intention-to-treat approach.

The results show that, compared to the control group, the intervention group experienced a significantly greater increase in spinal flexibility (P < .001), back leg strength (P < .001), HGE (P < .01), and QOL (P < .001) after three months of yoga.

The authors concluded that yoga can be used safely for older adults to improve flexibility, strength, and functional QOL. Larger randomized controlled trials with an active control intervention are warranted.

I agree with the authors that this trial was too small and not properly controlled. I disagree that their study shows yoga to be effective or safe. In fact, the two sentences of the conclusion do not seem to fit together at all.

Is it surprising that doing yoga exercises is better than doing nothing at all?


Is it relevant to demonstrate this fact in an RCT?


If anyone wants to test the value of yoga exercises, they must compare them to conventional exercises. And why don’t they do this? Could it be because they know they would be unlikely to show that yoga is superior?


The objective of this study was to evaluate the effect of acupuncture on cognitive task performance in college students.

Sixty students aged 18-25 years were randomly allocated into acupuncture group (AG) (n=30) and control group (CG) (n=30). The AG underwent 20 min of acupuncture/day, while the CG underwent their normal routine for 10 days. Assessments were performed before and after the intervention.

Between-group analysis showed a significant increase in AG’s six-letter cancellation test (SLCT) score compared with CG. Within-group analysis showed a significant increase in the scores of all tests (i.e. SLCT, forward and backward Digit span test [DST]) in AG, while a significant increase in backward DST was observed in CG.

The authors concluded that acupuncture has a beneficial effect on improving the cognitive function of college students.

I am unable to access the full paper [it is behind a paywall]. Thus, I am unable to assess the study in further detail. As I am skeptical about the validity of the effect, I can only assume that it is due to the expectation of the volunteers receiving acupuncture. There was not even an attempt to control for placebo effects!

The over-stated conclusion made me wonder what else the 1st author has published. It turns out he has three more Medline-listed papers to his name all of which are about so-called alternative medicine (SCAM).

The 1st one is an RCT similar to the one above, i.e. without an attempt to control for placebo effects. Its conclusion is equally over-stated: Acupuncture could be considered as an effective treatment modality for the management of primary dysmenorrhea.

The other two papers refer to one case report each. Despite the fact that case reports (as any researcher must know) do not lend themselves to conclusions about the effectiveness of the treatments employed, the authors’ conclusions seem to again over-state the case:

What does that tell us?

I don’t know about you, but I would not rely on acupuncture to improve my mental performance.

The present study was conducted to evaluate the effect of date palm on the sexual function of infertile couples. It was designed as a double-blind, placebo-controlled clinical trial conducted on infertile women and their husbands who referred to infertility clinics in Iran in 2019.

The intervention group was given a palm date capsule and the control group was given a placebo. Data were collected through female sexual function index and International Index of Erectile Function.

The total score of sexual function of females in the intervention group increased significantly from 21.06 ± 2.58 to 27.31 ± 2.59 (P < 0.0001). Also, other areas of sexual function in females (arousal, orgasm, lubrication, pain during intercourse, satisfaction) in the intervention group showed a significant increase compared to females in the control group, which was statistically significant (P < 0.0001).

All areas of male sexual function (erectile function, orgasmic function, sexual desire, intercourse satisfaction and overall satisfaction) significantly increased in the intervention group compared to the control group (P < 0.0001).

The authors concluded that the present study revealed that 1-month consumption of date palm has a positive impact on the sexual function of infertile couples.

In an attempt to explain the rational for this study, the authors state that, since ancient times, date palm has been used in Greece, China and Egypt to treat infertility and increase sexual desire and fertility in females. Rasekh indicated that Palm Pollen is effective in sperm parameters of infertile men. Administering date palm to male rats and measuring the sexual parameters of rats showed an improvement in their sexual function. Studies on animals have shown its effect on the parameters of semen analysis in male animals and increasing hormones.

So, the trial was what might call a ‘long shot’, even a very long one. But that does not render its findings less interesting. If the results could be confirmed, they would certainly have considerable significance.

But can they be confirmed?

I have some doubts.

Two things are remarkable, in my view.

  1. The study only had subjective endpoints.
  2. There was as good as no placebo effect in the control group.

How can this be?

One explanation might be that the verum and the placebo capsules were easily identified by their taste of other features. This would then lead to many patients being ‘deblinded’; in other words, the patients on verum would have known and expected to experience an effect, while the patients on placebo would have also known and be disappointed thus not even experiencing a placebo response.

This might be an apt reminder for trialists to include a check of the success of blinding in their list of outcome measures.


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