It was very exciting to see the results of this study, and overall, I think the authors did a great job! They nicely followed the preregistered plan, and I find their conclusions related to the preregistered analyses justified. There are a few issues that need to be considered, before recommending this manuscript, in my opinion:

1) Some small changes were made to the introduction, whereby additional references were added. I do not see a particular problem with it, but I am not sure to what extent changes like these can be made to the introduction at this point in the process.

2) One of the footnotes mentions “The number of trials in Experiments 1 and 2 differ from the registered trial numbers, due to correcting a mistake in the calculation of the required trials (360 instead of 432 in Experiment 1 and 512 instead of 572 in Experiment 2). This error was corrected prior to any data collection and after receiving the recommender’s approval on 22 June 2022”. I think it would be good to specify explicitly that the modification is, in fact, an *increase* in the number of trials (and thus more data). Also, for Experiment 2, the main text mentions 576 trials, but the footnote mentions 572 trials – this should be the same number.

3) On p. 21, the following sentence is hard to understand (does the second part need to read “we would recruit” instead?, or should the “if” be a “because”?): “If any of the three BFs did not reach the stopping rule of > 3 or < 1/3, we recruited four more participants and repeated the analyses” 

4) Figure 3 and 5: The names of the different conditions are put as the titles of the Y axis, which I find confusing. The title of the Y axis should be the measure that is displayed (here: Bayes factor). And then the names of the conditions can go above or below the graphs.

5) There are some model comparisons and interpretations of results that deserve some attention (these concern only exploratory analyses): 

5.1: p. 33 “The Bayesian rmANOVA generated the highest BF10 for the model that included only the TMS site factor (BF10 = 3.46), showing that the observed data are better represented by considering the ipsilateral and contralateral differences ).” –> the fact that the best model of the data included only the TMS site factor, shows that the data are best explained by *only* considering the differences between the ipsilateral and contralateral sites.

5.2: p. 33: the authors conclude that the Timing factor is not adequate to explain the observed data, because the Timing-only model was much worse than the null model (Experiment 1). However, that may not be the most appropriate model comparison to assess the evidence in the data for a main effect of Timing factor. Given that, for the main effect of Site, the authors start by stating the best model of the data (i.e., Site-only), it makes more sense to me to then examine how much worse this model fares if one now adds the Timing factor. Based on the values in Table 4, this would show that the data are inconclusive when it comes to the Timing factor: 3.46/3.02 = 1.15. There is a similar issue for Experiment 2, where the Timing-only model was compared to the null model, to examine the main effect of Timing, rather than by adding the Timing factor to the best model. Adding the Timing factor to the best model gives some evidence against a main effect of Timing (9.06/1.79=5.06) in Experiment 2. Related to these points, I think that some statements in the discussion may be too strong when it comes to the absence of a Timing main effect. Furthermore, it seems that some of the statements made in the general discussion about Timing effects are actually about the *interaction with Timing*, rather than the main effect of Timing. If that is indeed the case, the BF's of the relevant model comparisons should also be reported in the results section.

I reviewed the latest version of a Stage 2 manuscript of the authors' study, which comprises 2 experiments that utilize double-pulse TMS to modulate visual cortical activity during the maintenance phase of a change detection task. The methodology and planned analyses were already approved at Stage 1, in which I was also involved in one of the reviewing rounds. 

At this moment in the manuscript development, I can be short in stating that I find the manuscript a very impressive and enjoyable read. The Introduction is authoritative and well balanced, as the authors carefully describe the background literature in a detailed and disciplined manner, with emphasis not only on previous TMS work but also on the recent debate about whether the visual cortex supports (short-term) memory formation / consolidation. Methods are minutely described in relevant detail and experimental design decisions are well motivated. The Results are presented in a thorough, rigorous but also easily readable fashion, where I find the empirical evidence strong and convincing. The two experiments provide a strong combination of evidence, by replicating main results as well as extending the methodology to sham stimulation, which is an important but (in my view) also somewhat controversial procedure in TMS research. The Figures are clear to me (although lettering is sometimes a bit hard to read in the provided PDF). The Discussion carefully considers the findings in light of previous research and points to relevant future steps to gain further insight in how we retain visual information in memory. Overall, the manuscript is long but reads very easily. In this sense, I find the manuscript a strong and important contribution to the current literature and a stepping stone to future implementations.

The only two comments I would like to make are:

1) The results for 1000 msec timepoint of stimulation is less strong (BF just above 3) in comparison to other timepoints. While this surely can be considered as evidence for a "late" consolidation window in visual cortex (as the authors seem to do), I would have liked to see a bit more consideration of this effect. Especially in light of some studies also showing smaller (or null) effects for late timepoints (in TMS as well as in visual memory masking). Perhaps, at a BF just above 3, the glass is proverbially half full or half empty, depending on one's preference in this matter.

2) In the Discussion, I would have liked to see a reconsideration (however brief) of the current debate about the role of visual cortex in short-term consolidation / retention in light of the current findings. In her reviewing work, Xu (and colleagues) includes previous TMS findings in her considerations that visual cortex is not suited to store visual memories. One could have perhaps linked back to her argumentation and consider in how far this view is modulated by the current evidence.

However, I offer these comments are optional for the authors to consider. I do not wish to hold back this well written and elaborately described manuscript on just these points.