Recommendation
based on reviews by Samuel Westwood and 1 anonymous reviewer
Thank you to the authors for comprehensively addressing the comments I'd made. Their responses are reassuring, and I believe the changes they've made to their manuscript both alleviate my concerns, and provide a robust means to understand their planned analyses.
DOI or URL of the report: https://osf.io/hv9wd?view_only=7ffd92cd9af94dfcb97e8b1a8602a9dc
Version of the report: 2
, posted 20 Sep 2024, validated 20 Sep 2024Dear Joel Diaz-Fong,
Thank you for submitting your Stage 1 Registered Report entitled “Noninvasive Neuromodulation of Visual Perception and Neural Connectivity in Body Dysmorphic Disorder”.
I have now received reports from two expert reviewers who have provided thoughtful comments. Their feedback is generally positive, making constructive suggestions that will help strengthen the rationale for the study design, and more clearly justify certain analytical decisions.
One key issue to address is related to the power analyses presented in the Design Table in page 38. Please justify the numbers presented for expected effect sizes and auto-correlations. You will require reasonable objective reasons for why an effect would be just worth missing out on (https://doi.org/10.1525/collabra.28202) which should be done for every row in the Design Table. Exploratory tests should be excluded from the Design Table, and should not be mentioned in the Stage 1 submission, however, they can be reported in the Stage 2 in a non-pre-registered results section.
Best wishes,
Anna Furtjes
The authors plan to investigate body dysmorphic disorder (BDD), a psychiatric condition characterized by perceptual distortions of physical appearance, which may be linked to abnormalities in visual processing. They aim to examine the effects of combining two types of repetitive transcranial magnetic stimulation (continuous and intermittent theta burst stimulation) with a visual attention modulation paradigm on neural connectivity and visual perceptual biases in 40 adults with BDD or subclinical BDD. I have no hesitation this would make a valid contribution to the field, provded that make the following revisions:
Major Revisions
1. The authors do not provide a clear justification for why they are using theta burst stimulation (TBS) other than citing previous studies that have demonstrated significant effects. It would strengthen the rationale if the authors could explain whether theta rhythms are specifically associated with the core symptoms of BDD or if the visual processing deficits observed in BDD are linked to disrupted theta rhythms. Establishing a causal mechanism that connects theta rhythms to the underlying pathophysiology of BDD would provide a more compelling rationale for the use of TBS in this context. Additionally, this would help clarify the neurophysiological understanding of BDD and how it relates to the observed symptoms and visual processing abnormalities.
2. The authors’ description of TBS effects is potentially misleading because it does not account for the known variability in TBS responses among participants. Recent research, such as the study by Corp et al. (2020), has shown significant interindividual variability in TBS outcomes. The authors should acknowledge this variability and consider incorporating potential sources of this variation, such as baseline MEP amplitude, target muscle, age, time of day, and TBS timepoint, into their analysis model. This inclusion would enhance the accuracy and relevance of their findings.
A useful reference:
Corp, Daniel T. et al. (2020). Large-scale analysis of interindividual variability in theta-burst stimulation data: Results from the ‘Big TMS Data Collaboration’. Brain Stimulation: Basic, Translational, and Clinical Research in Neuromodulation, 13(5), 1476-1488.
3. The rationale for not including a sham condition in the study is not entirely persuasive. This issue could be addressed by either informing participants that they may receive sham or real stimulation (or even misleading them by stating that everyone will receive real stimulation), which would help manage prior expectations, or by stimulating a different, non-targeted brain region as a control to account for non-specific effects. Excluding a non-stimulation control seems like a missed opportunity, as it would provide valuable insight into whether the observed effects are due to a synergy between the stimulation and visual processing modification or if they are primarily attributable to the visual processing intervention alone.
4. The authors briefly mention the possible synergistic effect of TBS and visual attention modulation but do not adequately account for the fact that the effects of TBS, like any form of non-invasive brain stimulation (NIBS), are state-dependent. The final outcome is likely the net result of the ongoing brain activity and its interaction with TBS effects. This point reinforces the concerns raised in revisions 2 and 3. While it is unclear how the authors might address this issue, it is an important consideration that should be discussed and potentially factored into their analysis and interpretation.
Minor Revisions
1. Consider reducing the use of acronyms throughout the manuscript. For example, the sentence "that iTBS will increase DEC within the DVS and reduce DEC within the VVS during naturalistic own-face viewing, while cTBS will result in opposite effects: decreased DEC within the DVS and increased DEC within the VVS" was particularly difficult to parse. While the use of "TBS" is understandable, it would improve readability to spell out other terms, especially given that there does not appear to be a strict word count limitation.
Best
Samuel Westwood, PhD
(I always sign my reviews)
This proposed study is an interesting and innovative approach to BDD, combining both aspects of mechanistic understanding, and neurobiologically-grounded intervention. There is a good balance of objective and questionnaire-based assessments. It has strong potential to contribute to the field in this area. Here are a series of additional comments:
- Is there any evidence that cTBS could make the participants' symptoms worse? It would be reassuring to the reader to know whether or not this could be the case. It is appreciated this study already has ethical approval, but if there is a possibility of symptom exacerbation, then knowing this would be an important part of the informed consent process.
- Please could more justification be explicitly referred to in the selection of the TMS target coordinates? Lines 302-303.
- Please can it be made clearer earlier in the paper and in figure 1 that this is a crossover design, where all participants will receive both iTBS and cTBS.
- Participants' compliance with the fMRI task is being monitored via eye-tracking. When fMRI data is being preprocessed, how will this be incorporated into quality assurance procedures?
- Please could it be made explicit which ROIs are considered higher and lower within their respective visual streams?
-Concerning the statistical analyses, it is very important that the investigators be able to differentiate effects that are driven by iTBS vs cTBS. We don't want to be in the position where we're unable to say whether an apparently significant difference is due to (a) iTBS-mediated potentiation, with cTBS having minimal effect, or (b) iTBS having minimal effect, and cTBS-mediated inhibition. For the GLMs described from line 395, I'm not entirely sure from this model description if this would be the case. It would settle the matter if we could see the proposed model formulae.
- Seeing the formulae would also help provide reassurance that the repeated-measures aspect of this design is being appropriately accounted for/represented ie a mixed effects model.
- The investigators allude to a desire to incorporate depression/anxiety measures in their analysis - please could they describe how?