The authors have addressed all of my comments. I commend the study team for designing a study that I believe will make a great contribution to the literature.

The authors have addressed my comments. I only have a couple of suggestions based on the comments of Dr. Veniero and Dr. Oberman.

Comment 3 by Dr. Veniero. The authors should also mention that the MEPs will be recorded with the EEG cap on and with the same conditions as the TEPs.

Comment 2 by Dr. Oberman. The authors should consider Dr. Oberman's suggestion. The ISI the authors plan to use is short. See, for instance, https://doi.org/10.1016/j.brs.2023.02.009, section 3.2. TMS threshold determination.

Thank you

I have read the revised manuscript and the responses to my comments. I think all my points were addressed and I have no further comments. 

DV

This is a nice written report with a straightforward research plan and experimental design. I don't really have any major issues with the methodology or planned statistics. I only have one theoretical question and a few minor points. 

1- one of the aims of the study is to investigate changes in connectivity following LTP-PAS and LTD-PAS. However, we do know that at some level the excitability of the motor cortex changes as well. Part of this report is set to test which specific components reflect pure cortical changes in M1. My point is if there is a change in the responsiveness of this cortex, would this not be why there is less spread of activation?

2- I was wondering why you have to collect MEP and then TMS/EEG in different blocks, you will have 150 MEPs from this block.

3- Is the coil position identical in the Mep-block and TMS/EEG block?

4- In the methods section it is stated that to be considered effective, the 90%MT will have to generate no MEPs in 10 trials. I am assuming this is still in the APB muscle. However, it is possible that the pulse will activate other hand muscles at least in some participants. I would encourage recording from additional hand muscles to make sure there are no MEPs.

5- I suggest replacing "we could hypothesise" with "we hypothesise". This is repeated a few times.

6- Could you be clearer as to which direction you are expecting the N100 to change?

7-  Page 16: The electrodes to be included in the ROI will be verified by visual inspection of the greatest response amplitude after the TMS pulse. Could you explain what this means? Is it a component, a global mean field power, or the first response? Also, if you are planning to change electrodes based on the biggest response in each participant, it should be clearly stated. 

8- "The possible spread of M1-PAS plastic effects outside the motor cortex has been poorly investigated". What do you mean by poorly?

9- "At first, trials with artifacts (muscular or background noise) deviating from 200 μV". Do you mean exceeding?

This sounds like a well thought out study and one that will provide valuable information for the field. I have a few questions/concerns regarding the details of the methodology to ensure that this study will be optimally powered and designed to provide the data that the authors intend.

1. There is a good deal of heterogenetiy in response to the PAS protocols and in my personal experience, about 50% do not display the expected facilitation to PAS-LTP/suppression to PAS-LTD. Thus, perhaps may be best to do a pre-test to determine whether they will respond to the PAS intervention and/or increase the enrollment numbers to account for this attrition.

2. Time between visits (48 hours) and between single pulses (2000-2300ms) may not be sufficient to protect against visit-visit or pulse-pulse carryover. I would suggest longer (perhaps a week) between visits and longer (perhaps 5-8 seconds between single pulses). 

3. They seem to exclude those on anxiolytics and antihistamines. Since these medications are often used PRN, how long are the investigators requiring that the participants abstain from these medications to be included in the study?

4. I am not clear why the investigators separated out the "EMG" and "EEG" blocks rather than measuring both concurrently? If concurrently then the investigators could look pulse by pulse and equate the EMG response to the EEG response of a given trial rather than only averages.

Arrigoni and colleagues propose to use TMS-EEG to assess the cortical effects of the traditional PAS protocol proposed by Stefan and colleagues. This is an interesting study, and the experiment design suggested by the authors is straightforward. However, I have serious concerns about their methodology and hypotheses. My main critique is that they based their analysis and some of their hypotheses on the recent study by Costanzo et al., 2023 (doi: 10.3390/brainsci13060921). From my point of view, the study by Costanzo et al., 2023 has serious red flags that, unfortunately, were not detected by the reviewers; therefore, in my opinion their results are doubtful. In addition, the work by Arrigoni has a few conceptual interpretations that need to be clarified.

Please see below for specific comments.

1.   H0 (positive control): Effects of PAS protocols on MEP amplitude. This is valid and has value in the field for replicability of PAS-MEP results published in the literature.

2.   H1: Effects of PAS protocols on early positive TEP components (P30 and P60). I am concerned about the results published by Costanzo et al., 2023. Please note that my goal is not to criticize the work by Costanzo et al., 2023 but rather to avoid the same mistakes are repeated. First, Fig. 2 of their article suggests strong artifacts before 100 ms. The amplitude of components P30 and P60 are very large, and they look more like muscle artifacts or deflections produced by inappropriate data analysis. For instance, the deflection right after the time window the data the authors started to analyze is very large. Unfortunately, the time scale does not help. A Fig. showing the TEPs before using current source density (CSD) would have been helpful to assess the quality of the data. I am skeptical of the results reported by Costanzo et al., 2023. Arrigoni and colleagues put so much emphasis on the results by Constanzo et al., 2023. It is OK if Arrigoni and colleagues want to study those components, but a justification and rationale behind selecting those specific components is needed. Second, another critique about the experimental design by Costanzo et al., 2023 is that in one of their conditions, they stimulated with peripheral electrical stimulation alone and delivered 180 pulses, which could have induced modulation by itself. This is a major issue. Therefore, I suggest Arrigoni and colleagues rethink in more detail if they want to focus on investigating the effects of the PAS protocols on P30 and P60. Again, if they want to proceed like that it is O.K., but they need to include a better rationale on why those components want to study.

3.   H2: Effects of PAS protocols on the N100. Arrigoni and colleagues suggested “Based on previous literature about LTD and M1-TEPs (Casula et al., 2014), we hypothesize a modulation of the late N100 TEP component after delivering PASLTD but not after PASLTP.” This is not accurate. Indeed, N100 is a biomarker of inhibition as was suggested by Nikulin et al., 2003 (https://doi.org/10.1046/j.1460-9568.2003.02858.x) and see also the work by Kicic et al., 2008 (https://doi.org/10.1016/j.neuroscience.2008.01.043). However, the interpretation by Arrigone et al. is not accurate. When PAS induces LTP-like effects, it should be expected that N100 decreases because there is more excitation; in contrast, when PAS induces LTD-like effects, the amplitude of N100 should increase or not be affected because LTD reflects more inhibition. Please rethink this hypothesis and consult the literature to support your claims.

4. H3: Effects of PAS on cortico-cortical connectivity patterns. It is unclear how the authors will study cortico-cortical connectivity. If they aim to analyze the spatial distribution “topoplots” produced by the TEPs, this is not cortico-cortical connectivity but cortical excitability. They discussed in page 16, Section “Source reconstruction” they will do a source-level analysis. However, it is unclear or lacking how they will assess cortico-cortical connectivity. So far, the description is very generic.  

5. H4: Temporal evolution of induced plasticity. This is acceptable how is. 

6. H5: Effects of TMS pulse intensity on the modulation of P30 and P60 after PASLTP. Please see the comment about H1. I did not understand the goal of this approach. It seems the authors want to investigate whether an intensity of 90% has a minor effect on reafferent fibers compared to 110%. For studying only TEPs, this approach is valid. However, if the goal is to investigate the effect of PAS on TEPs, this approach could be problematic. Mainly because using subthreshold intensities for PAS may not be enough to activate the corticospinal tract and, together with electrical stimulation, will not affect cortical modulation. The authors may want to revise this approach. 

Other comments:

7. Introduction, page 3: “In detail, when the ISI matches the timing in which the afferent sensory signal from the median nerve electrical stimulation reaches M1 (i.e., 25 ms), LTP is induced (PASLTP), with an increase in post-PAS MEPs amplitude (Conde et al., 2012; Fratello et al., 2006; Nitsche et al., 2007; Stefan et al., 2000; Wolters et al., 2003; Ziemann et al., 2004).” To my knowledge, this statement is not accurate. To induce LTP the ISI should be slightly longer than the connection time. Please see in detail the introduction in the review by Suppa et al., 2017, and the work by Brzosko et al., 2019 (https://doi.org/10.1016/j.neuron.2019.05.041)

8.   EEG preprocessing, page 15-16. “Independent Component Analysis (FastICA, pop_tesa_fastica, ‘tahn’ contrast) after PCA compression to 30 components (pop_tesa_pcacompress) will be performed to remove blinks, eye movements, residual electrical artifacts, and spontaneous muscular activity by visual inspection.” You will first compress and then apply FastICA? If that is the case, please rewrite this sentence because it reads that you first will do FastICA and then PCA compression, which would be incorrect. Also, add the corresponding citation when discussing PCA compression (doi:10.1016/j.jneumeth.2012.05.029).

9. In general, the literature reviews should be deepened: please add more complete original papers where needed. 

Overall, this is an interesting study, but the logic, rationale, and plausibility of the proposed hypotheses and basic concepts need a major revision.