Got my electronic issue of Spine today, and upon browing the titles I came across this paper:
"Does maintained spinal manipulation therapy for chronic nonspecific low back pain result in better long-term outcome?" by Mohanned Senna and Shereen Machaly. Spine 2011 15 August; 36(18):1427-1437.
In a nutshell: 88 participants were randomized to one of 3 groups: group 1: sham manipulation over a 1-month period then ROM exercises for 10 months, group 2: 12 manipulations over a 1 month period then ROM exercises for 10 months, group 3: 12 manipulations over a 1 month period then continued 'maintenance' manips every 2 weeks for 10 months plus the same ROM exercises. Results very briefly: things worked out best for the maintenance group in terms of pain, disability, quality of life, ROM and global impressions of change.
So, guess that's it then, all of our chronic LBP patients should get spinal manipulation, then maintenance manips every 2 weeks for...ah...many years (quoting an episode of The Simpsons there).
Truth be told, this is actually a fairly well-designed study, as far as non-pharmaceutical clinical effectiveness trials go. We're told the assessors were blinded to group allocation, randomization appeared to have worked well, the three arms make sense given the question that's being answered. In fact this study would score well on most critical appraisal tools for an RCT. But there are one or two areas that I just want to address before we give this study our full stamp of approval.
First, recognize that this is an effectiveness, or pragmatic, study, which means we can't comment on mechanisms. An efficacy, or explanatory, study would be required for that. I suppose one could argue that the improvements seen in the maintained group at a point 10 months after the first two groups stopped receiving consistent care were due more to the ongoing contact and support of a health care provider rather than the actual manipulations. However, the fact that the two active treatment groups showed better outcomes after 1 month than did the sham group protects against the criticism somewhat.
Other things that come to my mind here, and these are not meant to be a severe criticism, as by and large this study has been conducted at least as well as most in this area, are largely to do with the more subtle nuances of the study. For example, the maximum reported mean difference in pain VAS score is 19.26 mm in the maintenance group. A statistically significant finding, but is it clinically significant? Most reports on the VAS would suggest a change of roughly 20% of the scale would be considered clinically significant. We aren't given the data required to calculate a 95% confidence interval on the change score, but chances are it would range from about 15 or 16 up to 23 or 24mm (based on the SE presented for the different point estimates). Speaking of statistical significance, with 6 measures captured across 4 times points, there are at minimum 24 comparisons being performed, with a 5% chance of making an alpha error each time (stating a difference exists where not truly does). We would expect that at least one of these findings would be significant (p<0.05) by chance alone, so something to keep in mind.
What bothers me most, and again I don't mean this to be damming, but something to consider when you're reading literature, are the fact that of 154 patients examined, 93 were eligible, and 88 completed the first month of treatment (57% of those screened). What we're missing here is a description of why those people screened but not enrolled were deemed ineligible. Even more troubling is that a full 50% of the control sample dropped out by the final 10 month follow-up. Again, we're not given the reasons why they dropped out, or whether those who dropped out were at least statistically similar to those who were retained. When one considers the reasons for dropping out of a prospective study, you have to consider either a severe worsening of a condition, or a major improvement, and we're not sure what occurred in this sample. Of course other things like moving or simply disinterest also occur, but it would have been good to know these things. The authors did use what appears to be a reasonable method for data imputation for missing data, but that's far from perfect especially when a large portion of your data is missing. Now keep in mind this may all be moot - it may well be the case that all 50% of the people in the control group dropped out because they were actually worsening, in which case the results would be even more compellingly in favour of maintenance manips had they been retained. But unfortunately we just don't know.
The bigger issue at hand now, is what happens when this report gets into the hands of the lay public? Does 'maintenance' therapy for chronic LBP become the norm? I would have to say I hope not, but here we go, evidence right in front of us. Truth be told, I wanted to review this paper and find some glaring weakness that would easily discredit it, but it wasn't there (unless I'm missing something). The authors are both MDs from Egypt, a quick google/pubmed search doesn't reveal anything troubling about them as far as vested interests in manipulative care. The study was unfunded, which can be viewed as either good (no shenanigans from an external private funder) or bad (does that mean the authors invested their own funds into the project? Did that influence the results?).
We all know one study doesn't prove or disprove anything, and there are other studies available to suggest that sham manipulation is as effective as active manipulation, or that active manipulation is not more beneficial than other types of treatment, but I do have to say that this particular study is one of the more well-designed ones in the field. So, I'd love to hear your comments on this - where do we go from here?