Can TMS-evoked potentials act as biomarkers of long-term potentiation or long-term depression induced by paired associative stimulation?

ORCID_LOGO based on reviews by Domenica Veniero, Lindsay Oberman and 1 anonymous reviewer
A recommendation of:

Neurophysiological correlates of plasticity induced by paired associative stimulation (PAS) targeting the motor cortex: a TMS-EEG registered report

Submission: posted 22 July 2023
Recommendation: posted 12 January 2024, validated 15 January 2024
Cite this recommendation as:
Edwards, G. (2024) Can TMS-evoked potentials act as biomarkers of long-term potentiation or long-term depression induced by paired associative stimulation?. Peer Community in Registered Reports, .


What are the neurophysiological correlates of paired associative stimulation (PAS) in inducing plastic changes in human motor cortex (M1)? Here, Arrigoni and colleagues (2024) will apply transcranial magnetic stimulation (TMS) to left M1 paired with electrical stimulation of the right median nerve at an ISI of 25 ms or 10 ms to induce long-term potentiation (LTP) or long-term depression (LTD), respectively. Arrigoni and colleagues (2024) will determine if these stimulation pairings effect cortical excitability using motor-evoked potentials (MEPs) and TMS-evoked potentials (TEPs). Specifically, they hypothesize PASLTP will increase the peak-to-peak amplitude of MEPs, whereas PASLTD will decrease the amplitude, replicating previous work. They will then extend these previous findings by examining TEPs. The authors anticipate modulation of the P30 and P60, which are TEPs thought to reflect local cortical excitability. They plan to account for the MEP reafference which may also mediate the P60 amplitude by stimulating at sub- and supra- motor threshold. Further, they hypothesize an increase of the N100, a marker of inhibitory processing mediated by GABA, by PASLTD. Finally, the authors will also examine the impact of cortical excitability over time to determine the duration of the PAS effects.   
This detailed examination of TEPs following PAS stimulation will determine which TEPs could be used as biomarkers with the induction of LTP and LTD through stimulation. The authors have built in an MEP replication for the PAS stimulation, supporting previous literature and acting as a positive control.  
The Stage 1 manuscript was evaluated by three expert reviewers across two rounds. Following in-depth review and responses from the authors, the recommender determined that Stage 1 criteria was met and awarded in-principle acceptance (IPA).
URL to the preregistered Stage 1 protocol: (under temporary private embargo)
Level of bias control achieved: Level 6. No part of the data or evidence that will be used to answer the research question yet exists and no part will be generated until after IPA. 
List of eligible PCI RR-friendly journals:

1. Arrigoni, E., Bolognini, N., Pisoni, A. & Guidali, G. (2024). Neurophysiological correlates of plasticity induced by paired associative stimulation (PAS) targeting the motor cortex: a TMS-EEG registered report. In principle acceptance of Version 3 by Peer Community in Registered Reports.
Conflict of interest:
The recommender in charge of the evaluation of the article and the reviewers declared that they have no conflict of interest (as defined in the code of conduct of PCI) with the authors or with the content of the article.

Evaluation round #2

DOI or URL of the report:

Version of the report: REV1

Author's Reply, 10 Jan 2024

Decision by ORCID_LOGO, posted 08 Dec 2023, validated 08 Dec 2023

Dear Dr. Guidali,

Thank you for your thorough reply to the reviewers and recommender. I have received positive responses from all three of our reviewers and ask you reply to the few remaining comments. Please reply with a point-by-point response to the reviewers and recommender, accompanied by a track-changes updated manuscript.

Our anonymous reviewer requests you revisit Dr Oberman’s suggestion of extending your inter-pulse interval and asks you explicitly state that the MEPs will be recorded with the EEG cap on using the same conditions as was used for the TEPs.

With regard to your response to my comments, I have a few minor issues I’d like to be addressed:

I appreciate that power analyses have been performed on concrete hypotheses, and that the more exploratory analyses have been removed from your Stage 1. However, there are multiple mentions of connectivity in the abstract and introduction which may be confusing to the reader as there are no planned connectivity analyses in the Stage 1. These should also be removed, and the connectivity only discussed in the Stage 2 if exploratory analyses are performed. The only reason we allow the mention of exploratory analyses in a Stage 1 is if there is a particular design component which is only selected to support an exploratory analysis, therefore requiring an explanation for readability. Along these lines, the analysis examining the modulation of the N100 following PASLTP should also only be mentioned in the Stage 2. 

Could you also outline the conclusions you could draw if your hypotheses are not upheld in the final column of the Study Table? You have most of this information in the “Interpretation given different outcomes” column. For example, for H0, what does it mean to the field if you are unable to replicate typical impact of PASLTP and PASLTD protocols on MEP? Investigation of TEPs in this case is highly interesting as modulation impact may be more obvious in this measure.   

Finally, please also define TEP (i.e. TMS evoked potentials) in the abstract prior to the first use of the acronym.

As you are already aware, there is a December 2023 submission closure until 10th January 2024. Looking forward to hearing from you in the New Year.



Reviewed by , 07 Nov 2023

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.

Reviewed by anonymous reviewer 1, 08 Dec 2023

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,, section 3.2. TMS threshold determination.

Thank you


Reviewed by ORCID_LOGO, 21 Nov 2023

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. 


Evaluation round #1

DOI or URL of the report:

Version of the report: 1

Author's Reply, 03 Nov 2023

Decision by ORCID_LOGO, posted 05 Oct 2023, validated 05 Oct 2023

Dear Dr. Guidali,

Thank you for your Stage 1 submission. I have received three insightful reviews on your proposed study. The reviewers see merit in the scientific question, and the design of the study to target the associated hypotheses, however there are some concerns about the theoretical support behind some of the hypotheses. To highlight some of the critical concerns:

Our anonymous reviewer requests you provide additional empirical and theoretical support for your hypotheses. For example, you already cite a few articles to support why the modulation of P30 and P60 align with empirical studies suggesting they are a valid marker for PAS-induced modulation, I suggest you expand on these citations and potentially add more to further support this hypothesis. Equally, the other hypotheses would benefit from further motivation. The anonymous reviewer and Dr. Veniero request clarity on the connectivity analysis and how it will result in evidence of connectivity modulation rather than change in cortical excitability. Finally, the anonymous reviewer highlighted that hypothesis 5 could simply result from subthreshold stimulation at 90% resting motor threshold. It is my interpretation that you hypothesize a modulation of the P60, with no impact on P30 – this would suggest 90% rMT is sufficient to activate the corticospinal tract. If that is the case, interpretation of a P60 modulation for H5 should be contingent on a lack of P30 modulation to preclude insufficient stimulation. A significant repeated measures ANOVA does not control for the lack of P30 modulation.

Dr. Oberman is concerned about the heterogeneity of your sample in producing expected PAS-LTP and PAS-LTD MEP effects. Dr. Oberman suggests a pre-test to include participants which show the expected potentiation and depreciation MEPs. I share Dr. Oberman’s concern and request that you consider this pre-test, finally including the number of participants necessary to power the expected results. Alternatively, you should write a contingency plan: How will you interpret your TEP results (hypotheses H1-H5) if the MEP analysis (H0) shows no significant difference between the PAS-LTP and PAS-LTD MEPs? Along these lines, please could the authors complete the final column of the study design table. It may be more relevant to consider this final column as the alternatives to the hypothesized outcome which can elucidate the best approach for future analyses.

Dr. Veniero and Dr. Oberman highlight that you plan to collect the MEP and TEP data in serial rather than concurrently. As the MEP analysis acts as a positive control for following analyses on the TEP data, it seems sensible to consider collecting the data concurrently. Dr. Veniero also noted that the language surrounding the hypotheses should be more direct, which is the standard for registered reports. Wording like “we could speculate…” on page 5, should be replaced by “we hypothesize”, and each hypothesis should be supported with the relevant empirical literature. Any hypotheses which seem more exploratory will need to be removed from the Stage 1 – please see my further comments on this below. Of course, this does not preclude these analyses from being performed in an exploratory section of the Stage 2.

From my position as a recommender, I have a few notes regarding the registered reports formatting:


Hypothesis three is currently not strongly formulated, making targeted analyses, and the powering of these analyses very difficult. Please evidence your hypothesis for a particular connectivity effect following PAS. If there are multiple avenues to examine, you may want to consider running connectivity analyses in a more exploratory manner, reserved only for Stage 2. The same could be said for hypothesis four. As is currently written in the manuscript, you say effects could remain or disappear (page. 9) and that you could not state a priori how these profiles would progress over time for each stimulation protocol (page 6). For a registered report, a more solid hypothesis is critical, especially for powering your expected effect size.

Power analyses:

For hypotheses H2 - H5 the authors indicate there are no prior studies which provide evidence for a hypothesized effect size. This is an understandable and common concern when running power analyses. At PCIRR, we recommend that the authors examine the literature for effects sizes which align with their effect of interest, for example regarding H2: TEP modulation for N100 with LTD like stimulation protocols (e.g. Casula et al., 2014). The same can be said for effect sizes associated with H3 to H5. Assuming a medium effect size for these hypotheses is risky and may mean you will not have the power to examine the effects of interest. Using an assumed small effect size would reduce this risk. Alternatively, if you believe there is no way to predict the effect size of interest for these hypotheses, these analyses become more exploratory in nature. In which case these four sets of analyses should be removed from the registration.


Please specify exactly where the EOG channels will be placed to pick up the blink and saccade artifacts, i.e. vertical and horizontal EOG.

With revisions following the suggestions from our three reviewers, I believe your manuscript has potential for in-principle acceptance. I would therefore request a revision and resubmission with a point-by-point reply to the reviewers and myself.




Reviewed by ORCID_LOGO, 03 Oct 2023

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?




Reviewed by , 02 Oct 2023

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.

Reviewed by anonymous reviewer 1, 02 Oct 2023

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 ( and see also the work by Kicic et al., 2008 ( 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 (

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.

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