The aim of this systematic review was to determine the efficacy of conventional treatments plus acupuncture versus conventional treatments alone for asthma, using a meta-analysis of all published randomized clinical trials (RCTs).
The researchers included all RCTs in which adult and adolescent patients with asthma (age ≥12 years) were divided into conventional treatments plus acupuncture (A+B) and conventional treatments (B). Nine studies were included. The results showed that A+B could improve the symptom response rate and significantly decrease interleukin-6. However, indices of pulmonary function, including the forced expiratory volume in one second (FEV1) and FEV1/forced vital capacity (FVC) failed to be improved with A+B.
The authors concluded that conventional treatments plus acupuncture are associated with significant benefits for adult and adolescent patients with asthma. Therefore, we suggest the use of conventional treatments plus acupuncture for asthma patients.
I am thankful to the authors for confirming my finding that A+B must always be more/better than B alone (the 2nd sentence of their conclusion is, of course, utter nonsense, but I will leave this aside for today). Here is the short abstract of my 2008 article:
In this article, we test the hypothesis that randomized clinical trials of acupuncture for pain with certain design features (A + B versus B) are likely to generate false positive results. Based on electronic searches in six databases, 13 studies were found that met our inclusion criteria. They all suggested that acupuncture is effective (one only showing a positive trend, all others had significant results). We conclude that the ‘A + B versus B’ design is prone to false positive results and discuss the design features that might prevent or exacerbate this problem.
Even though our paper was on acupuncture for pain, it firmly established the principle that A+B is always more than B. Think of it in monetary terms: let’s say we both have $100; now someone gives me $10 more. Who has more cash? Not difficult, is it?
But why do SCAM-fans not get it?
Why do we see trial after trial and review after review ignoring this simple and obvious fact?
I suspect I know why: it is because the ‘A+B vs B’ study-design never generates a negative result!
But that’s cheating!
And isn’t cheating unethical?
My answer is YES!
(If you want to read a more detailed answer, please read our in-depth analysis here)
The present trial evaluated the efficacy of homeopathic medicines of Melissa officinalis (MO), Phytolacca decandra (PD), and the combination of both in the treatment of possible sleep bruxism (SB) in children (grinding teeth during sleep).
Patients (n = 52) (6.62 ± 1.79 years old) were selected based on the parents report of SB. The study comprised a crossover design that included 4 phases of 30-day treatments (Placebo; MO 12c; PD 12c; and MO 12c + PD 12c), with a wash-out period of 15 days between treatments.
At baseline and after each phase, the Visual Analogic Scale (VAS) was used as the primary outcome measure to evaluate the influence of treatments on the reduction of SB. The following additional outcome measures were used: a children’s sleep diary with parent’s/guardian’s perceptions of their children’s sleep quality, the trait of anxiety scale (TAS) to identify changes in children’s anxiety profile, and side effects reports. Data were analyzed by ANOVA with repeated measures followed by Post Hoc LSD test.
Significant reduction of SB was observed in VAS after the use of Placebo (-1.72 ± 0.29), MO (-2.36 ± 0.36), PD (-1.44 ± 0.28) and MO + PD (-2.21 ± 0.30) compared to baseline (4.91 ± 1.87). MO showed better results compared to PD (p = 0.018) and Placebo (p = 0.050), and similar result compared to MO+PD (p = 0.724). The sleep diary results and TAS results were not influenced by any of the treatments. No side effects were observed after treatments.
The authors concluded that MO showed promising results in the treatment of possible sleep bruxism in children, while the association of PD did not improve MO results.
Even if one fully subscribed to the principles of homeopathy, this trial raises several questions:
- Why was it submitted and then published in the journal ‘Phytotherapy’. All the remedies were given as C12 potencies. This has nothing to do with phytomedicine.
- Why was a cross-over design chosen? According to homeopathic theory, a homeopathic treatment has fundamental, long-term effects which last much longer than the wash-out periods between treatment phases. This effectively rules out such a design as a means of testing homeopathy.
- MO is used in phytomedicine to induce sleep and reduce anxiety. According to the homeopathic ‘like cures like’ assumption, this would mean it ought to be used homeopathically to treat sleepiness or for keeping patients awake or for making them anxious. How can it be used for sleep bruxism?
Considering all this, I ask myself: should we trust this study and its findings?
What do you think?
Dengue is a viral infection spread by mosquitoes; it is common in many parts of the world. The symptoms include fever, headache, muscle/joint pain and a red rash. The infection is usually mild and lasts about a week. In rare cases it can be more serious and even life threatening. There’s no specific treatment – except for homeopathy; at least this is what many homeopaths want us to believe.
This article reports the clinical outcomes of integrative homeopathic care in a hospital setting during a severe outbreak of dengue in New Delhi, India, during the period September to December 2015.
Based on preference, 138 patients received a homeopathic medicine along with usual care (H+UC), and 145 patients received usual care (UC) alone. Assessment of thrombocytopenia (platelet count < 100,000/mm3) was the main outcome measure. Kaplan-Meier analysis enabled comparison of the time taken to reach a platelet count of 100,000/mm3.
The results show a statistically significantly greater rise in platelet count on day 1 of follow-up in the H+UC group compared with UC alone. This trend persisted until day 5. The time taken to reach a platelet count of 100,000/mm3 was nearly 2 days earlier in the H+UC group compared with UC alone.
The authors concluded that these results suggest a positive role of adjuvant homeopathy in thrombocytopenia due to dengue. Randomized controlled trials may be conducted to obtain more insight into the comparative effectiveness of this integrative approach.
The design of the study is not able to control for placebo effects. Therefore, the question raised by this study is the following: can an objective parameter like the platelet count be influenced by placebo? The answer is clearly YES.
Why do researchers go to the trouble of conducting such a trial, while omitting both randomisation as well as placebo control? Without such design features the study lacks rigour and its results become meaningless? Why can researchers of Dengue fever run a trial without reporting symptomatic improvements? Could the answer to these questions perhaps be found in the fact that the authors are affiliated to the ‘Central Council for Research in Homoeopathy, New Delhi?
One could argue that this trial – yet another one published in the journal ‘Homeopathy’ – is a waste of resources and patients’ co-operation. Therefore, one might even argue, such a study might be seen as unethical. In any case, I would argue that this study is irrelevant nonsense that should have never seen the light of day.
Power Point therapy (PPT) is not what you might think it is; it is not related to a presentation using power point. Power According to the authors of the so far only study of PPT, it is based on the theories of classic acupuncture, neuromuscular reflexology, and systems theoretical approaches like biocybernetics. It has been developed after four decades of experience by Mr. Gerhard Egger, an Austrian therapist. Hundreds of massage and physiotherapists in Europe were trained to use it, and apply it currently in their practice. The treatment can be easily learned. It is taught by professional PPT therapists to students and patients for self-application in weekend courses, followed by advanced courses for specialists.
The core hypothesis of the PPT system is that various pain syndromes have its origin, among others, in a functional pelvic obliquity. This in turn leads to a static imbalance in the posture of the body. This may result in mechanical strain and possible spinal nerve irritation that may radiate and thus affect dermatomes, myotomes, enterotomes, sclerotomes, and neurotomes of one or more vertebra segments. Therefore, treating reflex zones for the pelvis would reduce and possibly resolve the functional obliquity, improve the statics, and thus cure the pain through improved function. In addition, reflex therapy might be beneficial also in patients with unknown causes of back pain. PPT uses blunt needle tips to apply pressure to specific reflex points on the nose, hand, and feet. PPT has been used for more than 10 years in treating patients with musculoskeletal problems, especially lower back pain.
Sounds more than a little weird?
Yes, I agree.
Perhaps we need some real evidence.
The aim of this RCT was to compare 10 units of PPT of 10 min each, with 10 units of standard physiotherapy of 30 min each. Outcomes were functional scores (Roland Morris Disability, Oswestry, McGill Pain Questionnaire, Linton-Halldén – primary outcome) and health-related quality of life (SF-36), as well as blinded assessments by clinicians (secondary outcome).
Eighty patients consented and were randomized, 41 to PPT, 39 to physiotherapy. Measurements were taken at baseline, after the first and after the last treatment (approximately 5 weeks after enrolment). Multivariate linear models of covariance showed significant effects of time and group and for the quality of life variables also a significant interaction of time by group. Clinician-documented variables showed significant differences at follow-up.
The authors concluded that both physiotherapy and PPT improve subacute low back pain significantly. PPT is likely more effective and should be studied further.
I was tempted to say ‘there is nothing fundamentally wrong with this study’. But then I hesitated and, on second thought, found a few things that do concern me:
- The theory on which PPT is based is not plausible (to put it mildly).
- It would have been easy to conduct a placebo-controlled trial of PPT. The authors justify their odd study design stating this: This was the very first randomized controlled trial of PPT. Therefore, the study has to be considered a pilot. For a pivotal study, a clearly defined primary outcome would have been essential. This was not possible, as no previous experience was able to suggest which outcome would be the best. In my view, this is utter nonsense. Defining the primary outcome of a back pain study is not rocket science; there are plenty of validated measures of pain.
- The study was funded by the Foundation of Natural Sciences and Technical Research in Vaduz, Liechtenstein. I cannot find such an organisation on the Internet.
- The senior author of this study is Prof H Walach who won the prestigious award for pseudoscientist of the year 2012.
- Walach provides no less than three affiliations, including the ‘Change Health Science Institute, Berlin, Germany’. I cannot find such an organisation on the Internet.
- The trial was published in a less than prestigious SCAM journal, ‘Forschende Komplementarmedizin‘ – its editor in-chief: Harald Walach.
So, in view of these concerns, I think PPT might not be nearly as promising as this study implies. Personally, I will wait for an independent replication of Walach’s findings.
An impressive 17% of US chiropractic patients are 17 years of age or younger. This figure increases to 39% among US chiropractors who have specialized in paediatrics. Data for other countries can be assumed to be similar. But is chiropractic effective for children? All previous reviews concluded that there is a paucity of evidence for the effectiveness of manual therapy for conditions within paediatric populations.
This systematic review is an attempt to shed more light on the issue by evaluating the use of manual therapy for clinical conditions in the paediatric population, assessing the methodological quality of the studies found, and synthesizing findings based on health condition.
Of the 3563 articles identified through various literature searches, 165 full articles were screened, and 50 studies (32 RCTs and 18 observational studies) met the inclusion criteria. Only 18 studies were judged to be of high quality. Conditions evaluated were:
- attention deficit hyperactivity disorder (ADHD),
- cerebral palsy,
- cranial asymmetry,
- cuboid syndrome,
- infantile colic,
- low back pain,
- obstructive apnoea,
- otitis media,
- paediatric dysfunctional voiding,
- paediatric nocturnal enuresis,
- postural asymmetry,
- preterm infants,
- pulled elbow,
- suboptimal infant breastfeeding,
- suboptimal infant breastfeeding,
- temporomandibular dysfunction,
- upper cervical dysfunction.
Musculoskeletal conditions, including low back pain and headache, were evaluated in seven studies. Only 20 studies reported adverse events.
The authors concluded that fifty studies investigated the clinical effects of manual therapies for a wide variety of pediatric conditions. Moderate-positive overall assessment was found for 3 conditions: low back pain, pulled elbow, and premature infants. Inconclusive unfavorable outcomes were found for 2 conditions: scoliosis (OMT) and torticollis (MT). All other condition’s overall assessments were either inconclusive favorable or unclear. Adverse events were uncommonly reported. More robust clinical trials in this area of healthcare are needed.
There are many things that I find remarkable about this review:
- The list of indications for which studies have been published confirms the notion that manual therapists – especially chiropractors – regard their approach as a panacea.
- A systematic review evaluating the effectiveness of a therapy that includes observational studies without a control group is, in my view, highly suspect.
- Many of the RCTs included in the review are meaningless; for instance, if a trial compares the effectiveness of two different manual therapies none of which has been shown to work, it cannot generate a meaningful result.
- Again, we find that the majority of trialists fail to report adverse effects. This is unethical to a degree that I lose faith in such studies altogether.
- Only three conditions are, according to the authors, based on evidence. This is hardly enough to sustain an entire speciality of paediatric chiropractors.
Allow me to have a closer look at these three conditions.
- Low back pain: the verdict ‘moderate positive’ is based on two RCTs and two observational studies. The latter are irrelevant for evaluating the effectiveness of a therapy. One of the two RCTs should have been excluded because the age of the patients exceeded the age range named by the authors as an inclusion criterion. This leaves us with one single ‘medium quality’ RCT that included a mere 35 patients. In my view, it would be foolish to base a positive verdict on such evidence.
- Pulled elbow: here the verdict is based on one RCT that compared two different approaches of unknown value. In my view, it would be foolish to base a positive verdict on such evidence.
- Preterm: Here we have 4 RCTs; one was a mere pilot study of craniosacral therapy following the infamous A+B vs B design. The other three RCTs were all from the same Italian research group; their findings have never been independently replicated. In my view, it would be foolish to base a positive verdict on such evidence.
So, what can be concluded from this?
I would say that there is no good evidence for chiropractic, osteopathic or other manual treatments for children suffering from any condition.
And why do the authors of this new review arrive at such dramatically different conclusion? I am not sure. Could it perhaps have something to do with their affiliations?
- Palmer College of Chiropractic,
- Canadian Memorial Chiropractic College,
- Performance Chiropractic.
What do you think?
A recent blog-post pointed out that the usefulness of yoga in primary care is doubtful. Now we have new data to shed some light on this issue.
The new paper reports a ‘prospective, longitudinal, quasi-experimental study‘. Yoga group (n= 49) underwent 24-weeks program of one-hour yoga sessions. The control group had no yoga.
Participation was voluntary and the enrolment strategy was based on invitations by health professionals and advertising in the community (e.g., local newspaper, health unit website and posters). Users willing to participate were invited to complete a registration form to verify eligibility criteria.
The endpoints of the study were:
- quality of life,
- psychological distress,
- satisfaction level,
- adherence rate.
The yoga routine consisted of breathing exercises, progressive articular and myofascial warming-up, followed by surya namascar (sun salutation sequence; adapted to the physical condition of each participant), alignment exercises, and postural awareness. Practice also included soft twists of the spine, reversed and balance postures, as well as concentration exercises. During the sessions, the instructor discussed some ethical guidelines of yoga, as for example, non-violence (ahimsa) and truthfulness (satya), to allow the participant to have a safer and integrated practice. In addition, the participants were encouraged to develop their awareness of the present moment and their body sensations, through a continuous process of self-consciousness, keeping a distance between body sensations and the emotional experience. The instructor emphasized the connection between breathing and movement. Each session ended with a guided deep relaxation (yoga nidra; 5–10 min), followed by a meditation practice (5–10 min).
The results of the study showed that the patients in the yoga group experienced a significant improvement in all domains of quality of life and a reduction of psychological distress. Linear regression analysis showed that yoga significantly improved psychological quality of life.
The authors concluded that yoga in primary care is feasible, safe and has a satisfactory adherence, as well as a positive effect on psychological quality of life of participants.
Are the authors’ conclusions correct?
I think not!
Here are some reasons for my judgement:
- The study was far to small to justify far-reaching conclusions about the safety and effectiveness of yoga.
- There were relatively high numbers of drop-outs, as seen in the graph above. Despite this fact, no intention to treat analysis was used.
- There was no randomisation, and therefore the two groups were probably not comparable.
- Participants of the experimental group chose to have yoga; their expectations thus influenced the outcomes.
- There was no attempt to control for placebo effects.
- The conclusion that yoga is safe would require a sample size that is several dimensions larger than 49.
In conclusion, this study fails to show that yoga has any value in primary care.
Oh, I almost forgot: and yoga is also satanic, of course (just like reading Harry Potter!).
Excellent journals always publish excellent science!
If this is what you believe, you might want to read a study of chiropractic just published in the highly respected SCIENTIFIC REPORTS.
The objective of this study was to investigate whether a single session of chiropractic care could increase strength in weak plantar flexor muscles in chronic stroke patients. Maximum voluntary contractions (strength) of the plantar flexors, soleus evoked V-waves (cortical drive), and H-reflexes were recorded in 12 chronic stroke patients, with plantar flexor muscle weakness, using a randomized controlled crossover design. Outcomes were assessed pre and post a chiropractic care intervention and a passive movement control. Repeated measures ANOVA was used to asses within and between group differences. Significance was set at p < 0.05. Following the chiropractic care intervention there was a significant increase in strength (F (1,11) = 14.49, p = 0.002; avg 64.2 ± 77.7%) and V-wave/Mmax ratio (F(1,11) = 9.67, p = 0.009; avg 54.0 ± 65.2%) compared to the control intervention. There was a significant strength decrease of 26.4 ± 15.5% (p = 0.001) after the control intervention. There were no other significant differences. Plantar flexor muscle strength increased in chronic stroke patients after a single session of chiropractic care. An increase in V-wave amplitude combined with no significant changes in H-reflex parameters suggests this increased strength is likely modulated at a supraspinal level. Further research is required to investigate the longer term and potential functional effects of chiropractic care in stroke recovery.
In the article we find the following further statements (quotes in bold, followed by my comments in normal print):
- Data were collected by a team of researchers from the Centre for Chiropractic Research at the New Zealand College of Chiropractic. These researchers can be assumed to be highly motivated in generating a positive finding.
- The entire spine and both sacroiliac joints were assessed for vertebral subluxations, and chiropractic adjustments were given where deemed necessary, by a New Zealand registered chiropractor. As there is now near-general agreement that such subluxations are a myth, the researchers treated a non-existing entity.
- The chiropractor did not contact on a segment deemed to be subluxated during the control set-up and no adjustive thrusts were applied during any control intervention. The patients therefore were clearly able to tell the difference between real and control treatments. Participants were not checked for blinding success.
- Maximum isometric plantarflexion force was measured using an isometric strain gauge. Such measurements crucially depend on the motivation of the patient.
- The grant proposal for this study was reviewed by the Australian Spinal Research Foundation to support facilitation of funding from the United Chiropractic Association. Does this not mean the researchers had a conflict of interest?
- The authors declare no competing interests. Really? They were ardent subluxationists supported by the United Chiropractic Association, an organisation stating that chiropractic is concerned with the preservation and restoration of health, and focuses particular attention on the subluxation, and subscribes to to the obsolete concept of vitalism: we ascribe to the idea that all living organisms are sustained by an innate intelligence, which is both different from and greater than physical and chemical forces. Further, we believe innate intelligence is an expression of universal intelligence.
So, in essence, what we have here is an under-powered study sponsored by vitalists and conducted by subluxationists treating a mythical entity with dubious interventions without controlling for patients’ expectation pretending their false-positive findings are meaningful.
I cannot help wondering what possessed the SCIENTIFIC REPORTS to publish such poor science.
Acupuncture is all over the news today. The reason is a study just out in BMJ-Open.
The aim of this new RCT was to investigate the efficacy of a standardised brief acupuncture approach for women with moderate-tosevere menopausal symptoms. Nine Danish primary care practices recruited 70 women with moderate-to-severe menopausal symptoms. Nine general practitioners with accredited education in acupuncture administered the treatments.
The acupuncture style was western medical with a standardised approach in the pre-defined acupuncture points CV-3, CV-4, LR-8, SP-6 and SP-9. The intervention group received one treatment for five consecutive weeks. The control group received no acupuncture but was offered treatment after 6 weeks. Outcomes were the differences between the two groups in changes to mean scores using the scales in the MenoScores Questionnaire, measured from baseline to week 6. The primary outcome was the hot flushes scale; the secondary outcomes were the other scales in the questionnaire. All analyses were based on intention-to-treat analysis.
Thirty-six patients received the intervention, and 34 were in the control group. Four participants dropped out before week 6. The acupuncture intervention significantly decreased hot flushes, day-and-night sweats, general sweating, menopausal-specific sleeping problems, emotional symptoms, physical symptoms and skin and hair symptoms compared with the control group at the 6-week follow-up. The pattern of decrease in hot flushes, emotional symptoms, skin and hair symptoms was already apparent three weeks into the study. Mild potential adverse effects were reported by four participants, but no severe adverse effects were reported.
The authors concluded that the standardised and brief acupuncture treatment produced a fast and clinically relevant reduction in moderate-to-severe menopausal symptoms during the six-week intervention.
The only thing that I find amazing here is the fact the a reputable journal published such a flawed trial arriving at such misleading conclusions.
- The authors call it a ‘pragmatic’ trial. Yet it excluded far too many patients to realistically qualify for this characterisation.
- The trial had no adequate control group, i.e. one that can account for placebo effects. Thus the observed outcomes are entirely in keeping with the powerful placebo effect that acupuncture undeniably has.
- The authors nevertheless conclude that ‘acupuncture treatment produced a fast and clinically relevant reduction’ of symptoms.
- They also state that they used this design because no validated sham acupuncture method exists. This is demonstrably wrong.
- In my view, such misleading statements might even amount to scientific misconduct.
So, what would be the result of a trial that is rigorous and does adequately control for placebo-effects? Luckily, we do not need to rely on speculation here; we have a study to demonstrate the result:
Background: Hot flashes (HFs) affect up to 75% of menopausal women and pose a considerable health and financial burden. Evidence of acupuncture efficacy as an HF treatment is conflicting.
Objective: To assess the efficacy of Chinese medicine acupuncture against sham acupuncture for menopausal HFs.
Design: Stratified, blind (participants, outcome assessors, and investigators, but not treating acupuncturists), parallel, randomized, sham-controlled trial with equal allocation. (Australia New Zealand Clinical Trials Registry: ACTRN12611000393954)
Setting: Community in Australia.
Participants: Women older than 40 years in the late menopausal transition or postmenopause with at least 7 moderate HFs daily, meeting criteria for Chinese medicine diagnosis of kidney yin deficiency.
Interventions:10 treatments over 8 weeks of either standardized Chinese medicine needle acupuncture designed to treat kidney yin deficiency or noninsertive sham acupuncture.
Measurements: The primary outcome was HF score at the end of treatment. Secondary outcomes included quality of life, anxiety, depression, and adverse events. Participants were assessed at 4 weeks, the end of treatment, and then 3 and 6 months after the end of treatment. Intention-to-treat analysis was conducted with linear mixed-effects models.
Results: 327 women were randomly assigned to acupuncture (n = 163) or sham acupuncture (n = 164). At the end of treatment, 16% of participants in the acupuncture group and 13% in the sham group were lost to follow-up. Mean HF scores at the end of treatment were 15.36 in the acupuncture group and 15.04 in the sham group (mean difference, 0.33 [95% CI, −1.87 to 2.52]; P = 0.77). No serious adverse events were reported.
Limitation: Participants were predominantly Caucasian and did not have breast cancer or surgical menopause.
Conclusion: Chinese medicine acupuncture was not superior to noninsertive sham acupuncture for women with moderately severe menopausal HFs.
My conclusion from all this is simple: acupuncture trials generate positive findings, provided the researchers fail to test it rigorously.
Highly diluted homeopathic remedies are pure placebos! This is what the best evidence clearly shows. Ergo they cannot be shown in a rigorous study to have effects that differ from placebo. But now there is a study that seems to contradict this widely accepted conclusion.
Can someone please help me to understand what is going on?
In this double-blind, placebo-controlled RCT, 60 patients suffering from insomnia were treated either individualised homeopathy (IH) or placebo for 3 months. Patient-administered sleep diary and Insomnia Severity Index (ISI) were used the primary and secondary outcomes respectively, measured at baseline, and after 3 months.
Five patients dropped out (verum:2,control:3).Intention to treat sample (n=60) was analysed. Trial arms were comparable at baseline. In the verum group, except sleep diary item 3 (P= 0.371), rest of the outcomes improved significantly (all P < 0.01). In the control group, there were significant improvements in diary item 6 and ISI score (P < 0.01) and just significant improvement in item 5 (P= 0.018). Group differences were significant for items 4, 5 and 6(P < 0.01) and just significant (P= 0.014) for ISI score with moderate to large effect sizes; but non-significant (P > 0.01) for rest of the outcomes.
The authors concluded that in this double-blind, randomized, prospective, placebo-controlled, two parallel arms clinical trial conducted on 60 patients suffering from insomnia, there was statistically significant difference measured in sleep efficiency, total sleep time, time in bed, and ISI score in favour of homeopathy over placebo with moderate to large effect sizes. Group differences were non-significant for rest of the outcomes(i.e. latency to fall asleep, minutes awake in middle of night and minutes awake too early). Individualized homeopathy seemed to produce significantly better effect than placebo. Independent replications and adequately powered trials with enhanced methodological rigor are warranted.
I have studied this article in some detail; its methodology is nicely and fully described in the original paper. To my amazement, I cannot find a flaw that is worth mentioning. Sure, the sample was small, the treatment time short, the outcome measure subjective, the paper comes from a dubious journal, the authors have a clear conflict of interest, even though they deny it – but none of these limitations has the potential to conclusively explain the positive result.
In view of what I stated above and considering what the clinical evidence so far tells us, this is most puzzling.
A 2010 systematic review authored by proponents of homeopathy included 4 RCTs comparing homeopathic medicines to placebo. All involved small patient numbers and were of low methodological quality. None demonstrated a statistically significant difference in outcomes between groups.
My own 2011 not Medline-listed review (Focus on Alternative and Complementary Therapies Volume 16(3) September 2011 195–199) included several additional studies. Here is its abstract:
The aim of this review was the critical evaluation of evidence for the effectiveness of homeopathy for insomnia and sleep-related disorders. A search of MEDLINE, AMED, CINAHL, EMBASE and Cochrane Central Register was conducted to find RCTs using any form of homeopathy for the treatment of insomnia or sleep-related disorders. Data were extracted according to pre-defined criteria; risk of bias was assessed using Cochrane criteria. Six randomised, placebo-controlled trials met the inclusion criteria. Two studies used individualised homeopathy, and four used standardised homeopathic treatment. All studies had significant flaws; small sample size was the most prevalent limitation. The results of one study suggested that homeopathic remedies were superior to placebo; however, five trials found no significant differences between homeopathy and placebo for any of the main outcomes. Evidence from RCTs does not show homeopathy to be an effective treatment for insomnia and sleep-related disorders.
It follows that the new trial contradicts previously published evidence. In addition, it clearly lacks plausibility, as the remedies used were highly diluted and therefore should be pure placebos. So, what could be the explanation of the new, positive result?
As far as I can see, there are the following possibilities:
- some undetected/undisclosed bias,
- homeopathy works after all.
I would be most grateful, if someone could help solving this puzzle for me (if needed, I can send you the full text of the new article for assessment).
The objective of this ‘real world’ study was to evaluate the effectiveness of integrative medicine (IM) on patients with coronary artery disease (CAD) and investigate the prognostic factors of CAD in a real-world setting.
A total of 1,087 hospitalized patients with CAD from 4 hospitals in Beijing, China were consecutively selected between August 2011 and February 2012. The patients were assigned to two groups:
- Chinese medicine (CM) plus conventional treatment, i.e., IM therapy (IM group). IM therapy meant that the patients accepted the conventional treatment of Western medicine and the treatment of Chinese herbal medicine including herbal-based injection and Chinese patent medicine as well as decoction for at least 7 days in the hospital or 3 months out of the hospital.
- Conventional treatment alone (CT group).
The endpoint was a major cardiac event [MCE; including cardiac death, myocardial infarction (MI), and the need for revascularization].
A total of 1,040 patients finished the 2-year follow-up. Of them, 49.4% received IM therapy. During the 2-year follow-up, the total incidence of MCE was 11.3%. Most of the events involved revascularization (9.3%). Cardiac death/MI occurred in 3.0% of cases. For revascularization, logistic stepwise regression analysis revealed that age ⩾ 65 years [odds ratio (OR), 2.224], MI (OR, 2.561), diabetes mellitus (OR, 1.650), multi-vessel lesions (OR, 2.554), baseline high sensitivity C-reactive protein level ⩾ 3 mg/L (OR, 1.678), and moderate or severe anxiety/depression (OR, 1.849) were negative predictors (P<0.05); while anti-platelet agents (OR, 0.422), β-blockers (OR, 0.626), statins (OR, 0.318), and IM therapy (OR, 0.583) were protective predictors (P<0.05). For cardiac death/MI, age ⩾ 65 years (OR, 6.389) and heart failure (OR, 7.969) were negative predictors (P<0.05), while statin use (OR, 0.323) was a protective predictor (P<0.05) and IM therapy showed a beneficial tendency (OR, 0.587), although the difference was not statistically significant (P=0.218).
The authors concluded that in a real-world setting, for patients with CAD, IM therapy was associated with a decreased incidence of revascularization and showed a potential benefit in reducing the incidence of cardiac death or MI.
What the authors call ‘real world setting’ seems to be a synonym of ‘lousy science’, I fear. I am not aware of good evidence to show that herbal injections and concoctions are effective treatments for CAD, and this study can unfortunately not change this. In the methods section of the paper, we read that the treatment decisions were made by the responsible physicians without restriction. That means the two groups were far from comparable. In their discussion section, the authors state; we found that IM therapy was efficacious in clinical practice. I think that this statement is incorrect. All they have shown is that two groups of patients with similar diagnoses can differ in numerous ways, including clinical outcomes.
The lessons here are simple:
- In clinical trials, lack of randomisation (the only method to create reliably comparable groups) often leads to false results.
- Flawed research is currently being used by many proponents of SCAM (so-called alternative medicine) to mislead us about the value of SCAM.
- The integration of dubious treatments into routine care does not lead to better outcomes.
- Integrative medicine, as currently advocated by SCAM-proponents, is a nonsense.