Title: Mindfulness is associated with improved psychological well-being but no change in stress
biomarkers in breast cancer survivors with depression: a single group clinical pilot study
Version: 6 Date: 05 May 2022
Reviewer:  Lauren A. Zimmaro
Reviewer's report:
Thank you very much for the opportunity to review the paper entitled: “Mindfulness is associated
with improved psychological well-being but no change in stress biomarkers in breast cancer
survivors: a single group clinical pilot study.”  I found this article to be interesting and had
several strengths included the focus on a highly distressed (BDI>13) group of survivors and
the use of a range of biomarkers. The authors clearly put a lot of time and effort in not only
conducting this study, but in trying to address the comments put forth from the original review.
In the current form of the paper, I’m afraid that the novelty/impact of the work is a bit lost.
However, I have several suggestions in how the authors may wish to revise their work to
highlight a potential unique contribution that their study has, in light of the very saturated field
when it comes to MBSR, BC, and psychobiological outcomes.
Rationale/Intro :
1) Overall, it seemed that the paper relied on largely older literature, which undermined the
strength of the rationale. (Most recent studies on mindfulness/breast cancer/biomarkers were
in 2017, with the exception of one 2019 study which isn’t mentioned until the end of the
discussion.) Updated citations and relevant literature review would certainly be beneficial, as in
the current format, the novel nature of the current study is hidden.
2) On a related note, a stronger focus on what gap in the literature this study fills is needed, as
the authors themselves note that mindfulness in cancer and biomarkers have been extensively
studied. To me, the most important and novel aspect was the focus on a population with high
depressive symptoms. This would be really novel and important to bring out early and to focus
on generally in this work, given that many MBI’s don’t always require that participants meet a
certain distress threshold to enroll, despite those patients having the greatest need and the most
to gain.  If the authors were to highlight the unique nature of focusing on this population, it
could help clarify the nature of some of their findings (e.g. low at-home practice rates due to
low motivation or behavioral activation due to high depression; lack of change in biomarkers
given the potentially robust nature of the stress response system in highly depressed patients).
(See more about this in my comment #4)
3) Similarly, the authors should provide rationale for measures chosen other than that they
have not been done before. For example: How could knowing more about resilience add to our
understanding of MBSR in BC patients? Or how could these specific outcomes be important
outcomes to consider especially in the context of highly depressed survivors?
Study Design
4) Given that this was a pilot study, general feasibility (i.e. overall attendance rates for 8 sessions,
descriptives of home-practice rates) should be reported, and prior to describing preliminary
effects. (For example, it was unclear the number of sessions that were completed by the group,
the number of patients who did not practice at home at all, etc.)  Not only is that in line with
general standards for reporting on pilot studies, but understanding the feasibility of such a
program in a highly depressed population is a current gap in the field to the best of my knowledge
(see comment #2). In addition, this information would provide key context for the psychological/
biological null findings, given that the sample was likely experiencing depressive symptoms that
could interfere with program engagement (e.g. low behavioral activation, fatigue), which may
in turn explain the lack of changes observed in key MBSR mechanisms of greater mindfulness,
greater self-compassion, and decreased perceptions of stress, as well as no change in biological
outcomes.
Measures/Analyses
5) The authors used the FFMQ which is one of the most commonly used measures. However,
the total score is not suggested to be used by Baer et al and other validation studies of the FFMQ,
given that those five factors are quite distinct. In particular, the Observing subscale can be very
different for mindfulness naïve vs. mindfulness practitioners. It would be my suggestion to run
the following secondary analyses and perhaps include as footnotes or elsewhere in the paper:  a)
the same analyses you’ve done, but using the FFMQ score without the observing subscale added
in; b) analyses for changes in the 5 subscales independently – not for p-value level of change per
se, but for preliminary effect sizes and to explore whether there are any signals of change at all.
6) Along these lines, it seemed that it could be a compelling argument that a potential change
in FFMQ, SCS, and PSS could have been masked by including both “practitioners/adherent”
participants along with those who did not practice/adhere to the program or to home practice.
It would be worthwhile to explore whether those three measures changed but only within the
sample of N=15 (or if there ends up being a way to group participants based on # of completed
sessions to understand who was “adherent” vs not). The rationale for this would be that since
mindfulness, scs, and pss could possibly be considered mechanisms of change, it would make
sense that only the participants who engaged in these skills/practice would have changed in
those outcomes.
Minor Comments
1) Kindly closely review the manuscript for typos, grammar errors, and run on sentences. I
understand it can be hard to see those when using track changes, so they tend to be sometimes
get hidden within edited versions!
Thank you again for the opportunity to review this paper, and best of luck to the authors!