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

methodology

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The aim of this RCT was to examine symptom responses resulting from a home-based reflexology intervention delivered by a friend/family caregiver to women with advanced breast cancer undergoing chemotherapy, targeted, and/or hormonal therapy.

Patient-caregiver dyads (N = 256) were randomized to 4 weekly reflexology sessions or attention control. Caregivers in the intervention group were trained by a reflexology practitioner in a 30-min protocol. During the 4 weeks, both groups completed telephone symptom assessments using the M. D. Anderson Symptom Inventory. Those who completed at least one weekly call were included in this secondary analysis (N = 209). Each symptom was categorized as mild, moderate, or severe using established interference-based cut-points. Symptom response meant an improvement by at least one category or remaining mild. Symptom responses were treated as multiple events within patients and analysed using generalized estimating equations technique.

Reflexology was more successful than attention control in producing responses for pain with no significant differences for other symptoms. In the reflexology group, greater probability of response across all symptoms was associated with lower number of comorbid condition and lower depressive symptomatology at baseline. Compared to odds of responses on pain (chosen as a referent symptom), greater odds of symptom response were found for disturbed sleep and difficulty remembering with older aged participants.

Adjusted odds ratios (ORs) of symptom responses for reflexology arm versus control (adjusted for age, number of comorbid conditions, depressive symptoms at baseline, and treatment type: chemotherapy with or without hormonal therapy versus hormonal therapy alone)
Symptom                                 OR      (95% CI)        p value
Fatigue                                    1.76      (0.99, 3.12)       0.06
Pain                                         1.84      (1.05, 3.23)       0.03
Disturbed sleep                         1.45      (0.76, 2.77)       0.26
Shortness of breath                   0.58      (0.26, 1.30)       0.19
Remembering                           0.96      (0.51, 1.78)       0.89
Lack of appetite                        1.05      (0.45, 2.49)       0.91
Dry mouth                               1.84      (0.86, 3.94)       0.12
Numbness and tingling              1.40     (0.75, 2.64)        0.29
Depression                              1.38      (0.78, 2.43)       0.27

The authors concluded that home-based caregiver-delivered reflexology was helpful in decreasing patient-reported pain. Age, comorbid conditions, and depression are potentially important tailoring factors for future research and can be used to identify patients who may benefit from reflexology.

This is certainly one of the more rigorous studies of reflexology. It is well designed and reported. How valid are its findings? To a large degree, this seems to depend on the somewhat unusual statistical approach the investigators employed:

Baseline characteristics were summarized by study group for outcome values and potential covariates. The unit of analysis was patient symptom; multiple symptoms were treated as nested within the patient being analyzed, using methodology described by Given et al. [24] and Sikorskii et al. [17]. Patient symptom responses were treated as multiple events, and associations among responses to multiple symptoms within patients were accounted for by specifying the exchangeable correlation structure in the generalized estimating equations (GEE) model. The GEE model was fitted using the GENMOD procedure in SAS 9.4 [25]. A dummy symptom variable with 9 levels was included in the interaction with the trial arm to differentiate potentially different effects of reflexology on different symptoms. Patient-level covariates included age, number of comorbid conditions, type of treatment (chemotherapy or targeted therapy with or without
hormonal therapy versus hormonal therapy only), and the CES-D score at baseline. Odds ratios (ORs) and their 95% confidence intervals (CIs) were obtained for the essential parameter of study group for each symptom.

Another concern is the fact that the study crucially depended on the reliability of the 256 carers. It is conceivable, even likely, I think, that many carers from both groups were less than strict in adhering to the prescribed protocol. This might have distorted the results in either direction.

Finally, the study was unable to control for the possibly substantial placebo response that a reflexology massage unquestionably provokes. Therefore, we are not able to tell whether the observed effect is due to the agreeable, non-specific effects of touch and foot massages, or to the postulated specific effects of reflexology.

The objective of this RCT was to compare the effects of

  • spinal thrust-manipulation + electrical dry needling + various medications (TMEDN-group)
  • to non-thrust peripheral joint/soft-tissue mobilization + exercise + interferential current + various medications(NTMEX-group)

on pain and disability in patients with subacromial pain syndrome (SAPS).

Patients with SAPS were randomized into the TMEDN group (n=73) or the NTMEX group (n=72). Primary outcomes included the shoulder pain and disability index (SPADI) and the numeric pain rating scale (NPRS). Secondary outcomes included Global Rating of Change (GROC) and medication intake. The treatment period was 6 weeks; with follow-up at 2 weeks, 4 weeks, and 3 months.

At 3 months, the TMEDN group experienced significantly greater reductions in shoulder pain and disability compared to the NTMEX group. Effect sizes were large in favour of the TMEDN group. At 3 months, a greater proportion of patients within the TMEDN group achieved a successful outcome (GROC≥+5) and stopped taking medication.

The authors concluded that cervicothoracic and upper rib thrust-manipulation combined with electrical dry needling resulted in greater reductions in pain, disability and medication intake than non-thrust peripheral joint/soft-tissue mobilization, exercise and interferential current in patients with SAPS. These effects were maintained at 3 months.

The authors of this trial have impressive looking affiliations:

  • American Academy of Manipulative Therapy Fellowship in Orthopaedic Manual Physical Therapy, Montgomery, AL.
  • Montgomery Osteopractic Physiotherapy & Acupuncture Clinic, Montgomery, AL.
  • Research Physical Therapy Specialists, Columbia, SC.
  • Department of Physical Therapy, Occupational Therapy, Rehabilitation and Physical Medicine, Universidad Rey Juan Carlos, Alcorcón, Spain.
  • Cátedra de Clínica, Investigación y Docencia en Fisioterapia: Terapia Manual, Punción Seca y Ejercicio, Universidad Rey Juan Carlos, Alcorcón, Madrid, Spain.
  • Copper Queen Community Hospital, Bisbee, AZ.
  • BenchMark Physical Therapy, Atlanta, GA.
  • Eastside Medical Care Center, El Paso, TX.
  • Department of Physical Therapy, Georgia State University, Atlanta, GA.
  • Tybee Wellness & Osteopractic, Tybee Island, Georgia, GA.

If one expected a well-designed study from all this collective expertise, one would have been disappointed.

Any such clinical trial should be answering a simple question: is therapy XX effective? It is about pinning an observed effect on to a treatment. It is about establishing cause and effect. It is about finding an answer to a clinically relevant question.

The above study does none of that. Even if we accepted its result as valid, it could be interpreted as meaning one of many different things, for instance:

  1. Acupuncture was effective.
  2. Dry needling was effective.
  3. The electrical current was effective.
  4. Mobilisation made things worse.
  5. Exercise made things worse.
  6. one or multiple positive or negative interactions between the therapies.
  7. The drugs in the experimental group were more effective than those taken by controls.
  8. The experimental group adhered to their drug prescriptions better than controls.
  9. Any mixture of the above.

So, the reader of this paper can chose which of the interpretations he or she prefers. I suggest that:

  • Any researcher who designs a foreseeably nonsensical trial should go back to school.
  • Any ethics committee that passes such a study needs to retire.
  • Any funder who gives money for it wastes scarce resources.
  • Any reviewer who recommends publication needs to learn about trial design.
  • Any editor who publishes such a trial needs to go.

The point I am trying to make is that conducting a clinical trial comes with responsibilities. Poorly designed studies are not just a waste of resources, they are a disservice to patients, they undermine the public’s trust in science and they are unethical.

I want to thank our friend ‘OLD BOB’ for alerting me to Patrick Holford’s comment on a recent trial of vitamin C for COVID-19. Here are three short quotes from Holford:

… Overall, 5 out 26 people (19%) died in the vitamin C group while 10 out of 28 (36%) receiving the placebo died. That means that vitamin C almost halved the number of deaths. Those on vitamin C were 60% more likely to survive.

… Of those most critically ill, 4 people (18%) in the vitamin C group died, compared to 10 (50%) in the placebo group. That’s two-thirds less deaths. Statistically this meant that of those most critically ill who were given vitamin C, they were 80% less likely to die…

… now there is another proven treatment – vitamin C…

And here is the abstract of the actual trial Holford refers to:

Background: No specific medication has been proven effective for the treatment of patients with severe coronavirus disease 2019 (COVID-19). Here, we tested whether high-dose vitamin C infusion was effective for severe COVID-19.

Methods: This randomized, controlled, clinical trial was performed at 3 hospitals in Hubei, China. Patients with confirmed severe acute respiratory syndrome coronavirus 2 (SARS-CoV-2) infection in the ICU were randomly assigned in as 1:1 ratio to either the high-dose intravenous vitamin C (HDIVC) or the placebo. HDIVC group received 12 g of vitamin C/50 ml every 12 hours for 7 days at a rate of 12 ml/hour, and the placebo group received bacteriostatic water for injection in the same way. The primary outcome was invasive mechanical ventilation-free days in 28 days(IMVFD28). Secondary outcomes were 28-day mortality, organ failure, and inflammation progression.

Results: Only fifty-six critical COVID-19 patients were ultimately recruited due to the early control of the outbreak. There was no difference in IMVFD28 between two groups. During the 7-day treatment period, patients in the HDIVC group had a steady rise in the PaO2/FiO2 (day 7: 229 vs. 151 mmHg, 95% CI 33 to 122, P=0.01). Patients with SOFA scores ≥3 in the HDIVC group exhibited a trend of reduction in 28-day mortality (P=0.06) in univariate survival analysis. IL-6 in the HDIVC) group was lower than that in the placebo group (19.42 vs. 158.00; 95% CI -301.72 to -29.79; P=0.04) on day 7.

Conclusion: This pilot trial showed that HDIVC might show a potential signal of benefit for critically ill patients with COVID-19, improving oxygenation even though it failed to improve IMVFD28.

The following points are, I think, worth mentioning:

  • This was, according to its authors, a PILOT study.
  • It was far too small (n=56) to provide reliable results on mortality.
  • The trial authors know that and interpret their findings with sufficient caution.
  • The primary endpoint, the IMVFD28, showed NO significant difference between the groups.
  • The secondary endpoint: HDIVC infusion exhibited a non-significant trend of reduction in 28-day mortality (P=0.06).
  • In more severe patients (SOFA score ≥3), univariate survival analysis and Cox regression showed a similar results (P=0.07, HR, 0.32 [95% CI 0.10-1.06]).

And what does all of this mean? It means that, in this pilot study, vitamin C failed to produce a significant result. Only in a subgroup analysis related to a secondary endpoint was there a slight advantage of vitamin C. This effect is, of course, interesting and needs further investigation (I am sure that is happening as we speak). It could have some clinical significance but, just as likely, it could just be due to chance. There is not way of knowing which is which.

In other words, to hype the findings and to even make statements such as ‘now there is another proven treatment, vitamin C’ is not just exaggerated, it is irresponsible.

This begs the question: why does Mr Holford do it? In case you don’t already know about this man, go on the Internet, and you will quickly find possible answers. Here is an excerpt from his Wiki page which might give you a clue:

Patrick Holford is a British author and entrepreneur who endorses a range of controversial vitamin tablets. As an advocate of alternative nutrition and diet methods, he appears regularly on television and radio in the UK and abroad. He has 36 books in print in 29 languages. His business career promotes a wide variety of alternative medical approaches such as orthomolecular medicine, many of which are considered pseudoscientific by mainstream science and medicine.

Holford’s claims about HIV and autism are not in line with modern medical thought, and have been criticised for putting people in danger and damaging public health.

In 2006 Holford was discovered to be using his PR advisor to delete critical content from his Wikipedia page…

Holford has been the subject of criticism for his promotion of medically dubious techniques and products including hair analysis, his support of the now struck off doctor Andrew Wakefield, and advocating the use of “non-drug alternatives for mental health” for which he has been given an award by the Church of Scientology-backed Citizens Commission on Human Rights.

SAY NO MORE!

Or perhaps not?
Here is the announcement:

Research by a reputable independent research company done for Securivita a German insurance company shows that those receiving homeopathic care were much better off. Over 15,700 patients were involved in the study which also used a comparison group.

The study showed that in a wide range of patients with various pathological problems that if they had homeopathic care they faired dramatically better than those just getting conventional medicine.

Children having homeopathy treatment from birth, were particularly healthier and with less problems. Over the three year study period, the number of children needing antibiotics decreased by 16.7 per cent in the homeopathy group, whereby it increased by 73.9 per cent in the conventional medical comparison group!

The number of hospitalizations in the comparison group increased by 32.6 per cent whereby in the homeopathy treatment group it decreased by 9.8 per cent!

Adults and children treated homoeopathically had dramatic improvements in allergies, dermatitis, asthma, just to name a few.

These are just a few examples of the remarkable benefits of homeopathic treatment outlined in the study by by the Leipzig Health Forum , an independent analytical institute specializing in health services conducted for Securvita Krankenkasse Insurer.

“We don’t need fewer, but more homeopathic doctors who will continue on this successful path,” says Götz Hachtmann , director of the health insurance company Securvita.

The study is in German and can be found here.

____________________________

Blessed are those who don’t read German (at least in this instance)!

As I am not amongst the blessed, I ought to tell you a bit about the ‘massive’ study. The OHR, the ‘OFFICIAL HOMEOPATHIC RESOURCE’ (btw what makes the OHR ‘official’?) claims that the study can be found here. The OHR is evidently not well enough resourced for translating the German text into English; if they were, they would know that the link goes not to a ‘study’ but to some kind of a glossy marketing brochure about the ‘study’ (there is no actual published scientific paper on the ‘study’). It provides hardly any relevant information; all we learn is that 15 700 individuals who regularly consulted homeopathic physicians were compared over a three year period to an equally sized control group who did not consult homeopathic doctors… And that’s essentially it! No further relevant details are offered.

By contrast, quite a bit of information is offered about the findings, for instance:

  • In the homeopathy group, the hospitalisation rate of depressive patients dropped by 10%, while it increased in controls by 33%.
  • The days off work dropped by 17% vs an increase in controls of 17%.
  • The use of antibiotics decreased by 17% vs an increase of 74%.

And how do they explain these differences?

Yes, you guessed it:

they are due to homeopathy!

One does not need to have a perfumer’s nose to smell a few badly decomposing rats here, for example:

  1. We do not learn how many variables were tested in this ‘study’. Therefore, it is likely that the ‘results’ provided are the positive ones, while the not so positive potential effects of homeopathy remained unmentioned. Perhaps the death rate was higher in the homeopathy group? Perhaps they suffered more heart attacks? Perhaps they had a lower quality of life? Perhaps they caused more costs? Perhaps they committed more suicides? etc. etc.
  2. Even more obvious is the stench of selection bias. The individuals in the homeopathy group were clearly different from the controls to start with. They might have been more health conscious. They clearly were more cautious about antibiotics. They might have been of better general health. They might have been younger. They could have contained more women. They might have been more afraid of going into a hospital. They might have been keener to attend work. In fact, the only variable in which the two groups were comparable is sample size.

Even if we eventually we see this ‘study’ published in a peer-reviewed journal with full methodological details etc., it will not allow even the smartest spin-doctor to establish cause and effect. Its findings would not be more conclusive than those of previously discussed attempts to produce positive evidence for homeopathy. The ‘positive’ findings could have been the result of hundreds of causes, none of which are related to homeopathy.

In a nutshell: this new German ‘study’ is a textbook example for arguing in favour of conducting proper research rather that rampant pseudo-research.

But I must not always be so negative!!!

So, let me try to point out the positive sides of this ‘study’:

The ‘massive independent study’ is a true masterpiece of advertising and marketing for both Securivita and homeopathy.

Well done guys!

I am proud of you!

  • That’s exactly the stuff needed for successfully misleading the public.
  • That’s precisely the info required to increase your cash flow.
  • That’s helpful ‘research’ for convincing politicians.
  • That’s definitely the type of baloney to impresses the Ullmanns of this world.
  • That’s even the sort of ‘science’ which the ‘OFFICIAL HOMEOPATHIC RESOURCE’ cannot recognise for what it truly is:

invalid junk.

This recent review claimed to evaluate the evidence on the use of human and veterinary homeopathy, evidence level 1a studies were considered. Focusing on the external evidence on the use of homeopathy in infections, some evidence level 1a, 1b, 2c studies, and a case report, are described in more detail.

In conclusion, evidence for the effectiveness of human and veterinary homeopathy in general, and in particular, of homeopathic treatment for infections, is available. Especially, individualized homeopathy demonstrates effects at all quality levels according to Cochrane criteria, even in the methodologically high-quality studies. As in most areas of veterinary medicine and medicine, further good/excellent studies are necessary. In compliance with the principles of homeopathy, further methodologically high-quality trials focusing on the homeopathic treatment of infections are the next logical step. The selection of the simile (individually fitting homeopathic medicinal product) by appropriately trained homeopathic doctors/veterinarians is essential for the effectiveness of homeopathy. Implementation of studies at university facilities is a prerequisite for quality assurance. Consequently, further integration of homeopathy at universities is a necessary requirement for the patients’ best interests.

Who wrote this bizarre paper?

The authors who state to have no conflicts of interest are P Weiermayer 1M Frass 2T Peinbauer 3L Ellinger 4

  • 1Tierärztin, Tierarztpraxis Dr. Weiermayer, Diplom der Europ. Akademie für Veterinärhomöopathie (EAVH), Fachtierärztin für Homöopathie, Sprecherin der Sektion Forschung der Wissensch. Gesellsch. für Homöopathie (WissHom), Präsidentin ÖGVH, Wien, Österreich.
  • 2Facharzt für Innere Medizin und Internistische Intensivmedizin, em. Professor für Innere Medizin der Medizinischen Universität Wien, Diplom der Österreichischen Ärztekammer (ÖÄK) für Homöopathie sowie für Begleitende Krebsbehandlung, Wien, Österreich.
  • 3Arzt für Allgemeinmedizin, ÖÄK-Diplom für Homöopathie, Universitätslektor für Allgemeinmedizin und Modulbeauftragter für Komplementärmedizin, Medizinische Fakultät, Johannes Kepler Universität Linz, Österreich.
  • 4Tierärztin, Centaurea, Apeldoorn, Holland.

This already explains quite a lot, I think.

The paper itself is in German, so I will try to make some sense of part of it for you.

In their ‘methods section’, the authors explain that they evaluated meta-analyses and systematic reviews (SRs) of homeopathy for various conditions. Furthermore, they considered the ‘1st and 2nd’ NHMRC reports. Specifically for the question whether homeopathy is the answer to antibiotic resistance, the authors also considered RCTs, observational studies, heath service research and even case-studies. The authors then elaborate at length on the assumptions of homeopathy, on legal issues and on the nature of evidence-based medicine all of which I disregard for the moment (suffice to say that this material has been often and better reviewed before).

When finally discussing the evidence on homeopathy for human conditions, the authors state that, up until 2014, six comprehensive SRs had been published. In their opinion, these are the following 6 papers:

  1. Kleijnen, J., Knipschild, P., Ter Riet, G. (1991): Clinical trials
    of homeopathy. BMJ 302(6772): 316-23.
  2. Linde, K., Clausius, N., Ramirez, G., Melchart, D., Eitel, F.,
    Hedges, L.V., Jonas, W.B. (1997): Are the clinical effects of
    homeopathy placebo effects? A meta-analysis of placebo-controlled trials. Lancet 350(9081): 834–843.
  3. Linde, K., Scholz, M., Ramirez, G., Clausius, N., Melchart,
    D., Jonas, W.B. (1999): Impact of study quality on outcome
    in placebo-controlled trials of homeopathy. J Clin Epidemiol 52(7): 631–636.
  4. Cucherat, M., Haugh, M.C., Gooch, M., Boissel, J.P. (2000): Evidence of clinical efficacy of homeopathy. A meta-analysis of clinical trials. HMRAG. Homeopathic Medicines Research Advisory Group. Eur J Clin Pharmacol 56(1): 27–33.
  5. Mathie, R.T., Lloyd, S.M., Legg, L.A., Clausen, J., Moss, S.,Davidson, J.R.T., Ford, I. (2014a): Randomised placebocontrolled trials of individualised homeopathic treatment: systematic review and meta-analysis. Syst Rev 3: 142.
  6. Shang, A., Huwiler-Müntener, K., Nartey, L., Jüni, P., Dörig, S., Sterne, J.A.C., Pewsner, D., Egger, M. (2005): Are the clinical effects of homeopathy placebo effects? Comparative study of placebo-controlled trials of homeopathy and allopathy. Lancet 366(9487): 726–32.

(As it happens, I have reviewed these papers here and come to very different conclusions)

Without bothering about a critical assessment of these papers, the authors report that all arrived at a positive conclusion, except the last one. They then claim that the ‘1st’ NHMRC report was partly positive but was initially suppressed by the Australian government. Instead it was replaced with the 2nd NHMRC report which was designed to arrive at a wholly negative conclusion. Likewise, the ‘EASAC Statement’ neglected some of the available positive evidence. These facts, the authors believe, discredits all of these negative reports.

The authors then discuss the various reviews by Mathie et al and point out that, in their view, these papers are superior to all other documents as they arrive at very clearly positive conclusions.

Next the authors focus on the field of veterinary homeopathy, while admitting weaker and weaker evidence, inclusing case-reports. This is also where I lost the will to live and gave up my detailed criticism of the text; the task is too tedious and simply not worth it, I felt.

In summary, here are few points relating to the human evidence:

The authors seem to have no intention of conducting an objective, systematic review. Such a project is essentially based on two principles. Firstly, it needs to include all eligible evidence according to pre-defined criteria. Secondly, it must include a critical evaluation of the admitted evidence. This review fails on both of these principles.

There are virtually dozens of systematic reviews which the authors decided to ignore. Here are just six of them:

  1. … homoeopathy as a whole may be considered as a placebo treatment.
  2. We tested whether p-curve accurately rejects the evidential value of significant results obtained in placebo-controlled clinical trials of homeopathic ultramolecular dilutions. Our results suggest that p-curve can accurately detect when sets of statistically significant results lack evidential value.
  3. We found no evidence to support the efficacy of homeopathic medicinal products
  4. … no firm conclusions regarding the effectiveness and safety of homeopathy for the treatment of IBS can be drawn.
  5. Due to both qualitative and quantitative inadequacies, proofs supporting individualized homeopathy remained inconclusive.
  6. … the use of homeopathy currently cannot claim to have sufficient prognostic validity where efficacy is concerned.

Why do they do it? A reasonable reply to this question might be, because their findings did not fit the preconceived ideas of the authors. This omission alone makes the article little more than a poorly conceived marketing brochure.

Even more important is the second omission. The paper  lacks any kind of critical evaluation of the included evidence. On the contrary, the authors praise the evidence that generated what they think was a positive result (even in cases where the actual result was not all that positive; for instance: A meta-analysis of all extractable data leads to rejection of our null hypothesis, but analysis of a small sub-group of reliable evidence does not support that rejection. Reliable evidence is lacking in condition-specific meta-analyses, precluding relevant conclusions) and bash all negative findings. This goes as far as perpetuating untruth about the two NHMRC reports: what they call the 1st report was a draft that had been rejected because it was deemed to be of sub-standard quality. What is here called the ‘2nd’ report is thus the only valid document ever published. Similarly, the authors pretend that the Mathie reviews were all clearly positive and fail to mention even the most obvious problems with these articles, such as the facts that Mathie was paid by a homeopathy-lobby group or that even he included important caveats in his conclusions.

As to the focus of the review, the question whether homeopathy might be a solution to antibiotic resistance, the authors found virtually no compelling evidence from trials directly comparing antibiotics with homeopathy. This seems to bother the authors little – they conclude that “the data demonstrate the potential of a significant reduction of antibiotic usage through homeopathic treatments”. They seem to have reached this conclusion by turning a blind eye to all the evidence that does not fit their preconceived idea.

As the paper is published in German and in a journal which hardly anyone will ever read, one could easily argue that none of all this does really matter because it is merely a storm in a very small tea cup. Perhaps that’s true. But this paper nevertheless might attain some significance because it is already being heavily promoted by the homeopathy lobby. And no doubt, it will thus be cited in the English literature which, in turn, will be read by people who do not read German, unable to check the original and are thus likely to believe the nonsense promoted by Frass and friends.

For this reason, I want to conclude by making it quite clear that

this ‘review’ is a dilettante attempt to white-wash the evidence on homeopathy and mislead the public.

 

Researchers from the Department of Physiotherapy, Guru Jambheshwar University of Science and Technology, Hisar, Haryana, India, and the Mother Teresa Saket College of Physiotherapy, Saket, Panchkula, Haryana, India, have just published a systematic review which is remarkable in several ways. Let me therefore present to you the abstract unaltered:

Background: Spinal pain or misalignment is a very common disorder affecting a significant number of populations resulting in substantial disability and economic burden. Various manual therapeutic techniques such as spinal manipulations and mobilizations can be used to treat and manage pain and movement dysfunctions such as spinal mal-alignments and associated complications. These manual therapeutic techniques can affect the cardiovascular parameters.

Objective: The objective of this systematic review and meta-analysis is to assess the effect of spinal manipulation and mobilization on cardiovascular parameters.

Methods: We conducted a systematic review and meta-analysis to assess the effects of spinal mobilization and manipulation on cardiovascular responses. Mean changes in Systolic Blood Pressure (SBP), Diastolic Blood Pressure (DBP) and Heart Rate (HR) were primary outcome measures. RevMan 5.3 software was used for the meta-analyses. Quality of the included studies was assessed by PEDro Rating scale. Risk of bias was assessed by Cochrane collaboration tool of risk of bias.

Results: Results of meta-analysis showed that there was statistically significant decrease in SBP ( MD=-4.56 , 95% CI=-9.20 , 0.08; p≤0.05 ) with moderate heterogeneity ( I2=75% , p<0.0002 ) in experimental group as compared to control group. There was statistically non-significant decrease in DBP ( MD=-1.96 , 95% CI=-4.60 , 0.69; p=0.15 ) with high heterogeneity ( I2=91% , p<0.00001 ), Change HR was statistically non-significant ( MD=-0.24 , 95% CI=-3.59 , 3.11; p=0.89 ) with moderate heterogeneity ( I2=60% , p=0.01 ). Exclusion of short duration studies in sensitivity analysis revealed a statistically significant change in DBP ( MD=-0.94 , 95% CCI=-1.85 , -0.03 ; p=0.04 ). However, the result was statistically non-significant for HR after sensitivity analysis.

Conclusion: Spinal manipulations and mobilizations may result in significant decrease of systolic as well as diastolic Blood Pressure.

After reading the full paper, I was uncertain whether to laugh or to cry. Then I decided for the former option.

Any paper that starts with the statement ‘spinal pain or misalignment is a very common disorder affecting a significant number of populations resulting in substantial disability and economic burden‘ can only be a hoax! In case you are uncertain about the reason of my amusement: spinal pain is not the same as spinal misalignment, and spinal misalignment (in the sense it is used here) is the figment of the imagination of a 18 carat charlatan called DD Palmer.

The rest of the article offers more superb hilarity: the authors write, for instance, that spinal malalignments (such as scoliosis) are mainly caused by body’s abnormal posture, asymmetries in bone growth and abnormalities of neuromuscular system. Scoliosis is an abnormal lateral curvature of the spine, not a spinal malalignment and certainly not one that can be treated with spinal manipulation.

Then the authors state that spinal pain and malalignment mainly occur due to structure deterioration, altered biomechanics and abnormal posture. Workplace physical and psychosocial factors, emotional problems, smoking, poor job satisfaction, awkward posture and poor work environment can be the possible risk factors for spinal pain and malalignment. This leads to various musculoskeletal, psychosomatic, cardiovascular and respiratory dysfunctions which affect the functional capacity of the patient as well as quality of life. Oh really?

So, the findings of the authors’ meta-analysis do suggest a tiny effect on blood pressure.

Compared to what?

In the paper, the review authors repeatedly try to make us believe it is compared to placebo. However, this is not true; mostly it was compared to no treatment.

Was the hypotensive effect verified in hypertensive patients?

No, it was measured mostly in healthy volunteers.

Is the effect clinically relevant?

No, I don’t think so!

Is it comparable to or better than the one achievable with established treatments for hypertension?

No! In fact it is much smaller.

Does that bother the authors?

No, on the contrary, they state that in this meta-analysis, spinal manipulation and mobilization resulted in statistically significant reduction in SBP. Therefore, it can be used as an adjuvant therapy for the management of hypertension.

Were the studies using spinal manipulation as an adjuvant therapy?

No, mostly not.

Is the effect lasting long enough to be relevant for the management of hypertension?

No.

I better stop here because already my whole body hurts from laughing so much. Please, do read the full text, if you are in need of some comic relief.

And, I almost forgot: many thanks to the Indian researchers for this hilarious hoax!

Or did you perhaps mean all that seriously?

This recent Cochrane review assessed the effects of so-called alternative medicine (SCAM) for post-caesarean pain. Randomised clinical trials (RCTs), including quasi-RCTs and cluster-RCTs, comparing SCAM, alone or associated with other forms of pain relief, versus other treatments or placebo or no treatment, for the treatment of post-CS pain were included.

A total of 37 studies (3076 women) investigating 8 different SCAM therapies for post-CS pain relief were found. There was substantial heterogeneity among the trials. The primary outcome measures were pain and adverse effects. Secondary outcome measures included vital signs, rescue analgesic requirement at 6 weeks after discharge; all of which were poorly reported or not reported at all.

Acupuncture/acupressure

The quality of the RCTs was low. Whether acupuncture or acupressure (versus no treatment) or acupuncture or acupressure plus analgesia (versus placebo plus analgesia) have any effect on pain. Acupuncture or acupressure plus analgesia (versus analgesia) may reduce pain at 12 hours (standardised mean difference (SMD) -0.28, 95% confidence interval (CI) -0.64 to 0.07; 130 women; 2 studies; low-certainty evidence) and 24 hours (SMD -0.63, 95% CI -0.99 to -0.26; 2 studies; 130 women; low-certainty evidence). It is uncertain whether acupuncture or acupressure (versus no treatment) or acupuncture or acupressure plus analgesia (versus analgesia) have any effect on the risk of adverse effects.

Aromatherapy

Aromatherapy plus analgesia may reduce pain when compared with placebo plus analgesia at 12 hours (mean difference (MD) -2.63 visual analogue scale (VAS), 95% CI -3.48 to -1.77; 3 studies; 360 women; low-certainty evidence) and 24 hours (MD -3.38 VAS, 95% CI -3.85 to -2.91; 1 study; 200 women; low-certainty evidence). The authors were uncertain whether aromatherapy plus analgesia has any effect on adverse effects (anxiety) compared with placebo plus analgesia.

Electromagnetic therapy

Electromagnetic therapy may reduce pain compared with placebo plus analgesia at 12 hours (MD -8.00, 95% CI -11.65 to -4.35; 1 study; 72 women; low-certainty evidence) and 24 hours (MD -13.00 VAS, 95% CI -17.13 to -8.87; 1 study; 72 women; low-certainty evidence).

Massage

There were 6 RCTs (651 women), 5 of which were quasi-RCTs, comparing massage (foot and hand) plus analgesia versus analgesia. All the evidence relating to pain, adverse effects (anxiety), vital signs and rescue analgesic requirement was very low-certainty.

Music therapy

Music therapy plus analgesia may reduce pain when compared with placebo plus analgesia at one hour (SMD -0.84, 95% CI -1.23 to -0.46; participants = 115; studies = 2; I2 = 0%; low-certainty evidence), 24 hours (MD -1.79, 95% CI -2.67 to -0.91; 1 study; 38 women; low-certainty evidence), and also when compared with analgesia at one hour (MD -2.11, 95% CI -3.11 to -1.10; 1 study; 38 women; low-certainty evidence) and at 24 hours (MD -2.69, 95% CI -3.67 to -1.70; 1 study; 38 women; low-certainty evidence). It is uncertain whether music therapy plus analgesia has any effect on adverse effects (anxiety), when compared with placebo plus analgesia because the quality of evidence is very low.

Reiki

The investigators were uncertain whether Reiki plus analgesia compared with analgesia alone has any effect on pain, adverse effects, vital signs or rescue analgesic requirement because the quality of evidence is very low (one study, 90 women). Relaxation Relaxation may reduce pain compared with standard care at 24 hours (MD -0.53 VAS, 95% CI -1.05 to -0.01; 1 study; 60 women; low-certainty evidence).

Transcutaneous electrical nerve stimulation (TENS)

TENS (versus no treatment) may reduce pain at one hour (MD -2.26, 95% CI -3.35 to -1.17; 1 study; 40 women; low-certainty evidence). TENS plus analgesia (versus placebo plus analgesia) may reduce pain compared with placebo plus analgesia at one hour (SMD -1.10 VAS, 95% CI -1.37 to -0.82; 3 studies; 238 women; low-certainty evidence) and at 24 hours (MD -0.70 VAS, 95% CI -0.87 to -0.53; 108 women; 1 study; low-certainty evidence). TENS plus analgesia (versus placebo plus analgesia) may reduce heart rate (MD -7.00 bpm, 95% CI -7.63 to -6.37; 108 women; 1 study; low-certainty evidence) and respiratory rate (MD -1.10 brpm, 95% CI -1.26 to -0.94; 108 women; 1 study; low-certainty evidence). The authors were uncertain whether TENS plus analgesia (versus analgesia) has any effect on pain at six hours or 24 hours, or vital signs because the quality of evidence is very low (two studies, 92 women).

The authors concluded that some SCAM therapies may help reduce post-CS pain for up to 24 hours. The evidence on adverse events is too uncertain to make any judgements on safety and we have no evidence about the longer-term effects on pain. Since pain control is the most relevant outcome for post-CS women and their clinicians, it is important that future studies of SCAM for post-CS pain measure pain as a primary outcome, preferably as the proportion of participants with at least moderate (30%) or substantial (50%) pain relief. Measuring pain as a dichotomous variable would improve the certainty of evidence and it is easy to understand for non-specialists. Future trials also need to be large enough to detect effects on clinical outcomes; measure other important outcomes as listed in this review, and use validated scales.

I feel that the Cochrane Collaboration does itself no favours by publishing such poor reviews. This one is both poorly conceived and badly reported. In fact, I see little reason to deal with pain after CS differently than with post-operative pain in general. Some of the modalities discussed are not truly SCAM. Most of the secondary endpoints are irrelevant. The inclusion of adverse effects as a primary endpoint seems nonsensical considering that SCAM studies are notoriously bad at reporting them. Many of the allegedly positive findings rely on trial designs that cannot control for placebo effects (e.g A+B versus B); therefore they tell us nothing about the effectiveness of the therapy.

Most importantly, the conclusions are not helpful. I would have simply stated that none of the SCAM modalities are supported by convincing evidence as treatments for pain control after CS.

Patients with advanced non-small cell lung cancer (NSCLC) have limited treatment options. Alongside conventional anticancer treatment, additive homeopathy might help to alleviate side effects of conventional therapy. The aim of this study was to investigate whether additive homeopathy might influence quality of life (QoL) and survival in NSCLC patients.

In this prospective, randomized, placebo-controlled, double-blind, three-arm, multi-centre, phase III study, the researchers evaluated the possible effects of additive homeopathic treatment compared to placebo in patients with stage IV NSCLC, with respect to QoL in the two randomized groups and survival time in all three groups. Treated patients visited the university teaching hospital every 9 weeks: 150 patients with stage IV NSCLC were included in the study.

  1. 51 patients received individualized homeopathic remedies plus conventional treatments,
  2. 47 received placebo plus conventional treatments,
  3. 52 control patients without any homeopathic treatment were treated with conventional therapies and observed for survival only.

For groups 1 and 2, the study was double-blind. The constituents of the different homeopathic remedies were mainly of plant, mineral, or animal origin. The remedies were manufactured by stepwise dilution and succussion, thereby preparing stable GMP grade formulations.

QoL as well as functional and symptom scales showed significant improvement in the homeopathy group when compared with placebo after 9 and 18 weeks of homeopathic treatment (p < .001). Median survival time was significantly longer in the homeopathy group (435 days) versus placebo (257 days; p = .010) as well as versus control (228 days; p < .001). Survival rate in the homeopathy group differed significantly from placebo (p = .020) and from control (p < .001).

The authors concluded that QoL improved significantly in the homeopathy group compared with placebo. In addition, survival was significantly longer in the homeopathy group versus placebo and control. A higher QoL might have contributed to the prolonged survival. The study suggests that homeopathy positively influences not only QoL but also survival. Further studies including other tumour entities are warranted.

First of all, let me thank my friend Dana Ullman for alerting me to this new and interesting study. I have read what seems to be the full paper several times and have to admit that it puzzles me (and perhaps this version is just some type of pre-publication paper). Firstly, there seems to be no methods section (the abstract is followed by several tables and a discussion), and I am left guessing much of the details. Secondly, the paper raises several questions in my mind:

  1. What is the purpose of group 3? The authors call it a control group and state it allows assessing the real homeopathic effect on the homeopathic cohort as the real effect will be the natural historical effect minus the placebo effect and the homeopathic effect. Does that make sense?
  2. Was the study under-powered? From my reading of the text, the answer seems to be yes.
  3. What is the full list of conventional treatments the patients received, and did they differ between the 3 groups?
  4. If I understand it correctly, the study patients did not receive immuno-oncological therapy. Does that fact not render the study unethical?
  5. What homeopathic potencies were prescribed in group 1? The paper says: The constituents of the different homeopathic remedies were mainly of plant, mineral, or animal origin. This is unlikely, as most homeopathic remedies contain nothing.
  6. The authors seem to have used individualised homeopathy according to Hahnemann’s instructions. Did Hahnemann not strictly forbid combining his approach with other types of treatment?
  7. How well respected is THE ONCLOLOGIST, the journal that published the paper?
  8. Was the article peer-reviewed? If so, by whom?
  9. Was the placebo indistinguishable from the verum?
  10. Was the success of patient-blinding checked?
  11. Have similar findings regarding survival been reported previously? The authors call this finding ‘unexpected’; I find it more than that; it is baffling.
  12. Should we accept such surprising findings, or would it be more prudent to wait until independent replications are available?
  13. The first author of this trial is Prof Frass who has featured on this blog several times before (see for instance here, here, here, here and here). Frass has published several studies of homeopathy and invariably manages to produce positive results. Am I the only one to find this odd?

I would be most grateful, if the readers of this blog could assist me in finding answers to some of the above questions.

Several strands of evidence have indicated that vitamin D supplementation might be helpful for COVID-19 infections. Now we also have a study testing whether it works.

Spanish researchers evaluated the effect of calcifediol treatment on Intensive Care Unit Admission and Mortality rate among patients hospitalized for COVID-19 in a randomized, double blind clinical trial. A total of 76 consecutive patients hospitalized with COVID-19 infection and clinical picture of acute respiratory infection (confirmed by a radiographic pattern of viral pneumonia and by a positive SARS-CoV-2 PCR with CURB65 severity scale) were included. All patients received as best available therapy the same standard care. This consisted of a combination of:

  • hydroxychloroquine (400 mg every 12 h on the first day, and 200 mg every 12 h for the following 5 days),
  • azithromycin (500 mg orally for 5 days.

Eligible patients were allocated at a 2 calcifediol : 1 no calcifediol ratio through electronic randomization on the day of admission to take oral calcifediol (0.532 mg), or not. Patients in the calcifediol group continued with oral calcifediol (0.266 mg) on day 3 and 7, and then weekly until discharge or ICU admission. Outcomes of effectiveness included rate of ICU admission and deaths.

Of the 50 patients treated with calcifediol, one required admission to the ICU (2%), while of 26 untreated patients, 13 required admission (50 %). Univariate Risk Estimate Odds Ratio for ICU in patients with Calcifediol treatment versus without Calcifediol treatment: 0.02 (95 %CI 0.002-0.17). Multivariate Risk Estimate Odds Ratio for ICU in patients with Calcifediol treatment vs Without Calcifediol treatment ICU (adjusting by Hypertension and T2DM): 0.03 (95 %CI: 0.003-0.25). Of the patients treated with calcifediol, none died, and all were discharged, without complications. The 13 patients not treated with calcifediol, who were not admitted to the ICU, were discharged. Of the 13 patients admitted to the ICU, two died and the remaining 11 were discharged.

The authors concluded as follows:

Our pilot study demonstrated that administration of calcifediol may improve the clinical outcome of subjects requiring hospitalization for COVID-19. Whether that would also apply to patients with an earlier stage of the disease and whether baseline vitamin D status modifies these results is unknown. Therefore, a multicenter randomized controlled trial using calcifediol, properly matched (Prevention and Treatment With Calcifediol of COVID-19 Induced Acute Respiratory Syndrome (COVIDIOL)), in 15 Spanish hospitals, funded by Clinical Research Program at COVID-19 “Progreso y Salud” Foundation and Foundation for Biomedical Research of Córdoba (FIBICO), Spain, (registered as NCT04366908 in NIH Trialnet database) will be carried out with the number of patients recalculated from the data provided by this study.

An interesting perspective of the new COVIDIOL trial with the recently available information, could be to evaluate calcifediol associated to dexamethasone or other corticoid vs. dexamethasone or other corticosteroid, since dexamethasone, which has potent anti-inflammatory actions, has recently been shown to reduce mortality in hospitalized patients on Covid-19 who are on respiratory assistance; so that treatment guidelines have been updated to recommend the use of glucocorticoids (including dexametasone), now proposed as the best available treatment in many hospitals around the world.

It is undeniable that this trial has several important limitations (and its authors are very honest to point them out). However, it is equally undeniable, in my view, that it is an important contribution to our current knowledge.

In my last post, I reported that there are no rigorous studies of homeopathy for diabetes. This was only partly true: there are no such trials to test homeopathy’s effects on the disease itself, but I did find a study of homeopathy for diabetic complications.

It comes from India and seems to be based on proper preliminary ground-work:

A prospective multi-centric clinical observational study was published in 2013 in the journal ‘HOMEOPATHY’. It was carried out from October 2005 to September 2009 by Central Council for Research in Homeopathy (CCRH) at its five institutes/units. Its authors were Chaturbhuja Nayak 1Praveen OberaiRoja VaranasiHafeezullah BaigRaveender ChG R C ReddyPratima DeviBhubaneshwari SVikram SinghV P SinghHari SinghShashi Shekhar Shitanshu. Patients suffering from diabetes mellitus (DM) and presenting with symptoms of diabetic polyneuropathy (DPN) were screened, investigated and were enrolled in the study after fulfilling the inclusion and exclusion criteria. Patients were evaluated by the diabetic distal symmetric polyneuropathy symptom score (DDSPSS) developed by the Council. A total of 15 homeopathic medicines were identified after repertorizing the nosological symptoms and signs of the disease. The appropriate constitutional medicine was selected and prescribed in 30, 200 and 1 M potency on an individualized basis. Patients were followed up regularly for 12 months.

Of 336 patients (167 males and 169 females) enrolled in the study, 247 patients (123 males and 124 females) were analysed. All patients who attended at least three follow-up appointments and baseline curve conduction studies were included in the analysis.). A statistically significant improvement in DDSPSS total score (p = 0.0001) was found at 12 months from baseline. Most objective measures did not show significant improvement. Lycopodium clavatum (n = 132), Phosphorus (n = 27) and Sulphur (n = 26) were the medicines most frequently prescribed. Adverse event of hypoglycaemia was observed in one patient only.

The authors concluded that this study suggests homeopathic medicines may be effective in managing the symptoms of DPN patients. Further studies should be controlled and include the quality of life (QOL) assessment.

As good as their word, they then conducted a more rigorous trial which was published this year:

This study (authored in 2020 by Pritha Mehra 1Bindu Sharma 2Hafeezulla Baig 3Ch Raveendar 4R V R Prasad 5M Prakash Rao 6Kolli Raju 7J S Arya 8Raj K Manchanda 9Daisy Katarmal 10Arvind Kumar 11 and published in ‘EXPLORE’, an even worse journal than ‘HOMEOPATHY’, in my view) assessed the efficacy of individualized homoeopathic medicines in management of diabetic distal symmetric polyneuropathy (DDSP). It was designed as a multi-centric double-blind, placebo controlled, randomised clinical trial and conducted by the Central Council for Research in Homoeopathy at 6 centres with a sample size of 84. Based on earlier observational studies and repertorial anamnesis of DDSP symptoms 15 homoeopathic medicines were shortlisted and validated scales were used for evaluating the outcomes post-intervention.

The primary outcome measure was change in Neuropathy Total Symptom Score-6 (NTSS-6) from baseline to 12 months. Secondary outcomes included changes in peripheral nerve conduction study (NCS), World Health Organization Quality of Life BREF (WHOQOL-BREF) and Diabetic Neuropathy Examination (DNE) Score at 12 months.

The data of 68 enrolled cases was considered for data analysis. Statistically significant difference (p<0.014) was found in NTSS-6 post intervention in the Verum group. Positive trend was noted for Verum group as per the graph plotted for DNE score and assessment done for NCS. No significant difference was found between the groups for WHOQOL-Bref. Out of 15 pre-identified homoeopathic medicines 11 medicines were prescribed in potencies in ascending order from 6C to 1M.

The authors concluded that further studies must be taken up with larger sample size and defined parameters for NCS to assess the effectiveness of homoeopathy.

This looks to me as though the trial failed to produce a positive result on inter-group comparisons. The abstract is unfortunately not very clear, and I have no access to the full text (in case someone has, please send it to me). Judging from the abstract, the study has several important flaws. For instance, it was small and we don’t know why only 68 of 84 patients were considered for analysis. Normally, an intention to treat analysis would be needed for analysis of all 84 patients.

________________________________

So, does homeopathy have anything to offer to patients with diabetes?

As far as I can see, the answer is NO!

I’d be happy to change my mind, provided someone shows me convincing evidence.

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