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

methodology

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Qigong can be described as a mind-body-spirit practice that improves one’s mental and physical health by integrating posture, movement, breathing technique, self-massage, sound, and focused intent. But does it really improve health?

The purpose of this review was to evaluate the effectiveness of Qigong in improving the quality of life and relieving fatigue, sleep disturbance, and cancer-related emotional disturbances (distress, depression, and anxiety) in women with breast cancer.

The PubMed, Cochrane Central Register of Controlled Trials, Web of Science, Sinomed, Wanfang, VIP, and China National Knowledge Infrastructure databases were searched from their inceptions to March 2020 for controlled clinical trials. Two reviewers selected relevant trials that assessed the benefit of Qigong for breast cancer patients independently. A methodological quality assessment was conducted according to the criteria of the 12 Cochrane Back Review Group for risk of bias independently. A meta-analysis was performed using Review Manager 5.3.

A total of 17 trials were found in which 1236 cases were enrolled. The quality of the included trials was generally low, as only 5 of them were rated high quality. 14 studies were conducted in China. The types of qigong included Baduanjin Qigong (9 trials), Chan-Chuang Qigong (1 trial), Goulin New Qigong (2 Trials), Tai Chi Qigong (2 Trials), and Kuala Lumpur Qigong (1 trial). The course of qigong ranged from 21 days to more than 6 months. Four trials compared qigong to no treatment, one sham Qigong, seven compared to other types of exercise, and 6 to usual care.

The results showed significant positive effects of Qigong on quality of life (n = 950, standardized mean difference (SMD), 0.65, 95 % confidence interval (CI) 0.23–1.08, P =  0.002). Depression (n = 540, SMD = −0.32, 95 % CI −0.59 to −0.04, P =  0.02) and anxiety (n = 439, SMD = −0.71, 95 % CI −1.32 to −0.10, P =  0.02) were also significantly relieved in the Qigong group. There was no significant benefit on fatigue (n = 401, SMD = −0.32, 95 % CI  0.71 to 0.07, P = 0.11) or sleep disturbance relief compared to that observed in the control group (n = 298, SMD = −0.11, 95 % CI  0.74 to 0.52, P = 0.73).

The authors concluded that this review shows that Qigong is beneficial for improving quality of life and relieving depression and anxiety; thus, Qigong should be encouraged in women with breast cancer.

No, this review does not show that Qigong is beneficial for improving quality of life and relieving depression and anxiety!

Why?

  1. Most primary studies were of very poor quality.
  2. Most were from China, and we know (and have often discussed) that such trials are most unreliable.
  3. No trial even attempted to control for placebo effects.

A better conclusion would therefore be something like this:

Even though most trials conclude positively, the value of Qigong can, for a range of reasons, not be determined on the basis of the evidence available to date.

On 7/10/2020, I discussed a study suggesting that homeopathy improves the quality of life and survival of cancer patients. Now, these data have been carefully scrutinized by a group of members of the „INH“ and „Initiative für Wissenschaftliche Medizin“.

By guest bloggers Norbert Aust and Viktor Weisshäupl

Abstract

The first impression of the results of the study on the adjunctive homeopathic treatment of patients with non-small cell lung cancer (NSCLC) is that of a seemingly rigorous trial with valid results. But a more thorough review yields different insights:

  • The methods and definitions were pre-determined in a protocol and seem to have been maintained up to the end. But the date given in the document pointing at some point in time before enrollment began is wrong and misleading: This protocol was first published by uploading it to the register only two months after data assessment was completed with outcomes presumably available.
  • The data initially saved to the register are not in agreement with the information given in the published paper: important definitions were subjected to considerable modifications while the study was underway. None of these modifications are mentioned in the paper, neither a rationale nor a comment of their impact on the results was provided.
  • Some of the modifications with presumably heavy impact on the results were introduced with the upload of the protocol only, that is two months after data collection was completed. These were (a) a massive extension of the exclusion criteria: the number increased from 1 during initial registration to 20 in the final paper. and (b) an equally massive reduction of the follow-up time for the primary endpoint from two years to 18 weeks.
  • The paper discloses no reason why the additional exclusion criteria were introduced. Their selection seems arbitrary without any apparent necessity arising from the trial itself.
  • The patients who did not meet the added criteria and were thus excluded are not mentioned in the publication. The CONSORT flow chart does not give information either of their number or of the point in time when they were excluded.
  • The survival curves of the placebo and verum groups show some aspects that arise if the inter-group difference was due to the exclusion of unfavorable data.
  • It is hard to imagine that, in this trial, the homeopathic preparations had strong effects on the patients’ health, while other rigorous studies or systematic reviews failed to notice such effects.

Altogether, it seems much more plausible to assume that the positive results were achieved by post hoc data manipulation, namely by omitting patients with unfavorable outcomes, than by rigorous and valid science. A retraction of the paper seems the only appropriate measure to avoid misleading the public. 

Introduction

Due to its outstanding results, the study about adjunct homeopathic treatment of non-small cell lung cancer patients was met among homeopaths with enthusiasm. However, in this article, we will show that the enthusiasm is unjustified because the results may not be based on a rigorous trial meeting established scientific criteria. Crucial definitions were modified, while the study was underway or even after data collection was completed. It stands to reason that this introduced bias in favor of homeopathy.

For this analysis, we considered the following sources of information :

  • the text of the published paper (link)
  • the data that were uploaded during registration (link)
  • the history of changes of the registered data (link)
  • the study protocol included in the registration (link)

As all of this information is readily available on the internet, it is easy to double-check our findings and verify our statements. We also submitted a letter to the editor of the Oncologist, the journal where the paper was published which has not yet been published (status 06-06-2021).

The study

At first glance, the study meets the requirements for reliable evidence.

  • There is a study protocol dated January 11, 2011, well before recruiting of participants started. It provides definitions that were used until the end.
  • The study was registered at ClinicalTrials.gov before recruiting started.
  • The methods of randomization and blinding are suitable to meet the requirements for a low risk of bias rating.
  • The presentation of the paper follows the principles set out in the CONSORT-Statement.
  • The paper was published in a peer-reviewed journal of some reputation.

The study yielded formidable results in favor of homeopathy: In the group that received the adjunctive homeopathic treatment, the quality of life improved continuously throughout the follow-up time, while the patients in the placebo group deteriorated. In addition, the median survival time was only about two-thirds compared to the patients in the homeopathy group. However, the impression of a valid study does not stand up to closer scrutiny when the history of changes is taken into account.

Changes in study parameters 

Between the initial registration and data upload in January 2012 (Link), shortly before recruiting started in February 2012, and the publication in October 2020, multiple changes in essential study parameters occurred:

Registration January 2012 Publication October 2020
Number of participants 600 150
Number of study arms 2 3
Number of exclusion criteria 1 20
Follow-up time for Quality of life 104 weeks (*) 18 weeks
Number of cancer types 3 1
(*) Derived from “Time Frame: 7 Years” minus the recruitment period of 5 years.

Note the drastic reduction in the follow-up time for quality of life by more than 80 % which was defined as the primary endpoint. Furthermore, note the substantial increase in the number of exclusion criteria. Both issues will be discussed in more detail below.

In contrast to the requirements for a rigorous and valid trial, these modifications are not mentioned in the published paper, and no rationale is given as to why they became necessary. As a consequence, the authors do not discuss the possible impact these modifications may have had on the results.

The study protocol 

A study protocol is available in the registration database. It was first uploaded on September 18, 2019, about two months after the end of data collection in July 2019 (Link). The document itself is dated January 11, 2011, which would place it about a year before the study was registered. However, this date is obviously wrong: there are substantial discrepancies between the parameters specified in the protocol and the data provided one year later during initial registration:

Protocol, allegedly January 2011 Registration January 2012
Number of participants 300 600
Number of study arms 3 2
Number of exclusion criteria 9 1
Follow-up time for Quality of life 18 weeks 104 weeks (*)
Number of cancer types 1 3
(*) Derived from “Time Frame: 7 Years” minus the recruitment period of 5 years.

We see no sensible explanation why the parameters given in the study protocol allegedly compiled in January 2011 are in line with the publication nine years later, but not with the registration only one year after the protocol was compiled. The only sensible conclusion seems to be that this protocol was not completed on the date indicated, but at a much later point in time, maybe just shortly before its upload (September 2019). This impression is corroborated by the information presented in the document that was not available on the date given: On page 10 the software package used in data analysis is referenced as “IBM SPSS statistics 25.0” while, at the beginning of 2011, when the protocol was allegedly compiled, the current version number of this package was 19 only.

A second clue: Also on page 10 there is a reference “(EORTC-QLQ-C30 remaining dimensions; SF-36; subjective well-being)25.” with the number 25 indicating some reference. And some references that is, but not in the protocol – this does not have any references – but in the published paper, where the 25 indicates a paper on the SF-36 questionnaire. So it stands to reason that the number in the protocol originates from some messed up copy and paste procedure from the draft of the paper. Which would indicate that the paper and the protocol were at least partially developed in parallel.

It seems therefore reasonable to assume, that the protocol was finished only shortly before it being uploaded in September 2019, that is two months after data collection was completed.

However, the obviously inaccurate date given in the protocol supports the impression that the study parameters were set a year before the study began and were consistently maintained during the course of the trial, which is not the case, as the above tables show.

Change in exclusion criteria 

The initial registration data list pregnancy as the only exclusion criterion. But with the upload of the protocol, which took place two months after data collection was completed, the number of exclusion criteria was increased to nine, only to be enlarged once again in the final publication to the final number of twenty. It is beyond any doubt that at least the final increase of eleven criteria took place after the data collected from the patients were available. But all this is neither disclosed in the final paper nor is there any rationale given for this action.

The patients excluded by the additional criteria never appear anywhere, they are not included in the CONSORT-flow-chart, Fig 3 in the study. It is obvious that some patients were excluded: What was the reason to define such an abundance of criteria, if they were not to be applied? As a consequence, the CONSORT diagram seems to be incomplete which would be in violation of the CONSORT statement.

Thus, an unknown number of patients seems to have been excluded from the study by criteria defined at a time after data collection was completed with outcomes available. After all, eleven of the exclusion criteria were established even after the protocol had been uploaded, at least those were established well after the patients’ results were available.

This raises the question of why these exclusion criteria were introduced. One would assume that an intervention to treat stage III and stage IV lung cancer patients should be effective under the conditions that are usually present in such patients. One would expect that patients somewhat advanced in age, like in this study, usually suffer from some health problems, regardless of their cancer condition. What is the sense of excluding patients with hematological, hepatic, or renal pathology, with coronary heart disease or rheumatism? Homeopathy is claimed to be able to treat comorbidities based on the assessment of symptoms independent of what disease they belong to. And this apparently was the idea at the start of the trial where only pregnancy was specified as an exclusion criterion, while it was understood that elderly patients to be enrolled in the study would suffer from some additional medical problems.

On the other hand, not all health conditions that are associated with advanced age were excluded. Diabetes, hypertension, gastrointestinal diseases, or COPD were no reason to exclude any patient from participation. Only very few of the criteria are somewhat self-explanatory as to why they were defined as exclusion criteria, e.g. if a patient was unwilling to give her informed consent.

Altogether, the assumption seems reasonable that more patients had participated in the trial than accounted for in the publication, and that an unknown number of them were excluded according to criteria that were not present until after data collection was completed. If so, a substantial bias was introduced.

Median survival time

Here, we will focus on the comparison between the homeopathy and placebo groups and leave aside the third group not receiving any additional treatment at all.

If the favorable result in survival really was established by dropping unfavorable data, this might be recognized in some characteristics of the survival curves. Therefore, we modeled this situation starting with two random distributions somewhat tweaked to resemble the typical shape of natural survival functions.

This graph shows the two distributions (n = 80) defined in the range of 0 to 200 as thin lines. Both are very similar to each other with median survival at 27 weeks. If 15 of the 20 patients with the shortest survival are dropped from the thin blue line this would result in the solid blue line (“Hom”). If, on the other hand, 15 out of 20 patients with the longest survival are dropped from the other distribution this would yield the solid red line (“Plac”).

The new functions show some characteristic properties:

  • In the red line, median survival drops by 8 weeks to 19 weeks.
  • In the blue line median survival rises by 12 Weeks to 39 weeks.
  • The difference between the two functions arises from of the first 12 weeks alone. With the blue line, 8 people died, with the red line 23 people died during the first 12 weeks. After week 12 up to week 80, the same number of fatalities occur in both groups (blue: 36, red: 37).

After week 80, the two functions start to converge, which is due to the fact that at some future point all the patients of both groups will be dead. The survival functions that are reported in the study show the same characteristics.

Assuming that homeopathy did not have any effect, both groups should show more or less identical survival functions. In the paper 10.1 months = 303 days is cited from literature as to be expected under conventional care, maybe with some margin to the better because the data that yielded this value of 10.1 months were more than six years old at the time of the trial. The survival functions allegedly found in the trial show:

  • Median survival time with the placebo group is reduced by 46 days compared to conventional care alone.
  • Median survival time with the homeopathy group is increased by 132 days compared to conventional care alone.
  • The advantage of homeopathy arises within the first 9 weeks alone, where only two patients died (out of 51) in the homeopathy group compared to 11 (out of 47) in the placebo group. After this initial phase, the groups developed in parallel: By the end of the two-year follow-up time an additional 26 patients died with homeopathy, and about the same, namely 25 patients died with placebo.

The inevitable convergence of both functions apparently started outside the two-year follow-up. In other words, the survival functions given in the study for placebo and homeopathy treatments show characteristics that match what you would be expected, if two very similar functions were manipulated by dropping unwanted results, i.e. “good” survival data from placebo and “bad” survival data from homeopathy functions. After week 9, the two functions develop parallel to each other, indicating a lack of effect of homeopathy even though the treatment continued until the death of the patient or the end of the study. However, with ongoing effective treatment, the functions should continue to diverge. It seems implausible that homeopathy should be effective on a short time basis only, with a sudden complete loss of effectiveness later on.

Reduction of observation time

Quality of life was defined as the primary endpoint. On initial registration, it was specified that patients should be observed for the entire seven-year duration of the study which, allowing for the recruitment period of five years, results in a follow-up time of two years or 104 weeks for each individual patient. According to the information provided in the study, this was indeed done: “Patients were followed up every nine weeks until death” (or until the end of the study, of course), and questionnaires were completed to determine the quality of life.

The reduction of follow-up time from 104 to 18 weeks was first introduced when the protocol was uploaded. So it is obvious that this substantial reduction occurred after data collection was completed and that data from more than 80 % of the originally defined follow-up were omitted.

Incomplete outcome reporting, especially when a larger scope was defined at the beginning of the study, is considered a source of substantial bias and a major shortcoming in clinical trials: Maybe patients initially experienced an improvement in their quality of life due to whatever effect – but what were the results after this initial phase? Why were they omitted? Perhaps because they got worse than in the placebo group? The long-term development would have been a vital aspect for the evaluation of efficacy – and the study originally was designed to evaluate such long-term effects. Yet, the authors’ conclusions on the quality of life – notably: the primary outcome criterion – are based on less than 20 % of the follow-up in which a positive effect may have occurred due to bias or by chance. To extrapolate from this short time to the total period is not justified and may be misleading. A detailed review of the quality of life results is meaningless: they do not disclose any long-term effects and they are subject to bias caused by the post hoc exclusion of patients anyway.

Study results

The overall evidence on the effectiveness of homeopathy is not encouraging. The quintessence of all systematic reviews that have looked at homeopathy as a whole is that some marginal effect may be found, if all studies are included in the review, regardless of their quality. But this result is questionable due to the generally low quality of the primary studies (Link, in German). However, when quality is taken into account, the systematic reviews do not produce robust evidence for any positive effect beyond placebo. In addition, no review could identify a single condition in which homeopathy is of well-established therapeutic benefit.

This study on NSCLC contradicts the long-established and often-confirmed evidence. During the follow-up time for the patients who actually received the prescribed homeopathic preparations, the quality of life improved steadily in all subscales – even down to the patients’ financial situation – whereas the opposite was observed in the placebo patients. In addition, the mean survival time was about two-thirds longer for the homeopathy patients than for the placebo group.

After 200 years of clinical research into homeopathy, it seems unlikely that such a powerful effect of homeopathy should not have been noticed before. Another scenario seems to be much more plausible:

  • The survival times of the placebo group were worse than the data from the literature. This could be due to the fact that patients with relatively good outcomes were excluded by the introduction of additional exclusion criteria.
  • The survival times of the homeopathy group were considerably better than expected. This could also be due to the additional exclusion criteria, in that patients with poor outcomes were excluded retrospectively.
  • The long time frame where the survival functions run in parallel from week 9 onwards until the end of the two years observation period indicates the lack of effect of the homeopathic treatment. The advantage occurring in the first nine weeks alone seems to be the result of unwanted data being dropped.
  • In the case of quality of life (after all, not a “hard” criterion, but based on information from the patients ), the advantage in survival would have initially created a positive effect for the homeopathy group. Then, reporting was discontinued, once the initial positive effects presumably caused by the selective omission of patients had ended.

In conclusion, it seems likely that the substantial modifications of crucial study parameters that occurred after the study had been started and results had become available biased the results in favor of homeopathy. Therefore, this study does not meet strict scientific standards that were established to exclude any confounding factors or biases. If our analysis is correct, the results of this study are invalid, and the authors’ conclusions are not justified. Retraction of this study seems to be appropriate.

Reference

[1] Frass M, Lechleitner P, Gründling C et al. Homeopathic Treatment as an Add-On Therapy May Improve Quality of Life and Prolong Survival in Patients with Non-Small Cell Lung Cancer: A Prospective, Randomized, Placebo-Controlled, Double-Blind, Three-Arm, Multicenter Study. The Oncologist 2020;25:e1930–e1955 https://theoncologist.onlinelibrary.wiley.com/doi/epdf/10.1002/onco.13548

This systematic review and meta-analyses explored the strength of evidence on efficacy and safety of Ayurvedic herbs for hypercholesterolemia. Methods: Literature searches were conducted and all randomized controlled trials on individuals with hypercholesterolemia using Ayurvedic herbs (alone or in combination) with an exposure period of ≥ 3 weeks were included. The primary outcomes were total cholesterol levels, adverse events, and other cardiovascular events.

A total of 32 studies with 1386 participants were found. They tested three Ayurvedic herbs:

  • Allium sativum (garlic),
  • Commiphora mukul (Guggulu),
  • Nigella sativa (black cumin).

The average duration of intervention was 12 weeks. The meta-analysis of the trials showed that

  • Guggulu reduced total cholesterol and low-density lipoprotein levels by 16.78 mg/dL (95% C.I. 13.96 to 2.61; p-value = 0.02) and 18.78 mg/dL (95% C.I. 34.07 to 3.48; p = 0.02), respectively.
  • Garlic reduced LDL-C by 10.37 mg/dL (95% C.I. -17.58 to -3.16; p-value = 0.005).
  • Black cumin lowered total cholesterol by 9.28 mg/dL (95% C.I. -17.36, to -1.19, p-value = 0.02).

Reported adverse side effects were minimal.

The authors concluded that there is moderate to high level of evidence from randomized controlled trials that the Ayurvedic herbs guggulu, garlic, and black cumin are moderately effective for reducing hypercholesterolemia. In addition, minimal evidence was found for any side effects associated with these herbs, positioning them as safe adjuvants to conventional treatments.

For the following reasons, I fail to see how these conclusions can be justified:

  • Too many of the included studies are of poor quality.
  • Only for garlic are there a sufficient number of trials for attempting to reach a generalizable conclusion.
  • Giving garlic to patients with hypercholesterolemia is hardy Ayurvedic medicine.
  • Even the effect of the best-tested herbal remedy, garlic, is not as large as the effects of conventional lipid-lowering drugs.
  • Conclusions about the safety of medicines purely on the basis of RCTs are unreliable.
  • The affiliations of the authors include the College of Integrative Medicine, Maharishi International University, Fairfield, USA, the School of Science of Consciousness, Maharishi University of Information Technology, Noida, India, and the Maharishi International University, Fairfield.

I have not often seen a paper reporting a small case series with such an impressively long list of authors from so many different institutions:

  • Hospital of Lienz, Lienz, Austria.
  • WissHom: Scientific Society for Homeopathy, Koethen, Germany; Umbrella Organization for Medical Holistic Medicine, Vienna, Austria; Vienna International Academy for Holistic Medicine (GAMED), Otto Wagner Hospital Vienna, Austria; Professor Emeritus, Medical University of Vienna, Department of Medicine I, Vienna, Austria. Electronic address: office@ordination-frass.at.
  • Resident Specialist in Hygiene, Medical Microbiology and Infectious Diseases, Außervillgraten, Austria.
  • St Mary’s University, London, UK.
  • Umbrella Organization for Medical Holistic Medicine, Vienna, Austria.
  • Shaare Zedek Medical Center, The Center for Integrative Complementary Medicine, Jerusalem, Israel.
  • Apotheke Zum Weißen Engel – Homeocur, Retz, Austria.
  • Reeshabh Homeo Consultancy, Nagpur, India.
  • Umbrella Organization for Medical Holistic Medicine, Vienna, Austria; Vienna International Academy for Holistic Medicine (GAMED), Otto Wagner Hospital Vienna, Austria; Chair of Complementary Medicine, Medical Faculty, Sigmund Freud University Vienna, Austria; KLITM: Karl Landsteiner Institute for Traditional Medicine and Medical Anthropology, Vienna, Austria.
  • WissHom: Scientific Society for Homeopathy, Koethen, Germany.

In fact, there are 12 authors reporting about 13 patients! But that might be trivial – so, let’s look at the paper itself. The aim of this study was to describe the effect of adjunctive individualized homeopathic treatment delivered to hospitalized patients with confirmed symptomatic SARS-CoV-2 infection.

Thirteen patients with COVID-19 were admitted. The mean age was 73.4 ± 15.0 (SD) years. The treating homeopathic doctor was instructed by the hospital on March 27, 2020, to adjunctively treat all inpatient COVID-19 patients homeopathically. The high potency homeopathic medicinal products were administered orally. Five globules were administered sublingually where they dissolved, three times a day. In ventilated patients in the ICU, medication was administered as a sip from a water beaker or 1 ml three times a day using a syringe. All ventilated patients exhibited dry cough resulting in respiratory failure. They were given Influenzinum, as were the patients at the general inpatient ward.

Twelve patients (92.3%) were speedily discharged without relevant sequelae after 14.4 ± 8.9 days. A single patient admitted in an advanced stage of septic disease died in the hospital. A time-dependent improvement of relevant clinical symptoms was observed in the 12 surviving patients. Six (46.2%) were critically ill and treated in the intensive care unit (ICU). The mean stay at the ICU of the 5 surviving patients was 18.8 ± 6.8 days. In six patients (46.2%) gastrointestinal disorders accompanied COVID-19.

The authors conclude that adjunctive homeopathic treatment may be helpful to treat patients with confirmed COVID-19 even in high-risk patients especially since there is no conventional treatment of COVID-19 available at present.

In the discussion section of the paper, the authors state this: “Given the extreme variability of pathology and clinical manifestations, a single universal preventive homeopathic medicinal product does not seem feasible. Yet homeopathy may have a relevant role to play precisely because of the number and diversity of its homeopathic medicinal products which can be matched with the diversity of the presentations. Patients with mild forms of disease can use homeopathic medicinal products at home using our simple algorithm. As this Case series suggests, adjunctive homeopathic treatment can play a valuable role in more serious presentations. For future pandemics, homeopathy agencies should be prepared by establishing rapid-response teams and efficacious lines of communication.”

There is nothing in this paper that would lead me to conclude that the homeopathic remedies had a positive effect on the natural history of the disease. All this article actually does do is this: it provides a near-perfect insight into the delusional megalomania of some homeopaths. These people are even more dangerous than I had feared.

The aim of this “multicenter cross-sectional study” was to analyze a cohort of breast (BC) and gynecological cancers (GC) patients regarding their interest in, perception of, and demand for integrative therapeutic health approaches.

The BC and GC patients were surveyed at their first integrative clinic visit using validated standardized questionnaires. Treatment goals and potential differences between the two groups were evaluated.

A total of 340 patients (272 BC, 68 GC) participated in the study. The overall interest in IM was 95.3% and correlated with older age, recent chemotherapy, and higher education. A total of 89.4% were using integrative methods at the time of enrolment, primarily exercise therapy (57.5%), and vitamin supplementation (51.4%). The major short-term goal of the BC patients was a side-effects reduction of conventional therapy (70.4%); the major long-term goal was the delay of a potential tumor progression (69.3%). In the GC group, major short-term and long-term goals were slowing tumor progression (73.1% and 79.1%) and prolonging survival (70.1% and 80.6%). GC patients were significantly more impaired by the side-effects of conventional treatment than BC patients [pain (p = 0.006), obstipation (< 0.005)].

The authors concluded that these data demonstrate a high overall interest in and use of IM in BC and GC patients. This supports the need for specialized IM counseling and the implementation of integrative treatments into conventional oncological treatment regimes in both patient groups. Primary tumor site, cancer diagnosis, treatment phase, and side effects had a relevant impact on the demand for IM in our study population.

This paper is, in my mind, an excellent example of pseudo-research:

  1. The ‘study’ turns out to be little more than a survey.
  2. The sample is small and not representative; therefore the findings cannot be generalized and are meaningless.
  3. The patients surveyed are those who decided to attend clinics of integrative medicine.
  4. These patients had used alternative therapies before and are evidently in favor of alternative medicine.
  5. The most frequently used alternative therapies (exercise, vitamins, trace elements, massage, lymph drainage) are arguably conventional treatments in Germany where the survey was conducted.

I have repeatedly commented on the plethora of useless surveys in so-called alternative medicine (SCAM). But this one might beat them all in its uselessness. The fact that close to 100% of patients attending clinics of integrative medicine are interested in SCAM and use some form of SCAM says it all, I think.

Why do people waste their time on such pseudo-research?

The best answer to this question is that it can be used for promotion. I found the paper by reading what seems to be a press release entitled: “Eine Studie bestätigt Patientenwunsch nach naturheilkundlicher Unterstützung”. This translates into “a study confirms the wish of patients for naturopathic support”. Needless to explain that the survey did not even remotely show this to be true.

What will they think of next?

I suggest a survey run in a BC clinic which amazingly discovers that nearly 100% of all patients are female.

 

 

A new study evaluated the effects of yoga and eurythmy therapy compared to conventional physiotherapy exercises in patients with chronic low back pain.

In this three-armed, multicentre, randomized trial, patients with chronic low back pain were treated for 8 weeks in group sessions (75 minutes once per week). They received either:

  1. Yoga exercises
  2. Eurythmy
  3. Physiotherapy

The primary outcome was patients’ physical disability (measured by RMDQ) from baseline to week 8. Secondary outcome variables were pain intensity and pain-related bothersomeness (VAS), health-related quality of life (SF-12), and life satisfaction (BMLSS). Outcomes were assessed at baseline, after the intervention at 8 weeks, and at a 16-week follow-up. Data of 274 participants were used for statistical analyses.

The results showed no significant differences between the three groups for the primary and secondary outcomes. In all groups, RMDQ decreased comparably at 8 weeks but did not reach clinical meaningfulness. Pain intensity and pain-related bothersomeness decreased, while the quality of life increased in all 3 groups. In explorative general linear models for the SF-12’s mental health component, participants in the eurythmy arm benefitted significantly more compared to physiotherapy and yoga. Furthermore, within-group analyses showed improvements of SF-12 mental score for yoga and eurythmy therapy only. All interventions were safe.

Everyone knows what physiotherapy or yoga is, I suppose. But what is eurythmy?

It is an exercise therapy that is part of anthroposophic medicine. It consists of a set of specific movements that were developed by Rudolf Steiner (1861–1925), the inventor of anthroposophic medicine, in conjunction with Marie von Sievers (1867-1948), his second wife.

Steiner stated in 1923 that eurythmy has grown out of the soil of the Anthroposophical Movement, and the history of its origin makes it almost appear to be a gift of the forces of destiny. Steiner also wrote that it is the task of the Anthroposophical Movement to reveal to our present age that spiritual impulse that is suited to it. He claimed that, within the Anthroposophical Movement, there is a firm conviction that a spiritual impulse of this kind must enter once more into human evolution. And this spiritual impulse must perforce, among its other means of expression, embody itself in a new form of art. It will increasingly be realized that this particular form of art has been given to the world in Eurythmy.

Consumers learning eurythmy are taught exercises that allegedly integrate cognitive, emotional, and volitional elements. Eurythmy exercises are based on speech and direct the patient’s attention to their own perceived intentionality. Proponents of Eurythmy believe that, through this treatment, a connection between internal and external activity can be experienced. They also make many diffuse health claims for this therapy ranging from stress management to pain control.

There is hardly any reliable evidence for eurythmy, and therefore the present study is exceptional and noteworthy. One review concluded that “eurythmy seems to be a beneficial add-on in a therapeutic context that can improve the health conditions of affected persons. More methodologically sound studies are needed to substantiate this positive impression.” This positive conclusion is, however, of doubtful validity. The authors of the review are from an anthroposophical university in Germany. They included studies in their review that were methodologically too weak to allow any conclusions.

So, does the new study provide the reliable evidence that was so far missing? I am afraid not!

The study compared three different exercise therapies. Its results imply that all three were roughly equal. Yet, we cannot tell whether they were equally effective or equally ineffective. The trial was essentially an equivalence study, and I suspect that much larger sample sizes would have been required in order to identify any true differences if they at all exist. Lastly, the study (like the above-mentioned review) was conducted by proponents of anthroposophical medicine affiliated with institutions of anthroposophical medicine. I fear that more independent research would be needed to convince me of the value of eurythmy.

Neuropathic pain is difficult to treat. Luckily, we have acupuncture! Acupuncturists leave us in no doubt that their needles are the solution. But are they correct or perhaps victims of wishful thinking?

This review was aimed at determining the proportion of patients with neuropathic pain who achieve a clinically meaningful improvement in their pain with the use of different pharmacologic and nonpharmacologic treatments.

Randomized controlled trials were included that reported a responder analysis of adults with neuropathic pain-specifically diabetic neuropathy, postherpetic neuralgia, or trigeminal neuralgia-treated with any of the following 8 treatments: exercise, acupuncture, serotonin-norepinephrine reuptake inhibitors (SNRIs), tricyclic antidepressants (TCAs), topical rubefacients, opioids, anticonvulsant medications, and topical lidocaine.

A total of 67 randomized controlled trials were included. There was moderate certainty of evidence that anticonvulsant medications (risk ratio of 1.54; 95% CI 1.45 to 1.63; number needed to treat [NNT] of 7) and SNRIs (risk ratio of 1.45; 95% CI 1.33 to 1.59; NNT = 7) might provide a clinically meaningful benefit to patients with neuropathic pain. There was low certainty of evidence for a clinically meaningful benefit for rubefacients (ie, capsaicin; NNT = 7) and opioids (NNT = 8), and very low certainty of evidence for TCAs. Very low-quality evidence demonstrated that acupuncture was ineffective. All drug classes, except TCAs, had a greater likelihood of deriving a clinically meaningful benefit than having withdrawals due to adverse events (number needed to harm between 12 and 15). No trials met the inclusion criteria for exercise or lidocaine, nor were any trials identified for trigeminal neuralgia.

The authors concluded that there is moderate certainty of evidence that anticonvulsant medications and SNRIs provide a clinically meaningful reduction in pain in those with neuropathic pain, with lower certainty of evidence for rubefacients and opioids, and very low certainty of evidence for TCAs. Owing to low-quality evidence for many interventions, future high-quality trials that report responder analyses will be important to strengthen understanding of the relative benefits and harms of treatments in patients with neuropathic pain.

This review was published in a respected mainstream journal and conducted by a multidisciplinary team with the following titles and affiliations:

  • Associate Professor in the College of Pharmacy at the University of Manitoba in Winnipeg.
  • Pharmacist in Edmonton, Alta, and Clinical Evidence Expert for the College of Family Physicians of Canada.
  • Family physician and Assistant Professor at the University of Alberta.
  • Family physician and Associate Professor in the Department of Family Medicine at the University of Alberta.
  • Pharmacist, Clinical Evidence Expert Lead for the College of Family Physicians of Canada, and Associate Clinical Professor in the Department of Family Medicine at the University of Alberta.
  • Pharmacist in Edmonton and Clinical Evidence Expert for the College of Family Physicians of Canada.
  • Pharmacist and Clinical Evidence Expert at the College of Family Physicians of Canada.
  • Family physician, Director of Programs and Practice Support at the College of Family Physicians of Canada, and Adjunct Professor in the Department of Family Medicine at the University of Alberta.
  • Professor in the Faculty of Pharmaceutical Sciences at the University of British Columbia in Vancouver.
  • Pharmacist at the CIUSSS du Nord-de-l’lle-de-Montréal and Clinical Associate Professor in the Faculty of Pharmacy at the University of Montreal in Quebec.
  • Care of the elderly physician and Assistant Professor in the Department of Family Medicine at the University of Alberta.
  • Family physician and Professor in the Department of Family Medicine at the University of Alberta.
  • Assistant Professor in the Department of Family Medicine at Queen’s University in Kingston, Ont.
  • Research assistant at the University of Alberta.
  • Medical student at the University of Alberta.
  • Nurse in Edmonton and Clinical Evidence Expert for the College of Family Physicians of Canada.

As far as I can see, the review is of sound methodology, it minimizes bias, and its conclusions are therefore trustworthy. They suggest that acupuncture is not effective for neuropathic pain.

But how can this be? Do the authors not know about all the positive evidence on acupuncture? A quick search found positive recent reviews of acupuncture for all of the three indications in question:

  1. Diabetic neuropathy: Acupuncture alone and vitamin B combined with acupuncture are more effective in treating DPN compared to vitamin B.
  2. Herpes zoster: Acupuncture may be effective for patients with HZ.
  3. Trigeminal neuralgia: Acupuncture appears more effective than pharmacotherapy or surgery.

How can we explain this obvious contradiction?

Which result should we trust?

Do we believe pro-acupuncture researchers who published their papers in pro-acupuncture journals, or do we believe the findings of researchers who could not care less whether their work proves or disproves the effectiveness of acupuncture?

I think that these papers offer an exemplary opportunity for us to study how powerful the biases of researchers can be. They also remind us that, in the realm of so-called alternative medicine (SCAM), we should always be very cautious and not accept every conclusion that has been published in supposedly peer-reviewed medical journals.

The purpose of this study was to describe changes in opioid-therapy prescription rates after a family medicine practice included on-site chiropractic services. It was designed as a retrospective analysis of opioid prescription data. The database included opioid prescriptions written for patients seeking care at the family medicine practice from April 2015 to September 2018. In June 2016, the practice reviewed and changed its opioid medication practices. In April 2017, the practice included on-site chiropractic services. Opiod-therapy use was defined as the average rate of opioid prescriptions overall medical providers at the practice.

There was a significant decrease of 22% in the average monthly rate of opioid prescriptions after the inclusion of chiropractic services (F1,40 = 10.69; P < .05). There was a significant decrease of 32% in the prescribing rate of schedule II opioids after the inclusion of chiropractic services (F2,80 = 6.07 for the Group × Schedule interaction; P < .05). The likelihood of writing schedule II opioid prescriptions decreased by 27% after the inclusion of chiropractic services (odds ratio, 0.73; 95% confidence interval, 0.59-0.90). Changes in opioid medication practices by the medical providers included prescribing a schedule III or IV opioid rather than a schedule II opioid (F6,76 = 29.81; P < .05) and a 30% decrease in the daily doses of opioid prescriptions (odds ratio, 0.70; 95% confidence interval, 0.50-0.98).

The authors concluded that this study demonstrates that there were decreases in opioid-therapy prescribing rates after a family medicine practice included on-site chiropractic services. This suggests that inclusion of chiropractic services may have had a positive effect on prescribing behaviors of medical physicians, as they may have been able to offer their patients additional nonpharmaceutical options for pain management.

The authors are correct in concluding the inclusion of chiropractic services MAY have had a positive effect. And then again, it may not!

Cause and effect cannot be established by correlation alone.

CORRELATION IS NOT CAUSATION!

And even if the inclusion of chiropractic services caused the positive effect, it would not prove that chiropractic is effective in the management of pain. It would only mean that the physicians had an option that helped them to write fewer opioid prescriptions. Had they hired a crystal healer or a homeopath or a faith healer or any other practitioner of an ineffective therapy, the findings might have been very similar.

The long and short of it is this: if we want to use fewer opioids, there is only one way to achieve it: we must prescribe less.

 

The objective of this study was to assess a new treatment, Medi-Taping, which aims at reducing complaints by treating pelvic obliquity with a combination of manual treatment of trigger points and kinesio taping in a pragmatic RCT with pilot character.

One hundred ten patients were randomized at two study centers either to Medi-Taping or to a standard treatment consisting of patient education and physiotherapy as control. Treatment duration was 3 weeks. Measures were taken at baseline, end of treatment and at follow-up after 2 months. Main outcome criteria were low back pain measured with VAS, the Chronic Pain Grade Scale (CPGS) and the Oswestry Low Back Pain Disability Questionnaire (ODQ).

Patients of both groups benefited from the treatment by medium to large effect sizes. All effects were pointing towards the intended direction. While Medi-Taping showed slightly better improvement rates, there were no significant differences for the primary endpoints between groups at the end of treatment (VAS: mean difference in change 0.38, 95-CI [- 0.45; 1.21] p = 0.10; ODQ 2.35 [- 0.77; 5.48] p = 0.14; CPGS – 0.19 [- 0.46; 0.08] p = 0.64) and at follow-up. Health-related quality of life was significantly higher (p = .004) in patients receiving Medi-Taping compared to controls.

The authors concluded that Medi-Taping, a purported way of correcting pelvic obliquity and chronic tension resulting from it, is a treatment modality similar in effectiveness to complex physiotherapy and patient education.

This conclusion is obviously nonsense! The authors stated that their trial has ‘pilot character’. The study was not designed as an equivalence trial. Thus it is improper to draw conclusions about the comparative effectiveness of Medi-Taping.

Having clarified this crucial point, we might ask, what is this new therapy called Medi-Taping? This is how the authors of the above paper describe the technique:

…sessions started with an assessment of leg length difference. Patients were asked to lie on their back and the legs were slightly stretched by a soft pull at the ankles. Next, a continuous horizontal line was drawn on the inside of both calves indicating the position of the calves relative to each other. Then the patient was asked to sit up with the legs remaining outstretched. This procedure results in a shift of the line between the two calves for most people. This shift was measured in millimeters as leg length difference.

The patient was then asked to stretch out, lying supine, and the therapist palpated any myogeloses (areas of abnormal hardening in a muscle) and tense muscles areas that could be found next to the cervical spine between the base of the skull and seventh cervical vertebra on both sides. After this treatment the leg length difference assessment was repeated. If there was still a substantial difference. The same treatment was also performed on the thoracic and lumbar spine. Also, the mandibular joint was assessed for tense muscles and, if necessary, treated by palpation.

Next, the leg length difference was assessed again and several tapes were applied as follows: First, two parallel tapes were fixed on both sides of the spine above the erector spinae muscles ranging from the base of the skull to the sacrum. For the application patients were asked to bend forward and to lean on a bench. This position stretches the back and its anatomical structure before applying the tape and thus provides the tape with tension before fixing it. Next a star-shaped pattern of tape (three stripes meeting in one point) was placed on the lower back while the patient was still in the same bent position. Thus, the star tape covered the area of the patient’s maximum pain and additionally stabilized the sacroiliac joint. This tape was placed with maximum tension in the middle section by stretching the tape before application, with the ends (approx. 5 cm) applied without tension. If after this procedure there was still residual pain, a third tape was placed at the gluteus maximus muscle. This tape was first fixed distally from the greater trochanter then stretched up to approx. 80% of the possible tension before the other end was placed on the sacrum. On average six tapes were applied for the gluteus tape.

Patients were instructed to keep the tapes on as long as they stuck to the skin. If the patients had recurring low back pain (LBP) within the same week, they were asked to see the therapist again immediately. Otherwise, the second and the third treatment were scheduled once a week for the following 2 weeks, respectively.

(Elsewhere MEDI-Taping is described differently as a technique using an elastic tape. The tape comes in different colors that are used depending on the patient’s need. The fabric and adhesive are made from cotton and other all natural materials. The tape can be ‘stretched’ in order to better support a given joint or muscle. Through the stretch, the underlying areas are relieved of tension, circulation is improved, and as a result injuries are healing faster. While it is applied to the skin, the tape gently massages the affected area as the body is moving. As the tape is applied, an improvement in motor function and pain relief should be felt immediately.)

Considering the above, I think that the most likely explanation of the outcome of this study (if it ever got confirmed in a properly designed equivalence trial) is that Medi-Taping itself is fairly useless. The fact that it did as well as (more precisely perhaps not worse than) standard physiotherapy is due to its exotic and novel flair which raised expectations and thus contributed to a large placebo response.

Whether my speculation is true or not, I don’t feel that Medi-Taping is the solution to back or any other problems.

 

PS

The senior author of this study is Harad Walach who has been a regular feature on this blog, and I could not help but notice that he now has 4 affiliations:

Thread embedding acupuncture therapy (TEAT) involves the insertion of thread at specific points on the body surface. The claim is that TEAT provides a sustained stimulation of acupoints and is therefore superior to needle acupuncture. Initially, TEAT was used in China to treat obesity, today it is employed to treat many conditions, including musculoskeletal conditions such as ankle sprain, shoulder pain, lumbar intervertebral disc herniation, and plantar fasciitis. Its effectiveness is, however, doubtful and so is its safety.

This review evaluated the safety of thread embedding acupuncture therapy (TEAT) and discuss the prevention and treatment of some adverse events (AEs).

Databases, including China National Knowledge Infrastructure (CNKI), CBMdisc, Wanfang, VIP databases and PubMed, MEDLINE, EMBASE, and Web of Science, were searched from their inception to January 2020. Included were randomized controlled trials (RCTs) and case reports in which AEs with TEAT were reported. Cochrane Collaboration’s tool and RevMan V.5.3.3 software were used to evaluate the quality of the studies.

A total of 61 articles (45 RCTs and 16 case reports) with a total of 620 cases of AEs were included in this review. These studies were published in two countries: China and South Korea. Twenty-eight kinds of AEs were noted. The most common AEs were induration, bleeding and ecchymosis, redness and swelling, fever, and pain. They accounted for 75.35% of all AEs.  Most AEs were mild.; The rarest AEs were epilepsy, irregular menstruation, skin ulcer, thread malabsorption, and fat liquefaction, with 1 case each. Not all of them had a clear causal relationship with TEAT. Most of the AEs were local reactions and systemic reactions accounted for only 1.27%. Although the included studies showed that AEs were very commonly encountered (11.09%), only 5 cases of severe AEs reported from 2013 to 2017 (0.1%) by using catgut thread, which is rarely employed nowadays with new absorbable surgical suture being more popular. All of the patients with severe AEs were recovered after symptomatic treatment with no sequelae.

The authors concluded that the evidence showed that TEAT is a relatively safe and convenient therapy especially since application of new absorbable surgical suture. Improving practitioner skills, regulating operations, and paying attention to the patients’ conditions may reduce the incidence of AEs and improve safety of TEAT.

TEAT was initially used in China only but recently it has become popular elsewhere as well. Therefore the question about its risks has become relevant. The present paper is interesting in that it demonstrates that AEs do occur with some regularity. The authors’ conclusion that TEAT is “relatively safe” is, however, not justified because:

  1. the total sample size was not large enough for a generalizable conclusion;
  2. only RCTs and case reports were included, whereas case series and case-control studies (which would provide more relevant data) were excluded or might not even exist;
  3. RCTs of acupuncture often fail to mention or under-report AEs;
  4. acupuncture papers from China are notoriously unreliable.

So, all we can conclude from the evidence presented here is that AEs after TEAT do occur and do not seem to be all that rare. As the efficacy of TEAT has not been shown beyond doubt, this must inevitably lead to the conclusion that the risk-benefit balance of TEAT is not positive. In turn, that means that TEAT cannot be recommended as a treatment for any condition.

 

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