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

study design

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This study was aimed at evaluating group-level and individual-level change in health-related quality of life among persons with chronic low back pain or neck pain receiving chiropractic care in the United States.

A 3-month longitudinal study was conducted of 2,024 patients with chronic low back pain or neck pain receiving care from 125 chiropractic clinics at 6 locations throughout the US. Ninety-one percent of the sample completed the baseline and 3-month follow-up survey (n = 1,835). Average age was 49, 74% females, and most of the sample had a college degree, were non-Hispanic White, worked full-time, and had an annual income of $60,000 or more. Group-level and individual-level changes on the Patient-Reported Outcomes Measurement Information System (PROMIS) v2.0 profile measure were evaluated: 6 multi-item scales (physical functioning, pain, fatigue, sleep disturbance, social health, emotional distress) and physical and mental health summary scores.

Within group t-tests indicated significant group-level change for all scores except for emotional distress, and these changes represented small improvements in health. From 13% (physical functioning) to 30% (PROMIS-29 Mental Health Summary Score) got better from baseline to 3 months later.

The authors concluded that chiropractic care was associated with significant group-level improvement in health-related quality of life over time, especially in pain. But only a minority of the individuals in the sample got significantly better (“responders”). This study suggests some benefits of chiropractic on functioning and well-being of patients with low back pain or neck pain.

These conclusions are worded carefully to avoid any statement of cause and effect. But I nevertheless feel that the authors strongly imply that chiropractic caused the observed outcomes. This is perhaps most obvious when they state that this study suggests some benefits of chiropractic on functioning and well-being of patients with low back pain or neck pain.

To me, it is obvious that this is wrong. The data are just as consistent with the opposite conclusion. There was no control group. It is therefore conceivable that the patients would have improved more and/or faster, if they had never consulted a chiropractor. The devil’s advocate therefore concludes this: the results of this study suggest that chiropractic has significant detrimental effects on functioning and well-being of patients with low back pain or neck pain.

Try to prove me wrong!

PS

I am concerned that a leading journal (Spine) publishes such rubbish.

Bee venom acupuncture is a form of acupuncture in which bee venom is applied to the tips of acupuncture needles, stingers are extracted from bees, or bees are held with an instrument exposing the stinger, and applied to acupoints on the skin.

Bee venom consisting of multiple anti-inflammatory compounds such as melittin, adolapin, apamin. Other substances such as phospholipase A2 can be anti-inflammatory in low concentrations and pro-inflammatory in others. However, bee venom also contains proinflammatory substances, melittin, mast cell degranulation peptide 401, and histamine.

Bee venom acupuncture has been used to treat a number of conditions such as lumbar disc disease, osteoarthritis of the knee, rheumatoid arthritis, adhesive capsulitis, lateral epicondylitis, peripheral neuropathies, stroke and Parkinson’s Disease. The quality of these studies tends to be so poor that any verdict on the effectiveness of bee venom acupuncture would be premature.

A new clinical trial of bee-venom acupuncture for rheumatoid arthritis (RA) might change this situation. A total of 120 cases of RA patients were randomized into bee-sting acupuncture group (treatment) and western medicine group (control). The patients of the control group were treated by oral administration of Methotrexate (10 mg, once a week) and Celecoxlb (0.2 g, once a day). Those of the treatment group received 5 to 15 bee stings of Ashi-points or acupoints according to different conditions and corporeity, and with the bee-sting retained for about 5 min every time, once every other day. The treatment lasted for 8 weeks. The therapeutic effect was assessed by examining:

  • symptoms and signs of the affected joints as morning stiffness duration,
  • swollen/tender joint counts (indexes),
  • handgrip strength,
  • 15 m-walking time,
  • visual analogue scale (VAS),
  • Disease Activity Score including a 28-joint count (DAS 28),
  • rheumatoid factor (RF),
  • erythrocyte sedimentation rate (ESR),
  • C-reactive protein (CRP),
  • anti-cyclic citrullinated peptide antibody (ACCPA).

For assessing the safety of bee-venom acupuncture, the patients’ responses of fever, enlargement of lymph nodes, regional red and swollen, itching, blood and urine tests for routine were examined.

Findings of DAS 28 responses displayed that of the two 60 cases in the control and bee-venom acupuncture groups, 15 and 18 experienced marked improvement, 33 and 32 were effective, 12 and 10 ineffective, with the effective rates being 80% and 83. 33%, respectively. No significant difference was found between the two groups in the effective rate (P>0.05). After the treatment, both groups have witnessed a marked decrease in the levels of morning stiffness duration, arthralgia index, swollen joint count index, joint tenderness index, 15 m walking time, VAS, RF, ESR, CRP and ACCPA, and an obvious increase of handgrip strength relevant to their own levels of pre-treatment in each group (P<0.05). There were no significant differences between the two groups in the abovementioned indexes (P>0.05). The routine blood test, routine urine test, routine stool test, electrocardiogram result, the function of liver and kidney and other security index were within the normal range, without any significant adverse effects found after bee-stinging treatment.

The authors (from the Department of Acupuncture and Moxibustion, Bao’an Hospital of Traditional Chinese Medicine, Shenzhen, China) concluded that bee-venom acupuncture therapy for RA patients is safe and effective, worthy of popularization and application in clinical practice.

Where to start? There is so much – perhaps I just comment on the conclusion:

  • Safety cannot be assessed on the basis of such a small sample. Bee venom can cause anaphylaxis, and several deaths have been reported in patients who successfully received the therapy prior to the adverse event. Because there is no adverse-effect monitoring system, the incidence of adverse events is unknown. Stating that it is safe, is therefore a big mistake.
  • The trial was a non-superiority study. As such, it needs a much larger sample to be able to make claims about effectiveness.
  • From the above two points, it follows that popularization and application in clinical practice would be a stupid exercise.

So, what is left over from this seemingly rigorous RCT?

NOTHING!

(except perhaps a re-affirmation of my often-voiced fear that we must take TCM-studies from China with more than just one pinch of salt)

The aim of this RCT was to investigate the effects of an osteopathic manipulative treatment (OMT) which includes a diaphragm intervention compared to the same OMT with a sham diaphragm intervention in chronic non-specific low back pain (NS-CLBP).

Participants (N=66) with a diagnosis of NS-CLBP lasting at least 3 months were randomized to receive either an OMT protocol including specific diaphragm techniques (n=33) or the same OMT protocol with a sham diaphragm intervention (n=33), conducted in 5 sessions provided during 4 weeks.

The primary outcomes were pain (evaluated with the Short-Form McGill Pain Questionnaire [SF-MPQ] and the visual analog scale [VAS]) and disability (assessed with the Roland-Morris Questionnaire [RMQ] and the Oswestry Disability Index [ODI]). Secondary outcomes were fear-avoidance beliefs, level of anxiety and depression, and pain catastrophization. All outcome measures were evaluated at baseline, at week 4, and at week 12.

A statistically significant reduction was observed in the experimental group compared to the sham group in all variables assessed at week 4 and at week 12. Moreover, improvements in pain and disability were clinically relevant.

The authors concluded that an OMT protocol that includes diaphragm techniques produces significant and clinically relevant improvements in pain and disability in patients with NS-CLBP compared to the same OMT protocol using sham diaphragm techniques.

This seems to be a rigorous study. The authors describe in detail their well-standardised interventions in the full text of their paper. This, of course, will be essential, if someone wants to repeat the trial.

I have but a few points to add:

  1. What I fail to understand is this: why the authors call the interventions osteopathic? The therapist was a physiotherapist and the techniques employed are, if I am not mistaken, as much physiotherapeutic as osteopathic.
  2. The findings of this trial are encouraging but almost seem a little too good to be true. They need, of course, to be independently replicated in a larger study.
  3. If that is done, I would suggest to check whether the blinding of the patient was successful. If not, there is a suspicion that the diaphragm technique works partly or mostly via a placebo effect.
  4. I would also try to make sure that the therapist cannot influence the results in any way, for instance, by verbal or non-verbal suggestions.
  5. Finally, I suggest to employ more than one therapist to increase generalisability.

Once all these hurdles are taken, we might indeed have made some significant progress in the manual therapy of NS-CLBP.

Osteopathy is a form of manual therapy invented by the American Andrew Taylor Still (1828-1917). Today, US osteopaths (doctors of osteopathy or DOs) practise no or little manual therapy; they are fully recognised as medical doctors who can specialise in any medical field after their training which is almost identical with that of MDs. Outside the US, osteopaths practice almost exclusively manual treatments and are considered alternative practitioners. This post deals with the latter category of osteopaths.

Still defined his original osteopathy as a science which consists of such exact, exhaustive, and verifiable knowledge of the structure and function of the human mechanism, anatomical, physiological and psychological, including the chemistry and physics of its known elements, as has made discoverable certain organic laws and remedial resources, within the body itself, by which nature under the scientific treatment peculiar to osteopathic practice, apart from all ordinary methods of extraneous, artificial, or medicinal stimulation, and in harmonious accord with its own mechanical principles, molecular activities, and metabolic processes, may recover from displacements, disorganizations, derangements, and consequent disease, and regained its normal equilibrium of form and function in health and strength.

Based on such vague and largely nonsensical statements, traditional osteopaths feel entitled to offer treatments for most human diseases, conditions and symptoms. The studies they produce to back up their claims tend to be as poor as Still’s original assumptions were fantastic.

Here is an apt example:

The aim of this new study was to study the effect of osteopathic manipulation on pain relief and quality of life improvement in hospitalized oncology geriatric patients.

The researchers conducted a non-randomized controlled clinical trial with 23 cancer patients. They were allocated to two groups: the study group (OMT [osteopathic manipulative therapy] group, N = 12) underwent OMT in addition to physiotherapy (PT), while the control group (PT group, N = 12) underwent only PT. Included were postsurgical cancer patients, male and female, age ⩾65 years, with an oncology prognosis of 6 to 24 months and chronic pain for at least 3 months with an intensity score higher than 3, measured with the Numeric Rating Scale. Exclusion criteria were patients receiving chemotherapy or radiotherapy treatment at the time of the study, with mental disorders (Mini-Mental State Examination [MMSE] = 10-20), with infection, anticoagulation therapy, cardiopulmonary disease, or clinical instability post-surgery. Oncology patients were admitted for rehabilitation after cancer surgery. The main cancers were colorectal cancer, osteosarcoma, spinal metastasis from breast and prostatic cancer, and kidney cancer.

The OMT, based on osteopathic principles of body unit, structure-function relationship, and homeostasis, was designed for each patient on the basis of the results of the osteopathic examination. Diagnosis and treatment were founded on 5 models: biomechanics, neurologic, metabolic, respiratory-circulatory, and behaviour. The OMT protocol was administered by an osteopath with clinical experience of 10 years in one-on-one individual sessions. The techniques used were: dorsal and lumbar soft tissue, rib raising, back and abdominal myofascial release, cervical spine soft tissue, sub-occipital decompression, and sacroiliac myofascial release. Back and abdominal myofascial release techniques are used to improve back movement and internal abdominal pressure. Sub-occipital decompression involves traction at the base of the skull, which is considered to release restrictions around the vagus nerve, theoretically improving nerve function. Sacroiliac myofascial release is used to improve sacroiliac joint movement and to reduce ligament tension. Strain-counter-strain and muscle energy technique are used to diminish the presence of trigger points and their pain intensity. OMT was repeated once every week during 4 weeks for each group, for a total of 4 treatments. Each treatment lasted 45 minutes.

At enrolment (T0), the patients were evaluated for pain intensity and quality of life by an external examiner. All patients were re-evaluated every week (T1, T2, T3, and T4) for pain intensity, and at the end of the study treatment (T4) for quality of life.

The OMT added to physiotherapy produced a significant reduction in pain both at T2 and T4. The difference in quality of life improvements between T0 and T4 was not statistically significant. Pain improved in the PT group at T4. Between-group analysis of pain and quality of life did not show any significant difference between the two treatments.

The authors concluded that our study showed a significant improvement in pain relief and a nonsignificant improvement in quality of life in hospitalized geriatric oncology patients during osteopathic manipulative treatment.

GOOD GRIEF!

Where to begin?

Even if there had been a difference in outcome between the two groups, such a finding would not have shown an effect of OMT per se. More likely, it would have been due to the extra attention and the expectation in the OMT group (or caused by the lack of randomisation). The A+B vs B design used for this study  does not control for non-specific effects. Therefore it is incapable of establishing a causal relationship between the therapy and the outcome.

As it turns out, there were no inter-group differences. How can this be? I have often stated that A+B is always more than B alone. And this is surely true!

So, how can I explain this?

As far as I can see, there are two possibilities:

  1. The study was underpowered, and thus an existing difference was not picked up.
  2. The OMT had a detrimental effect on the outcome measures thus neutralising the positive effects of the extra attention and expectation.

And which possibility does apply in this case?

Nobody can know from these data.

Integrative Cancer Therapies, the journal that published this paper, states that it focuses on a new and growing movement in cancer treatment. The journal emphasizes scientific understanding of alternative and traditional medicine therapies, and the responsible integration of both with conventional health care. Integrative care includes therapeutic interventions in diet, lifestyle, exercise, stress care, and nutritional supplements, as well as experimental vaccines, chrono-chemotherapy, and other advanced treatments. I feel that the editors should rather focus more on the quality of the science they publish.

My conclusion from all this is the one I draw so depressingly often: fatally flawed science is not just useless, it is unethical, gives clinical research a bad name, hinders progress, and can be harmful to patients.

I remember reading this paper entitled ‘Comparison of acupuncture and other drugs for chronic constipation: A network meta-analysis’ when it first came out. I considered discussing it on my blog, but then decided against it for a range of reasons which I shall explain below. The abstract of the original meta-analysis is copied below:

The objective of this study was to compare the efficacy and side effects of acupuncture, sham acupuncture and drugs in the treatment of chronic constipation. Randomized controlled trials (RCTs) assessing the effects of acupuncture and drugs for chronic constipation were comprehensively retrieved from electronic databases (such as PubMed, Cochrane Library, Embase, CNKI, Wanfang Database, VIP Database and CBM) up to December 2017. Additional references were obtained from review articles. With quality evaluations and data extraction, a network meta-analysis (NMA) was performed using a random-effects model under a frequentist framework. A total of 40 studies (n = 11032) were included: 39 were high-quality studies and 1 was a low-quality study. NMA showed that (1) acupuncture improved the symptoms of chronic constipation more effectively than drugs; (2) the ranking of treatments in terms of efficacy in diarrhoea-predominant irritable bowel syndrome was acupuncture, polyethylene glycol, lactulose, linaclotide, lubiprostone, bisacodyl, prucalopride, sham acupuncture, tegaserod, and placebo; (3) the ranking of side effects were as follows: lactulose, lubiprostone, bisacodyl, polyethylene glycol, prucalopride, linaclotide, placebo and tegaserod; and (4) the most commonly used acupuncture point for chronic constipation was ST25. Acupuncture is more effective than drugs in improving chronic constipation and has the least side effects. In the future, large-scale randomized controlled trials are needed to prove this. Sham acupuncture may have curative effects that are greater than the placebo effect. In the future, it is necessary to perform high-quality studies to support this finding. Polyethylene glycol also has acceptable curative effects with fewer side effects than other drugs.

END OF 1st QUOTE

This meta-analysis has now been retracted. Here is what the journal editors have to say about the retraction:

After publication of this article [1], concerns were raised about the scientific validity of the meta-analysis and whether it provided a rigorous and accurate assessment of published clinical studies on the efficacy of acupuncture or drug-based interventions for improving chronic constipation. The PLOS ONE Editors re-assessed the article in collaboration with a member of our Editorial Board and noted several concerns including the following:

  • Acupuncture and related terms are not mentioned in the literature search terms, there are no listed inclusion or exclusion criteria related to acupuncture, and the outcome measures were not clearly defined in terms of reproducible clinical measures.
  • The study included acupuncture and electroacupuncture studies, though this was not clearly discussed or reported in the Title, Methods, or Results.
  • In the “Routine paired meta-analysis” section, both acupuncture and sham acupuncture groups were reported as showing improvement in symptoms compared with placebo. This finding and its implications for the conclusions of the article were not discussed clearly.
  • Several included studies did not meet the reported inclusion criteria requiring that studies use adult participants and assess treatments of >2 weeks in duration.
  • Data extraction errors were identified by comparing the dataset used in the meta-analysis (S1 Table) with details reported in the original research articles. Errors included aspects of the study design such as the experimental groups included in the study, the number of study arms in the trial, number of participants, and treatment duration. There are also several errors in the Reference list.
  • With regard to side effects, 22 out of 40 studies were noted as having reported side effects. It was not made clear whether side effects were assessed as outcome measures for the other 18 studies, i.e. did the authors collect data clarifying that there were no side effects or was this outcome measure not assessed or reported in the original article. Without this clarification the conclusion comparing side effect frequencies is not well supported.
  • The network geometry presented in Fig 5 is not correct and misrepresents some of the study designs, for example showing two-arm studies as three-arm studies.
  • The overall results of the meta-analysis are strongly reliant on the evidence comparing acupuncture versus lactulose treatment. Several of the trials that assessed this comparison were poorly reported, and the meta-analysis dataset pertaining to these trials contained data extraction errors. Furthermore, potential bias in studies assessing lactulose efficacy in acupuncture trials versus lactulose efficacy in other trials was not sufficiently addressed.

While some of the above issues could be addressed with additional clarifications and corrections to the text, the concerns about study inclusion, the accuracy with which the primary studies’ research designs and data were represented in the meta-analysis, and the reporting quality of included studies directly impact the validity and accuracy of the dataset underlying the meta-analysis. As a consequence, we consider that the overall conclusions of the study are not reliable. In light of these issues, the PLOS ONE Editors retract the article. We apologize that these issues were not adequately addressed during pre-publication peer review.

LZ disagreed with the retraction. YM and XD did not respond.

END OF 2nd QUOTE

Let me start by explaining why I initially decided not to discuss this paper on my blog. Already the first sentence of the abstract put me off, and an entire chorus of alarm-bells started ringing once I read further.

  • A meta-analysis is not a ‘study’ in my book, and I am somewhat weary of researchers who employ odd or unprecise language.
  • We all know (and I have discussed it repeatedly) that studies of acupuncture frequently fail to report adverse effects (in doing this, their authors violate research ethics!). So, how can it be a credible aim of a meta-analysis to compare side-effects in the absence of adequate reporting?
  • The methodology of a network meta-analysis is complex and I know not a lot about it.
  • Several things seemed ‘too good to be true’, for instance, the funnel-plot and the overall finding that acupuncture is the best of all therapeutic options.
  • Looking at the references, I quickly confirmed my suspicion that most of the primary studies were in Chinese.

In retrospect, I am glad I did not tackle the task of criticising this paper; I would probably have made not nearly such a good job of it as PLOS ONE eventually did. But it was only after someone raised concerns that the paper was re-reviewed and all the defects outlined above came to light.

While some of my concerns listed above may have been trivial, my last point is the one that troubles me a lot. As it also related to dozens of Cochrane reviews which currently come out of China, it is worth our attention, I think. The problem, as I see it, is as follows:

  • Chinese (acupuncture, TCM and perhaps also other) trials are almost invariably reporting positive findings, as we have discussed ad nauseam on this blog.
  • Data fabrication seems to be rife in China.
  • This means that there is good reason to be suspicious of such trials.
  • Many of the reviews that currently flood the literature are based predominantly on primary studies published in Chinese.
  • Unless one is able to read Chinese, there is no way of evaluating these papers.
  • Therefore reviewers of journal submissions tend to rely on what the Chinese review authors write about the primary studies.
  • As data fabrication seems to be rife in China, this trust might often not be justified.
  • At the same time, Chinese researchers are VERY keen to publish in top Western journals (this is considered a great boost to their career).
  • The consequence of all this is that reviews of this nature might be misleading, even if they are published in top journals.

I have been struggling with this problem for many years and have tried my best to alert people to it. However, it does not seem that my efforts had even the slightest success. The stream of such reviews has only increased and is now a true worry (at least for me). My suspicion – and I stress that it is merely that – is that, if one would rigorously re-evaluate these reviews, their majority would need to be retracted just as the above paper. That would mean that hundreds of papers would disappear because they are misleading, a thought that should give everyone interested in reliable evidence sleepless nights!

So, what can be done?

Personally, I now distrust all of these papers, but I admit, that is not a good, constructive solution. It would be better if Journal editors (including, of course, those at the Cochrane Collaboration) would allocate such submissions to reviewers who:

  • are demonstrably able to conduct a CRITICAL analysis of the paper in question,
  • can read Chinese,
  • have no conflicts of interest.

In the case of an acupuncture review, this would narrow it down to perhaps just a handful of experts worldwide. This probably means that my suggestion is simply not feasible.

But what other choice do we have?

One could oblige the authors of all submissions to include full and authorised English translations of non-English articles. I think this might work, but it is, of course, tedious and expensive. In view of the size of the problem (I estimate that there must be around 1 000 reviews out there to which the problem applies), I do not see a better solution.

(I would truly be thankful, if someone had a better one and would tell us)

Psoriasis is one of those conditions that is

  • chronic,
  • not curable,
  • irritating to the point where it reduces quality of life.

In other words, it is a disease for which virtually all alternative treatments on the planet are claimed to be effective. But which therapies do demonstrably alleviate the symptoms?

This review (published in JAMA Dermatology) compiled the evidence on the efficacy of the most studied complementary and alternative medicine (CAM) modalities for treatment of patients with plaque psoriasis and discusses those therapies with the most robust available evidence.

PubMed, Embase, and ClinicalTrials.gov searches (1950-2017) were used to identify all documented CAM psoriasis interventions in the literature. The criteria were further refined to focus on those treatments identified in the first step that had the highest level of evidence for plaque psoriasis with more than one randomized clinical trial (RCT) supporting their use. This excluded therapies lacking RCT data or showing consistent inefficacy.

A total of 457 articles were found, of which 107 articles were retrieved for closer examination. Of those articles, 54 were excluded because the CAM therapy did not have more than 1 RCT on the subject or showed consistent lack of efficacy. An additional 7 articles were found using references of the included studies, resulting in a total of 44 RCTs (17 double-blind, 13 single-blind, and 14 nonblind), 10 uncontrolled trials, 2 open-label nonrandomized controlled trials, 1 prospective controlled trial, and 3 meta-analyses.

Compared with placebo, application of topical indigo naturalis, studied in 5 RCTs with 215 participants, showed significant improvements in the treatment of psoriasis. Treatment with curcumin, examined in 3 RCTs (with a total of 118 participants), 1 nonrandomized controlled study, and 1 uncontrolled study, conferred statistically and clinically significant improvements in psoriasis plaques. Fish oil treatment was evaluated in 20 studies (12 RCTs, 1 open-label nonrandomized controlled trial, and 7 uncontrolled studies); most of the RCTs showed no significant improvement in psoriasis, whereas most of the uncontrolled studies showed benefit when fish oil was used daily. Meditation and guided imagery therapies were studied in 3 single-blind RCTs (with a total of 112 patients) and showed modest efficacy in treatment of psoriasis. One meta-analysis of 13 RCTs examined the association of acupuncture with improvement in psoriasis and showed significant improvement with acupuncture compared with placebo.

The authors concluded that CAM therapies with the most robust evidence of efficacy for treatment of psoriasis are indigo naturalis, curcumin, dietary modification, fish oil, meditation, and acupuncture. This review will aid practitioners in advising patients seeking unconventional approaches for treatment of psoriasis.

I am sorry to say so, but this review smells fishy! And not just because of the fish oil. But the fish oil data are a good case in point: the authors found 12 RCTs of fish oil. These details are provided by the review authors in relation to oral fish oil trials: Two double-blind RCTs (one of which evaluated EPA, 1.8g, and DHA, 1.2g, consumed daily for 12 weeks, and the other evaluated EPA, 3.6g, and DHA, 2.4g, consumed daily for 15 weeks) found evidence supporting the use of oral fish oil. One open-label RCT and 1 open-label non-randomized controlled trial also showed statistically significant benefit. Seven other RCTs found lack of efficacy for daily EPA (216mgto5.4g)or DHA (132mgto3.6g) treatment. The remainder of the data supporting efficacy of oral fish oil treatment were based on uncontrolled trials, of which 6 of the 7 studies found significant benefit of oral fish oil. This seems to support their conclusion. However, the authors also state that fish oil was not shown to be effective at several examined doses and duration. Confused? Yes, me too!

Even more confusing is their failure to mention a single trial of Mahonia aquifolium. A 2013 meta-analysis published in the British Journal of Dermatology included 5 RCTs of Mahonia aquifolium which, according to these authors, provided ‘limited support’ for its effectivenessHow could they miss that?

More importantly, how could the reviewers miss to conduct a proper evaluation of the quality of the studies they included in their review (even in their abstract, they twice speak of ‘robust evidence’ – but how can they without assessing its robustness? [quantity is not remotely the same as quality!!!]). Without a transparent evaluation of the rigour of the primary studies, any review is nearly worthless.

Take the 12 acupuncture trials, for instance, which the review authors included based not on an assessment of the studies but on a dodgy review published in a dodgy journal. Had they critically assessed the quality of the primary studies, they could have not stated that CAM therapies with the most robust evidence of efficacy for treatment of psoriasis …[include]… acupuncture. Instead they would have had to admit that these studies are too dubious for any firm conclusion. Had they even bothered to read them, they would have found that many are in Chinese (which would have meant they had to be excluded in their review [as many pseudo-systematic reviewers, the authors only considered English papers]).

There might be a lesson in all this – well, actually I can think of at least two:

  1. Systematic reviews might well be the ‘Rolls Royce’ of clinical evidence. But even a Rolls Royce needs to be assembled correctly, otherwise it is just a heap of useless material.
  2. Even top journals do occasionally publish poor-quality and thus misleading reviews.

Medline is the biggest electronic databank for articles published in medicine and related fields. It is therefore the most important source of information in this area. I use it regularly to monitor what new papers have been published in the various fields of alternative medicine.

As the number of Medline-listed papers dated 2018 on homeopathy has just reached 100, I thought it might be the moment to run a quick analysis on this material. The first thing to note is that it took until August for 100 articles dated 2018 to emerge. To explain how embarrassing this is, we need a few comparative figures. At the same moment (6/9/18), we have, for instance:

  • 126576 articles for surgery
  • 5001 articles or physiotherapy
  • 30215 articles for psychiatry
  • 60161 articles for pharmacology

Even compared to other types of alternative medicine, homeopathy is being dwarfed. Currently the figures are, for instance:

  • 2232 for herbal medicine
  • 1949 for dietary supplements
  • 1222 for acupuncture

This does not look as though homeopathy is a frightfully active area of research, if I may say so. Looking at the type of articles (yes, I did look at all the 100 papers and categorised them the best I could) published in homeopathy, things get even worse:

  • 29 were comments, letters, editorials, etc.
  • 16 were basic and pre-clinical papers,
  • 12 were non-systematic reviews,
  • 10 were surveys,
  • 7 were case-reports,
  • 5 were pilot or feasibility studies,
  • 5 were systematic reviews,
  • 5 were controlled clinical trials,
  • 2 were case series,
  • the rest of the articles was not on homeopathy at all.

I find this pretty depressing. Most of the 100 papers turn out to be no real research at all. Crucial topics are not being covered. There was, for example, not a single paper on the risks of homeopathy (no, don’t tell me it is harmless; it can and does regularly cost the lives of patients who trust the bogus claims of homeopaths). There was no article investigating the important question whether the practice of homeopathy does not violate the rules of medical ethics (think of informed consent or the imperative to do more harm than good). And a mere 5 clinical trials is just a dismal amount, in my view.

In a previous post, I have already shown that, in 2015, homeopathy research was deplorable. My new analysis suggests that the situation has become much worse. One might even go as far as asking whether 2018 might turn out to be the year when homeopathy research finally died a natural death.

PROGRESS AT LAST!!!

This systematic review included 18 studies assessing homeopathy in depression. Two double-blind placebo-controlled trials of homeopathic medicinal products (HMPs) for depression were assessed. The first trial (N = 91) with high risk of bias found HMPs were non-inferior to fluoxetine at 4 (p = 0.654) and 8 weeks (p = 0.965); whereas the second trial (N = 133), with low risk of bias, found HMPs was comparable to fluoxetine (p = 0.082) and superior to placebo (p < 0.005) at 6 weeks.

The remaining research had unclear/high risk of bias. A non-placebo-controlled RCT found standardised treatment by homeopaths comparable to fluvoxamine; a cohort study of patients receiving treatment provided by GPs practising homeopathy reported significantly lower consumption of psychotropic drugs and improved depression; and patient-reported outcomes showed at least moderate improvement in 10 of 12 uncontrolled studies. Fourteen trials provided safety data. All adverse events were mild or moderate, and transient. No evidence suggested treatment was unsafe.

The authors concluded that limited evidence from two placebo-controlled double-blinded trials suggests HMPs might be comparable to antidepressants and superior to placebo in depression, and patients treated by homeopaths report improvement in depression. Overall, the evidence gives a potentially promising risk benefit ratio. There is a need for additional high quality studies.

It is worth having a look at these two studies, I think.

The 1st (2011) study is from Brazil

Here is its abstract:

Homeopathy is a complementary and integrative medicine used in depression, The aim of this study is to investigate the non-inferiority and tolerability of individualized homeopathic medicines [Quinquagintamillesmial (Q-potencies)] in acute depression, using fluoxetine as active control. Ninety-one outpatients with moderate to severe depression were assigned to receive an individualized homeopathic medicine or fluoxetine 20 mg day−1 (up to 40 mg day−1) in a prospective, randomized, double-blind double-dummy 8-week, single-center trial. Primary efficacy measure was the analysis of the mean change in the Montgomery & Åsberg Depression Rating Scale (MADRS) depression scores, using a non-inferiority test with margin of 1.45. Secondary efficacy outcomes were response and remission rates. Tolerability was assessed with the side effect rating scale of the Scandinavian Society of Psychopharmacology. Mean MADRS scores differences were not significant at the 4th (P = .654) and 8th weeks (P = .965) of treatment. Non-inferiority of homeopathy was indicated because the upper limit of the confidence interval (CI) for mean difference in MADRS change was less than the non-inferiority margin: mean differences (homeopathy-fluoxetine) were −3.04 (95% CI −6.95, 0.86) and −2.4 (95% CI −6.05, 0.77) at 4th and 8th week, respectively. There were no significant differences between the percentages of response or remission rates in both groups. Tolerability: there were no significant differences between the side effects rates, although a higher percentage of patients treated with fluoxetine reported troublesome side effects and there was a trend toward greater treatment interruption for adverse effects in the fluoxetine group. This study illustrates the feasibility of randomized controlled double-blind trials of homeopathy in depression and indicates the non-inferiority of individualized homeopathic Q-potencies as compared to fluoxetine in acute treatment of outpatients with moderate to severe depression.

There are many important points to make about this trial:

  1. Contrary to what the reviewers claim, the trial had no placebo group.
  2. It was a double-dummy equivalence study comparing individualised homeopathy with the antidepressant fluoxetine.
  3. Fluoxetine might have been under-dosed (see below).
  4. Equivalence studies require large sample sizes, and with just 91 patients (only 55 of whom finished the study), this trial was underpowered which means the finding of equivalence is false positive.
  5. The authors noted that a higher percentage of troublesome adverse effects reported by patients receiving fluoxetine. This means that the trial was not double-blind; patients were able to tell by their side-effects which group they were in.
  6. The authors also state that more patients randomized to homeopathy than to fluoxetine were excluded due to worsening of their depressive symptoms. I think this confirms that homeopathy was ineffective.

The 2nd (2015) study is from Mexico

Here is its abstract:

Background: Perimenopausal period refers to the interval when women’s menstrual cycles become irregular and is characterized by an increased risk of depression. Use of homeopathy to treat depression is widespread but there is a lack of clinical trials about its efficacy in depression in peri- and postmenopausal women. The aim of this study was to assess efficacy and safety of individualized homeopathic treatment versus placebo and fluoxetine versus placebo in peri- and postmenopausal women with moderate to severe depression.

Methods/Design: A randomized, placebo-controlled, double-blind, double-dummy, superiority, three-arm trial with a 6 week follow-up study was conducted. The study was performed in a public research hospital in Mexico City in the outpatient service of homeopathy. One hundred thirty-three peri- and postmenopausal women diagnosed with major depression according to DSM-IV (moderate to severe intensity) were included. The outcomes were: change in the mean total score among groups on the 17-item Hamilton Rating Scale for Depression, Beck Depression Inventory and Greene Scale, after 6 weeks of treatment, response and remission rates, and safety. Efficacy data were analyzed in the intention-to-treat population (ANOVA with Bonferroni post-hoc test).

Results: After a 6-week treatment, homeopathic group was more effective than placebo by 5 points in Hamilton Scale. Response rate was 54.5% and remission rate, 15.9%. There was a significant difference among groups in response rate definition only, but not in remission rate. Fluoxetine-placebo difference was 3.2 points. No differences were observed among groups in the Beck Depression Inventory. Homeopathic group was superior to placebo in Greene Climacteric Scale (8.6 points). Fluoxetine was not different from placebo in Greene Climacteric Scale.

Conclusion: Homeopathy and fluoxetine are effective and safe antidepressants for climacteric women. Homeopathy and fluoxetine were significantly different from placebo in response definition only. Homeopathy, but not fluoxetine, improves menopausal symptoms scored by Greene Climacteric Scale.

And here are my critical remarks about this trial:

  1. The aim of a small study like this cannot be to assess or draw conclusions about the safety of the interventions used; for this purpose, we need sample sizes that are at least one dimension bigger.
  2. Fluoxetine might have been under-dosed (see below).
  3. The blinding of patients might have been jeopardized by patients experiencing the specific side-effects of fluoxetine. The authors reported adverse effects in all three groups. However, the characteristic and most common side-effects of fluoxetine (such as hives, itching, skin rash, restlessness, inability to sit still) were not included.

________________________________________________

Usual Adult Dose for Depression

Immediate-release oral formulations:
Initial dose: 20 mg orally once a day in the morning, increased after several weeks if sufficient clinical improvement is not observed
Maintenance dose: 20 to 60 mg orally per day
Maximum dose: 80 mg orally per day

Delayed release oral capsules:
Initial dose: 90 mg orally once a week, commenced 7 days after the last daily dose of immediate-release fluoxetine 20 mg formulations.

_________________________________________________

Considering all this, I feel that the conclusions of the above review are far too optimistic and not justified. In fact, I find them misleading, dangerous, unethical and depressing.

Bacterial vaginosis is a common condition which is more than a triviality. It can have serious consequences including pelvic inflammatory disease, endometritis, postoperative vaginal cuff infections, preterm labor, premature rupture of membranes, and chorioamnionitis. Therefore, it is important to treat it adequately with antibiotics. But are there other options as well?

There are plenty of alternative or ‘natural’ treatments on offer. But do they work?

This trial was conducted on 127 women with bacterial vaginosis to compare a vaginal suppository of metronidazole with Forzejeh, a vaginal suppository of herbal Persian medicine combination of

  • Tribulus terrestris,
  • Myrtus commuis,
  • Foeniculum vulgare,
  • Tamarindus indica.

The patients (63 in metronidazole group and 64 in Forzejeh group) received the medications for 1 week. Their symptoms including the amount and odour of discharge and cervical pain were assessed using a questionnaire. Cervical inflammation and Amsel criteria (pH of vaginal discharge, whiff test, presence of clue cells and Gram staining) were investigated at the beginning of the study and 14 days after treatment.

The amount and odour of discharge, Amsel criteria, pelvic pain and cervical inflammation significantly decreased in Forzejeh and metronidazole groups (p = <.001). There was no statistically significant difference between the metronidazole and Fozejeh groups with respect to any of the clinical symptoms or the laboratory assessments.

The authors concluded that Forzejeh … has a therapeutic effect the same as metronidazole in bacterial vaginosis.

The plants in Fozejeh are assumed to have antimicrobial activities. Forzejeh has been used in folk medicine for many years but was only recently standardised. According to the authors, this study shows that the therapeutic effects of Forzejeh on bacterial vaginosis is similar to metronidazole.

Yet, I am far less convinced than these Iranian researchers. As this trial compared two active treatments, it was an equivalence study. As such, it requires a different statistical approach and a much larger sample size. The absence of a difference between the two groups is most likely due to the fact that the study was too small to show it.

If I am correct, the present investigation only demonstrates yet again that, with flawed study-designs, it is easy to produce false-positive results.

In one of his many comments, our friend Iqbal just linked to an article that unquestionably is interesting. Here is its abstract (the link also provides the full paper):

Objective: The objective was to assess the usefulness of homoeopathic genus epidemicus (Bryonia alba 30C) for the prevention of chikungunya during its epidemic outbreak in the state of Kerala, India.

Materials and Methods: A cluster- randomised, double- blind, placebo -controlled trial was conducted in Kerala for prevention of chikungunya during the epidemic outbreak in August-September 2007 in three panchayats of two districts. Bryonia alba 30C/placebo was randomly administered to 167 clusters (Bryonia alba 30C = 84 clusters; placebo = 83 clusters) out of which data of 158 clusters was analyzed (Bryonia alba 30C = 82 clusters; placebo = 76 clusters) . Healthy participants (absence of fever and arthralgia) were eligible for the study (Bryonia alba 30 C n = 19750; placebo n = 18479). Weekly follow-up was done for 35 days. Infection rate in the study groups was analysed and compared by use of cluster analysis.

Results: The findings showed that 2525 out of 19750 persons of Bryonia alba 30 C group suffered from chikungunya, compared to 2919 out of 18479 in placebo group. Cluster analysis showed significant difference between the two groups [rate ratio = 0.76 (95% CI 0.14 – 5.57), P value = 0.03]. The result reflects a 19.76% relative risk reduction by Bryonia alba 30C as compared to placebo.

Conclusion: Bryonia alba 30C as genus epidemicus was better than placebo in decreasing the incidence of chikungunya in Kerala. The efficacy of genus epidemicus needs to be replicated in different epidemic settings.

________________________________________________________________________________

I have often said the notion that homeopathy might prevent epidemics is purely based on observational data. Here I stand corrected. This is an RCT! What is more, it suggests that homeopathy might be effective. As this is an important claim, let me quickly post just 10 comments on this study. I will try to make this short (I only looked at it briefly), hoping that others complete my criticism where I missed important issues:

  1. The paper was published in THE INDIAN JOURNAL OF RESEARCH IN HOMEOPATHY. This is not a publication that could be called a top journal. If this study really shows something as revolutionarily new as its conclusions imply, one must wonder why it was published in an obscure and inaccessible journal.
  2. Several of its authors are homeopaths who unquestionably have an axe to grind, yet they do not declare any conflicts of interest.
  3. The abstract states that the trial was aimed at assessing the usefulness of Bryonia C30, while the paper itself states that it assessed its efficacy. The two are not the same, I think.
  4. The trial was conducted in 2007 and published only 7 years later; why the delay?
  5. The criteria for the main outcome measure were less than clear and had plenty of room for interpretation (“Any participant who suffered from fever and arthralgia (characteristic symptoms of chikungunya) during the follow-up period was considered as a case of chikungunya”).
  6. I fail to follow the logic of the sample size calculation provided by the authors and therefore believe that the trial was woefully underpowered.
  7. As a cluster RCT, its unit of assessment is the cluster. Yet the significant results seem to have been obtained by using single patients as the unit of assessment (“At the end of follow-ups it was observed that 12.78% (2525 out of 19750) healthy individuals, administered with Bryonia alba 30 C, were presented diagnosed as probable case of chikungunya, whereas it was 15.79% (2919 out of 18749) in the placebo group”).
  8. The p-value was set at 0.05. As we have often explained, this is far too low considering that the verum was a C30 dilution with zero prior probability.
  9. Nine clusters were not included in the analysis because of ‘non-compliance’. I doubt whether this was the correct way of dealing with this issue and think that an intention to treat analysis would have been better.
  10. This RCT was published 4 years ago. If true, its findings are nothing short of a sensation. Therefore, one would have expected that, by now, we would see several independent replications. The fact that this is not the case might mean that such RCTs were done but failed to confirm the findings above.

As I said, I would welcome others to have a look and tell us what they think about this potentially important study.

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