In response to treatment of neck pain

Dear Editor We wish to comment on the recent article “Treatment of Neck Pain” and the findings and conclusions provided by the Bone and Joint Decade Task Force [2]. Specifically, we wish to address the issues of radiofrequency (RF) neurotomy. The task force conclusion that “radiofrequency neurotomy for neck pain showed no clear advantage compared to sham or placebo procedures when subjects were selected by the person’s responses to anesthetic injections” is dissonant with the results of the Lord study [6]. We wish to clarify the facts and reality of the Lord study and demonstrate how the task force misrepresented the Lord study to reach an erroneous conclusion. The task force stated subjects were selected on the basis of a non-validated response to facet blocks as Lord did not require longer-duration pain relief with the longer duration anesthetic nor was pain relief required in any reasonably expected pharmacologic range. The reality is that Lord purposely did not rely on comparative blocks. Rather, Lord used a placebo-controlled triple block paradigm, which is the highest standard for diagnostic blocks and ensures maximal specificity [5]. Additionally, to qualify as a positive response, Lord required complete relief of pain with anesthetic injection and no response to placebo injection. The task force failed to recognize this fact. The task force stated that the randomization process resulted in an unequal distribution of potentially confounding baseline variables. They cite that 10/12 sham versus 4/12 active subjects were involved in litigation. The fact that unequal numbers occurred is evidence of the honesty of the randomization process. The implied criticism is that litigation biases outcomes from RF neurotomy. However, the study did not show any difference in the active group between those patients involved in litigation and those not involved in litigation. Additionally, four subsequent RF neurotomy studies [1, 4, 7, 8] have consistently shown that litigation does not significantly affect outcomes statistically. The task force reported that blinding was in doubt as 42% of the active group developed long-term anesthetic or dysesthetic areas of skin and none of the control group developed changes. They stated that these changes revealed the treatment assignment in nearly half of the active treatment group. Subjects did not have any expectation that they would or would not develop numbness or dysesthesia post procedure. Subjects were only warned when they were given informed consent to expect the possibility of such side effects. Further, these changes develop as a normal consequence of the neurotomy procedure and are impossible to mask. The reality is that, given the difficulty of blinding with any study involving an invasive procedure, Lord maintained blinding of subjects admirably well. The difficulty of performing such a study is evidenced by the extremely limited number of published sham studies involving an invasive treatment. The task force states there was no statistical difference between groups at 3 months after surgery (seven subjects in the RF group reported >50% improvement in pain vs. three subjects in the control group (P = 0.21) (Fischer exact test). The task force elected to modify the statistics reported in the study in order to claim that there was no statistically significant difference in outcome. One could interpret this as evidence of premeditated bias against the study. The paper was subjected to statistical evaluation by the consultant statistician of the New England Journal of Medicine. The New England Journal of Medicine is not known to publish material that is statistically flawed. The fact is the task force applied inappropriate statistical methods. The methods of the study did not use ad hoc tests of association, such as Fisher’s exact test, at arbitrary time intervals. Prospectively, the study used Kaplan Meier Survival Curves and Cox’s Proportional Hazards Model, which is the appropriate test for small studies but ones which have protracted follow-up periods (in this case over 1 year). Indeed there was a statistically significant difference in the Lord study. The primary outcome used in the Lord study was the median time to return to at least 50% of the pre-treatment pain level. The fact is that it took 263 days for the active versus 8 days for the sham group (P = 0.04) (Mantel-Haenszel test) to return to 50% of their original pain. The Lord study also used very stringent criteria for successful outcome. Success was not defined as 50% relief of pain. Rather, for the treatment to be considered successful, a patient had to report “complete relief from the pain for which he or she was treated”. Complete relief was defined as a score of 0–5 of a possible 100 on the visual analog scale, a word count of three or less on the McGill Pain Questionnaire, and the restoration of all four subject-specific activities of daily living that the patient had listed before the operation to be substantially limited. Additionally, to the questions “Is your usual pain present?” and “Do you require further treatment?” the patient had to answer in the negative. In fact, 7/12 (58%) of the active group versus 1/12 (8%) of the sham group met this stringent criteria of success at 6.5 months. The task force also states that the randomization code was broken at 3 months, creating the impression that the study was unblinded at 3 months by misrepresenting the facts. The paper states that the unblinding took place at 3 months in a limited fashion. Only patients who obtained no relief were unblinded, so that they could be offered escape treatment. This was an ethical obligation and a practical consideration. None of the patients who obtained relief were unblinded, and the independent assessor was never unblinded. In those patients, blinding was maintained for up to 1 year. Additionally, investigators who have successfully completed a sham-controlled study know all too well that it is extremely difficult to recruit patients without allowing for crossover to the active treatment. Given the success of the treatment, it would have been impractical and unethical to withhold treatment of the sham group. The task force also states the re-operation rate was the same in each group. The task force falsely uses re-operation rate as an outcome measure to imply that there was no difference in outcome. What the task force chose not to reveal was that the so-called re-operation was for different purposes in the two groups. In the active group, re-operation reinstated relief, and in the sham group it provided relief after sham treatment had failed to do so. The task force accuses Lord of not having used validated outcome measures. VAS and McGill pain questionnaire were utilized. To our knowledge, these were and are considered validated outcome measures. Furthermore, additional outcome measures were used, which might easily be overlooked by an imperceptive reader. To be considered a success, subjects had to restore four nominated activities of daily living, such as return to work, and have no need for other health care. Although not validated at the time of publication, these secondary outcome measures, now known as patient-specified functional outcomes, have been validated [3, 9, 10]. The criticism of outcome measures is, therefore, unfounded. The task force in Table 2 states that there is not enough evidence to make a determination of whether RF neurotomy is helpful for cervicogenic headache. The task force stated that due to a “small number of direct comparative trials in the literature we considered the results of extraordinary clinical case series”. They failed to acknowledge one such extraordinary study, that is, a study on third occipital nerve neurotomy for C2–3 zygapophysial joint pain in which cervicogenic headache was the primary complaint [4]. In this study, Govind selected 49 patients with upper axial neck pain and cervicogenic headache based upon complete relief of pain following comparative bupivicaine and lidocaine third occipital nerve blocks. RF neurotomy was performed with a large gauge electrode with overlapping lesions to compensate for the variable location of the third occipital nerve. Success was defined at complete relief of pain, no narcotic usage and full restoration of patient specific ADLs. Success occurred in 43/49 (88%) patients with a median duration of relief of 297 days. These results are unparalleled in the treatment of cervicogenic headache. I trust the readers can now appreciate the truth revealed by the Lord and Govind studies: cervical medial branch and third occipital radiofrequency neurotomy has been shown to be a powerful and valid treatment for neck pain in appropriately selected patients.