Are We Treating Women With Postmenopausal Osteoporosis for Their Low BMD or High Fracture Risk? (2005)

Editor's Preface In our August 2005 issue, we published a Letter to the Editor by Dr Murat Api entitled, Are We Treating Women With Postmenopausal Osteoporosis for Their Low BMD or High Fracture Risk? His letter related in part to the paper Ten Years' Experience With Alendronate for Osteoporosis in Postmenopausal Women, which had been published in the New England Journal of Medicine in 2004. Whereas Dr Api's letter successfully passed through the review process, we failed to provide the authors of the earlier study with a chance to respond. It has always been our position to provide the Letters to the Editor that we choose to publish to the authors whose study is being critiqued so they can respond. Although the original paper was not published in JBMR, we accept it would have been better to have given the original authors a chance to respond. We apologize for this oversight in this case. A response by those original authors follows. In a recent letter, Dr Api concluded that our study, reported in the New England Journal of Medicine last year,1 lacked adequate statistical power to compare antifracture efficacy between the groups we studied. This of course is correct, as we pointed out in the publication. The study was designed with change in BMD as the primary endpoint. The occurrence of vertebral and nonvertebral fractures was monitored as part of the safety analysis, as we explained. Unfortunately, many of Dr Api's other comments are erroneous. One problem is that Dr Api attempted to reanalyze our baseline data without having inquired as to whether his assumptions were correct. Dr Api inferred that there was a significant difference in the prevalence of vertebral fractures between the groups at baseline. In fact, the baseline spine films for six of the participants in the 10-mg group and two in the discontinuation group, while adequate for determining eligibility for a trial with BMD as the principal endpoint, were not technically adequate to conclusively determine whether a baseline vertebral deformity was present. For this reason, application of the percentages that we reported to the entire set of patients was not appropriate. When the correct numbers are used, the baseline prevalence of vertebral deformities did not differ significantly between groups by the χ2 test or Fisher's exact test. Dr Api's letter contains a number of additional conceptual errors. For example, Fig. 1 ostensibly presents morphometric vertebral fracture occurrence data from our reports1, 2 and the data of Silverman et al. from MORE3 as rates. However, these are actually cumulative incidence percentages over the respective observation periods, not occurrence rates. As we noted in the original publication, such rates cannot be precisely calculated because the time to occurrence is generally not known for morphometric vertebral fractures. Silverman et al.3 made the same distinction. Even if true fracture occurrence rates had been available for our study, it would not be appropriate to compare them directly with rates from independent trials, because participants in different trials come from different population pools, at different time-points, and may be recruited with different entry criteria, and are treated differently and monitored over different intervals. Furthermore, fracture assessment techniques cannot be assumed to be identical between trials. Notably, Dr Api's figure attempts to directly compare cumulative percentages over our first 3 years with our last 5 years and 3 years of observation by Silverman et al. Whereas comparison of occurrence rates would be problematic, it is clearly even more inappropriate to compare cumulative incidences over such different intervals. Any comparison of data from our first 3 years2 with our follow-up study (years 6–10) should also take into account the important contribution of aging to fracture risk (as we did in our report). In addition, Dr Api's comments contain a number of specific factual errors. In Fig. 1, the incidence of fractures should be 5.0% in our 10-mg group, and the percentages reported for the placebo groups of Silverman et al. were 4.26% and 20.2% and not 1.5% and 7.7%. There seems to be some lack of clarity concerning the distinction between data that are suitable for primary efficacy analysis and those that are suitable for safety evaluation but insufficient to support an efficacy comparison. From the beginning, we have been clear that the primary endpoints in our study have always been changes in BMD, particularly at the lumbar spine. Changes in biochemical markers of bone remodeling activity were secondary endpoints. It has been pointed out that changes in BMD and biochemical turnover markers are associated with differences in efficacy among anti-catabolic drugs.4 The sample size in our trial is a fraction of that required for a formal antifracture efficacy comparison between actively treated individuals.5 That is a point that we clearly made in our report. However, there is value in examining the occurrence of relatively infrequent events to determine whether there is a “signal” of a safety problem. As we reported, there was no such signal suggesting any harmful effect on bone fragility even in individuals on the higher dose of alendronate for the full 10 years in comparison with those with shorter exposure or a lower dose. Nothing about our findings supports Dr Api's conclusion that they are “biologically unexplainable.” In fact, our findings are quite consistent with the original 3-year publication and support our original conclusions that continuous treatment with alendronate 10 mg daily for 10 years was associated with sustained therapeutic effects on BMD and bone remodeling, with no indication of any discordance between these effects and fracture safety data from our trial.