Regular readers of this blog will be aware of the many bogus claims made by chiropractors. One claim, however, namely the one postulating chiropractors can effectively treat low back pain with spinal manipulation, is rarely viewed as being bogus. Chiropractors are usually able to produce evidence that does suggest the claim to be true, and therefore even most critics of chiropractic back off on this particular issue.
But is the claim really true?
A recent trial might provide the answer.
The purpose of this study was to compare the effectiveness of chiropractic spinal manipulative therapy (cSMT) to a sham intervention on pain (Visual Analogue Scale, SF-36 pain subscale), disability (Oswestry Disability Index), and physical function (SF-36 subscale, Timed Up and Go) by performing a randomized placebo-controlled trial at 2 Veteran Affairs Clinics.
Older veterans (≥ 65 years of age) who were naive to chiropractic were recruited. A total of 136 who suffered from chronic low back pain (LBP) were included in the study – with 69 being randomly assigned to cSMT and 67 to the sham intervention. Patients were treated twice per week for 4 weeks. The outcomes were assessed at baseline, 5, and 12 weeks post baseline.
Both groups demonstrated significant decrease in pain and disability at 5 and 12 weeks. At 12 weeks, there was no significant difference in pain and a statistically significant decline in disability scores in the cSMT group when compared to the control group. There were no significant differences in adverse events between the groups.
The authors concluded that cSMT did not result in greater improvement in pain when compared to our sham intervention; however, cSMT did demonstrate a slightly greater improvement in disability at 12 weeks. The fact that patients in both groups showed improvements suggests the presence of a nonspecific therapeutic effect.
Hold on, I hear you say, this does not mean that cSMT is a placebo in the treatment of LBP! There are other studies that yield positive results. Let’s not cherry-pick our evidence!
Absolutely correct! To avoid cherry-picking, lets see what the current Cochrane review tells us about cSMT and chronic LBP. Here is the conclusion of this review based on 26 RCTs: High quality evidence suggests that there is no clinically relevant difference between SMT and other interventions for reducing pain and improving function in patients with chronic low-back pain.
Nonspecific neck pain is extremely common, often disabling, and very costly for us all. If we believe those who earn their money with them, effective treatments for the condition abound. One of these therapies is osteopathy. But does osteopathic manipulation/mobilisation really work?
The objective of a recent review (the link I originally put in here does not work, I will supply a new one as soon as the article becomes available on Medline) was to find out. Specifically, the authors wanted to assess the effectiveness of osteopathic manipulative treatment (OMT) in the management of chronic nonspecific neck pain regarding pain, functional status, and adverse events.
Electronic literature searches unrestricted by language were performed in March 2014. A manual search of reference lists and personal communication with experts identified additional studies. Only randomized clinical trials (RCTs) were included, and studies of specific neck pain or single treatment techniques were excluded. Primary outcomes were pain and functional status, and secondary outcome was adverse events.
Studies were independently reviewed using a standardized data extraction form. Mean difference (MD) or standard mean difference (SMD) with 95% confidence intervals (CIs) and overall effect size were calculated for primary outcomes. GRADE was used to assess quality of the evidence.
Of 299 identified articles, 18 were evaluated and 15 excluded. The three included RCTs had low risk of bias. The results show that moderate-quality evidence suggested OMT had a significant and clinically relevant effect on pain relief (MD: -13.04, 95% CI: -20.64 to -5.44) in chronic nonspecific neck pain, and moderate-quality evidence suggested a non-significant difference in favour of OMT for functional status (SMD: -0.38, 95% CI: -0.88 to -0.11). No serious adverse events were reported.
The authors concluded that, based on the three included studies, the review suggested clinically relevant effects of OMT for reducing pain in patients with chronic nonspecific neck pain. Given the small sample sizes, different comparison groups, and lack of long-term measurements in the few available studies, larger, high-quality randomized controlled trials with robust comparison groups are recommended.
Yet again I am taken aback by several things simultaneously:
- the extreme paucity of RCTs, particularly considering that neck pain is one of the main indication for osteopaths,
- the rather uncritical text by the authors,
- the nonsensical conclusions.
Let me offer my own conclusions which are, I hope, a little more realistic:
GIVEN THE PAUCITY OF THE RCTs AND THEIR SMALL SAMPLE SIZES, IT IS NOT POSSIBLE TO CLAIM THAT OMT FOR NONSPECIFIC NECK PAIN IS AN EVIDENCE-BASED APPROACH
The purpose of this study was to evaluate the impact of early and guideline adherent physical therapy for low back pain on utilization and costs within the Military Health System (MHS).
Patients presenting to a primary care setting with a new complaint of LBP from January 1, 2007 to December 31, 2009 were identified from the MHS Management Analysis and Reporting Tool. Descriptive statistics, utilization, and costs were examined on the basis of timing of referral to physical therapy and adherence to practice guidelines over a 2-year period. Utilization outcomes (advanced imaging, lumbar injections or surgery, and opioid use) were compared using adjusted odds ratios with 99% confidence intervals. Total LBP-related health care costs over the 2-year follow-up were compared using linear regression models.
753,450 eligible patients with a primary care visit for LBP between 18-60 years of age were considered. Physical therapy was utilized by 16.3% (n = 122,723) of patients, with 24.0% (n = 17,175) of those receiving early physical therapy that was adherent to recommendations for active treatment. Early referral to guideline adherent physical therapy was associated with significantly lower utilization for all outcomes and 60% lower total LBP-related costs.
The authors concluded that the potential for cost savings in the MHS from early guideline adherent physical therapy may be substantial. These results also extend the findings from similar studies in civilian settings by demonstrating an association between early guideline adherent care and utilization and costs in a single payer health system. Future research is necessary to examine which patients with LBP benefit early physical therapy and determine strategies for providing early guideline adherent care.
These are certainly interesting data. Because LBP is such a common condition, it costs us all dearly. Measures to reduce this burden in suffering and expense are urgently needed. The question is whether early referral to a physiotherapist is such a measure. The present data show that this is possible but they do not prove it.
I applaud the authors for realising this point and discussing it at length: The results of this study should be examined in light of the following limitations. Given the favorable natural history of LBP, many patients improve regardless of treatment. Those referred to physical therapy early are also more likely to have a shorter duration of pain, thus the potential for selection bias to have influenced these results. We accounted for a number of co-morbidities available in the data set and excluded patients with prior visits for LBP to mitigate against this possibility. However, the retrospective observational design of this study imposes limitations on extending the associations we observed to causation. Although we attempted to exclude patients with a specific spinal pathology, it is possible that a few patients may have been inadvertently included in the data set, in which case advanced imaging may be indicated. Additionally, although our results support that early physical therapy which adheres to practice guidelines may be less resource intense, we cannot conclude without patient-centered clinical outcomes (i.e., pain, function, disability, satisfaction, etc.) that the care was more cost effective. Further, it may be that the standard we used to judge adherence to practice guidelines (CPT codes) was not sufficiently sensitive to determine whether care is consistent with clinical practice guidelines. We also did not account for indirect or out-of-pocket costs for treatments such as complementary care, which is common for LBP. However, it is likely that the observed effects on total costs would have been even larger had these costs been considered.
I was originally alerted to this paper through a tweet claiming that these results demonstrate that chiropractic has an important role in LBP. However, the study does not even imply such a conclusion. It is, of course, true that many chiropractors use physical therapies. But they do not have the same training as physiotherapists and they tend to use spinal manipulations far more frequently. Virtually every LBP-patient consulting a chiropractor would be treated with spinal manipulations. As this approach is neither based on sound evidence nor free of risks, the conclusion, in my view, cannot be to see chiropractors for LBP; it must be to consult a physiotherapist.
A few years ago, I fell ill with shingles. When patients had consulted me for this condition, during the times when I still was a clinician, I always had to stop myself smiling; they complained bitterly but, really, this was far from serious. Now, affected myself, I did not smile a bit: this was incredibly painful!
I promptly saw my GP in Exeter who, to my utter amazement, prescribed paracetamol. She too seemed to think that this was really nothing to bother her with. As I had feared, the paracetamol did absolutely nothing to my pain. After a few sleepless nights, I went back and asked for something a little more effective. She refused, and I decided to change GP.
Meanwhile, we went on a scheduled holiday to France. I had hoped my shingles would come to a natural end, but my pain continued unabated. People could see it on my face; so our kind neighbour asked whether she could help. I explained the situation, and she instantly claimed to have just the right treatment for me: she knew a healer who lived just round the corner and had helped many of her friends when they had suffered from pain.
“A healer?” I asked, “you cannot be serious.” I explained that I had conducted studies and done other research into this particular subject. Without exception, the results had shown that healing is a pure placebo. “I prefer to carry on taking even something as useless as paracetamol!” I insisted.
But she would have none of it. The next time I saw her, she declared triumphantly that she had made an appointment for me, and there was no question: I had to go.
As it happened, the day before she announced this, I had met up with a doctor friend of mine who, seeing I was in agony, gave me a prescription for gabapentin. In fact, I was just on the way to the pharmacist to pick it up. Thus I was in hopeful that my ordeal was coming to an end. In this optimistic mood I thanked my neighbour for her effort and concern and said something non-committal like “we shall see”.
A few days later, we met again. By this time, the gabapentin had done it’s trick: a was more or less pain-free, albeit a little dazed from the powerful medication. When my neighbour saw me, she exclaimed: “I see that that you are much improved. Wonderful! Yesterday’s healing session has worked!!!”
In my daze, I had forgotten all about the healing, and I had, of course, not been to see the healer. She was so delighted with her coup, that I did not have the heart to tell her the truth. I only said “yes much better, merci”
These events happened a few years ago, but even today, my kind and slightly alternative neighbour believes that, despite having been highly sceptical, healing has cured me of my shingles. To my embarrassment, she occasionally mentions my ‘miraculous cure’.
One day, I must tell her the truth… on second thoughts, perhaps not, she might claim it was distant healing!
On this blog, we have discussed the Alexander Technique before; it is an educational method promoted for all sorts of conditions, including neck pain. The very first website I found when googling it stated the following: “Back and neck pain can be caused by poor posture. Alexander Technique lessons help you to understand how to improve your posture throughout your daily activities. Many people, even those with herniated disc or pinched nerve, experience relief after one lesson, often permanent relief after five or ten lessons.”
Sounds too good to be true? Is there any good evidence?
The aim of this study, a randomized controlled trial with 3 parallel groups, was to test the efficacy of the Alexander Technique, local heat and guided imagery on pain and quality of life in patients with chronic non-specific neck pain. A total of 72 patients (65 females, 40.7±7.9 years) with chronic, non-specific neck pain were recruited. They received 5 sessions of the Alexander Technique, while the control groups were treated with local heat application or guided imagery. All interventions were conducted once a week for 45 minutes each.
The primary outcome measure at week 5 was neck pain intensity quantified on a 100-mm visual analogue scale; secondary outcomes included neck disability, quality of life, satisfaction and safety. The results show no group differences for pain intensity for the Alexander Technique compared to local heat. An exploratory analysis revealed the superiority of the Alexander Technique over guided imagery. Significant group differences in favor of the Alexander Technique were also found for physical quality of life. Adverse events were mild and mainly included slightly increased pain and muscle soreness.
The authors concluded that Alexander Technique was not superior to local heat application in treating chronic non-specific neck pain. It cannot be recommended as routine intervention at this time. Further trials are warranted for conclusive judgment.
I am impressed with these conclusions: this is how results should be interpreted. The primary outcome measure failed to yield a significant effect, and therefore such a negative conclusion is the only one that can be justified. Yet such clear words are an extreme rarity in the realm of alternative medicine. Most researchers in this area would, in my experience, have highlighted the little glimpses of the possibility of a positive effect and concluded that this therapeutic approach may be well worth a try.
In my view, this article is a fine example for demonstrating the difference between true scientists (who aim at testing the effectiveness of interventions) and pseudo-scientists (who aim at promoting their pet therapy). I applaud the authors of this paper!
Twenty years ago, I published a short article in the British Journal of Rheumatology. Its title was ALTERNATIVE MEDICINE, THE BABY AND THE BATH WATER. Reading it again today – especially in the light of the recent debate (with over 700 comments) on acupuncture – indicates to me that very little has since changed in the discussions about alternative medicine (AM). Does that mean we are going around in circles? Here is the (slightly abbreviated) article from 1995 for you to judge for yourself:
“Proponents of alternative medicine (AM) criticize the attempt of conducting RCTs because they view this is in analogy to ‘throwing out the baby with the bath water’. The argument usually goes as follows: the growing popularity of AM shows that individuals like it and, in some way, they benefit through using it. Therefore it is best to let them have it regardless of its objective effectiveness. Attempts to prove or disprove effectiveness may even be counterproductive. Should RCTs prove that a given intervention is not superior to a placebo, one might stop using it. This, in turn, would be to the disadvantage of the patient who, previous to rigorous research, has unquestionably been helped by the very remedy. Similar criticism merely states that AM is ‘so different, so subjective, so sensitive that it cannot be investigated in the same way as mainstream medicine’. Others see reasons to change the scientific (‘reductionist’) research paradigm into a broad ‘philosophical’ approach. Yet others reject the RCTs because they think that ‘this method assumes that every person has the same problems and there are similar causative factors’.
The example of acupuncture as a (popular) treatment for osteoarthritis, demonstrates the validity of such arguments and counter-arguments. A search of the world literature identified only two RCTs on the subject. When acupuncture was tested against no treatment, the experimental group of osteoarthritis sufferers reported a 23% decrease of pain, while the controls suffered a 12% increase. On the basis of this result, it might seem highly unethical to withhold acupuncture from pain-stricken patients—’if a patient feels better for whatever reason and there are no toxic side effects, then the patient should have the right to get help’.
But what about the placebo effect? It is notoriously difficult to find a placebo indistinguishable to acupuncture which would allow patient-blinded studies. Needling non-acupuncture points may be as close as one can get to an acceptable placebo. When patients with osteoarthritis were randomized into receiving either ‘real acupuncture or this type of sham acupuncture both sub-groups showed the same pain relief.
These findings (similar results have been published for other AMs) are compatible only with two explanations. Firstly acupuncture might be a powerful placebo. If this were true, we need to establish how safe acupuncture is (clearly it is not without potential harm); if the risk/benefit ratio is favourable and no specific, effective form of therapy exists one might still consider employing this form as a ‘placebo therapy’ for easing the pain of osteoarthritis sufferers. One would also feel motivated to research this powerful placebo and identify its characteristics or modalities with the aim of using the knowledge thus generated to help future patients.
Secondly, it could be the needling, regardless of acupuncture points and philosophy, that decreases pain. If this were true, we could henceforward use needling for pain relief—no special training in or equipment for acupuncture would be required, and costs would therefore be markedly reduced. In addition, this knowledge would lead us to further our understanding of basic mechanisms of pain reduction which, one day, might evolve into more effective analgesia. In any case the published research data, confusing as they often are, do not call for a change of paradigm; they only require more RCTs to solve the unanswered problems.
Conducting rigorous research is therefore by no means likely to ‘throw out the baby with the bath water’. The concept that such research could harm the patient is wrong and anti-scientific. To follow its implications would mean neglecting the ‘baby in the bath water’ until it suffers serious damage. To conduct proper research means attending the ‘baby’ and making sure that it is safe and well.
The discussion whether acupuncture is more than a placebo is as long as it is heated. Crucially, it is also quite tedious, tiresome and unproductive, not least because no resolution seems to be in sight. Whenever researchers develop an apparently credible placebo and the results of clinical trials are not what acupuncturists had hoped for, the therapists claim that the placebo is, after all, not inert and the negative findings must be due to the fact that both placebo and real acupuncture are effective.
Laser acupuncture (acupoint stimulation not with needle-insertion but with laser light) offers a possible way out of this dilemma. It is relatively easy to make a placebo laser that looks convincing to all parties concerned but is a pure and inert placebo. Many trials have been conducted following this concept, and it is therefore highly relevant to ask what the totality of this evidence suggests.
A recent systematic review did just that; specifically, it aimed to evaluate the effects of laser acupuncture on pain and functional outcomes when it is used to treat musculoskeletal disorders.
Extensive literature searches were used to identify all RCTs employing laser acupuncture. A meta-analysis was performed by calculating the standardized mean differences and 95% confidence intervals, to evaluate the effect of laser acupuncture on pain and functional outcomes. Included studies were assessed in terms of their methodological quality and appropriateness of laser parameters.
Forty-nine RCTs met the inclusion criteria. Two-thirds (31/49) of these studies reported positive effects. All of them were rated as being of high methodological quality and all of them included sufficient details about the lasers used. Negative or inconclusive studies mostly failed to demonstrate these features. For all diagnostic subgroups, positive effects for both pain and functional outcomes were more consistently seen at long-term follow-up rather than immediately after treatment.
The authors concluded that moderate-quality evidence supports the effectiveness of laser acupuncture in managing musculoskeletal pain when applied in an appropriate treatment dosage; however, the positive effects are seen only at long-term follow-up and not immediately after the cessation of treatment.
Surprised? Well, I am!
This is a meta-analysis I always wanted to conduct and never came round to doing. Using the ‘trick’ of laser acupuncture, it is possible to fully blind patients, clinicians and data evaluators. This eliminates the most obvious sources of bias in such studies. Those who are convinced that acupuncture is a pure placebo would therefore expect a negative overall result.
But the result is quite clearly positive! How can this be? I can see three options:
- The meta-analysis could be biased and the result might therefore be false-positive. I looked hard but could not find any significant flaws.
- The primary studies might be wrong, fraudulent etc. I did not see any obvious signs for this to be so.
- Acupuncture might be more than a placebo after all. This notion might be unacceptable to sceptics.
I invite anyone who sufficiently understands clinical trial methodology to scrutinise the data closely and tell us which of the three possibilities is the correct one.
Neck pain is a common problem which often causes significant disability. Chiropractic manipulation has become one of the most popular forms of alternative treatment for such symptoms. This seems surprising considering that neck manipulations are neither convincingly effective nor free of adverse effects.
The current Cochrane review on this subject could not be clearer: “Done alone, manipulation and/or mobilization were not beneficial; when compared to one another, neither was superior.” In the absence of compelling evidence for efficacy, any risk of neck manipulation would tilt the risk/benefit balance into the negative.
Adverse effects of neck manipulations range from mild symptoms, such as local neck tenderness or stiffness, to more severe injuries involving the spinal cord, peripheral nerve roots, and arteries within the neck. A recent paper reminds us that another serious complication has to be added to this already long list: phrenic nerve injury.
The phrenic nerve is responsible for controlling the contractions of the diaphragm, which allows the lungs to take in and release air and make us breathe properly. The phrenic nerve is formed from C3, C4, and C5 nerve fibres and descends along the anterior surface of the scalenus anterior muscle before entering the thorax to supply motor and sensory input to the diaphragm. Its anatomic location in the neck leaves it vulnerable to traumatic injury. Phrenic nerve injury can result in paralysis of the diaphragm and often leads to deteriorating function of the diaphragm, which can lead to partial or complete paralysis of the muscle and, as a result, serious breathing problems.
Patients who experience such problems may require emergency medical treatment or surgery. Sudden, severe damage to the phrenic nerve can make it impossible for the diaphragm to contract on its own. In order to make sure that the patient can breathe, a breathing tube needs to be inserted, a process called intubation. Artificial respiration would then be required.
American neurologists published a case report of a healthy man who consulted a chiropractor for his neck pain. Predictably, the chiropractor employed cervical manipulation to treat this condition. The result was bilateral diaphragmatic paralysis.
Similar cases have been reported previously, for instance, here and here and here and here. Damage to other nerves has also been documented to be a possible complication of spinal manipulation, for instance, here and here.
The authors of this new case report conclude that physicians must be aware of this complication and should be cautious when recommending spinal manipulation for the treatment of neck pain, especially in the presence of preexisting degenerative disease of the cervical spine.
I know what my chiropractic friends will respond to this post:
- I am alarmist,
- I cherry-pick articles that are negative for their profession,
- these cases are extreme rarities,
- conventional medicine is much more dangerous.
To this I reply: Imagine a conventional therapy about which the current Cochrane review says that it has no proven effect for the condition in question. Imagine further that this therapy causes mild to moderate adverse effects in about 50% of all patients in addition to very dramatic complications which are probably rare but, as no monitoring system exists, of unknown frequency. Imagine now that the professionals using this treatment more regularly than any other clinicians steadfastly deny that the risk/benefit balance is way out of kilter.
Would you call someone who repeatedly tries to warn the public of this situation ‘alarmist’?
Would you not consider the professionals who continue to practice the therapy in question to be irresponsible?
Highly diluted homeopathic remedies are pure placebos; at least this is what sceptics have been saying for about 200 years. This assumption is based on the fact that homeopathy’s plausibility is close to zero and that the totality of the reliable evidence fails to demonstrate that it works beyond placebo for any condition.
But, if this is true, why do so many patients swear by homeopathy and experience benefit from it? This question has been answered many times: THE BENEFIT IS NOT DUE TO THE REMEDY BUT TO NON-SPECIFIC EFFECTS OF THE CONSULTATION.
More confirmation for this conclusion comes from an unexpected source.
Indian homeopaths recently published a trial of individualized homeopathy in osteoarthritis. To be more precise, it was a prospective, parallel-arm, double-blind, randomized, placebo-controlled pilot study which was conducted from January to October 2014 involving 60 patients (homeopathy, n = 30; placebo, n = 30). All patients were suffering from acute painful episodes of knee osteoarthritis and visiting the outpatient clinic of Mahesh Bhattacharyya Homeopathic Medical College and Hospital, West Bengal, India.
The results show statistically significant reduction in 3 visual analogue scales (measuring pain, stiffness, and loss of function) and Osteoarthritis Research Society International scores in both groups over 2 weeks (P < .05). However, group differences were not significant (P > .05).
The authors conclude that, overall, homeopathy did not appear to be superior to placebo; still, further rigorous evaluation in this design involving a larger sample size seems feasible in future.
Considering what I wrote above, I would alter these conclusion to something much more reasonable: further studies of homeopathy are certainly feasible. However, they are neither necessary nor desirable.
TO PUT IT DIFFERENTLY: HOMEOPATHY BELONGS IN THE BOOKS OF MEDICAL HISTORY.
A reader of this blog recently sent me the following message: “Looks like this group followed you recent post about how to perform a CAM RCT!” A link directed me to a new trial of ear-acupressure. Today is ‘national acupuncture and oriental medicine day’ in the US, a good occasion perhaps to have a critical look at it.
The aim of this study was to assess the effectiveness of ear acupressure and massage vs. control in the improvement of pain, anxiety and depression in persons diagnosed with dementia.
For this purpose, the researchers recruited a total of 120 elderly dementia patients institutionalized in residential homes. The participants were randomly allocated, to three groups:
- Control group – they continued with their routine activities;
- Ear acupressure intervention group – they received ear acupressure treatment (pressure was applied to acupressure points on the ear);
- Massage therapy intervention group – they received relaxing massage therapy.
Pain, anxiety and depression were assessed with the Doloplus2, Cornell and Campbell scales. The study was carried out during 5 months; three months of experimental treatment and two months with no treatment. The assessments were done at baseline, each month during the treatment and at one and two months of follow-up.
A total of 111 participants completed the study. The ear acupressure intervention group showed better improvements than the two other groups in relation to pain and depression during the treatment period and at one month of follow-up. The best improvement in pain was achieved in the last (3rd) month of ear acupressure treatment. The best results regarding anxiety were also observed in the last month of treatment.
The authors concluded that ear acupressure and massage therapy showed better results than the control group in relation to pain, anxiety and depression. However, ear acupressure achieved more improvements.
The question is: IS THIS A RIGOROUS TRIAL?
My answer would be NO.
Now I better explain why, don’t I?
If we look at them critically, the results of this trial might merely prove that spending some time with a patient, being nice to her, administering a treatment that involves time and touch, etc. yields positive changes in subjective experiences of pain, anxiety and depression. Thus the results of this study might have nothing to do with the therapies per se.
And why would acupressure be more successful than massage therapy? Massage therapy is an ‘old hat’ for many patients; by contrast, acupressure is exotic and relates to mystical life forces etc. Features like that have the potential to maximise the placebo-response. Therefore it is conceivable that they have contributed to the superiority of acupressure over massage.
What I am saying is that the results of this trial can be interpreted in not just one but several ways. The main reason for that is the fact that the control group were not given an acceptable placebo, one that was indistinguishable from the real treatment. Patients were fully aware of what type of intervention they were getting. Therefore their expectations, possibly heightened by the therapists, determined the outcomes. Consequently there were factors at work which were totally beyond the control of the researchers and a clear causal link between the therapy and the outcome cannot be established.
An RCT that is aimed to test the effectiveness of a therapy but fails to establish such a causal link beyond reasonable doubt cannot be characterised as a rigorous study, I am afraid.
Sorry! Did I spoil your ‘national acupuncture and oriental medicine day’?