MD, PhD, MAE, FMedSci, FRSB, FRCP, FRCPEd.

study design

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According to its authors, this study‘s objective was to demonstrate that acupuncture is beneficial for decreasing the risk of ischaemic stroke in patients with rheumatoid arthritis (RA).

The investigation was designed as a propensity score-matched cohort nationwide population-based study. Patients with RA diagnosed between 1 January 1997 and 31 December 2010, through the National Health Insurance Research Database in Taiwan. Patients who were administered acupuncture therapy from the initial date of RA diagnosis to 31 December 2010 were included in the acupuncture cohort. Patients who did not receive acupuncture treatment during the same time interval constituted the no-acupuncture cohort. A Cox regression model was used to adjust for age, sex, comorbidities, and types of drugs used. The researchers compared the subhazard ratios (SHRs) of ischaemic stroke between these two cohorts through competing-risks regression models.

After 1:1 propensity score matching, a total of 23 226 patients with newly diagnosed RA were equally subgrouped into acupuncture cohort or no-acupuncture cohort according to their use of acupuncture. The basic characteristics of these patients were similar. A lower cumulative incidence of ischaemic stroke was found in the acupuncture cohort (log-rank test, p<0.001; immortal time (period from initial diagnosis of RA to index date) 1065 days; mean number of acupuncture visits 9.83. In the end, 341 patients in the acupuncture cohort (5.95 per 1000 person-years) and 605 patients in the no-acupuncture cohort (12.4 per 1000 person-years) experienced ischaemic stroke (adjusted SHR 0.57, 95% CI 0.50 to 0.65). The advantage of lowering ischaemic stroke incidence through acupuncture therapy in RA patients was independent of sex, age, types of drugs used, and comorbidities.

The authors concluded that this study showed the beneficial effect of acupuncture in reducing the incidence of ischaemic stroke in patients with RA.

It seems obvious that the editors of ‘BMJ Open’, the peer reviewers of the study and the authors are unaware of the fact that the objective of such an investigeation is not to to demonstrate that acupuncture is beneficial but to test whether acupuncture is beneficial. Starting a study with the intention to to show that my pet therapy works is akin to saying: “I am intending to mislead you about the value of my intervention”.

One needs therefore not be surprised that the authors of the present study draw very definitive conclusions, such as “acupuncture therapy is beneficial for ischaemic stroke prevention”. But every 1st year medical or science student should know that correlation is not the same as causation. What the study does, in fact, show is an association between acupuncture and stroke. This association might be due to dozens of factors that the ‘propensity score matching’ could not control. To conclude that the results prove a cause effect relationship is naive bordering on scientific misconduct. I find it most disappointing that such a paper can pass all the hurdles to get published in what pretends to be a respectable journal.

Personally, I intend to use this study as a good example for drawing the wrong conclusions on seemingly rigorous research.

 

 

There are many variations of acupuncture. Electroacupuncture (EA) and Laseracupuncture (LA) are but two examples both of which are commonly used. However, it remains uncertain whether LA is as effective as EA. This study aimed to compare EA and LA head to head in dysmenorrhea.

A crossover, randomized clinical trial was conducted. EA or LA was applied to selected acupuncture points. Participants were randomized into two sequence treatment groups who received either EA or LA twice per week in luteal phase for 3 months followed by 2-month washout, then shifted to other groups (sequence 1: EA > LA; sequence 2: LA > EA). Outcome measures were heart rate variability (HRV), prostaglandins (PGs), pain, and quality-of-life (QoL) assessment (QoL-SF12). We also compared the effect of EA and LA in low and high LF/HF (low frequency/high frequency) status.

43 participants completed all treatments. Both EA and LA significantly improved HRV activity and were effective in reducing pain (Visual Analog Scale [VAS]; EA: p < 0.001 and LA: p = 0.010) and improving QoL (SF12: EA: p < 0.001, LA, p = 0.017); although without intergroup difference. EA reduced PGs significantly (p < 0.001; δ p = 0.068). In low LF/HF, EA had stronger effects than LA in increasing parasympathetic tone in respect of percentage of successive RR intervals that differ by more than 50 ms (pNN50; p = 0.053) and very low-frequency band (VLF; p = 0.035).

The authors concluded that there is no significant difference between EA and LA in improving autonomic nervous system dysfunction, pain, and QoL in dysmenorrhea. EA is prominent in PGs changing and preserving vagus tone in low LF/HF; yet LA is noninvasive for those who have needle phobia. Whether LA is equivalent with EA and the mechanism warrants further study.

Looking at the affiliations of the authors, one might expect that they should be able to design a meaningful study:

  • 1Division of Hemato-Oncology, Department of Internal Medicine, Branch of Zhong-Zhou, Taipei City Hospital, Taipei, Taiwan.
  • 2Institute of Traditional Medicine, National Yang-Ming Chiao Tung University, Taipei, Taiwan.
  • 3Department of Traditional Medicine, Branch of Yang-Ming, Taipei City Hospital, Taipei, Taiwan.
  • 4Department of Traditional Medicine, Branch of Kunming, Taipei City Hospital, Taipei, Taiwan.
  • 5Department of Gynecology and Obstetrics, Branch of Yang-Ming, Taipei City Hospital, Taipei, Taiwan.

Sadly, this assumption is evidently mistaken.

The trial certainly does not show what they claim and neither had it ever the chance to show anything relevent. A clinical trial is comparable to a mathematical equation. It can be solved, if it has one unkown; it cannot produce a result, if it has two unknowns.

The efficacy of EA and LA for dysmenorrhea are both unknown. A comparative study with two unknowns cannot produce a meaningful result. EA and LA did not both improve autonomic nervous system dysfunction, pain, and QoL in dysmenorrhea but most likely they both had no effect. What caused the improvement was not the treatment per se but the ritual, the placebo effect, the TLC or other non-specific factors. The maginal differences in other parameters are meaningless; they are due to the fact that – as an equivalence trial – the study was woefully underpowered and thus open to coincidental differences.

Clinical trials should be about contributing to our knowledge and not about contributing to confusion.

Acute Otitis Media (AOM) is one of the most common acute infections in children and often injudiciously treated by antibiotics. Homeopathy has been claimed to work but is it really effective?

This open label, randomized, controlled, parallel arm trial was conducted on children (aged 0–12 years), suffering from AOM. The primary outcome was changes in Tympanic Membrane Examination scale (TMES) and Acute Otitis Media-Severity of Symptoms (AOM-SOS) scale, time to improvement in pain through Facial Pain Scale-Revised (FPS-R) over 10 days. The need for antibiotics in both groups and the recurrence of subsequent episodes of AOM over 12 months were also compared.

Intention-to-treat analysis was performed on 222 children; Homeopathy (n = 117) (H-group), Allopathy (A-group) (n = 105). There was a statistically significant reduction of scores in H-group compared with A-group at each time point: at day 3 (mean diff. ± sd: 1.71 ± 0.19; 95% CI: 1.34 to 2.07; p = 0.0001), at day 7 (mean diff. ± sd: 1.29 ± 0.24; 95% CI: 0.82 to 1.76; p = 0.0001) and at day 10 (mean diff. ± sd: 1.23 ± 0.25; 95% CI = 0.74 to 1.71; p = 0.0001) favoring homeopathy. Clinical failure by the third day of treatment was observed in 11% and 24% of children in H-group vs A-group (OR: 0.03; 95% CI: 0.001 to 0.52; p = 0.03). None of the children in the H-group required antibiotics, whereas 14 children in the A-group did.

The authors concluded that both therapies seemed to produce comparable effects and appeared safe. The study consolidated the findings observed during a pilot study, i.e., homeopathy is non-inferior to allopathy in managing AOM in children and antibiotics in children can be avoided.

This study was published in the journal ‘Homeopathy’ and originates from the Central Council for Research in Homeopathy, New Delhi, India. Sadly, I do not have the full text of the paper and cannot therefore scrutinize it adequately.

Let me just mention these three facts:

  1.  The journal ‘Homeopathy’ never publishes negative results.
  2. Indian researchers of homeopathy publish as good as no negative results.
  3. As far as I can see, the Central Council for Research in Homeopathy, New Delhi, has never published a negative result.

These points do, of course, not necessarily mean that the study is false-positive, but they do not inspire me with confidence. In any case, it seems wise to insist on better evidence. To render it credible, we would need:

  1. Several rigorous RCTs that test homeopathy for AOM against placebo.
  2. If (and only then) they show that homeopathy is better than placebo, at least one independent replication of the present study.

As the biological plausibility of all this is close to zero, the chances that this will happen are also zero.

Jennifer Jacobs started publishing peer-reviewed papers on homeopathy in the early 1990s. This happens to be around the same time as I did. So, we both have about 30 years of research into homeopathy behind us.

Jennifer just authored a paper entitled “Thirty Years of Homeopathic Research – Lessons Learned“. Here is its abstract:

Conducting double-blind randomized controlled trials is difficult, even in the allopathic medical system. Doing so within the paradigm of classical homeopathy is even more challenging. More than thirty years of experience in carrying out such trials has taught me much about the pitfalls to avoid as well as the factors that can lead to success. The initial steps of putting together a research protocol, securing funding, and obtaining human subjects’ approval can be daunting. After that comes developing questionnaires and surveys, hiring study personnel, and recruitment of subjects. The actual implementation of the research comes with its own set of possible missteps. Sample size determination, entry criteria, as well as type, frequency and duration of treatment are all crucial. Finally, statistical analysis must be performed to a high standard and a manuscript prepared to submit for publication. Even then there can be one or more manuscript revisions to make, based on feedback from reviewers, before a study is actually published. The entire process can take at least two years and is usually much longer.

Mistakes at any one of these steps can damage the outcome, as well as the impact of the study. With examples from my body of research, I will discuss some of the things that I wish I had done differently, as well as those that turned out to be correct. Homeopathic research is held to a much higher standard than conventional trials. Any flaws in study design, implementation, and analysis can be used by critics to negate the results. I am hopeful that the next generation of homeopathic researchers will learn from my experiences and carry on with great success.

Jennifer’s example motivated me to follow suit and contribute some very brief thoughts about my 30 years of homeopathy research and the lessons I have learnt:

  Conducting double-blind randomized controlled trials is difficult in any area of medicine. Yet these types of studies are by far the best way to find out which treatments work and which don’t. Therefore, they need doing, regardless of the obstacles they may pose.

In homeopathy, we now have a large body of such trials. Sadly, not all of them are reliable. Those that are, according to accepted criteria, tend to fail to show that homeopathy works better than a placebo. Understandably, homeopaths are disappointed with this overall result and have made numerous attempts to invalidate it.

The main problem with research into homeopathy is not the research methodology. It is well established for clinical trials and can be easily modified to fit all the demands made by individualised treatment or other pecularities that may apply to homeopathy. The main problem is the homeopath who finds it impossible to accept the truth, namely that highly diluted homeopathic remedies are pure placebos and any observed benefits of homeopathy are due to non-specific effects such as the empathetic encounter or a placebo response.

The lesson to be learned from the past is that, in medicine, even the most obsessive belief, conviction or wishful thinking will eventually have to give way to the scientific evidence. In the case of homeopathy, this process has taken an extraordinary amount of time and effort but, finally, we are almost there and the writing is on the wall for everyone to see.

Two resumes of 30 years of work, research and experience!

And what a difference between them!

Who do you think gets closer to the truth,

Jennifer or I?

Of all the forms of so-called alternative medicine (SCAM), Reiki is amongst the least plausible. It is a form of paranormal or ‘energy healing’ popularised by Japanese Mikao Usui (1865–1926). Reiki is based on the assumptions of Traditional Chinese Medicine and the existence of ‘chi’, the life-force that is assumed to determine our health.

Reiki practitioners believe that, with their hands-on healing method, they can transfer ‘healing energy’ to a patient which, in turn, stimulates the self-healing properties of the body. They assume that the therapeutic effects of this technique are obtained from a ‘universal life energy’ that provides strength, harmony, and balance to the body and mind.

Despite its implausibility, Reiki is used for a very wide range of conditions. Some people are even convinced that it has positive effects on sexuality. But is that really so?

This randomised clinical trial was aimed at finding out. Specifically, its authors wanted to determine the effect of Reiki on sexual function and sexual self-confidence in women with sexual distress*. It was was conducted with women between the ages of 15–49 years who were registered at a family health center in the eastern region of Turkey and had sexual distress.

The sample of the study consisted of 106 women, 53 in the experimental group and 53 in the control group. Women in the experimental group received Reiki once a week for four weeks, while no intervention was applied to those in the control group. Data were collected using the Female Sexual Distress Scale-Revised (FSDS-R), the Arizona Sexual Experiences Scale (ASEX), and the Sexual Self-confidence Scale (SSS).

The levels of sexual distress, sexual function, and sexual self-confidence of women in both groups were similar before the intervention, and the difference between the groups was not statistically significant (p > 0.05). After the Reiki application, the FSDS-R and ASEX mean scores of women in the experimental group significantly decreased, while their SSS mean score significantly increased, and the difference between the groups was statistically significant (p < 0.05).

The authors concluded that Reiki was associated with reduced sexual distress, positive outcomes in sexual functions, and increase sexual self-confidence in women with sexual distress. Healthcare professionals may find Reiki to positively enhance women’s sexuality.

Convinced?

I hope not!

The study has the most obvious of all design flaws: it does not control for a placebo effect, nor the effect of empaty/sympathy received from the therapist, nor the negative impact of learning that you are in the control group and will thus not receive any treatment or attention.

To me, it is obvious that these three factors combined must be able to bring about the observed outcomes. Therefore, I suggest to re-write the conclusions as follows:

The intervention was associated with reduced sexual distress, positive outcomes in sexual functions, and increase sexual self-confidence in women with sexual distress. Considering the biological plausibility of a specific effect of Reiki, the most likely cause for the outcome are non-specific effects of the ritual.

*[Sexual distress refers to persistent, recurrent problems with sexual response, desire, orgasm or pain that distress you or strain your relationship with your partner. Yes, I had to look up the definition of that diagnosis.]

 

Current interventions for posttraumatic stress disorder (PTSD) are efficacious, yet effectiveness may be limited by adverse effects and high withdrawal rates. Acupuncture is an intervention with some positive preliminary but methodologically flawed data for PTSD.  Therefore a new study compared verum acupuncture with sham acupuncture (minimal needling) on clinical and physiological outcomes.

This was a 2-arm, parallel-group, prospective blinded randomized clinical trial hypothesizing superiority of verum to sham acupuncture. The study was conducted at a single outpatient-based site, the Tibor Rubin VA Medical Center in Long Beach, California, with recruitment from April 2018 to May 2022, followed by a 15-week treatment period. Following exclusion for characteristics that are known PTSD treatment confounds, might affect biological assessment, indicate past nonadherence or treatment resistance, or indicate risk of harm, 93 treatment-seeking combat veterans with PTSD aged 18 to 55 years were allocated to group by adaptive randomization and 71 participants completed the intervention protocols.

Verum and sham were provided as 1-hour sessions, twice weekly, and participants were given 15 weeks to complete up to 24 sessions. The primary outcome was pretreatment to posttreatment change in PTSD symptom severity on the Clinician-Administered PTSD Scale-5 (CAPS-5). The secondary outcome was pretreatment to posttreatment change in fear-conditioned extinction, assessed by fear-potentiated startle response. Outcomes were assessed at pretreatment, midtreatment, and posttreatment. General linear models comparing within- and between-group were analyzed in both intention-to-treat (ITT) and treatment-completed models.

A total of 85 male and 8 female veterans (mean [SD] age, 39.2 [8.5] years) were randomized. There was a large treatment effect of verum (Cohen d, 1.17), a moderate effect of sham (d, 0.67), and a moderate between-group effect favoring verum (mean [SD] Δ, 7.1 [11.8]; t90 = 2.87, d, 0.63; P = .005) in the intention-to-treat analysis. The effect pattern was similar in the treatment-completed analysis: verum d, 1.53; sham d, 0.86; between-group mean (SD) Δ, 7.4 (11.7); t69 = 2.64; d, 0.63; P = .01). There was a significant pretreatment to posttreatment reduction of fear-potentiated startle during extinction (ie, better fear extinction) in the verum but not the sham group and a significant correlation (r = 0.31) between symptom reduction and fear extinction. Withdrawal rates were low.

The authors concluded that the acupuncture intervention used in this study was clinically efficacious and favorably affected the psychobiology of PTSD in combat veterans. These data build on extant literature and suggest that clinical implementation of acupuncture for PTSD, along with further research about comparative efficacy, durability, and mechanisms of effects, is warranted.

I am not sure that the authors’ enthusiastic verdict is correct. Its lead author was even quoted stating that his study, which used improved controls, was needed to “definitively” support acupuncture for PTSD. He noted that “acupuncture ought to be considered a potential first-line treatment for PTSD.”

While the study is an improvement on the previous research in this area, it is by no means compelling. My main point of criticism is the nature of the sham acupuncture. Such controls are used to account for placebo effects which, of course, can be considerable in the case of acupuncture.

For this concept to work adequately, the patient and the therapist need to be blinded. In the case of acupuncture, therapist blinding is difficult (but not impossible). In this study, therepists were not blinded. Thus they could have influenced the outcome by verbal and non-verbal clues given to the patient. As acupuncturists inevitably have an interest in the positive result of their study, this effect seems inevitable to me.

More important, however, is the adequate blinding of the patient. In this study, it was attempted by using shallow needling as a sham intervention. Yet, shallow needling can easily distinguished from real acupuncture by the patient. At the very least, patients should be asked what treatment – sham or real – they thought they had received. This did not happen, and we therefore might assume that the effect of patient de-blinding – combined with the confounder described above – was sufficient to bring about the relatively small effect sizes observed by the authors.

One might argue that this does not really matter; all that counts is to alleviate the suffering of the patients, never mind by what mechanism. I think, this would be erroneous. It matters because, if acupuncture itself is ineffective (which I suggest), settling for acupuncture as a first line therapy for PTSD is in nobody’s interest and a disservice to severely suffering patients. It would inhibit meaningful research aimed at finding an optimal therapy (one that works beyond placebo) and be a waste of resources.

 

This pilot study is “delving into the potential benefits of Reiki therapy as a complementary intervention for the treatment and management of stress and anxiety”.

A total of 31 volunteers self-reporting stress, anxiety, or psychological disorders were enrolled. Health-related quality of life (HRQoL) was assessed using the 36-Item Short Form Health Survey (SF-36) Questionnaire for anxiety and depression. Pre- and post-treatment HRQoL scores were meticulously compared, and the significance of the disparities in these scores was meticulously computed.

Analysis was restricted to volunteers who completed the 3-day Reiki sessions. Statistically significant enhancements were discerned across all outcome measures, encompassing positive affect, negative affect, pain, drowsiness, tiredness, nausea, appetite, shortness of breath, anxiety, depression, and overall well-being (P<0.0001).

The authors concluded that the constancy and extensive scope of these improvements suggest that Reiki therapy may not only address specific symptoms but also contribute significantly to a predominant escalation of mental and physical health.

This study is almost comical.

Amongst all the many forms of so-called alternative medicine (SCAM), Reiki is perhaps the most ridiculous scam. It is a form of paranormal or ‘energy healing’ popularised by Japanese Mikao Usui (1865–1926). Rei means universal spirit (sometimes thought of as a supreme being) and ki is the assumed universal life energy. It is based on the assumptions of Traditional Chinese Medicine and the existence of ‘chi’, the life-force that is assumed to determine our health.

Reiki practitioners believe that, with their hands-on healing method, they can transfer ‘healing energy’ to a patient which, in turn, stimulates the self-healing properties of the body. They assume that the therapeutic effects of this technique are obtained from a ‘universal life energy’ that provides strength, harmony, and balance to the body and mind. There is no scientific basis for such notions, and reiki is therefore not plausible.

Reiki is used for a number of conditions, including the relief of stress, tension and pain. There have been several clinical trials testing its effectiveness. Those that are rigorous fail to show that the treatment is effective – and those that are dripping with bias, like the one discussed here, tend to produce false-positive results.

The present study has many flaws that are too obvious to even mention. While reading it, I asked myself the following questions:

  • How could a respectable university ever allow this pseudo-research to go ahead?
  • How could a respectable ethics committee ever permit it?
  • How could a respectable journal ever publish it?

The answers must be that, quite evidently, they are not respectable.

 

This study tested whether trigger point acupuncture (TrPA) is beneficial for office workers who have reduced job performance (presenteeism) due to chronic neck and shoulder pain (katakori).

A 4-week single-center randomized clinical trial was conducted on 20 eligible female office workers with chronic neck and shoulder pain of at least 3-month duration. The control group implemented only workplace-recommended presenteeism measures, whereas the intervention group received TrPA up to 4 times per month in addition to the presenteeism measures recommended by each workplace. The major outcome measure was the relative presenteeism score on the World Health Organization Health and Work Performance (WHO-HPQ). The secondary outcome measures were pain intensity (numerical rating scale), absolute presenteeism (WHO-HPQ), anxiety and depression (Hospital Anxiety and Depression Scale; HADS), catastrophic thoughts related to pain (Pain Catastrophizing Scale; PCS), and sleep (Athens Insomnia Scale; AIS).

All 9 cases in the intervention group and 11 cases in the control group were analyzed. TrPA up to 4 times per month reduced the intensity of neck and shoulder pain by 20% (P < .01, d = 1.65) and improved labor productivity (relative presenteeism value) by 0.25 (P < .01, d = 1.33) compared with the control group over 1 month. No significant differences were observed between the 2 groups in terms of absolute presenteeism score, HADS, PCS, or AIS.

The authors concluded that these results suggest that regular intervention with TrPA may be effective in the relative presenteeism score before and after the intervention and the degree of neck and shoulder pain over 28 days compared with the control group.

Sure, TrPA may be effective.

But is it?

I thought the trial was aimed at answering that question!

But it didn’t!

Why not?

Because, as we have discussed ad nauseam on this blog, the A+B versus B study design cannot answer it. On the contrary, it will always generate a positive result without determining whether the treatment or a nonspecific (placebo) effect caused the outcome (which, of course, is the reason why this study design is so popular in SCAM research).

In view of this, I suggest to re-formulate the conclusions as follows:

The study suggests that the researchers were ill-informed when designing it. Therefore, the findings show nothing of value.

Getting old is not nice – but think of the alternative!

I think it was Woody Allen who said something to that extent. But there is a third way, at least this is waht Tai Chi advocates want us to believe.

Utilizing a hybrid design, this study aimed to test whether both long-term and short-term Tai Chi (TC) training are associated with age-related decline in physical function in healthy older adults.

The authors first conducted cross-sectional comparisons among TC-naïve older adults (n = 60, 64.2 ± 7.7 years), TC-expert older adults (n = 27, 62.8 ± 7.6 years, 24.5 ± 12 years experience), and TC-naïve younger adults (n = 15, 28.7 ± 3.2 years) to inform long-term effects of TC training on physical function, including single leg stance time with eyes closed, grip strength, Timed Up and Go, maximum walking speed, functional reach, and vertical jump for lower-extremity power. There were significant differences among the three groups on all the six tests. For most functional tests, TC-experts performed better than age-matched TC-naïve controls and were statistically indistinguishable from young healthy adult controls. Long-term TC training was associated with higher levels of physical function in older adults, suggesting a potential preventative healthy aging effect.

In the randomized longitudinal trial, TC-naïve subjects were randomized (n = 31 to Tai Chi group, n = 29 to usual care control group) to evaluate the short-term effects of TC over 6 months on all outcomes. TC’s short-term impacts on physical function were small and not statistically significant. The impact of short-term training in healthy adults is less clear.

The authors concluded that both potential longer-term preventive effects and shorter-term restorative effects warrant further research with rigorous, adequately powered controlled clinical trials.

Even though the authors imply that their cross-sectional comparison points to a causal effect, this is clearly not true. For instance, it could easily be that people who are somehow destined to keep fit and agile are the ones who keep up Tai Chi. So, rather than being the result of Tai Chi, the proneness to fitness and agility could be the cause for doing Tai Chi.

The authors laudably were aware of these problems and therefore also did an RCT. Sadly this RCT did not yield significant findings. Essentially this means that eitherTai Chi did not work, or the study was naively inadequate, e.g. too small and too short-term.

Thus the authors finish with the usual statement that MORE RESEARCH IS NEEDED. This might be true, but is a definitive RCT likely?

I don’t think so.

A long time ago I had designed such a definitive study. It needed to be very large considering that many participants might drop out. Crucially, it also had to be long- term, i.e. years, not months.

And what happened to my study?

I never managed to get it funded, mainly because the costs would have been astronomical.

Supportive care is often assumed to be beneficial in managing the anxiety symptoms common in patients in sterile hematology unit. The authors of this study hypothesize that personal massage can help the patient, particularly in this isolated setting where physical contact is extremely limited.

The main objective of this study therefore was to show that anxiety could be reduced after a touch-massage performed by a nurse trained in this therapy.

A single-center, randomized, unblinded controlled study in the sterile hematology unit of a French university hospital, validated by an ethics committee. The patients, aged between 18 and 65 years old, and suffering from a serious and progressive hematological pathology, were hospitalized in sterile hematology unit for a minimum of three weeks. They were randomized into either a group receiving 15-minute touch-massage sessions or a control group receiving an equivalent amount of quiet time once a week for three weeks.

In the treated group, anxiety was assessed before and after each touch-massage session, using the State-Trait Anxiety Inventory questionnaire with subscale state (STAI-State). In the control group, anxiety was assessed before and after a 15-minute quiet period. For each patient, the difference in the STAI-State score before and after each session (or period) was calculated, the primary endpoint was based on the average of these three differences. Each patient completed the Rosenberg Self-Esteem Questionnaire before the first session and after the last session.

Sixty-two patients were randomized. Touch-massage significantly decreased patient anxiety: a mean decrease in STAI-State scale score of 10.6 [7.65-13.54] was obtained for the massage group (p ≤ 0.001) compared with the control group. The improvement in self-esteem score was not significant.

The authors concluded that this study provides convincing evidence for integrating touch-massage in the treatment of patients in sterile hematology unit.

I find this conclusion almost touching (pun intended). The wishful thinking of the amateur researchers is almost palpable.

Yes, I mean AMATEUR, despite the fact that, embarrassingly, the authors are affiliated with prestigeous institutions:

  • 1Nantes Université, CHU Nantes, Service Interdisciplinaire Douleur, Soins Palliatifs et de Support, Médecine intégrative, UIC 22, Nantes, F-44000, France.
  • 2Université Paris Est, EA4391 Therapeutic and Nervous Excitability, Creteil, F-93000, France.
  • 3Nantes Université, CHU Nantes, Hematology Department, Nantes, F-44000, France.
  • 4Nantes Université, CHU Nantes, CRCI2NA – INSERM UMR1307, CNRS UMR 6075, Equipe 12, Nantes, F-44000, France.
  • 5Institut Curie, Paris, France.
  • 6Université Paris Versailles Saint-Quentin, Versailles, France.
  • 7Nantes Université, CHU Nantes, Direction de la Recherche et l’Innovation, Coordination Générale des Soins, Nantes, F-44000, France.
  • 8Methodology and Biostatistics Unit, DRCI CHU Nantes CHD Vendée, La Roche Sur Yon, F-85000, France.
  • 9Nantes Université, CHU Nantes, Service Interdisciplinaire Douleur, Soins Palliatifs et de Support, Médecine intégrative, UIC 22, Nantes, F-44000, France. [email protected].

So, why do I feel that they must be amateurs?

  • Because, if they were not amateurs, they would know that a clinical trial should not aim to show something, but to test something.
  • Also, if they were not amateurs, they would know that perhaps the touch-massage itself had nothing to do with the outcome, but that the attention, sympathy and empathy of a therapist or a placebo effect can generate the observed effect.
  • Lastly, if they were not amateurs, they would not speak of convincing evidence based on a single, small, and flawed study.
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