Chiropractic spinal manipulation for neck pain: reply
Article Outline
The critiques by Bogduk and by Peloso and Gross are a welcome opportunity for me to clarify several important points. Bogduk stated that the conclusions drawn from my systematic review are “not constrained by methodologic flaws” and that I was “somewhat generous” in my assessment. I obviously agree with these statements, but I doubt that the majority of chiropractors would. The bottom line of Bogduk's comments is that the balance of risk and balance of chiropractic spinal manipulation is disappointing; therefore chiropractic spinal manipulation is inferior to other treatment options.
The critique by Peloso and Gross is considerably more biting because these authors found flawed methodology and unsupported opinion in my article. They implied that my review was a “traditional narrative review,” yet in truth it was a systematic review without a meta-analytical approach. The latter was deemed impossible and largely irrelevant (only 2 long-term studies were found). I did not follow the Cochrane guidelines, but, having published several dozen of such articles, I am aware of the recent literature “on the proper conduct of a systematic review in the last 10 years.”
Specifically, Peloso and Gross stated that my review suffered from selection bias. I think they should name exactly which studies I omitted (I think none) rather than making an abstract allegation. They also seemed to ignore the fact that manipulation and mobilization are 2 different therapeutic techniques. Manipulation typically includes the forceful movement of a joint beyond its physiologic range of motion, whereas mobilization does not.
Peloso and Gross then wrote, “Ernst suggests that the articles on spinal manipulation should be limited to chiropractic manipulation.” This is clearly not true. Whether one conducts a systematic review of chiropractic manipulation or of manipulation in general relates to the research question one asks. I defined mine, and others may define theirs. One could argue that mine is too narrow but I would disagree, and the reasons for that are provided in my article. If I had included all manipulation studies and (perhaps) generated a negative overall result, would not chiropractors have criticized me because in some of these studies manipulation was performed by healthcare providers less skilled in these techniques than they are? Similarly, if I had included whiplash studies, would I not be open to criticism for lumping together conditions that have little in common, ie, traumatic and nontraumatic neck pain?
Peloso and Gross are most definitely wrong when stating that the Jadad score “was developed for studies of drugs.” In fact, even the original article included a subset of studies that “were selected randomly from a set of controlled studies published between 1966 and 1991, which had been identified by a high yield Medline strategy”1—not a word about drugs! Even if the score had originally been designed for drug trials, it is unquestionably used today by many for other studies as well. Peloso and Gross mislead us when writing that hands-on techniques defy double-blinding. It is often possible to blind the patient and almost always possible to blind the assessor of the primary outcome measure. What is sometimes not possible is therapist blinding. Regarding blinding pain assessments, the Jadad score was specifically designed for pain studies. The Cochrane Back Pain Group might have elected another score, but a systematic comparison of most scores available to date showed that any score has its problems and implied that the Jadad score is at least as good as most of its competitors.2 Peloso and Gross are furthermore wrong in stating that my “review excluded trials of outcome measures, such as range of motion … ” Such trials were included if they also measured pain.
Peloso and Gross rightly state that “mistakes can easily be made by using a single data extractor.” I recognize that 2 or 3 reviewers would have been preferable. Yet, in my view, it would be more relevant to show that I did make mistakes in data extraction. In the absence of such a demonstration, the argument is largely irrelevant as a specific critique of my article.
Peloso and Gross amused me with their statement “pain might be the cardinal symptom of neck troubles.” It was meant to show that my review neglected other outcome measures. The fact is, however, that my review was not about “neck troubles” but about neck pain. Who would argue against the relevance of pain in neck pain?
I wish Peloso and Gross were correct in stating that chiropractors are moving away from historical (false and even dangerous3) concepts. It is my impression that, internationally, many chiropractors do the opposite. To the best of my knowledge, there are no reliable data to show which proportion is moving in this and which in that direction.
Perhaps the most important issue raised by Peloso and Gross is that of harm through chiropractic manipulation. “Rather than report some of the recent data on harm, Ernst largely quotes his own studies and an opinion piece…[which] does not present data on the incidence, prevalence, or risk factors for harm … ” The very reason why I quote my own work is to show that underreporting in our series was 100%, which renders the calculation of incidence or prevalence figures nonsensical.4 I therefore suggest that most such figures published so far are unreliable. Essentially this means that we urgently need to generate reliable data.
Peloso and Gross pointed out that other treatments for neck pain are also not supported by good evidence. However, they only mentioned drug treatment and omitted exercise therapy as mentioned by Bogduk and by me. Finally, Peloso and Gross quoted data on patient satisfaction with chiropractic care. Yet I would insist that patient satisfaction and effectiveness of treatment are 2 distinct entities. I agree with Peloso and Gross that interdisciplinary finger pointing is not called for. My aim was to “evaluate the effectiveness of chiropractic spinal manipulation for neck pain.” This, I hope, should be a permissible objective even at a time when we all seem to bend over backwards with political correctness.
References
- . Assessing the quality of reports of randomized clinical trials (Is blinding necessary?). Control Clin Trials. 1996;17:1–12
- . The hazards of scoring the quality of clinical trials for meta-analysis. JAMA. 1999;282:1054–1060
- . Aspects of MMR. BMJ. 2002;325:597
- . Neurological complications of cervical spine manipulation. J R Soc Med. 2001;94:107–110
PII: S1526-5900(03)00736-3
doi:10.1067/S1526-5900(03)00736-3
© 2003 American Pain Society. Published by Elsevier Inc. All rights reserved.
