No relevant conflicts of interest.
Letter to the Editor:
I’m writing regarding the article by George et al. on TMS in the May
2010 issue (Volume 67, No. 5, pages 507-516).
I’ve always been skeptical regarding the efficacy of TMS, partly
because it affects primarily the superficial layers of the cortex, while
moods like depression are thought to involve deeper structures in the
brain (e.g. the limbic lobe). So I may be overly critical, but I question
whether this study is, as the authors state, a “relatively unambiguous
demonstration of a treatment effect in the absence of unblinding”.
Several issues deserve clarification. In their “Concomitant
Treatments” section, the authors indicate that remission was defined as a
Ham-D score of 3 or less; was this a misprint? “3” is unusually low; if
they really used 3 to define remitters, was this chosen a priori, before
seeing the data.
The percentage of responders was quite low, only 15% in the active
group and 5% in the sham group. It’s true that these were relatively
refractory patients, but one still might have expected a higher response
rate. Somewhat paradoxically, perhaps, the response rate in Phase II,
which provided open TMS treatment, yielded a much higher response rate,
about 30%, whether patients received active or sham treatment during Phase
I. This is hard to explain, and suggests that patients were not so very
While the authors present a number of analyses, they don’t present
what I think would still be considered the most standard analysis,
including all data, last observation carried forward, on an intent to
treat basis. Their footnote “a” on Table 5 indicates that scores missing
at the end of Phase I were considered as missing observations, rather than
using LOCF. This resulted in the loss of about 10% of patients, in data
analyses. There are pros and cons to different statistical approaches,
but I think the standard analyses should be presented, even if other
analyses were stated a priori to be primary and were therefore given more
The authors report under “Site Differences” that 15 of the 18
remitters came from only two of the four sites. They relate this to those
two sites also having less treatment resistant individuals, but since the
response to Phase II was so much better than to Phase I, I think that they
should also indicate whether most of the remitters at the end of Phase II
also came from those two sites. I think too that the authors should state
which sites had the large number of remitters; clearly one of the sites
(MUSC) has been most involved with the development of TMS, and might have
the most conflict of interest (even if this conflict is not financial).
The authors made a valiant attempt to preserve the blind, but treaters, as
they indicate, were able to guess whether patients were receiving active
treatment or sham, better than chance. This may also occur in medication
studies, but I think it’s especially relevant when trying to document
efficacy with novel treatments.
Jeffrey A. Mattes, M.D.