Yu-Po Lee, MD
Assistant Clinical Professor, UCSD Department of Orthopaedic Surgery
I am writing this letter in response to “A Randomized Trial of Vertebroplasty for Osteoporotic Spinal Fractures,” published August 6, 2009 in the New England Journal of Medicine.1 First of all, I must commend the authors of this article for attempting to conduct a prospective, randomized clinical trial, which is inevitably very difficult to execute. While I do not doubt the good intentions of the authors and the Journal for publishing this paper, I have some major concerns regarding the methodology and presentation of the results.
Only 131 patients were included in the study, which was conducted at 11 centers. Of the pool of eligible patients, only 7% were enrolled. We know that enrollment is a common problem in all randomized, controlled studies; in this particular study, because such a large number of patients declined to be in the enrolled, a potential selection bias may exist. A patient with severe pain could have declined to be in the study, electing to have the “real” procedure. This leads potentially to a bias where patients who were improving, or had less pain and were more likely to improve on their own in a short period of time, were entered.
Additionally, the authors revised their inclusion criteria to include patients who had relatively low VAS pain ratings. While the authors mentioned that the reason why they included patients with a pain scale of 3 was so that they could increase enrollment in the study, I believe that this ultimately had a detrimental effect on the study. Patients who complain of pain at level 3 do not have much room for improvement and, thus, any “significant differences” between the control and experimental group would be difficult to detect. Furthermore, very few clinicians would do a vertebroplasty on a patient with a pain score of less than 5. Thus, some of the patients in this study were not truly representative of the typical vertebroplasty patient and, so, the results of this study cannot be said to be typical of vertebroplasty. It should be pointed out here that the authors published their protocol for this study in 2007 in BMC Musculoskeletal Disorders.2 In their initial pilot study, the vertebroplasty patients had an average pain reduction of 7.1 on the VAS scale. This is more than twice the pain reduction reported in this study. This suggests that modifying the protocol to include patients with a pain level of 3 probably altered the results of this study.
Despite these concerns, the authors noted that “there was a trend toward a higher rate of clinically meaningful improvement in pain (30% decrease from baseline) in the vertebroplasty group (64% vs 48%, P = .06).” Inclusion of more patients with higher pain scores, and not changing their initial outcome end point, could have led to a significant difference.
The crossover rate is also a significant area of concern. “At three months, there was a higher cross over rate in the control group than in the vertebroplasty group (43% vs 12%, P < 0.001),” which was statistically significant. The interpretation is that 43% of patients in the control group were not satisfied with their treatment, compared to only 12% in the vertebroplasty group. This is an important point. This may be a more objective measure of success of a procedure than the standard pain scores, which are subjective, and can be affected by the patients' mood, aches/pains, medical condition, or memory.
The study used an intent-to-treat model. That works best when there is a relatively equal amount of crossovers from group to group, and when the crossover numbers are not excessive (43% is almost half of the patients in the control group). The SPORT trial with its various components published by Weinstein et al had similar difficulties in crossovers.3 Though the SPORT trial authors started with an intent to treat, and published that, they also analyzed groups as treated and looked at an observational cohort to see how those patients did. That should have been done here, especially with these very low enrollment numbers.
Furthermore, the authors do not appear to have assessed their failures in a manner that most clinicians do. If a patient had a poor outcome, it is unclear from the report that they had a new workup, including new images (radiographs, MRIs, CT scans) and/or laboratory studies to see if: a) the correct level was done; b) cement had leaked out in the vertebroplasty group; c) a new fracture had occurred; and/or d) another etiology for the pain could be determined. This would be standard treatment in failure assessment in most clinically active practices. With this diagnosis, in this age group, it should have been done here, if it was not.
The entry criteria also seem weak. An MRI to determine levels of fracture(s) (occasionally there are more fractures noted on an MRI than on preoperative radiographs) and age of fracture (by edema on MRI) were not routinely done unless “the age of the fracture was uncertain.” This, to us, is not standard practice, and may have resulted in missed fractures or included fractures that had already healed (no residual edema or MRI).
Just because this was a randomized controlled trial (RCT) does not make it a good, scientifically valid study. When the numbers are low, the ranges and standard deviations high, the outcome end-points modified during the procedure, and the entry criteria and follow-up soft, the study needs to be questioned. There are a host of non-RCT articles on this topic demonstrating excellent results from vertebroplasty compared to nonoperative care. The success with vertebroplasty, in general, is reported as significantly higher than demonstrated here, which raises the question as to indications, follow-up, and possibly technique.
Finally, the authors state that there had to have been a placebo/surgical intervention effect as demonstrated by the control group, as the bupivacaine treatment could not last throughout the follow-up period. Patients who develop compression fractures are older and often have concomitant degenerative disk disease and facet joint arthritis that often respond to local treatments. Additionally, soft tissue trauma accompanies bone fractures.
The soft tissue injury is often underappreciated and difficult to assess on imaging studies (particularly on radiographs). A local injection over the facet joints and/or in the muscles/ligaments with bupivacaine and lidocaine could act as a nerve block or a treatment for “muscle pain.” Manchikanti et al have shown that facet injections with bupivacaine can last up to 3 months or more.4 Other studies also support the fact that nerve blocks with local anesthetics can last 3 months or more.5, 6 Thus, instead of concluding that vertebroplasty was no better than a sham procedure, they should have questioned their control group, especially when the control group pain level decreased from a baseline of 7 to 4 at follow-up. The use of normal saline would probably have been a better control group for this study.
In summary, I have some reservations about the methods of this study and the conclusions drawn. My concern is that this will mislead patients and physicians into believing that vertebral augmentation is not beneficial despite the extensive literature demonstrating the efficacy of vertebral augmentation. Hopefully, more prospective studies, particularly with appropriate sample size and placebo control group, on vertebral augmentation will elucidate its efficacy.