meta-analysis
This systematic review and meta-analysis aimed to evaluate the effectiveness and safety of Chinese herbal medicine (CHM) combined with Western medicine (WM) in comparison with WM in reducing systolic and diastolic blood pressure for patients with primary hypertension (PHTN).
Various literature searches located a total of 29 studies that included 2623 patients. The results showed that the clinical effectiveness in the treatment of hypertension with CHM+WM was considerably higher than that with WM alone, clinical effective (RR 1.23, 95% CI [1.17, 1.30], P < 0.00001), and markedly effective (ME) in the patients (RR 1.66, 95% CI [1.52, 1.80], and P < 0.00001). Random effect in SBP (MD 7.91 mmHg,[6.00, 983], P < 0.00001) and DBP (MD 5.46 mmHg, [3.88, 6.43], P < 0.00001), a subgroup analysis was carried out based on the type of intervention, duration of treatment, and CHM formulas that showed significance. Furthermore, no severe side effects were reported, and no patients stopped treatment or withdrawal due to any severe adverse events.
The authors concluded that compared to WM alone, the therapeutic effectiveness of CHM combined with WM is significantly improved in the treatment of hypertension. Additionally, CHM with WM may safely and efficiently lower systolic blood pressure (SBP) and diastolic blood pressure (DBP) in individuals with PHTN. However, rigorous randomized controlled trials with a large sample, high quality, long duration of treatment, and follow-up are recommended to strengthen this clinical evidence.
The authors can boast of an impressive list of affiliations:
- 1Heilongjiang University of Chinese Medicine, Harbin, 150040, Heilongjiang, China; School of Pharmacy, Lebanese International University, 18644, Sana’a, Yemen.
- 2Heilongjiang University of Chinese Medicine, Harbin, 150040, Heilongjiang, China.
- 3Key Laboratory of Chinese Materia Medica, Ministry of Education of Heilongjiang University of Chinese Medicine, Harbin, 150040, Heilongjiang, China.
- 4Department of Urology, Affiliated Hospital of Qingdao Binhai University, Qingdao, Shandong, China.
- 5Department of Respiratory Diseases, Shandong Second Provincial General Hospital, Shandong University, Shandong, China.
- 6Heilongjiang University of Chinese Medicine, Harbin, 150040, Heilongjiang, China. Electronic address: [email protected]
Impressive in the sense of being impressively prone to bias, particularly knowing that ~80% of Chinese research findings have been shown to be fabricated and considering that Chinese authors as good as never publish anything negative about TCM.
But perhaps you still believe that the results reported here are 100% true? In this case, I might even agree with you. The reason is that the authors demonstrate in exemplary fashion what I have been saying so often before:
Blood pressure is one of the many endpoints that are highly prone to placebo effects. Therefore, even the addition of an ineffective CHM to WM would lower blood pressure more effectively than WM alone.
But there is a third way of explaining the findings of this review: some herbal remedies might actually have a hypotensive effect. The trouble is that this review does come not even close to telling us which.
This meta-analysis of randomized clinical trials (RCTs) was aimed at evaluating the effects of massage therapy in the treatment of postoperative pain.
Three databases (PubMed, Embase, and Cochrane Central Register of Controlled Trials) were searched for RCTs published from database inception through January 26, 2021. The primary outcome was pain relief. The quality of RCTs was appraised with the Cochrane Collaboration risk of bias tool. The random-effect model was used to calculate the effect sizes and standardized mean difference (SMD) with 95% confidential intervals (CIs) as a summary effect. The heterogeneity test was conducted through I2. Subgroup and sensitivity analyses were used to explore the source of heterogeneity. Possible publication bias was assessed using visual inspection of funnel plot asymmetry.
The analysis included 33 RCTs and showed that MT is effective in reducing postoperative pain (SMD, -1.32; 95% CI, −2.01 to −0.63; p = 0.0002; I2 = 98.67%). A similarly positive effect was found for both short (immediate assessment) and long terms (assessment performed 4 to 6 weeks after the MT). Neither the duration per session nor the dose had a significant impact on the effect of MT, and there was no difference in the effects of different MT types. In addition, MT seemed to be more effective for adults. Furthermore, MT had better analgesic effects on cesarean section and heart surgery than orthopedic surgery.
The authors concluded that MT may be effective for postoperative pain relief. We also found a high level of heterogeneity among existing studies, most of which were compromised in the methodological quality. Thus, more high-quality RCTs with a low risk of bias, longer follow-up, and a sufficient sample size are needed to demonstrate the true usefulness of MT.
The authors discuss that publication bias might be possible due to the exclusion of all studies not published in English. Additionally, the included RCTs were extremely heterogeneous. None of the included studies was double-blind (which is, of course, not easy to do for MT). There was evidence of publication bias in the included data. In addition, there is no uniform evaluation standard for the operation level of massage practitioners, which may lead to research implementation bias.
Patients who have just had an operation and are in pain are usually thankful for the attention provided by carers. It might thus not matter whether it is provided by a massage or other therapist. The question is: does it matter? For the patient, it probably doesn’t; However, for making progress, it does, in my view.
In the end, we have to realize that, with clinical trials of certain treatments, scientific rigor can reach its limits. It is not possible to conduct double-blind, placebo-controlled studies of MT. Thus we can only conclude that, for some indications, massage seems to be helpful (and almost free of adverse effects).
This is also the conclusion that has been drawn long ago in some countries. In Germany, for instance, where I trained and practiced in my younger years, Swedish massage therapy has always been an accepted, conventional form of treatment (while exotic or alternative versions of massage therapy had no place in routine care). And in Vienna where I was chair of rehab medicine I employed about 8 massage therapists in my department.
When I conduct my regular literature searches, I am invariably delighted to find a paper that shows the effectiveness of a so-called alternative medicine (SCAM). Contrary to the impression that I might give to some, I like positive results as much as the next person. So, today you find me pleased to yet again report about one of my favorite SCAMs.
The purpose of this systematic review was to evaluate the effectiveness of manual lymphatic drainage (MLD) in breast cancer-related lymphedema (BCRL) patients.
In total, 11 RCTs involving 1564 patients could be included, and 10 trials were deemed viable for inclusion in the meta-analysis. Due to the effects of MLD for BCRL, statistically significant improvements were found on the incidence of lymphedema (RR = 0.58, 95% CI [0.37, 0.93], P =.02) and pain intensity (SMD = -0.72, 95% CI [-1.34, -0.09], P = .02). Besides, the meta-analysis carried out implied that the effects that MLD had on volumetric changes of lymphedema and quality of life, were not statistically significant.
The authors concluded that the current evidence based on the RCTs shows that pain of BCRL patients undergoing MLD is significantly improved, while our findings do not support the use of MLD in improving volumetric of lymphedema and quality of life. Note that the effect of MLD for preventing BCRL is worthy of discussion.
Lymph drainage is so well-established in cancer care that most people would probably consider it a conventional treatment. If, however, you read for which conditions its inventor, Emil Vodder, used to promote it, they might change their minds. Vodder saw it as a cure for most illnesses, even those for which there is no plausibility or good evidence.
As far as I can see, lymph drainage works well for reducing lymph edema but, for all other conditions, it is not evidence-based. And this is the reason why I still categorize it as a SCAM.
Today, you cannot read a newspaper or listen to the radio without learning that there has been a significant, sensational, momentous, unprecedented, etc. breakthrough in the treatment of Alzheimer’s disease. The reason for all this excitement (or is it hype?) is this study just out in the NEJM:
BACKGROUND
The accumulation of soluble and insoluble aggregated amyloid-beta (Aβ) may initiate or potentiate pathologic processes in Alzheimer’s disease. Lecanemab, a humanized IgG1 monoclonal antibody that binds with high affinity to Aβ soluble protofibrils, is being tested in persons with early Alzheimer’s disease.
METHODS
We conducted an 18-month, multicenter, double-blind, phase 3 trial involving persons 50 to 90 years of age with early Alzheimer’s disease (mild cognitive impairment or mild dementia due to Alzheimer’s disease) with evidence of amyloid on positron-emission tomography (PET) or by cerebrospinal fluid testing. Participants were randomly assigned in a 1:1 ratio to receive intravenous lecanemab (10 mg per kilogram of body weight every 2 weeks) or placebo. The primary end point was the change from baseline at 18 months in the score on the Clinical Dementia Rating–Sum of Boxes (CDR-SB; range, 0 to 18, with higher scores indicating greater impairment). Key secondary end points were the change in amyloid burden on PET, the score on the 14-item cognitive subscale of the Alzheimer’s Disease Assessment Scale (ADAS-cog14; range, 0 to 90; higher scores indicate greater impairment), the Alzheimer’s Disease Composite Score (ADCOMS; range, 0 to 1.97; higher scores indicate greater impairment), and the score on the Alzheimer’s Disease Cooperative Study–Activities of Daily Living Scale for Mild Cognitive Impairment (ADCS-MCI-ADL; range, 0 to 53; lower scores indicate greater impairment).
RESULTS
A total of 1795 participants were enrolled, with 898 assigned to receive lecanemab and 897 to receive placebo. The mean CDR-SB score at baseline was approximately 3.2 in both groups. The adjusted least-squares mean change from baseline at 18 months was 1.21 with lecanemab and 1.66 with placebo (difference, −0.45; 95% confidence interval [CI], −0.67 to −0.23; P<0.001). In a substudy involving 698 participants, there were greater reductions in brain amyloid burden with lecanemab than with placebo (difference, −59.1 centiloids; 95% CI, −62.6 to −55.6). Other mean differences between the two groups in the change from baseline favoring lecanemab were as follows: for the ADAS-cog14 score, −1.44 (95% CI, −2.27 to −0.61; P<0.001); for the ADCOMS, −0.050 (95% CI, −0.074 to −0.027; P<0.001); and for the ADCS-MCI-ADL score, 2.0 (95% CI, 1.2 to 2.8; P<0.001). Lecanemab resulted in infusion-related reactions in 26.4% of the participants and amyloid-related imaging abnormalities with edema or effusions in 12.6%.
CONCLUSIONS
Lecanemab reduced markers of amyloid in early Alzheimer’s disease and resulted in moderately less decline on measures of cognition and function than placebo at 18 months but was associated with adverse events. Longer trials are warranted to determine the efficacy and safety of lecanemab in early Alzheimer’s disease. (Funded by Eisai and Biogen; Clarity AD ClinicalTrials.gov number, NCT03887455. opens in new tab.)
It’s a good study, and I (like everyone else) hope that it will mean tangible progress in the management of that devastating disease. Most media outlets are announcing the news with the claim that it is the FIRST TIME that any treatment has been shown to delay the cognitive decline of Alzheimer’s disease patients.
But is this true?
I think not!
There have been several studies showing that the herbal remedy GINKGO BILOBA slows the Alzheimer-related decline. Here is the latest systematic review of the subject:
Background: Ginkgo biloba is a natural medicine used for cognitive impairment and Alzheimer’s disease. The objective of this review is to explore the effectiveness and safety of Ginkgo biloba in treating mild cognitive impairment and Alzheimer’s disease.
Methods: Electronic search was conducted from PubMed, Cochrane Library, and four major Chinese databases from their inception up to 1(st) December, 2014 for randomized clinical trials on Ginkgo biloba in treating mild cognitive impairment or Alzheimer’s disease. Meta-analyses were performed by RevMan 5.2 software.
Results: 21 trials with 2608 patients met the inclusion criteria. The general methodological quality of included trials was moderate to poor. Compared with conventional medicine alone, Ginkgo biboba in combination with conventional medicine was superior in improving Mini-Mental State Examination (MMSE) scores at 24 weeks for patients with Alzheimer’s disease (MD 2.39, 95% CI 1.28 to 3.50, P<0.0001) and mild cognitive impairment (MD 1.90, 95% CI 1.41 to 2.39, P<0.00001), and Activity of Daily Living (ADL) scores at 24 weeks for Alzheimer’s disease (MD -3.72, 95% CI -5.68 to -1.76, P=0.0002). When compared with placebo or conventional medicine in individual trials, Ginkgo biboba demonstrated similar but inconsistent findings. Adverse events were mild.
Conclusion: Ginkgo biloba is potentially beneficial for the improvement of cognitive function, activities of daily living, and global clinical assessment in patients with mild cognitive impairment or Alzheimer’s disease. However, due to limited sample size, inconsistent findings and methodological quality of included trials, more research are warranted to confirm the effectiveness and safety of ginkgo biloba in treating mild cognitive impairment and Alzheimer’s disease.
I know, the science is not nearly as good as that of the NEJM trial. I also know that the trial data for ginkgo biloba are not uniformly positive. And I know that, after several studies showed good results, later trials tended not to confirm them.
But this is what very often happens in clinical research: studies are initially promising, only to be disappointing as more studies emerge. I sincerely hope that this will not happen with the new drug ‘Lecanemab’ and that today’s excitement will not turn out to be hype.
Acupuncture is emerging as a potential therapy for relieving pain, but the effectiveness of acupuncture for relieving low back and/or pelvic pain (LBPP) during pregnancy remains controversial. This meta-analysis aimed to investigate the effects of acupuncture on pain, functional status, and quality of life for women with LBPP pain during pregnancy.
The authors included all RCTs evaluating the effects of acupuncture on LBPP during pregnancy. Data extraction and study quality assessments were independently performed by three reviewers. The mean differences (MDs) with 95% CIs for pooled data were calculated. The primary outcomes were pain, functional status, and quality of life. The secondary outcomes were overall effects (a questionnaire at a post-treatment visit within a week after the last treatment to determine the number of people who received good or excellent help), analgesic consumption, Apgar scores >7 at 5 min, adverse events, gestational age at birth, induction of labor and mode of birth.
Ten studies, reporting on a total of 1040 women, were included. Overall, acupuncture
- relieved pain during pregnancy (MD=1.70, 95% CI: (0.95 to 2.45), p<0.00001, I2=90%),
- improved functional status (MD=12.44, 95% CI: (3.32 to 21.55), p=0.007, I2=94%),
- improved quality of life (MD=−8.89, 95% CI: (−11.90 to –5.88), p<0.00001, I2 = 57%).
There was a significant difference in overall effects (OR=0.13, 95% CI: (0.07 to 0.23), p<0.00001, I2 = 7%). However, there was no significant difference in analgesic consumption during the study period (OR=2.49, 95% CI: (0.08 to 80.25), p=0.61, I2=61%) and Apgar scores of newborns (OR=1.02, 95% CI: (0.37 to 2.83), p=0.97, I2 = 0%). Preterm birth from acupuncture during the study period was reported in two studies. Although preterm contractions were reported in two studies, all infants were in good health at birth. In terms of gestational age at birth, induction of labor, and mode of birth, only one study reported the gestational age at birth (mean gestation 40 weeks).
The authors concluded that acupuncture significantly improved pain, functional status and quality of life in women with LBPP during the pregnancy. Additionally, acupuncture had no observable severe adverse influences on the newborns. More large-scale and well-designed RCTs are still needed to further confirm these results.
What should we make of this paper? 
In case you are in a hurry: NOT A LOT!
In case you need more, here are a few points:
- many trials were of poor quality;
- there was evidence of publication bias;
- there was considerable heterogeneity within the studies.
The most important issue is one studiously avoided in the paper: the treatment of the control groups. One has to dig deep into this paper to find that the control groups could be treated with “other treatments, no intervention, and placebo acupuncture”. Trials comparing acupuncture combined plus other treatments with other treatments were also considered to be eligible. In other words, the analyses included studies that compared acupuncture to no treatment at all as well as studies that followed the infamous ‘A+Bversus B’ design. Seven studies used no intervention or standard of care in the control group thus not controlling for placebo effects.
Nobody can thus be in the slightest surprised that the overall result of the meta-analysis was positive – false positive, that is! And the worst is that this glaring limitation was not discussed as a feature that prevents firm conclusions.
Dishonest researchers?
Biased reviewers?
Incompetent editors?
Truly unbelievable!!!
In consideration of these points, let me rephrase the conclusions:
The well-documented placebo (and other non-specific) effects of aacupuncture improved pain, functional status and quality of life in women with LBPP during the pregnancy. Unsurprisingly, acupuncture had no observable severe adverse influences on the newborns. More large-scale and well-designed RCTs are not needed to further confirm these results.
PS
I find it exasperating to see that more and more (formerly) reputable journals are misleading us with such rubbish!!!
This systematic review, meta-analysis, and meta-regression investigated the effects of individualized interventions, based on exercise alone or combined with psychological treatment, on pain intensity and disability in patients with chronic non-specific low-back pain.
Databases were searched up to January 31, 2022, to retrieve respective randomized clinical trials of individualized and/or personalized and/or stratified exercise interventions with or without psychological treatment compared to any control.
The findings show:
- Fifty-eight studies (n = 10084) were included. At short-term follow-up (12 weeks), low-certainty evidence for pain intensity (SMD -0.28 [95%CI -0.42 to -0.14]) and very low-certainty evidence for disability (-0.17 [-0.31 to -0.02]) indicates superior effects of individualized versus active exercises, and very low-certainty evidence for pain intensity (-0.40; [-0.58 to -0.22])), but not (low-certainty evidence) for disability (-0.18; [-0.22 to 0.01]) compared to passive controls.
- At long-term follow-up (1 year), moderate-certainty evidence for pain intensity (-0.14 [-0.22 to -0.07]) and disability (-0.20 [-0.30 to -0.10]) indicates effects versus passive controls.
Sensitivity analyses indicate that the effects on pain, but not on disability (always short-term and versus active treatments) were robust. Pain reduction caused by individualized exercise treatments in combination with psychological interventions (in particular behavioral-cognitive therapies) (-0.28 [-0.42 to -0.14], low certainty) is of clinical importance.
The certainty of the evidence was downgraded mainly due to evidence of risk of bias, publication bias, and inconsistency that could not be explained. Individualized exercise can treat pain and disability in chronic non-specific low-back pain. The effects in the short term are of clinical importance (relative differences versus active 38% and versus passive interventions 77%), especially in regard to the little extra effort to individualize exercise. Sub-group analysis suggests a combination of individualized exercise (especially motor-control-based treatments) with behavioral therapy interventions to boost effects.
The authors concluded that the relative benefit of individualized exercise therapy on chronic low back pain compared to other active treatments is approximately 38% which is of clinical importance. Still, sustainability of effects (> 12 months) is doubtable. As individualization in exercise therapies is easy to implement, its use should be considered.
Johannes Fleckenstein, the 1st author from the Goethe-University Frankfurt, Institute of Sports Sciences, Department of Sports Medicine and Exercise Physiology, sees in the study “an urgent health policy appeal” to strengthen combined services in care and remuneration. “Compared to other countries, such as the USA, we are in a relatively good position in Germany. For example, we have a lower prescription of strong narcotics such as opiates. But the rate of unnecessary X-ray examinations, which incidentally can also contribute to the chronicity of pain, or inaccurate surgical indications is still very high.”
Personally, I find the findings of this paper rather unsurprising. As a clinician, many years ago, prescribing exercise therapy for low back pain was my daily bread. None of my team would have ever conceived the idea that exercise does not need to be individualized according to the needs and capabilities of each patient. Therefore, I suggest rephrasing the last sentence of the conclusion: As individualization in exercise therapies is easy to implement, its use should be standard procedure.
One of the numerous conditions chiropractors, osteopaths, and other manual therapists claim to treat effectively is tension-type headache (TTH). For this purpose, they (in particular, chiropractors) often use high-velocity, low-amplitude manipulations of the neck. They do so despite the fact that the evidence for these techniques is less than convincing.
This systematic review evaluated the evidence about the effectiveness of manual therapy (MT) on pain intensity, frequency, and impact of pain in individuals with tension-type headache (TTH).
Medline, Embase, Scopus, Web of Science, CENTRAL, and PEDro were searched in June 2020. Randomized clinical trials that applied MT not associated with other interventions for TTH were selected. The level of evidence was synthesized using GRADE, and Standardized Mean Differences (SMD) were calculated for meta-analysis.
Fifteen studies were included with a total sample of 1131 individuals. The analyses show that high-velocity, low-amplitude techniques were not superior to no treatment in reducing pain intensity (SMD = 0.01, low evidence) and frequency (SMD = -0.27, moderate evidence). Soft tissue interventions were superior to no treatment in reducing pain intensity (SMD = -0.86, low evidence) and frequency of pain (SMD = -1.45, low evidence). Dry needling was superior to no treatment in reducing pain intensity (SMD = -5.16, moderate evidence) and frequency (SMD = -2.14, moderate evidence). Soft tissue interventions were not superior to no treatment and other treatments on the impact of headache.
The authors concluded that manual therapy may have positive effects on pain intensity and frequency, but more studies are necessary to strengthen the evidence of the effects of manual therapy on subjects with tension-type headache. Implications for rehabilitation soft tissue interventions and dry needling can be used to improve pain intensity and frequency in patients with tension type headache. High velocity and low amplitude thrust manipulations were not effective for improving pain intensity and frequency in patients with tension type headache. Manual therapy was not effective for improving the impact of headache in patients with tension type headache.
So, this review shows that:
- soft tissue interventions are better than no treatment,
- dry needling is better than no treatment.
These two results fail to impress me. Due to a placebo effect, almost any treatment should be better than no therapy at all.
ALMOST, because high-velocity, low-amplitude techniques were not superior to no treatment in reducing the intensity and frequency of pain. This, I feel, is an important finding that needs an explanation.
As it is only logical that high-velocity, low-amplitude techniques must also produce a positive placebo effect, the finding can only mean that these manipulations also generate a negative effect that is strong enough to cancel the positive response to placebo. (In addition, they can also cause severe complications via arterial dissections, as discussed often on this blog.)
Too complicated?
Perhaps; let me, therefore, put it simply and use the blunt words of a neurologist who once was quoted saying this:
DON’T LET THE BUGGARS TOUCH YOUR NECK!
Placebo effects are a fascinating subject. In so-called alternative medicine (SCAM), they are particularly important because much of SCAM seems to rely on little more than placebo effects. Therefore, I think this new paper is of some relevance to us.
The aim of this systematic review was to quantify the placebo effect of intraarticular injections for knee osteoarthritis in terms of pain, function, and objective outcomes. Factors influencing placebo effect were investigated.
Out of 2,363 records, 50 articles on 4,076 patients were included. The meta-analysis showed significant improvements up to the 6-month follow-up: Visual Analogue Scale (VAS)-pain −13.4 mean difference (MD) (95% confidence interval [CI]: −21.7/−5.1; P < 0.001), Western Ontario and McMaster Osteoarthritis Index (WOMAC)-pain −3.3 MD (95% CI: −3.9/−2.7; P < 0.001). Other significant improvements were WOMAC-stiffness −1.1 MD (95% CI: −1.6/−0.6; P < 0.001), WOMAC-function −10.1 MD (95% CI: −12.2/−8.0; P < 0.001), and Evaluator Global Assessment −21.4 MD (95% CI: −29.2/−13.6; P < 0.001). The responder rate was 52% (95% CI: 40% to 63%). Improvements were greater than the “minimal clinically important difference” for all outcomes (except 6-month VAS-pain). The level of evidence was moderate for almost all outcomes.
The authors concluded that the placebo effect of knee injections is significant, with functional improvements lasting even longer than those reported for pain perception. The high, long-lasting, and heterogeneous effects on the scales commonly used in clinical trials further highlight that the impact of placebo should not be overlooked in the research on and management of knee osteoarthritis.
The authors furthermore confirmed that “the main finding of this meta-analysis is that placebo is an important component of the effect of injective treatments for patients with KOA, with saline injections being able to provide relevant and long-lasting results not only in terms of pain relief but also with respect to stiffness resolution and function improvement. These results are both statistically and clinically significant and can be perceived by patients up to 6 months.”
I would dispute that!
To explain why it might help to read our 1995 BMJ paper on the subject:
We often and wrongly equate the response seen in the placebo arm of a clinical trial with the placebo effect. In order to obtain the true placebo effect, other non-specific effects can be identified by including an untreated control group in clinical trials. A review of the literature shows that most authors confuse the perceived placebo effect with the true placebo effect. The true placebo effect is highly variable, depending on several factors that are not fully understood. A distinction between the perceived and the true placebo effects would be helpful in understanding the complex phenomena involved in a placebo response.
In other words, what the authors picked up in their analysis (i.e. the changes that occurred in the placebo groups between the start of a trial and after placebo application) is not just the placebo response; it is, in fact, a combination of a placebo effect, concomitant interventions/care, regression towards the mean, natural history of the condition and possibly other factors.
Does it matter?
Yes, it does!
Placebo effects are not nearly as powerful and long-lasting as the authors conclude. And this means virtually all their implications for clinical practice are incorrect.
Zinc has been in the limelight recently. The reason is that it has been recommended as a preventative and/or treatment of COVID infections. The basis for such recommendations has been some trial evidence suggesting it is effective for viral respiratory tract infections (RTIs). But the evidence has been full of contradictions which means, we need a systematic review that critically evaluated the totality of the available data.
This systematic review was aimed at evaluating the benefits and risks of zinc formulations compared with controls for the prevention or treatment of acute RTIs in adults.
Seventeen English and Chinese databases were searched in April/May 2020 for randomized clinical trials (RCTs), and from April/May 2020 to August 2020 for SARS-CoV-2 RCTs. Cochrane rapid review methods were applied. Quality appraisals used the Risk of Bias 2.0 and Grading of Recommendations, Assessment, Development and Evaluation (GRADE) approach.
Twenty-eight RCTs with 5446 participants were identified. None were specific to SARS-CoV-2. Compared with placebo, oral or intranasal zinc prevented 5 RTIs per 100 person-months (95% CI 1 to 8, numbers needed to treat (NNT)=20, moderate-certainty/quality). Sublingual zinc did not prevent clinical colds following human rhinovirus inoculations (relative risk, RR 0.96, 95% CI 0.77 to 1.21, moderate-certainty/quality). On average, symptoms resolved 2 days earlier with sublingual or intranasal zinc compared with placebo (95% CI 0.61 to 3.50, very low-certainty/quality) and 19 more adults per 100 were likely to remain symptomatic on day 7 without zinc (95% CI 2 to 38, NNT=5, low-certainty/quality). There were clinically significant reductions in day 3 symptom severity scores (mean difference, MD -1.20 points, 95% CI -0.66 to -1.74, low-certainty/quality), but not average daily symptom severity scores (standardised MD -0.15, 95% CI -0.43 to 0.13, low-certainty/quality). Non-serious adverse events (AEs) (eg, nausea, mouth/nasal irritation) were higher (RR 1.41, 95% CI 1.17 to 1.69, NNHarm=7, moderate-certainty/quality). Compared with active controls, there were no differences in illness duration or AEs (low-certainty/quality). No serious AEs were reported in the 25 RCTs that monitored them (low-certainty/quality).
The authors concluded that in adult populations unlikely to be zinc deficient, there was some evidence suggesting zinc might prevent RTIs symptoms and shorten duration. Non-serious AEs may limit tolerability for some. The comparative efficacy/effectiveness of different zinc formulations and doses were unclear. The GRADE-certainty/quality of the evidence was limited by a high risk of bias, small sample sizes and/or heterogeneity. Further research, including SARS-CoV-2 clinical trials is warranted.
The authors provide a short comment on the assumed mode of action of zinc. The rationale for topical intranasal and sublingual zinc is based on the in vitro effects of zinc ions that can inhibit viral replication, stabilize cell membranes and reduce mucosal inflammation. Other conceivable mechanisms include the activation of T lymphocytes, monocytes, and granulocytes.
The authors also remind us to be cautious: clinicians and consumers need to be aware that considerable uncertainty remains regarding the clinical efficacy of different zinc formulations, doses, and administration routes, and the extent to which efficacy might be influenced by the ever changing epidemiology of the viruses that cause RTIs. The largest body of evidence comes from sublingual lozenges and zinc gluconate and acetate salts, suggesting these are suitable choices. Yet, this does not mean that other administration routes and zinc salts are less effective. The new evidence on the prophylactic effects of low-dose nasal sprays adds weight to the otherwise inconclusive findings from the handful of RCTs evaluating zinc nasal sprays or gels for acute treatment. A minimum therapeutic dose for zinc is also yet to be determined. An earlier review suggested the minimum dose for sublingual lozenges is 75 mg. However, the present analysis does not support this conclusion. Furthermore, a daily oral dose of 15 mg has been shown to upregulate lymphocytes within days, so it is plausible that much lower doses might also be effective.
Should Acupuncture-Related Therapies be Considered in Prediabetes Control?
No!
If you are pre-diabetic, consult a doctor and follow his/her advice. Do NOT do what acupuncturists or other self-appointed experts tell you. Do NOT become a victim of quackery.
But the authors of a new paper disagree with my view.
So, let’s have a look at the evidence.
Their systematic review was aimed at evaluating the effects and safety of acupuncture-related therapy (AT) interventions on glycemic control for prediabetes. The Chinese researchers searched 14 databases and 5 clinical registry platforms from inception to December 2020. Randomized controlled trials involving AT interventions for managing prediabetes were included.
Of the 855 identified trials, 34 articles were included for qualitative synthesis, 31 of which were included in the final meta-analysis. Compared with usual care, sham intervention, or conventional medicine, AT treatments yielded greater reductions in the primary outcomes, including fasting plasma glucose (FPG) (standard mean difference [SMD] = -0.83; 95% confidence interval [CI], -1.06, -0.61; P < .00001), 2-hour plasma glucose (2hPG) (SMD = -0.88; 95% CI, -1.20, -0.57; P < .00001), and glycated hemoglobin (HbA1c) levels (SMD = -0.91; 95% CI, -1.31, -0.51; P < .00001), as well as a greater decline in the secondary outcome, which is the incidence of prediabetes (RR = 1.43; 95% CI, 1.26, 1.63; P < .00001).
The authors concluded that AT is a potential strategy that can contribute to better glycemic control in the management of prediabetes. Because of the substantial clinical heterogeneity, the effect estimates should be interpreted with caution. More research is required for different ethnic groups and long-term effectiveness.
But this is clearly a positive result!
Why do I not believe it?
There are several reasons:
- There is no conceivable mechanism by which AT prevents diabetes.
- The findings heavily rely on Chinese RCTs which are known to be of poor quality and often even fabricated. To trust such research would be a dangerous mistake.
- Many of the primary studies were designed such that they failed to control for non-specific effects of AT. This means that a causal link between AT and the outcome is doubtful.
- The review was published in a 3rd class journal of no impact. Its peer-review system evidently failed.
So, let’s just forget about this rubbish paper?
If only it were so easy!
Journalists always have a keen interest in exotic treatments that contradict established wisdom. Predictably, they have been reporting about the new review thus confusing or misleading the public. One journalist, for instance, stated:
Acupuncture has been used for thousands of years to treat a variety of illnesses — and now it could also help fight one of the 21st century’s biggest health challenges.
New research from Edith Cowan University has found acupuncture therapy may be a useful tool in avoiding type 2 diabetes.
The team of scientists investigated dozens of studies covering the effects of acupuncture on more than 3600 people with prediabetes. This is a condition marked by higher-than-normal blood glucose levels without being high enough to be diagnosed as diabetes.
According to the findings, acupuncture therapy significantly improved key markers, such as fasting plasma glucose, two-hour plasma glucose, and glycated hemoglobin. Additionally, acupuncture therapy resulted in a greater decline in the incidence of prediabetes.
The review can thus serve as a prime example for demonstrating how irresponsible research has the power to mislead millions. This is why I have often said that poor research is a danger to public health.
And what can be done about this more and more prevalent problem?
The answer is easy: people need to behave more responsibly; this includes:
- trialists,
- review authors,
- editors,
- peer-reviewers,
- journalists.
Yes, the answer is easy in theory – but the practice is far from it!
