Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: AGE-RELATED ALTERATIONS IN INHIBITORY CONTROL INVESTIGATED USING THE MINIMALLY DELAYED OCULOMOTOR RESPONSE TASK
Review round: 1
Reviewer: 1

Output:
Basic reporting: Knox and Panusuru investigated the oculomotor inhibitory control by employing a task that required the subjects to make a saccade when a visually presented target disappear (after a delay of 200 or 1000ms since its appearance). This task involves inhibitory control because it requires subjects to refrain from making a saccade as soon as the target appears in their visual field. Making a saccade towards a target as soon as it appears is typical behavior in humans. Overall the paper is well written.
However, while the task has the potential to investigate oculomotor control, I have some comments and suggestions that I hope will help to improve the manuscript.

Introduction:
Lines 46-47. Please rephrase “In the AS task…target position”. In the phrase,  “mirror image” makes difficult to understand the task. Better to write "the opposite direction" or something similar.
Experimental design: Most of the concerns are, at the moment, of experimental nature, related to the methods and analysis. The analysis seems too complicated. I suggest the authors employ a simpler design to analyze the data. In the current version of the paper, too much emphasis is done to data and results (f.e. stratified analysis in results) that do not reach significance.  I have some concerns also about the sample size for old subjects (n=20), but by adding the effect sizes, the possible limitation can be at least be evident to the readers.
Furthermore, it is not really clear to me after reading the paper if the differences between young and old are showing a difference in inhibitory control or a “general slowing of the saccadic system”, as stated by the authors, line 287 and in the conclusion. It seems that the most important results are hidden in the text to give an immediate take-home message.
Methods.
Ethics and participants.
Line 93. Comparison data were available from younger participants from previous experiments.
Is it necessary to use some statistical correction? Did the authors use it?

Apparatus and Stimuli
Line 111. “They  were explicitly instructed not to saccade to the onset of the target.”
Which is the complete instruction that they provided to the subjects?

Procedures
General: To help the self-sufficiency of the paper, I think it is better to add the description of the experimental procedure employed with the “young group” too.
The authors compared 39 young subjects to 22 old subjects (although I recommend to reduce the sample to 20, because two subjects performed very poorly, see below for line 195). Why did they do not collect data from a higher number of old participants? Please motivate this choose (it can also be a practical reason).
Line 104. Which is the amount of the step in the fixation randomized period (0.5-1.5s)?
Line 114. Please add the duration of the break between sessions.
Lines 114-116. “The quality of the performance was carefully monitored…[…]…as necessary.”  What does “as necessary means”? Which were the criteria to provide feedback?
Lines 116-119. As I understood the experimental sequence was: Run-Calibration-Run-Calibration.
Did the authors use some form of training for the subjects before the experiment started? Did they discard the first trials of the first Run sequence? (I guess that subjects will be learning a bit the task in this phase).
Are the initial calibration trials different from the last calibration trials? I am asking this because I would expect some “Switching”  like effect, related to the different rules applied for oculomotor control in the two contexts. This effect could be different between young and old subjects.
Please, add a figure that illustrates the task.

Analysis
Line 32 How are the saccades between 0 and 80 ms after target onset classified?
Lines 134-135 “Similarly…[..]..as a correct response”. The authors employed an interval of 80-1000ms to collect correct saccades. However, they compare these data with those of young people in which the interval was 80-600ms (Knox et al. EBR 2018). I am wondering if such a difference could have affected the results. Did the subjects receive some feedback while performing the task? How much time were they allowed during the trial to make a saccade? Related to this topic, I did not understand (but I am sure I am missing something) how it is possible to have few subjects with a median latency very close to 600ms in Figure 2 (Knox et al. EBR 2018, right upper panel (MDOR sync)).

Line 135 “For each participant …mean error rate“. Why did the authors employ the median for the latency and the mean for the error rate?
Line 138 “ We used median saccade latency collapsed ..”. Is there a difference between latencies for the two targets eccentricities? If this is the case, I think the 5° should be a better option.
Validity of the findings: Results
The main goal of the paper is to investigate the age-related alteration in inhibitory control using the minimally-delayed oculomotor response. To this aim, it is necessary to compare the performances of the old-subjects with the performances of the young subject.
To make it simpler I would suggest employing an ANOVA design with groups (old, young) as between factor and tasks (calibration, MODR (with two levels(TDD): 200 and 1000ms))as a within-subjects factor.
This can be applied to both errors and latencies.
Alternatively, it is possible to run a Group x TDD design twice: one with the real values, the other correcting for the calibration values.
The same design should be used for the last analysis performed (Ref. Figure 6).
Line 157 The stratified analysis does not report any real effect. As such Figure 2 and 3 can be deleted. I suggest the authors run an exploration analysis by using a regression model.
Line 195: “The data of two older participants…”. These subjects must be excluded from the beginning. The sample of the old subjects should be reduced to 20.
Line 206 The variability of the older group can be just related to the higher variability of the age. I suggest the authors calculate the intra-subjects variability (see f.e. Pani et al. 2013 RDD) to make the comparison. Typically the variance is linearly related to RT, but it does not change always consistently.
I also suggest the authors, if this is possible, to calculate some after-effects. For example what happens to the latency of the saccade when an error is committed in the previous trial? I do not know if this can be done, because it is not clear to me if subjects had some feedback for every early saccade or the classification was done only after data collection.
Effect sizes should be included.
Data  files:
In the. xls file provided, would be useful to have a measure of variance (standard deviation or inter-quartile range together with the median latencies.
Additional comments: I also think that the discussion must be re-written. Once the new analyses are done, and the results are briefly reported, I suggest to make some comparison not only with the anti-saccade task but also with the stop-signal task, considering its diffusion (Verbruggen et al. 2019 Elife). Furthermore, while the topic of the paper is inhibition, I think that other processes must be accounted for. For example, shorter latencies for longer TDD reminds me of the delay preparatory effect. As such the effect observed by the authors can be due to a higher level of movement preparation. This is not necessarily against the decline in inhibition, but maybe it is related to the nature of the delay task and to the interaction between movement generation and inhibition often observed ( Duque,  Greenhouse et al. 2017 TICS). Furthermore another topic that can be discussed is the proactive inhibitory control (Elchlepp H, Lavric A, et al. 2016 Cogn, Psych.; Pouget, Logan et al. 2011 Jour of Neurosci; Lo CC, Boucher et al. 2009, Jour of Neurosci; Wardak C, Ramanoël S,et al 2012 EJN). Furthermore, related to the fixation activity see for example Stevenson SA, Elsley JK, Corneil BD (2009) J Neurophysiol.
I am not asking the authors to cite all these works, but I think they can be of help for the discussion.

AS stated above, I think the discussion must be rewritten once the analyses are done.
Here I add just some comment on sentences that grabbed  my attention:

Lines- 242-244: Our motivation…target inhibitory control more precisely …[..].
The inhibitory process always involves different stages (see Verbruggen et al. 2014, Perspect Psychol Sci.), so caution must be taken when talking about inhibition as a unitary concept or a simple process(see also  Salum GA, Sergeant J, et al (2014) Psychol Med 44; Montanari Giamundo et al.  EBR 2017; Indrajeet and  Ray 2019 EJN).  I think this topic must be explicitly discussed.

Lines 283-289.   In the discussion, the authors refer to the stratification analysis to support their argument. But the results lack statistic significance. This part must be removed.
Line 291- 292 (discussed in detail in Knox et al. 2018).  I think the paper must include all the arguments necessary.  Please, give at least a summary of the detailed discussion to make the paper “self-sufficient”.
Lines 291-303: please consider also the preparatory effect in accounting for reduced latency with increasing delay.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: AGE-RELATED ALTERATIONS IN INHIBITORY CONTROL INVESTIGATED USING THE MINIMALLY DELAYED OCULOMOTOR RESPONSE TASK
Review round: 1
Reviewer: 2

Output:
Basic reporting: In their paper, Knox and Pasunuru used the MDOR task to test for inhibitory processes in older adult population. The MDOR task has the advantage, contrary to the antisaccade task (AS), of not involving other higher cognitive processes, hence, giving a more ‘pure’ measure of inhibitory control. They observed that not only saccade latency was increased in the MDOR task compared to reflexive prosaccade task, but also that error rates were higher in the older population compared to younger adults. Majority of these errors in the older population was due to a failure to inhibit reflexive saccade. The authors conclude that not only MDOR task showed a classical slowing of the oculomotor system with aging, it also showed deficit in inhibitory control.
The article is clearly written and I am enthusiastic about the MDOR task developed by Knox and colleagues and the idea that this task could be used to assess for age-related deficit of inhibitory control. Although the introduction could benefit from some improvement, the major weakness of this paper is the results section (see comments in section 3).

Major comments:
1) If found that problematic very interesting, but I also found that the authors go a bit too fast on the link between aging and inhibitory control. The introduction could benefit from more emphasis on why inhibitory processes are important to study, particularly in aging, which would lead to how do we assess for this and why MDOR task should be preferred to AS task.In this regard, I would suggest developing a bit more around the aging thematic. Some information could be added to the second paragraph where the authors only state “a range of task has been used to investigate the effect of aging on behaviourally inhibitory control”. But the notion of inhibitory control is not defined, nor is the notion of executive functions. I would suggest to briefly give a definition of executive functions (EFs), then maybe briefly state the basic processes included in the EFs. Then focus on inhibition, how do we define it, how we generally assess for it (e.g., go no-go tasks (e.g., Potter & Grealy, 2008), stop-signal tasks (e.g., Rush, Barch, & Braver, 2006), negative priming tasks (e.g., Hasher, Stoltzfus, Zacks & Rypma, 1991). And then, go onto AS task (paragraph from L69).

2) Line 90/91 the authors state that the problem related to AS task is the fact that it involves attentional and working memory resources, which are believed to be important mechanisms for executive functions. But a reader not familiar with EFs, can wonder why this is an important issue, especially for aging. If the authors define what are the EFs and what processes they include from the very beginning, that it would be easier to follow the logic of why MDOR could be a better alternative to AS.

3) In the next paragraph, the authors sum up their previous findings using the MDOR task with younger population. They summarize their observation, and report that “Saccade latency in the MDOR task is much longer than is consistent with simple prosaccade responses to target onsets, and modulated by TDD”. Although the sentence itself needs rewriting, I would also like the authors to develop a little bit more here, give the reader some explanation why is that.

4) Line 105, the authors underline the observation that neither a gap nor an overlap affect error rates or latencies in the MDOR task, contrary to AS tasks. Why? The authors give an explanation in their 2018 paper, which could be beneficial here.

Minor comments:
L. 80 -  “a manual version of the AS task […] complicating the interpretation of the results”.
I would like the authors to develop a bit more here
L 110 - Could the authors state the age of the participants? Also “multiple groups” – can the authors specify how many.

The results section structure could be improved with adding subsection as for example:
1.	Latency & Error rates
2.	Latency & error rates by group age
3.	Comparison between young and old groups
4.	Distribution of error and correct responses timings

Figures are clear although they need some improvements :
Figure 2  - Error bars are missing.

Figure 5 & 6 - Only the upper limit for the aged group and the lower limit of the young group of the CIs are shown
Experimental design: As stated before, I found the research question here very interesting and meaningful.
The method section could benefit from minor improvements.

I would rather have the number of participants and age in the participant sub-section of the methods than at the beginning of the result section.

L 125 “We used the same apparatus[…]” Can the authors give the reference of the publication here?
I would also like to have a figure of the paradigm, I suggest using figure 1 from the 2018 paper.

L 133 “Light background” It can sound a bit meticulous, but how light is light? Can the authors give the value in cd/m²?

L 157 please specify how many trials were rejected for 1)blinks, 2)brake of fixation.

L 158 “valid trials” – is it “correct” trials? I would find informative the average accuracy in both the MDOR and the calibration task (see also comment above), could the information be put either in a table or in a supplementary material?
Validity of the findings: As stated above, my major issue regarding the manuscript is the result section. My first issue is related to the latency results and the comparison between the MDOR task and the control/calibration phase. Not only I feel that the author should report the latency/accuracy of the saccades in the calibration phase in more details, but I also think that the way they compute what they refer to as “corrected latency” is not really correct. Second, regarding the analysis according to the age is also problematic, first given the few numbers of participants per group and also given the large variability in the error rate. Thirdly, the comparison between young and old group should also be taken cautiously, as the number of participants in each group is quite different (n = 39 for the young, n = 22 for the old). I will develop these three points below.

Major comments:

In the first paragraph of the results, the authors briefly report the average saccade latencies (SL) and error rates, and state that on average SLs were longer in the MDOR task than would be expected in the prosaccade task. To prove their point they report the average SLs in the MDOR task separately for 200 ms TDD and 1000 ms TDD, and the average SL in the calibration task. I do not doubt about the fact that the MDOR task leads inevitably to an increase in SL. But there are numerous differences between these two tasks that make them hardly directly comparable.
Contrary to the previous experiment, the authors did not use a control task which they justify by the fact that they did not want the experiment to last too long, especially with older participants. Thus, they used the data from a calibration phase to measure for the prosaccade latencies and calculate the ‘corrected latency’, which is the difference between latency in the MDOR task and the latency in the calibration task. I understand the rationale here but directly subtracting the latencies from the calibration to the latencies from the MDOR poses different problems.

1) The numbers of trials between the two tasks are very different. The authors collected 240 trials for the MDOR task, and only 64 trials for the calibration phase, which is 4 times less. To be able to directly compare the two measures; the number of trials should be about the same between the two tasks.

2) The authors do not report any selection criteria for the calibration phase. If the calibration phase is here to be considered as the baseline for prosaccade latencies, then some selection criteria should be used (amplitude, anticipation, direction…).

3) In the MDOR task, the target was always presented at 5° whereas in the calibration, it could be at 5 or 10°. The author stated that they collapsed all the data between eccentricities and direction to measure for reflexive saccade latency. Before doing that, they should ensure that there was no direction effect and no significant differences in latencies between 5° and 10°. I would also like to see the data for this calibration phase reported in a table. Same comment for the TDD, the TDD of 200 ms and 1000 ms were only present in the MDOR task, and not the calibration.
Given the three problems described above, I do not find the corrected latency measure valid. If the authors want to have a pure measure of how long participants are in the MDOR task compared to prosaccade tasks, then they should do a proper control task with the same eccentricity, TDD and the same number of trials.

4) Looking at Figure 1a and 1 b, it looks like in the 200ms TDD participants are longer but they also show fewer errors, and reversely, in the 1000 ms, participants are faster but show also more errors, which is confirmed by the average values reported in the 1st paragraph of the results section. How about the landing position? Are the participants more accurate in the 200 ms?

5) As one can see on figure 1b, one participant showed more than 90% or error and two other about 80% of error. This high error rate suggests that these participants did not perform the task properly, hence, only very few trials were kept for the latency analysis for these participants. On the other hand, some participants showed close to no error at all, especially in the 200 ms TDD. But in figure 1a we can see that some participants show very long latencies, about 700 ms for one participant in particular. I was wondering whether this participant showing very long latencies in the correct trials was also the one showing lowest error score. Same apply for the high error score: is the one showing more than 90% of errors is the one with the shortest latency in the correct trials.

6) Regarding the data analysis stratified according to age, as the authors concede, the number of participants in each group is very small, between 8 and 6 making results hard to interpret. The observation that latencies of the older group were higher compared to the two other ones is not surprising. However, I would have thought that this group would also exhibit more errors, which is not the case. Regarding the high variability observed on figure 1b, will it be possible that the participants showing between 90 & 80 % or errors were part of group 2? As the errors bars are not reported on the graphs, it is hard to tell.

7) Regarding the comparison between young and old groups, the number of participants in each group is pretty different – 39 participants for the young group and 22 for the older group, which is clearly not ideal. Which makes me wonder how the authors decided on the number of participants for this second experiment? Besides, in the comparison between old and young groups, the corrected latency in the later has been made using a control task.

8) Regarding the distribution of error and correct responses as a function of response timing, the authors first took the distribution of all trials (whether the response is correct or incorrect). We can clearly see bimodal distributions, with one peak appearing early (which corresponds to errors) and a second peak appearing later (which corresponds to correct responses). Correct me if I am wrong here, but the error rate was recalculated– instead of taking 80 ms before/after target, they used 100 / 150 ms for the 200 ms and -950 / -650 for the 1000 ms. They report the average error rate using this new calculation and performed an ANOVA on the remaining data. I found this analysis clever, although I would rather suggest doing the distribution for each individual separately. I would then measure the number of error in the first peak ‘bin’ for each individual and then take the average number of errors. Also, I do not see the separate plots for the error and the correct responses?

I found the discussion clear, the authors nicely point out the limitations of the MDOR task and suggest how to improve it.
As for the introduction, some part of the discussion could benefit from more details. For example, L274 the authors stated “We have discussed previously”, I understand that there is no need to re-discuss the issue here. However, one or two sentences summarizing the discussion could be added. Same regarding the “other delayed saccade tasks” (L276).

Minor comments:
Results
L 166 “none of these differences reached statistical significance” - can the authors please give the reader the F value here?
L 202 “tested previously” – please give the reference here
L208 – with the F values, can the authors add the effect size?
L 215 -  The authors looked at the difference between TDD separately for each group. Then they measure the “difference as a percentage of the average of the two TDD”. I don’t get the measure, how is it calculated?
L 232 - The authors observed a significant interaction, can they report any post-hoc analysis?
L 234 – I do not find that the calculation of the CoV really adds anything to the results already reported
L 240 – Can the authors specify the bin used (50 ms?)

Discussion
L 262 “performances decline with age” – specify to which type of performances the authors refer here
L 288 “Latency […] (TDD) – suggest rephrasing
L 298 “These […] saccade tasks” – can the authors give some references here
L 304 – add some references here as well
Additional comments: My suggestion would be to either get rid of the 'corrected saccade' data - just report the average latency and accuracy in the calibration phase in a table and describe the data as part of the first paragraph (same as it is now). In turn, this will restrain the conclusions you can make regarding the increase of SL in the MDOR task, which is quite problematic.
The other suggestion, which would be really great but I understand much more costly, would be to add a second experiment with increasing the number of participants so as to have about 36 participants in total, 12 participants for each group age. This not only will increase the number of participant per group for the stratified analysis but will also reduce the difference with the young group, allowing a better between groups comparison. I would also suggest adding a proper control, all the more if the authors want to assess for an increase in latency in the MDOR compared to prosaccades.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: AGE-RELATED ALTERATIONS IN INHIBITORY CONTROL INVESTIGATED USING THE MINIMALLY DELAYED OCULOMOTOR RESPONSE TASK
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: Dear Editor,
Dear authors,
here are my comments on this new version.

--Previous revision:

1.6 General: To help the self-sufficiency of the paper, I think it is better to add the description of the experimental procedure employed with the “young group” too.
The authors compared 39 young subjects to 22 old subjects (although I recommend to reduce the sample to 20, because two subjects performed very poorly, see below for line 195). Why did they do not collect data from a higher number of old participants? Please motivate this choose (it can also be a practical reason).

R1.6 The experimental procedures (stimuli, tasks, equipment, instructions) employed for the young participants were identical to those used for the older group. The comment added in response to R1.5 further emphasizes this.

-And the second reviewer wrote:
2.24 Regarding the comparison between young and old groups, the number of participants in each group is pretty different – 39 participants for the young group and 22 for the older group, which is clearly not ideal. Which makes me wonder how the authors decided on the number of participants for this second experiment? Besides, in the comparison between old and young groups, the corrected latency in the later has been made using a control task.
R2.24 The 39 younger participants were those from pervious experiments who were aged 19-27y. There seemed to no good reason to restrict ourselves to the same number as the older group. The N for the older group was a convenience sample as a starting point.

--How did they establish the “convenience”?  Did they perform a power analysis? Please state it in the paper.

--Previous revision:

1.14 Line 32 How are the saccades between 0 and 80 ms after target onset classified?

R1.14. These are classified as anticipations, not uninhibited responses to the onset. There is an extensive literature of saccade latency ranges for different type of saccade (eg see Amatya et al. 2011; Knox and Wolohan 2014).

--Please add this to the text.

Previous revision:
1.15 Lines 134-135 “Similarly…[..]..as a correct response”. The authors employed an interval of 80-1000ms to collect correct saccades. However, they compare these data with those of young people in which the interval was 80-600ms (Knox et al. EBR 2018). I am wondering if such a difference could have affected the results.

R1.15 The period from 600ms to 1000ms post-target offset accounts for an average of 2.5% of responses in the older group, and about 1.9% of responses in the younger group (a difference of 0.6%). We do not believe this materially affects the results.

--Please add this to the text.

--Results.

--Line 245 and in other lines…,
   please add the df for the t-test

--Line 266 reference must be to Fig. 3b

--Line 268.
 “Given that the group data suggested the modulation of latency by TDD might differ between
the two groups (although the interaction term in the ANOVA was not statistically significant),we calculated the difference in latency between the 200ms and 1000ms conditions for each participant and then summarised for the groups. The mean difference was 164±81ms in the older group and 96±47ms in the younger group, statistically significantly different (t=3.4; p=0.002; d=1.12).”

--Honestly, I cannot see how “the group data suggested” considering that the interaction between factors is not significant and that in line 285 they found an interaction effect for the errors but the authors did not analyze it.

--Furthermore I do not understand how it is possible that the effect that they are looking for (the size of the modulation in latency related to the age) it is not detected by the interaction in the ANOVA,  but it is detected by looking at the differences.
The part in the discussion (lines 401-408) should be more cautious. I don’t see a strong effect here if it is detected by the t-test on the differences and not by the ANOVA.

--Line 285. Please perform the post-hoc on the interaction.

--I am wondering if the main effect between groups it is driven by the difference in error rates between old and young just for the long TDD.

--Furthermore, please add a reference to figure 4.

--Line 289. I wrote a comment in the previous revision.

--Previous revision:
1.24 Line 206:  The variability of the older group can be just related to the higher variability of the age. I suggest the authors calculate the intra-subjects variability (see f.e. Pani et al. 2013 RDD) to make the comparison. Typically the variance is linearly related to RT, but it does not change always consistently.

--And the authors replied:

R1.24 The CoV has been used in previous studies of aging effects on oculomotor control (eg Munoz et al, 1998, Exp Br Res 121:391) and provides useful comparative information. We could not find the suggested reference with the information supplied.

--I agree with the second reviewer that what the authors wrote, line 288
 “For both latency and error rate, the results for the older group appeared to be more variable than for the younger participants. This was checked by calculating the coefficient of variation (CoV). For latency, CoV was consistently higher in the older group for both the 200ms condition (22% vs 15%) and the 1000ms condition (24% vs 16%). There was less of a difference for error rate (200ms: 96% vs 82%; 1000ms: both 49%)”, does not add anything to the results, at least in this form.

--Furthermore, they refer to the paper of Munoz et al. 1998, but they present a different analysis. They present the results as percentages (and this is not clear to me).
In the previous revision, I suggested looking at the intra-subject variability (not at the inter-).
It does not matter to me if they use the CoV instead of the SD; indeed Munoz et al. 1998  looked at the intra-subject variability:
 “ From the data of each subject, we computed the following values in the eight experimental conditions representing the factorial combination of saccade task (anti vs. pro), fixation condition (gap vs. overlap), and target direction (right vs. left): the mean saccadic reaction time (SRT) for correct trials; the coefficient of variation of SRT for correct trials [(CV=standard deviation/mean)*100]; the percentage of express saccades (latency: 90±140 ms; Fischer et al. 1993); and the percentage of direction errors (saccades away from the target in the pro-saccade task; saccades toward the target in the anti-saccade task).”
Furthermore,  in the same paper, pag. 395
“To ensure that the measure of variance was not biased by variations in mean SRTs between age groups, we used the coefficient of variation (CV). The CV was lower in the gap condition (mean CV: 26.1) than in the overlap condition (mean CV: 27.1) [F(1, 167)=5.85, P<0.0001  due in part to a reduced express mode leading to a tighter anti-SRT distribution”.

So I would ask the authors to perform the same analysis as in Munoz et al. 1998. They have to run the same ANOVA performed on latencies and error rates on the CoV.

And again, the inter-subject variability that they report can just be an epiphenomenon related to the ages of the groups. In the old group (as in the xls file added by the authors) the SD is 7.28 years; in the young group, it is 1.89 years.

Previous revision:
1.27 Data files:
In the. xls file provided, would be useful to have a measure of variance (standard deviation or inter-quartile range together with the median latencies.

R1.27 We don’t propose to change the supplied information.

I cannot imagine a valid opposition to this request.
The authors have calculated the CoV; thus add the columns (4!) should be very easy.
Additional comments: no comment


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: AGE-RELATED ALTERATIONS IN INHIBITORY CONTROL INVESTIGATED USING THE MINIMALLY DELAYED OCULOMOTOR RESPONSE TASK
Review round: 2
Reviewer: 2

Output:
Basic reporting: I am really positive regarding the use of eye-tracking in aging studies, and as I previously mentioned I found the MDOR task very interesting. The authors made clear responses regarding my first set of comments and made good points regarding some objections I had previously. Besides, I really appreciate the improvements made in the results section. I still have few comments regarding the methods and results section.
Experimental design: In my first set of comments, I asked the authors to specify the number of rejected trials separately for blinks and break of fixation. I understand that the authors did not record these separately, however, just for replicability purpose, can the authors specify their criteria for "poor fixation" (or "unstable fixation"). My guess would be that saccadic eye movements made during the random fixation period were discarded, if so, what was the saccade amplitude criteria here? Was it 1° as well?

Instead of describing the analysis as a "repeated measure anova" I suggest to rather use the term of "mixed anova" as there is one between and one within-subject factor here.

As previously noted in my first review, regarding the interaction reported on l.285, the authors responded that further analysis "would not add anything". The interaction itself indicates that indeed, old and young participants showed different error rates to the TDDs - and this is showed on Figure 4. However, I still think that further analysis to determine the exact nature of the interaction should be reported here.

I am not sure that only showing one of the two CI error bars is really correct. I understand that bars might be overlapping and that the authors prefer not to display them for clarity. However, CI bars are informative and even though the authors suggest that this information can be seen from figure 6 (which is figure 5 in the revised manuscript), both CI should be shown on the line graphs as well. To get around the clarity issue, the author could use shadows instead to represent +/- 95% CI.

The figures referred to in the result section do not correspond to the figures reported (e.g., l 266 - fig. 4b should be fig.3 b, l281- fig5 should be fig.4).
Validity of the findings: no comment
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: AGE-RELATED ALTERATIONS IN INHIBITORY CONTROL INVESTIGATED USING THE MINIMALLY DELAYED OCULOMOTOR RESPONSE TASK
Review round: 3
Reviewer: 1

Output:
Basic reporting: none
Experimental design: none
Validity of the findings: none
Additional comments: Two main points (A and B):
A- In the rebuttal letter the authors skipped this point:
--Line 268.
“Given that the group data suggested the modulation of latency by TDD might differ between
the two groups (although the interaction term in the ANOVA was not statistically significant), we calculated the difference in latency between the 200ms and 1000ms conditions for each participant and then summarised for the groups. The mean difference was 164±81ms in the older group and 96±47ms in the younger group, statistically significantly different (t=3.4; p=0.002; d=1.12).

--Honestly, I cannot see how “the group data suggested” considering that the interaction between factors is not significant and that in line 285 they found an interaction effect for the errors but the authors did not analyze it.
--Furthermore I do not understand how it is possible that the effect that they are looking for (the size of the modulation in latency related to the age) is not detected by the interaction in the ANOVA, but it is detected by looking at the differences.

They  just replied to this last part:
The part in the discussion (lines 401-408) should be more cautious. I don’t see a strong effect here if it is detected by the t-test on the differences and not by the ANOVA.
I kindly ask them to reply to the first part too.

B- Raw data.
I asked to add values in the raw data (4 columns) that should be easily available (because in the previous version of the paper they estimated the CV), but they wrote that this would be time-consuming.  I am sorry but I cannot accept this position, in a period in which data availability is a synonym of transparency and is requested almost everywhere.
If the authors do not make these data available I will not consider the paper ready for publication.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: AGE-RELATED ALTERATIONS IN INHIBITORY CONTROL INVESTIGATED USING THE MINIMALLY DELAYED OCULOMOTOR RESPONSE TASK
Review round: 4
Reviewer: 1

Output:
Basic reporting: I am satisfied with the answers.
The paper, in my opinion, is now ready for publication.
Experimental design: none
Validity of the findings: none
Additional comments: none


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: VALIDITY AND RELIABILITY EVIDENCE OF A POINT OF CARE ASSESSMENT OF SALIVARY CORTISOL AND Α-AMYLASE: A PRE-REGISTERED STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: ABSTRACT
Concise and well written
•	Line 27 and throughout the manuscript, please be consistent with the terminology to refer to the iPro Lab reader (also appears as Lab LFD reader) and the iPro Cube reader (also appears as iPro Cube, iPro Cube LFD reader and iPro Cube LFD)
INTRODUCTION
Well written
•	Line 68 – please review sentence as meaning of “…is advocated within stress…” is unclear
•	Line 83 – please review “…through from plasma…”
•	Line 88 – suggest to briefly include examples of other indicators for context
•	Line 110 – please review grammar “It…”?
Experimental design: MATERIALS AND METHODS
Overview of the relevant components of the registered methodology was provided
•	The methodology registered indicated participants were originally University students and subsequently “individuals from the public” however the use of Army personnel is referred to in the text – please clarify the population utilised.
•	Lines 152-154 – this justification has little applicability without any reference(s) to support the intensity is indeed representative of Army specific training scenarios. Suggest to readdress the justification of utilising the PWC75%HRmax assessment.
•	Line 166 – please review grammar “the iPro salivary cortisol ɑ-amylase samples was”
Validity of the findings: RESULTS
Text was sufficient and Tables are clear and adequate.
•	Much of the discussion focusses on under- and over-estimation of samples between iPro Cube LFD reader and ELISA yet no explanation or results of such are presented in the results section. Suggest considering the inclusion of variations in mean differences into Table 1 or the text.

DISCUSSION
•	Line 234 – Aren’t the results of the PWC75%HRmax assessment relative to 55%, 66% and 77% rather than low? You also state “moderate-to-vigorous intensity” as well as “light to somewhat hard efforts“.  Clarity around the participant composition (such as active, sedentary, military etc) may provide some support to your notion of insufficient stimuli.
•	Line 239 – “relatively low-intensity” – see previous comment.
•	Line 244 – reference to “the 10:00 participants” is unexplained in either methodology (registered or this manuscript); the methodology in the manuscript states that “All study procedures were completed in one testing session between 8-10 am to minimise any effect from circadian variations.” Please clarify or amend accordingly.
•	Line 274 – “relatively moderate intensity” – see previous comments and suggest to revise for consistency throughout the manuscript

CONCLUSION
•	Suggest including a conclusive statement regarding the poor validity of the ɑ-amylase
Additional comments: Thank you for the opportunity to review this manuscript which offers an important and practical contribution to the credibility of point of care diagnostics for monitoring and evaluating physiological responses to exercise. The manuscript is well written and provides sufficient overview in its representation of the study methodology, analysis and interpretation albeit differing from the original registered methodology with respect to participants and psychophysiological focus. I agree with the concerns you discuss in your manuscript around the inclusion of the 9 min sub-maximal exercise protocol to elicit meaningful changes in [sCort] which I have mentioned throughout the review. Additionally, the manuscript contains a number of inconsistencies and grammatical errors and with that in mind, I believe some revisions are required for the manuscript and as such, have a few suggestions for your consideration.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: VALIDITY AND RELIABILITY EVIDENCE OF A POINT OF CARE ASSESSMENT OF SALIVARY CORTISOL AND Α-AMYLASE: A PRE-REGISTERED STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: This study aimed to investiagte the reliability and validity of iPro Cube LFD, a portable-of-care device, for the immediate assessment of salivary cortisol and alpha-amylase by comparing it to a laboratory standard method, ELISA. Twenty-nine volunteers, undergoing a moderate exercise (3x 3-6 min cycle ergometer at 75%HRmax) in the morning (8-10 am), provided three saliva samples, two swab samples for the iPro and one passive drool sample for the later ELISA analysis (Salimetrics), at three occasions: before, immediately after and 30 min after completion of the exercise. Findings indicate moderate to large correlations for cortisol and low to moderate correlation for alpha-amylase.

This study may contribute to the field by investigating possible reliable and valid alternatives to laboratory methods such as LC-MS/MS and immunoassays. Thus, this study is of most importance and valuable for research and practical implications.

The introduction is somewhat missing conjuctions between and within passages which may cause confusions, misunderstandings and makes is difficult to follow the storyline.
For example, it may seem arbitrary why this study focused on salivary cortisol and alpha-amylase which it is not, of course. You may add a sentence within the first paragraph, naming the two most prominent stress-related biological systems, namely HPA axis and ANS (autonomic nerous system). In doing so, the second and third paragraph dedicated to cortisol and alpha-amylase, respectively, are not disconnected to the previous paragraph anymore.

I have some minor comments concerning the content and cited litertaure.
- Line 57-58: You may add that some analytes may also be affected by the venepucture (for example, see Weckesser et al., 2014 PNEC).
- Line 67: You may add „free versus protein-bound cortisol“. Note, salivary cortisol is only reflecting a fracture of free, unbound, biologically active cortisol.
- Line 69: Please check the reference whether this sentence is true for „free“ plasma cortisol.
- Line 75: Please check the correctness/applicabilty of the reference.
Line 76. What is meant by „chronic response“ and can it really be captured by salivary markers?
- Line 77-89: Although salivary alpha-amylase was originally introduced as an SNS marker, recent reasearch (e.g., Schumacher et al., 2013 PNEC) strongly suggest salivary alpha-amylase as a surrogate for the autonomic nervous system, given that both branches PNS and SNS are involved (e.g., Proctor et al., 2000 Periodontology).
- Line 119/ 122: It is not clear why a moderate and large correlations are assumed (hypothesis 1 and 2, respectively).
Experimental design: In general, I may suggest to structure this section and using subsections/ subheadings:
- Participants: description and recruitment
- Procedure: study design incl. exercise/ prerigisteration information + saliva collection method
- Assessment of cortisol and alpha-amylase: iPro Cube LFD and ELISA
Statistical analyses: statistical procedure

Further comments:
- Line 124-133: Please provide more information about the participants (reference to preregistertaion is not enough, considering that another sample was recruited in the end). Please provide the following information: descriptives such as age (also range), sex, BMI, smoking status (maybe even provide a suppl. table), in- and exclusion criteria beyond the already mentioned ones (e.g., chronic disorders, smoking, medication/ drug intake), and recruitment (apparently, students from the Sports and Exercise Psychology Unit were not recruited?).
- Line 138: Was, by any chance, the time of awakening on the day of assessment was documented, considering the morning awakening response? This might be of help for discussing the non-response in cortisol.
- Line 163: Were saliva samples run in duplicates for the ELISAs?
- Line 171: What data were used for the bivariate correlations - the mean of iPro Cube LFD or the single values of iPro Cube LFD?
- Line 186: How many data were missing in total, and why?
Validity of the findings: The main problem I see is that results and discussion are somewhat all mixed together. For example, in line 224-226 „new“ findings are reported in the discussion.
My suggestion is that you may focus on your main research question but however, I agree that it is important to report the findings of the experiment as well for the interpretation of the results. Please keep in mind, the experiment is not the main research question. Saying that, you may restructure the result section as follows:
- Validation check of the stress induction: biref summary of the findings (later discuss these findings);
- Realibility and validity of iPro Cube LFD: basically the already reported results;

Further comments,
- Line 205-217: I may missed it, would you please provide a table with all correlations.
- Table 1: Apparently, cortisol concentration were not detectable in some of the saliva samples using iPro Cube LFD. How many samples were not detectable? Please discuss this critically.

Another important issue concerns the limitations which should be addressed in a separate section at the end. Some limitations are the following:
- experiment in the morning may overlap with the morning awakening response
- detecable limits of iPro Cube LFD (and ELISAs)
- CV of iPro Cube LFD (also compared to ELISAs) which is also an indicator for reliability in a way
- differences in saliva collection methods that may also partly explain differences and low correlations
Additional comments: All in all, this study provides valuable findings for the field.
At the current state, the manuscript is somewhat missing a clear structure and important information which required to understand the study design and findings. The manuscript may benefit from rewriting and restructuring some passages and addressing the concerns raised (see comments above).


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: VALIDITY AND RELIABILITY EVIDENCE OF A POINT OF CARE ASSESSMENT OF SALIVARY CORTISOL AND Α-AMYLASE: A PRE-REGISTERED STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I wish to commend the authors on their comprehensive revisions and as such, believe the manuscript successfully meets the PeerJ criteria and should be accepted. Thank you for the opportunity to review your work.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: VALIDITY AND RELIABILITY EVIDENCE OF A POINT OF CARE ASSESSMENT OF SALIVARY CORTISOL AND Α-AMYLASE: A PRE-REGISTERED STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have addressed all raised concerns adequately. Thank you for clarification and revising the manuscript accordingly.

As to 6, in stress research field and as to my understanding, "response" indicates always a change over at least two time points (pre-post change) and cannot by captured by a single timepoint measure; “chronic stress”, on the other hand, indicates other measures such as urinary or hair cortisol, for example. However, I assume the terms “acute” and “chronic” responses might be used differently, depending on the research field. The addition “short-term” and “long-term” has further contributed to the understanding of what is meant by the two terms.

Please check and correct the spelling of a-amylase in line 223-225 (accidently spelled "a-amaylase").
Experimental design: I appreciate that the authors stucture the manuscript in a reader-friendly way by adding respective subheadings.

As to 8, thank you for introducing salivary alpha-amylase as a surrogate of the ANS.

As to 10, thank you for clarification that the participants were indeed a student sample. Were the students recruited from the Sports and Exercise Psychology Unit only or from various departments?

Again, please provide range in age, BMI (calculated by body mass and height). Thank you.

As to 11, thank you for clarification. The authors have now reported that the assessment started at least 1 hour after awakening which indeed should cover the time period after the morning awakening responses in both biomarkers.

As to 13, you may add the information about how to read the table in the ‘note” under the table as other readers may also ask themselves this question. Thank you.
Validity of the findings: For the interpretation of the findings, I may respond to two authors' repsonses.

As to 15, I see the authors’ point. I agree with the authors that the narrative findings on the exercise performance may not be essential for answering the main research question, as I have stated previously ("... the experiment is not the main research question."). I personally would avoid reporting new findings in the discussion, no matter whether the readers may (or may not) read and interpret the results from the tables by their own. I guess this a question of personal writing style.

As to 16, I may suggest, that the authors may again refer to table 3 in the manuscript. Thank you.
Additional comments: Please accept my apologies for missing some points (comments 4, 12, 18) that have already been addressed in the previous original manuscript. The editiors were desperately in need of a second reviewer and kindly asked me to review the manuscript before the deadline (with the best intention of the editors, namely, to avoid another delay in the already long-lasting peer review process). Thus, I had to review your manuscript under (time) pressure, and I was worried that I may have overlooked some information that have already been reported in the manuscript. This worry has been justified as I see now. This is not an excuse, rather an explanation. Sorry for any inconvenience this may caused. Nonetheless, I hope you could benefit from some of my comments.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: QUANTIFICATION OF THE INFLUENCE OF DRUGS ON ZEBRAFISH LARVAE SWIMMING KINEMATICS AND ENERGETICS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The write-up is organized and clear. There were two typos in equations that I have mentioned below.
Experimental design: Methods are well-described and adequately validated.
Validity of the findings: conclusions are fine. Just the statements regarding the need for CFD needs to be softened as I mention below because it was not directly shown in this paper.
Additional comments: For transparency, I had reviewed this manuscript for another journal before. This paper is much clearer (except a few equations as pointed below) and the numerical methods are well-described. The sensitivity and validation studies are adequate. The results are presented clearly. My only concern is that the statements regarding the need for CFD to measure muscle power for drug testing need to be softened because it was not directly shown in the paper. The authors can make it as part of future work or potential applications. Here, the zebra fish in the acetic environment showed higher frequency that the control. Higher tail beat frequency is directly related to higher velocities and power consumption based on previous work. Therefore, CFD was not really required to show this. This aspect needs to be softened in the manuscript.
Specific comments:
Equations 1 and 2 are not equations. There are no = sign. Please correct.
Equation 7b: sigma_j is not defined. It might be a typo.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: QUANTIFICATION OF THE INFLUENCE OF DRUGS ON ZEBRAFISH LARVAE SWIMMING KINEMATICS AND ENERGETICS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Please see the general comment section below.
Experimental design: The research question is well defined and the aim is clearly stated. The investigation performed meets the technical and ethical standard.

Methods are described well with the relevant references provided in the method section.
Validity of the findings: The CFD model has been validated in two different fish model with differing morphology. The authors have tested the CFD model in both the control and treated conditions. However, this study would have been robust if the authors perform experiment for different treatment conditions. Please, look at my general comments below.
The discussion of the results is limited mostly to supporting results with the authors  mentioning the limitations of this model as well.
Additional comments: Review comments:
In this manuscript titled QUANTIFICATION OF THE INFLUENCE OF MEDICINE ON ZEBRAFISH LARVAE SWIMMING KINEMATICS AND ENERGETICS, the authors have tried to develop a zebrafish CFD model for objectively evaluating the effect of drugs in muscle power and energy consumption. The authors have described clearly their objectives and discussed the limitations of their study. Also, the model has been validated in the jellyfish model which has completely different morphology compared to the zebrafish larvae. However, there are some major and minor points that the authors can do to give clarity to the manuscript.
Major points:
1)	Major drawback of this study:
In line 499-500 of discussion, the authors have speculated that this approach may be able to evaluate the potential analgesic drugs for pain relief. While potentially true, this study uses only one drug to develop a model. It is better if the authors try to test this zebrafish larvae- CFD model in at least 3 drugs (positive effect, no effect and negative effect) with diverse effects.
As acetic acid increases the movement in zebrafish larvae, could this model also be used to study the drugs that decreases the locomotion in zebrafish larvae? The authors have focused on the benefit of this model in developing drugs affecting nociception. But can this model have broader implications, not only in the analgesic drugs, but also in neuroactive drugs?
2)	The authors should be more descriptive in the figures. For example, please see the following comments regarding the figures.
Figure 1: In line 135, 500 fps is mentioned, while in the figure, there is 300 fps.
Figure 3:
In the corresponding results section in the text of the manuscript, authors have not mentioned about the acetic acid treatment.
Also, the authors need to make this figure clear. It would be good for the readers if authors mention the full form of M, MIT and F also in the figure. So as the unit of force-mN.
Also, its difficult to understand if this is the result done in simulation zebrafish larvae model or in zebrafish larvae.
Figure 4: there is a lack of clarity in this figure. Authors have to mention what are D max, theta 1,                   theta 2, theta 3.
Figure 7: Authors have to be more descriptive about this figure as it is difficult to understand what they are trying to explain. For example: they have to mention what the vortex rings in the right side and left side of the panel represent. Also, it would be good to mention to the readers what to look into when they are looking at the vortex rings on the right and left panels.
Figure 8 b: Bars at 1 and 10 are incomplete. Also, authors have mentined this bar as a comparison between hydrodynamic power and mechanical power. But I only see the hydrodynamic power in the figure.
Figure 10: It is unclear, specifically the scale bar showing the grade of Z vorticity. Also, there is no labelling of the figures in both the left and right panel (ditto as figure 7). It would be better if the authors describe the differences between the figures in right and left panel by placing arrow mark/arrow head/ circle. It would help the readers understand the results that the authors have described in the corresponding text in the manuscript (line 438-440).
3)	Line 85: I would request authors to change medicines to drugs, not only here, but also throughout   the manuscript.
4)	Line 105: I think pharmacological study would be better rather than medication study.

Minor points:
 Line 82-83: The authors have written that “pure observation alone is not effective in ascertaining the influence of drugs in swimming behavior of fish”. If I understood correctly, the authors are referring this sentence to line 73-74. However, this is not only pure observation, its rather an objective quantification of the zebrafish larvae behavior based on distance travelled and velocity.
Line 83-84: This line is unclear. “Fish swimming kinematics are completely controlled by internal muscle and body” Authors have to clarify this sentence specifically the role of central nervous system and peripheral nervous system in swimming.
Line 117 -118: Authors have to clarify/restructure the phrase “how this study has established a foundation for the development of new analgesic drugs”.
Line 129-131: The total number of embryos per group is unclear. 20 or 40 embryos for each group should be clearly mentioned.
Line 344: “gestures of CFD model” should be clarified or rewritten.
Line 373-374: Authors have to restructure the sentence. It is not scientifically sound to mention that “Energy is passed along the fish body”.
Line 375-376: Author has to make this sentence clear, specifically the “Passive viscous dissipation of fish body”. It would be better to give an estimated energy (for example: 5% or 1%) rather than writing some energy.
516: The phrase “mystery of body stiffness” should be written scientifically.
518: Rather than “influences on muscle tissue”, effect on muscle tissue is appropriate.
The manuscript will be better with thorough editing and use of scientific terms.
Suggestions to the authors:
In this study, the authors have taken into account the movement of zebrafish larvae in the light. While zebrafish larvae move more in the dark and less in the light, it would be interesting to see the corresponding results in the dark period.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: QUANTIFICATION OF THE INFLUENCE OF DRUGS ON ZEBRAFISH LARVAE SWIMMING KINEMATICS AND ENERGETICS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have addressed the issues I have raised that were within the scope of their study. Now, the manuscript is looking good. To further make it better, I expect the authors to thoroughly proofread the paper to correct the minor grammatical and spelling errors For example: I noticed that the authors have written "wildly" in line 62, which I think they mean widely. Similarly, in line 579, the authors have stated that "our future work could focus on evaluating potential analgesic drugs". I would prefer to say "would" rather than could. Please, look at this type of mistakes and correct them. It would be beneficial for the authors as well as the readers.
Other minor comments:
Line 431: Please replace the word deform with bend. Deform indicates abnormal morphology.
Line 568: In this line, it would be better to write replicate if the authors mean the results of this study are similar to the previously published studies.
Line 563-565: please provide clarity to the phrases "development stages" and "reversed results".


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DNA METHYLATION PROFILING IN RECURRENT MISCARRIAGE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript titled “DNA methylation profiling in recurrent miscarriages” by Pi et al. seems to be technically sound with extensive experimental performance. The authors have presented an important research gap in light of recurrent miscarriages and how DNA methylation has potential in shedding light on the etiology of recurrent miscarriages. The authors have provided adequate background and literature referenced. However, certain issues needs to be resolved.

In line 152 and 153, the authors mentioned that those genes showed differential methylation levels. Is the differences in methylation level with respect to other genes or are they talking about the differential methylation levels of these genes with respect to the cases and control?

In line 205, the authors can rephrase the sentence as “…collected from 15 RM patients and 15 control.” The cases are the patients and the controls are health normal individuals.

In line 220, the authors can replace the word “relevancy” by “relevance”

In general, English language used needs to be improved.
Experimental design: In any good research paper, aims and objectives are clearly stated in the introduction section. After going through the manuscript, in the introduction section from line 64 till line 72, the authors seemed to have stated their aim. However, that section seems to be more of stating the methodologies and technologies used rather than stating the importance why this research is needed and how this research will be helpful. The authors need to justify their study and state clear aims and objectives.

Methylation is one of the dynamic mechanism which is likely to be vary with age, gestation, disease profile and medication. In materials and method section, the selection of cases should be more elaborated and justified. Also the given criteria for selecting the controls is not sufficient. Has the authors matched for age, gestation, parity, ethnicity?

In line 90 what does the authors mean by “…minced into small fragments and stored in RNAlater tissue collection solution”. Is this a standard protocol? if yes, the protocol needs to be explained more elaborately and give reason as to why this step is important.

The sample size seems to be small, but that cannot be changed now. So, the authors should at least be able to justify the sample size in light of published literature.
Validity of the findings: Discussion should be more subjective and merely not talking about the software used or supporting/constricting the results obtained. Differential methylation (if I understand correctly) between cases and controls with respect to the five genes is a good outcome. However, the so observed methylation could be cause or consequence of RM. So the authors need to discuss in light of this. The authors may go through a paper by Mishra et al., 2019 for the same (Differential global and MTHFR gene specific methylation patterns in preeclampsia and recurrent miscarriages: A case-control study from North India; Elsevier Gene).
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DNA METHYLATION PROFILING IN RECURRENT MISCARRIAGE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The Results and the Discussion section should be more descriptive. The current version is a direct report of the outcomes of the bioinformatic tools without much detail.

The article misses any context of previous studies in this field. Is this the first study looking at RM methylation data? If not, provide the outcomes of previous studies in different population. Also, include whether the findings of the current study are in accordance or not with prior studies.
Experimental design: The study does not have enough power? The sample size is too small.

The inclusion and exclusion criteria are not explained.

Whether the two study groups were matched for factors (especially maternal age) other than recurrent miscarriage (RM) are not clearly indicated.

The article does not mention about Ethical approval.
Validity of the findings: The methylation data was generated from the arrays and then differential methylation analysis done. But no validations (technical or biological) are performed. It is important to validate the findings of the differential methylation analysis.
Additional comments: The present manuscript identifies biological markers and processes involved in recurrent miscarriage (RM) by differential methylation analysis of CpGs in 450K array. The study reports some significant findings but a lot of important details are missing from the manuscript.

1.	Was the study approved by the ethics committee? If so, please provide the details.
2.	Given the incidence of RM (1-5%), the sample size of the study appears to be too small for differential methylation analyses. Does the study have enough power? Please include the sample size calculations in the manuscript.
3.	How was the differential methylation analysis validated?
4.	Do mention the inclusion and exclusion criteria in detail.
5.	Please provide the demographic details of the samples in a table.
6.	Were the two groups matched for maternal age?
7.	Did the control patients had any previous pregnancies or were they pregnant for the first time? Also, did all the enrolled pregnancies resulted in live births?
8.	The Results and the Discussion section should be more descriptive. The current version is a direct report of the outcomes of the bioinformatic tools without much detail.
9.	Where were the methylation variable positions (MVPs) located in the genes? Did they come from CpG islands or non CpG islands? Were the MVPs located in promoters for the  genes showing differential expression?
10.	Is this the first study looking at RM methylation data? If not, provide the outcomes of previous studies in different population. Also, include whether the findings of the current study are in accordance or not with prior studies.
11.	English language needs to be improved throughout the manuscript.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DNA METHYLATION PROFILING IN RECURRENT MISCARRIAGE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have satisfactorily incorporated all the suggestions made from the previous review
Experimental design: The authors have satisfactorily incorporated all the suggestions made from the previous review
Validity of the findings: The authors have satisfactorily incorporated all the suggestions made from the previous review
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DEVELOPMENT OF AN AUTOPHAGY-RELATED GENE PROGNOSTIC SIGNATURE IN LUNG ADENOCARCINOMA AND LUNG SQUAMOUS CELL CARCINOMA
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The manuscript Zhu et al provides a comprehensive analysis of autophagy-related gene expression profiles in two types of lung cancer and their prognostic value in predicting the clinical outcome. The authors run a comprehensive bioinformatic analysis and identify 6, autophagy-related genes and then classify them based on their positive or negative prognostic contributions to both diseases. They then establish that this signature is independent and highly predictive. The manuscript is nicely written, and the data are well-presented. Only a few minor edits are required before its accepted.

-	Minor spelling and grammar check are required. Many factual sentences in the Introduction and Discussion are mentioned without appropriate referencing. The authors are encouraged to run a more careful revision of the writing.
-	Although the authors do a great job on discussing the functional role of the 6 autophagy-related genes in the Discussion, they are invited to arrange those genes in a table, identifying their contribution to the autophagy pathways, and recent evidence on their prognostic roles individually. Some genes, e.g., FADD is not directly a part of canonical autophagy pathways, and while the authors mention that, the table will be an easier way to look at the role of each gene. This will be of great help to the reader.
-	Have the authors thought about how their analysis reflects on the current debate on the contribution of autophagy to cancer outcomes? Whether the induction/inhibition of autophagy would have a better outcome? How is this prognostic tool will be interpreted in the context of the different functional roles of autophagy in response to cancer therapy?
-	The authors are encouraged to include more on their future studies and the major limitations of their prognostic tool.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DEVELOPMENT OF AN AUTOPHAGY-RELATED GENE PROGNOSTIC SIGNATURE IN LUNG ADENOCARCINOMA AND LUNG SQUAMOUS CELL CARCINOMA
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this paper, the researchers analyzed clinical data using a univariate Cox proportional regression model to identify autophagy-related prognostic genes for lung adenocarcinoma and lung squamous cell carcinoma. Overall the paper has provided enough data analysis to support the conclusion, however, there are a few things needed to be addressed to increase the quality of the paper.
Experimental design: See below
Validity of the findings: See below
Additional comments: 1.	The language needs to be examined thoroughly by a native English speaker to avoid gramma mistakes.
2.	The author needs to be careful with giving full descriptions of abbreviations, for example, what is AUC in lane 37?
3.	It will be better if the author can list the identified genes in the abstract part
4.	The author needs to provide more recent information in the introduction, for example, in Lane 44, the statistical data was from 2012, which is really out of date


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: DEVELOPMENT OF AN AUTOPHAGY-RELATED GENE PROGNOSTIC SIGNATURE IN LUNG ADENOCARCINOMA AND LUNG SQUAMOUS CELL CARCINOMA
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comments
Experimental design: Can the authors describe more extensively how the risk score was calculated ?
Validity of the findings: The validity of the findings can be confirmed by applying the signatures in the clinical treatments / does the authors have any plans to proceed in this direction?
Additional comments: can the authors add future work to the paper?


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: EXERCISE MODE AND ATTENTIONAL NETWORKS IN OLDER ADULTS: A CROSS-SECTIONAL STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: -The English language is clear. However, there are some tiny mistakes. For example, in line 180 you used "trails" instead of "trials". Maybe I am missing something  ( I am not an English native speaker).
Experimental design: -Why do you choose the International Physical Activity Questionnaire and an exercise mode questionnaire?. Previous research using the same questionnaire/s should be included as well as reliability and statistical validity.

-Sample size should be justified by providing a power statement.

-How do you measure the laterality of the participants?. Edinburgh Handedness Inventory should be included (Oldfield, 1971). Even more,  Waterloo Footedness Questionnaire Revised (WFQ-R; Elias, et al., 1998), would be desirable to include in the described methods.

- Was the numerical keyboard aligned with the middle of the screen?. Please, include this information.
Validity of the findings: The main result shows that that open-skill group had signiﬁcantly higher executive network eﬃciency compared to the closed-skill and sedentary groups. The major implication (or conclusion) is well established, highlighting that open-skills exercises improve executive control.

Overall, data are new and statistically well controlled. and important for the field.
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: EXERCISE MODE AND ATTENTIONAL NETWORKS IN OLDER ADULTS: A CROSS-SECTIONAL STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: According to the results of various studies and meta-analyses (see references bellow), the effect of physical exercise on executive function is very small (<0.2), which means that the sample size of this study is too small to detect such an effect. Authors should have conducted a power analysis based on reported effect sizes before selecting their sample size. Consequently, the reported "significant" findings are most probably due to type I error.

Also, please note that in a recent meta-analysis (Sanabria, D., et al. (2019). The relationship between vigilance capacity and physical exercise: a mixed-effects multistudy analysis. PeerJ, 7, e7118.) we find an effect of externally-paced sports (open-skill) on alertness, measured by the Psychomotor Vigilance Task. The fact that this study does not detect this much larger effect of exercise on alertness is further indicative of its low statistical power, although it could also be related to the sensitivity of the ANT.

References
Xue, Y., Yang, Y., & Huang, T. (2019). Effects of chronic exercise interventions on executive function among children and adolescents: A systematic review with meta-analysis. British Journal of Sports Medicine, bjsports-2018-099825. https://doi.org/10.1136/bjsports-2018-099825
Northey, J. M., Cherbuin, N., Pumpa, K. L., Smee, D. J., & Rattray, B. (2018). Exercise interventions for cognitive function in adults older than 50: A systematic review with meta-analysis. British Journal of Sports Medicine, 52(3), 154-160. https://doi.org/10.1136/bjsports-2016-096587
Verburgh, L., Königs, M., Scherder, E. J. A., & Oosterlaan, J. (2013). Physical exercise and executive functions in preadolescent children, adolescents and young adults: A meta-analysis. British Journal of Sports Medicine. https://doi.org/10.1136/bjsports-2012-091441
Fedewa, A. L., & Ahn, S. (2011). The effects of physical activity and physical fitness on children’s achievement and cognitive outcomes: A meta-analysis. Research Quarterly for Exercise and Sport, 82(3), 521-535. https://doi.org/10.1080/02701367.2011.10599785
Etnier, J. l., Salazar, W., Landers, D. m., Petruzzello, S. j., Han, M., & Nowell, P. (1997). The influence of physical fitness and exercise upon cognitive functioning: A meta-analysis. / L ’ influence de la condition physique et de l ’ exercice sur les fonctions cognitives: une meta analyse. Journal of Sport & Exercise Psychology, 19(3), 249-277.
Young, J., Angevaren, M., Rusted, J., & Tabet, N. (2015). Aerobic exercise to improve cognitive function in older people without known cognitive impairment. En Cochrane Database of Systematic Reviews. https://doi.org/10.1002/14651858.CD005381.pub4
Angevaren, M., Aufdemkampe, G., Verhaar, H. J. J., Aleman, A., & Vanhees, L. (2008). Physical activity and enhanced fitness to improve cognitive function in older people without known cognitive impairment. The Cochrane Database of Systematic Reviews, (3), CD005381. https://doi.org/10.1002/14651858.CD005381.pub3
Singh, A. S., Saliasi, E., van den Berg, V., Uijtdewilligen, L., de Groot, R. H. M., Jolles, J., Chinapaw, M. J. M. (2019). Effects of physical activity interventions on cognitive and academic performance in children and adolescents: A novel combination of a systematic review and recommendations from an expert panel. British Journal of Sports Medicine, 53(10), 640-647. https://doi.org/10.1136/bjsports-2017-098136
Kramer, A. F., & Colcombe, S. (2018). Fitness Effects on the Cognitive Function of Older Adults: A Meta-Analytic Study-Revisited. Perspectives on Psychological Science: A Journal of the Association for Psychological Science, 13(2), 213-217. https://doi.org/10.1177/1745691617707316
Additional comments: I would recommend that the authors run a power analysis based on the size of the reported effects of exercise on executive function and increase the sample size accordingly.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: EXERCISE MODE AND ATTENTIONAL NETWORKS IN OLDER ADULTS: A CROSS-SECTIONAL STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is well written but requires proofreading, e.g. in the abstract in the Background section 'the attentional network' is ambiguous as there are three types of attention and related networks are rightly stated in the Introduction.
The recent literature is referred to, there is another, older, review on RCTs which could be of use (https://www.ncbi.nlm.nih.gov/pubmed/24862109);
The structure of the manuscript is good and the results are commented in relation to the hypotheses.
Raw data need clearer headings or a legend tab.
Experimental design: The research question is clear and the paradigm used is standard for the question explored. The utilization of 'natural' groups has limitations, but the study is still sound.
Validity of the findings: The analyses conducted are in line with other papers utilising the ANT and the conclusions are supported. One limitation that should be acknowledged is the likely different level of social interaction in the two kinds of exercise groups, open skill does not only require to respond to an unpredictable environment, but, often, requires some form of social interaction. Consider ANCOVA for amount of regular exercise, or correlation with results (although the sample is not very large).
Additional comments: The study is interesting and the manuscript is well written.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: EXERCISE MODE AND ATTENTIONAL NETWORKS IN OLDER ADULTS: A CROSS-SECTIONAL STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: All my remarks have been addressed in a satisfactory manner.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: EXERCISE MODE AND ATTENTIONAL NETWORKS IN OLDER ADULTS: A CROSS-SECTIONAL STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: As this is the second round of review please find my final comments below
Experimental design: Good
Validity of the findings: Good
Additional comments: The authors have increased the sample size and made some appropriate changes to the manuscript, there is proofreading still needed; the study is interesting and I feel that once the final proofreading has occurred it is ready for publication.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: RISK OF PHOSPHORUS LOSSES IN SURFACE RUNOFF FROM AGRICULTURAL LAND IN THE BALTIC COMMUNE OF PUCK IN THE LIGHT OF ASSESSMENT PERFORMED ON THE BASIS OF DPS INDICATOR
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript would clearly benefit language edition for correctness and clarity.
Argumentation would be stronger if more references would be used to discuss the conflict between environmental and agronomic interpretations.
All raw data is not shared.
My impression is that the current data is not enough to show which assessment is more correct.
Comments are given in General Comments section.
Experimental design: This is an original research.
The question is clearly defined, but I have some doubt if it can be answered with the presented data. However, this is an important topic which I wish the authors can elaborate further.
Some details on methods should be added.
Comments are given in General Comments section.
Validity of the findings: All data are not presented.
The authors should work on to provide direct evidence on their conclusions.
Comments are given in General Comments section.
Additional comments: Review of PeerJ manuscript “Risk of phosphorus loss in surface runoff from agricultural land in the Baltic Commune of Puck” by Pietrzak et al.
The manuscript describes a soil survey study in the Polish Baltic Sea coast, with an aim to test a P loss risk evaluation method. The manuscript is based on soil samples that are analyzed using various soil P tests. This manuscript deals with an important topic when Baltic Sea countries try to curb P losses from land to sea, and agriculture is on the central position because of the high share of anthropogenic P loading to the Sea originating from agricultural activities.
The data shows an interesting conflict between environmental and agronomic assessments. Which of the two assessments is more biased remains an open question with the data provided. A major issue is that there are no direct measurements on P losses, or data that would show that soil P status would restrict plant growth. However, this conflict is interesting by itself and should be studied further, because plants are efficient in extracting P from very low concentrations of soil solution. If the soils release high concentrations of P in water extraction, it is puzzling how the plants would be deficient in P. In its present form the data does not provide any answer on this discrepancy. I especially missed data on reactive Al and Fe contents, because they are the main P sorption components in non-calcareous soils and their concentration may vary widely in different geographic areas. These data would help in understanding P reactions in the studied soils.
As the authors mention, degree of P saturation (DPS) it is traditionally derived from as measured soil P content as related to the major P sorbing constituents (extractable Al and Fe). Because DPS is an established term for this kind of an approach, it should not be used for other ones. It is unfortunate that the term has been already used by some authors, because it will create confusion in readers who are not very familiar with environmental soil science. The equation of Pöthig (2010) is merely a model that uses soil WPS concentration to estimate the relationship between P sorption maximum and a soil’s total P content. The equation is not likely a “universal” one, because not all P associations are similarly contributing to WSP (e.g. native apatite-P is a very stable P compound), which affects the ratio of P sorption maximum to total P. It may be that the data presented here is an indication of non-universality of the approach.
The manuscript would benefit from editing the English by a native person who is familiar with soil science. I also suggest that you use throughout the text more specific terms and expressions (see the detailed comments below). One such terminology issue is “available P” and “P content”, because the former can be only obtained with exhaustion experiments with plants and the latter rather refers to total P stock. Use instead the term “agronomic soil test P (STP)”.
My suggestion is that the manuscript is returned to the authors for complementation and corrections. It is necessary that conflicts between environmental and agronomic assessments are studied and published. However, one should be able to show with measured data which one has a flaw in it. Unfortunately the present data is not sufficient to clarify this.
Detailed comments:
23: The word “determination” implies that DPS is actually determined by analyzing sorbed P and the sorption components (Al, Fe), but this approach is rather “estimation based on P concentration of water extract”.
26: You could be more specific here: “a critical analysis of assessment results was carried out”; I think it’s more like “compared to the agronomic interpretation of soil test P concentrations”.
29: “P content was determined” could be changed to “P was extracted”…
35: “ascertained” is a rather strong word, because deficiencies were not quantified. The agronomic interpretation on what P concentrations are considered sufficient also changes with time, see e.g. Buczko et al. 2017 (DOI 10.1007/s13280-017-0971-1), because large safety margins were commonly applied in the past when making P recommendations and in setting limits for optimal soil test P.
36-39: I would like to see a more decisive statement at the end of Abstract. There is clearly a conflict between the environmental and agronomic interpretations, or on how the environmental and agronomic soil tests work on these soils.
42-72: It would be good to back the statements in the start of Introduction with references. Now there’s only two sources used, Helcom and National…(could the National Water Management Board be referred in text to as NWMB?). Research on these issues should be given a credit, not only reports or summaries that are based on them.
Please avoid unclear references to what has been said previously, because they may confuse a reader. As example line 51 (of the mentioned component), 61 (the above), 67 (the component in question), … It is better to be specific so that a reader does not to need go back to the previous sentence and look what these words refer to.
92: “P saturation in surface runoff”, change to “P concentration in surface runoff”.
93-98: This paragraph would benefit from rewriting. For testing the approach’s usefulness in predicting P loss risk, one should actually measure P losses. Assuming that analyzing agronomic P indices would reveal P losses is not enough. The last sentence of this paragraph is cryptic why it needs rephrasing and specifying the meaning.
115: Please tell how sampling was made, e.g. from how many subsamples a sample was composed of.
117-130: There seems to be repetition here, please rephrase.
133: Please indicate that WSP was calculated to mg/kg soil.
137: I assume 10% was the SOM content, not C?
145-146: “The basis for the assessment was the percentage share of the soil samples tested in individual reaction and abundance classes.” Please clarify. Do you mean that agronomic interpretation of STP is not based on STP and pH only, but the STP distribution also affects the class division? Maybe it’s the word abundance that makes the confusion – do you mean P concentration, or the number of soils in a STP class?
158-164: I’m not sure how these analyses were used, otherwise than for constructing the example Fig. 2. Maybe these were meant for Table 5 (that in its current seems unnecessary)?
179-184: Please describe more specifically the terms “medium”, “light”, “very light” soils. I suspect you’re meaning textural classes and naming the major soil separates and clay contents would be more easily understood (e.g., loamy soils with X-X% clay).
Could these data be combined with STP and WSP data to show if there are some obvious risk areas?
209-210: Be consistent in using abbreviations: PH2O -> WSP.
215: Please elaborate the conflict between agronomic and environmental interpretation after this paragraph. To be interesting to a reader, you should tell something about the sorption properties of the studied soils. Minimum would be extractable Al and Fe, e.g. by the oxalate method which is the most widely used. Otherwise there just are two opposite interpretations, of which one appears to be wrong but one cannot guess which. Are there some P fertilization studies done at the area (at least in line 262 P deficiencies are mentioned, please elaborate that)? Reference to such data would tremendously strengthen the paper. The recent paper of Fischer et al. (http://dx.doi.org/10.1016/j.scitotenv.2017.03.143) shows that the earlier German target STP was in practice always associated with high P loss risk (assessed according to Pöthig et al.). Because the target STP could be lowered in 2015, it is likely that there was a good safety margin associated with the old one. Is there a possibility that the interpretation in Poland could be similarly “on the safe side” as the past German agronomic interpretation? Or is P buffering of the Puck area soils so low that once P concentration in soil solution declines, there is no buffering by the adsorbed P that would replenish it?
When ending: “There was a high risk of P loss from these soils to water following the approach to determining this risk suggested by Pöthig et al. (2010).”, I wonder what is your own interpretation? If a soil contains about 25 mg WSP/kg, it would mean that P concentration in (1:50) water extract would be about 0.5 mg/L. To me it seems quite high, but how does it relate to dissolved P concentration in runoff waters? Can you compare with some Polish studies on runoff water quality?
220-222: Please re-read these sentences: “There was a relatively low correlation between the pH value of the soil and its P content determined by the Egner-Riehm method both in the layer up to 5 and 30 cm. However, this correlation indicates that by reducing the acidity of soils plant available P would increase.” I’m not sure that a poor correlation between pH and STP would indicate that plants could utilize more P if pH is elevated. Increasing pH of an acidic soil will make P more soluble, but justifying this conclusion by the preceding sentence is not sound reasoning.
227-228: Not sure the meaning of this sentence. Please define what you mean by “topsoil” (0-5 or 0-30 cm). Secondly, a correlation between P concentrations in these two sections does not prove that P was homogenously accumulated (I guess you mean dispersed), just that the concentrations rank in a relatively similar order. However, your supplemental data shows that there is no vertical stratification in STP concentrations.
228-230: Please clarify this sentence. Do you mean that it is equally good to use whole 0-30 cm section samples in environmental risk assessment? Is it a general recommendation, or valid for the study area only?
236-237: All abbreviations (PH2O_w1) should be opened when coming first time.
254-255: “… soils practically in the whole analysed area of agricultural lands were overly supplied with P…” Is it also possible that the studied soils’ P retention capacity is very low and therefore the environmental and agronomic interpretations disagree?
268: If “This treatment” refers to liming, note that liming in itself does not increase P resources, but the solubility of the reserve. But I totally agree that liming would be a first remedy for the soils that fall into the low pH categories.
270: Change “DPS-based analyses” to “WSP analysis” (WSP was analyzed, DPS was calculated).
276-278: Maybe it could be stated that P loss risk index is just one component and needs to be complemented with others that tell about the delivery from soil to water. Good references are found by searching “Lemunyon and Gilbert P index” and “P loss continuum”. The discussion section would in all cases benefit from more references.
Fig 1: Please indicate that the R2-value refers to the data of Pöhlig et al.
Fig. 4: Please add explanation that these are soil test P classes in the figure caption and replace “P content” with “Soil test P class”.
Table 1 caption: Use rather something like: “Soil test P concentrations according to the Polish agronomic interpretation…”, change “abundance” to “Soil test P”, “assessment” to “interpretation”, remove “ingredient”. There are unnecessary left parentheses markers in the table and > markers are on the wrong side of the range values.
Table 2 caption: Replace “thresholds” with “classes”.
Tables 3 and 4: Unnecessary row at the bottom (DPS).
Table 5: Should there be data of the study area in this table?
Supplemental: what is P-wod_w1? I have an impression that the Journal encourages publishing all data. I could not find anything about clay and SOM content. Also, a file with measured STP and WSP could be useful in development or calibration of agro-environmental models, and much appreciated by that community.