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: IMPACT OF THE ANTIDEPRESSANT CITALOPRAM ON THE BEHAVIOUR OF TWO DIFFERENT LIFE STAGES OF BROWN TROUT
Review round: 1
Reviewer: 1

Output:
Basic reporting: In general, the results and statistics are well presented. However, the writing is at times difficult to follow and the wording ambiguous. I have made a few comments to help. In places, arguments are not justified or supported by references, please ensure appropriate supporting references are added. Line by line feedback is copied below.

Abstract background: In the background section, switching between the frequency of human prescriptions vs environmental presence of antidepressants is potentially confusing. I would recommend a more linear framework. There are also a few small typos. I would recommend the following changes… “Over the last two decades, there has been a constant increase in prescription rates of antidepressants. In parallel, neuroactive pharmaceuticals are making their way into aquatic environments at increasing concentrations. Among the antidepressants detected in the environment citalopram, a selective serotonin reuptake inhibitor, is one of the most prevalent. Given citalopram is specifically designed to alter mood and behaviour in humans, there is growing concern it can adversely affect the behaviour on non-target wildlife.”

Abstract methods: For the method section, there is no mention of what endpoints were actually measured at each life stage, or the nominal concentrations used. Both should be added. Further, I would recommend removing “Real water concentrations well reflected nominal concentrations.”, this is not necessary in the methods section. For example…“In our study, brown trout were exposed to environmentally relevant citalopram concentrations (nominal concentrations 1, 10, 100, 1000 ug/L)  at two different life stages, a larvae exposure (eyed ova stage until 8 weeks post yolk sac consumption) and a juvenile exposure (X age for a 4-week exposure). At both stages, we measured…XX.”
Results: In the results section, you may consider replacing “sojourn” it is not a very commonly used term (as far as I have seen). Instead… “both larvae and juvenile fish exposed to the highest test concentration of citalopram (1 mg/L) had higher swimming activity and decreased anxiety (i.e. spent longer in the upper part of the aquaria) compared to control fish.

Line 53: “in rising product types” do you mean an increasing number of different psychoactive drugs?  If so, perhaps it could be re-worded to make this clearer.

Line 56–57: “Within the group of antidepressant drugs, the selective serotonin reuptake inhibitors (SSRI) play a major role (Schwabe and Paffrath, 2016).” — This is a little ambiguous, play a major role in what? Treating patients? Please clarify.

Line 63: Add a comma after Germany.

Lines 67–69: “In wastewater treatment plant effluents, citalopram concentrations range from 44 ng/L to 840 μg/L in the effluent of drug manufacturers (Himmelsbach et al., 2006; Larsson et al., 2007; Silva et al., 2014).” — This sentence is ambiguous; do you is this only in effluent of drug manufacturers or more broadly in wastewater treatment plant effluents. Please clarify.

Lines 74–82: It needs to be more clear which results refer to which studies when comparing and contrasting past studies. It should also be made more clear which results are in agreement and which are not. For example, “At present, the impacts of citalopram on anxiety-related behaviour of fish have been mixed (REF all studies). X studies reported a decrease in anxiety behaviour at X concentrations with X length exposure… whereas, X studies reported…” At the moment it does appear that there are many discrepancies.

Line 79 and 81: Please give exact concentration instead of low ug/L.

Line 88–89: “Due to these diverse outcomes, it is important to assess different endpoints in different life stages to detect the diverse effects that citalopram can have on aquatic organisms” — With the above examples it is really not clear which are divergent and why? Across these studies there are many different concentrations, dose duration, and species could you make this clearer as you make these comparisons. I fear that you may be exaggerating inconstancies across studies, which makes the impacts of citalopram on fish behaviour seem weak and unrepeatable. Please make these comparisons more clearly, as to which results are contrary to each other, as well as including concentrations, dose duration, and species for each.

Line 100: Again, I think sojourn is not used very frequently, it might help to replace it with simpler language.

Line 123: Sub-heading is not bolded like the others.

Line 125–126: “both 7°C and 11°C, in order to reveal influences of temperature on the effects investigated” – This is an interesting point of difference of your study, it would be good to highlight this objective in the introduction and abstract.

Line 225: “Artificial swimming measurement device” – This is a form of novel tank test, right? I would change the name to novel tank test throughout as most readers will be familiar with this terminology.
Experimental design: I believe there were some issues with experimental design in the project. Most importantly, the methods used to measure 'Swimming behaviour during exposure', as well as low sample sizes more generally. I have detailed my thoughts in line by line feedback below.

Line 136–138: “At 7 days post-hatch, the heart rate of 5 individuals of each control and the highest concentration tank was measured and, whenever a difference was revealed, the other treatments were also assessed.” – I would not recommend such a protocol in future experiments; SSRIs are increasingly reported to have non-monotonic dose-response relationships. Therefore, you may miss an effect at your low dosage that was not reflected at the higher dosage. As one example, in the highest dosage you may see phenotypes of a toxic effect of the chemical, which has opposite effects to what you would see based on the therapeutic action of the chemical. Obviously, it is not possible to change this protocol now, but I would recommend that it is avoided in future experiments.

Line 141–143: “Here, 5 fish from each tank were transferred into small glass aquaria and swimming behaviour was recorded for 18 minutes. Terminally, fish were sampled 8 weeks after yolk sac consumption.” —A sample of 5 fish is not an adequate sample size to draw a comprehensive behavioural conclusion on the effect of low dose chemical exposure. All conclusion from this behavioural data should be very circumspect and should acknowledge the limited sample size and thus the power of the results.

Line 218–220: “For experiments with brown trout larvae, 3 pictures were taken per day of each photographable tank at an interval of 5 minutes, from one-week prior to the experiment until sampling (Apr 03 – Apr 13, 2017).” — Please justify that this method is robust enough to capture changes in swimming behaviour. This is a novel method, therefore, extra justification of whether it can capture changes in swimming behaviour is necessary. My ‘knee jerk’ reaction is that it is not sufficient to detect changes in swimming behaviour, as it captures a total of only 27 frames of the swimming behaviour over a week, in video terms, this is less than a second (i.e. 30 fps) of behaviour over a week. Fish move rapidly and will change their behaviour based on an observer being present (as they would have been during the photo). I think more detailed information on fish swimming behaviour is required than that capture in this method. This is further compounded by small sample size.

Line 228: “and five brown trout larvae were placed in there” – Again, 5 fish is not an adequate sample size to draw behavioural conclusions. Indeed, looking at table one I note a huge amount of variability in total distance moved in all fish groups. Subtle effect at the lower dosages could have been missed due to low statistical power.
Validity of the findings: The arguments for the behavioural effects reported need to be supported with references. In addition, the small sample size of this study make it difficult to make concrete conclusions on the effects of low-dose exposure.

Line 449–450: “higher locomotor activity of the exposed fish (Stewart et al., 2012)” — I do not believe can you conclude this if you didn’t measure swimming velocity (using the photographic method). Spending time in the upper part of the tank doesn’t necessary mean they had higher swimming velocities.

Line 456–458: “For this reason and the inherent variation in this setup for behaviour measurement the biological relevance of the slight effect in the 1 and 10 μg/L treatment has to be confirmed with a bigger sample size.” — This is true for all the behavioural results in this study, whether they are ‘positive’ or ‘negative’ results.

Line 475–480: “The transfer of fish into an ASMD leads to a stress reaction in fish, which basically results in a startle reflex and increased escape behaviour and thus, an increase in locomotor activity. Since citalopram is an anxiolytic drug and reduces anxiety, fish are reasonably soothed when exposed to 100 μg/L or 1000 μg/L citalopram as they swam slower and less bustling than control fish. Therefore, the total distance they moved and their mean swimming velocity were lower than that of the controls.” – I understand the logic of this argument, however, it could just as easily be argued that decreased anxiety would increase activity in a novel stressful environment. A fish that remains more activity and exploratory in a novel environment stressful environment is typically considered bolder and less anxiety in the behavioural literature (as you have argued in the section above). If these fish are preforming a stress escape/startle response, it should not last the whole trial, instead, you would expect that they return to normal activity levels over the duration of the experiment. Perhaps looking at your velocity data over time will give some insights. Alternatively, is there a study which has confirmed your argument in which you can cite.
Additional comments: The work you are doing is very important. We need to generate more data on the impacts of low-dose pharmaceutical exposure on sublethal endpoints. However, I would encourage the authors to use larger sample sizes in future experiments, the effects of these chemicals can be 'messy' (and understandably so given their mode of action), large statistical power is essential to identify the realised effects of these drugs. If the authors make a point of explaining these issues forthrightly and acknowledge the limitation of the behavioural conclusions—specifically at the lower dosages that had high within-group variability—the data generated would be useful to the wider ecological community.


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: IMPACT OF THE ANTIDEPRESSANT CITALOPRAM ON THE BEHAVIOUR OF TWO DIFFERENT LIFE STAGES OF BROWN TROUT
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is overall well written and easy to understand, although the authors introduce new terms that are not commonly used in the field (e.g. sojourn, ASMD). I have added suggestions to replace these with more commonly used terminology.

Literature references are appropriate and a good overview of the studies on citalopram in fish is provided in the introduction. However, in the discussion only the studies confirming the results from the present paper are reitterated, while the discussion section would benefit from a more balanced review of how the current results relate to previous studies.

The article is well structured. However, I request more information in the form of tables and figures on the behavioral parameters from the "ASMD". The current conclusions are not supported by only presenting average values of distance moved and velocity. Also ammonium levels are missing from the water conditions table (supplement). Raw data is currently not shared.
Experimental design: The article fills a knowledge gap as studies effects of citalopram pollution on fish have reported diverging results, and citalopram is one of the most commonly used SSRIs in Germany.

The experiment is generally well performed, although there is room for improvement with regards to the reporting of the egg exposure experimental design, reporting of behavioral measurements and reporting of ammonium levels (considering the high fish density and infrequent water changes).

The experimental design (exposure setup) and statistical analyses are sound.
Validity of the findings: Impact and novelty are assessed and meaningful replication is encouraged.

Not all underlying data has been provided (see below).

My main 2 objections to the conclusions rest on the interpretation of the behavioral data:
1) The first behavioral test measuring the duration spent in the upper/ lower half of the arena was performed in groups of fish in the exposure arena. However, the diving response should be measured in a novel tank on individual fish. The authors do not address this issue while they clearly state that they have based this test on the novel tank diving test originally developed for zebrafish. The authors should first verify the use of this behavioral test, by showing that also brown trout display a diving response (not all fish species show this characteristic movement to the bottom!), and second, show that high concentrations of anxiolytics (SSRIs, benzodiazepines) affect the brown trout diving response. In the present form the sojourn preference results cannot be interpreted as anxiolytic. If these verifications can no longer be made because the experiment is finished, then these interpretation problems should at least be thoroughly discussed.
2) The reporting of the second behavioral test (ASMD) is insufficient to support the conclusion that control trout were startled while citalopram exposed trout were not startled. Ideally, velocity (in cm/s), velocity (in bodylengths/s) should be reported over time (in minutes) in addition to total duration not moving (in sec) over the whole trial. This to clearly show the initial startle response in the controls drove the observed treatment effect on velocity. At the moment, the lower velocity of the citalopram exposed fish could mean they were freezing more and citalopram therefore had an anxiogenic or sedative effect!

The first point can be solved by authors by discussing the differences between the sojourn preference and the novel tank diving test. The second point can be solved by adding more ethovision parameters and discussing possible alternative explanations for the findings in the ASMD.
Additional comments: - Line 28 remove "which could be suspected to alter behavioural and physiological parameters in fish". You could add this information to a separate sentence after this sentence, but at the moment this sentence is hard to read because of this subordinate clause.
- Line 29: with "most prevalent" do you mean that citalopram is the SSRI that is detected at the highest frequency or at the highest concentration?
- Line 32: please state exact concentrations and add between brackets which of these reflects the
environmentally relevant, low, medium and high concentration.
- Line 36 "sojourn": this is not a term that is often used in the fish behavior literature. I suggest changing it to the more commonly used "duration (of time) in" or "time spent in".
- Line 35 "decreased anxiety" is an interpretation. Anxiety is a human mental state and it is hard to investigate if fish experience this or how to measure this in fish. However you state explicitely which behavioral parameters measured which is very informative. Perhaps rephrase to "showed higher swimming activity and increased their time spent in the upper part of the arena, behavioral changes that are indicative of decreased anxiety".
- Line 39 "display": please change to "displayed"
- Line 51: "all surface waters" and "all trophic levels". This is not known since not every stream in the whole world has been sampled. There are probably still some pristine streams. Please change "all" to "most" or "most human-influenced waters".
- Line 53 "found in rising product types and concentrations in surface waters": it is unclear to me what you mean with "found in rising product types". Please consider rephrasing to "increasingly detected in rivers and surface waters". This more accurately reflects increases due to increased reporting/ more measurements as well as increased prescription rates.
- Line 53/ 54 reference to Fick et al. 2009: this paper is about pharmaceutical pollution by bulk production plants and therefore presents a special/ worst case. A more appropriate reference for surface water concentrations of psychoactive pharmaceuticals is Hughes et al. 2012 (global) or Loos et al. 2009 (EU), or Batt et al. 2016 (USA). Same for line 383.
Hughes, S.R., Kay, P., Brown, L.E., 2012. Global Synthesis and Critical Evaluation
of Pharmaceutical Data Sets Collected from River Systems. Environ. Sci.
Technol. 47, 661–677.
Loos, R., Gawlik, B.M., Locoro, G., Rimaviciute, E., Contini, S., Bidoglio, G.,
2009. EU-wide survey of polar organic persistent pollutants in European river waters. Environ. Pollut. 157, 561–568.
Batt, A.L., Kincaid, T.M., Kostich, M.S., Lazorchak, J.M., Olsen, A.R., 2016. Evaluating the extent of pharmaceuticals in surface waters of the United States using a National-scale Rivers and Streams Assessment survey. Environ. Toxicol. Chem. 35, 874–881.
- Line 57: change "(SSRI)" to "(SSRIs)"
- Line 58 "serotonin reuptake transporter": this transporter is called the serotonin transporter (SERT).
- Line 59: "presynapse membrane" please change to "presynaptic membrane"
- Line 68: please remove "in the effluent of drug manufacturers" and move the citation to Larsson et al. 2007 to the next sentence in order to separate the case of the outlet of bulk drug production sites from "ordinary" waste-water treatment plant effluents.
- Line 71/72: "one of the most common antidepressants" please rephrase to "one of the most commonly prescribed antidepressants".
- Line 62-71: the authors give a thorough overview of the citalopram concentrations detected in different environmental matrices. Since you make a comparison to fluoxetine in line 73, it would be interesting to compare the citalopram concentrations to fluoxetine concentrations (give approximate range in the environment). Also the potency and bioconcentration factor of both drugs should be taken into account when comparing these 2 SSRIs. Based on these considerations, Fick et al. 2010 have calculated that the predicted critical environmental effect concentration of citalopram is 141 ng L-1 while for fluoxetine is 489 ng L-1. A reference to this article could further strenghten your argument that citalopram is understudied.
Fick, Lindberg, R.H., Tysklind, M., Larsson, D.G.J., 2010. Predicted critical environmental concentrations for 500 pharmaceuticals. Regul. Toxicol. Pharmacol. 58, 516–523.
- Line 72: change "SSRI" to "SSRIs"
- Line 73: "like fluoxetine" : add a number of key references.
- Line 76: please add the species of stickleback used in this study. I think it is three-spined stickleback (Gasterosteus aculeatus).
- Line 75-90: indeed the results from different citalopram studies on fish have been quite contradictive even within the same species. I think this paragraph would benefit from placing the contractive results on the same species next to each other. For example, discuss Kellner 2015, 2016 and 2017 on stickleback in one go, highlighting that citalopram increased activity in the 2016 study while developmental exposure had the opposite effect on activity and even increased aggressive behavior (Kellner 2017). Another reason for the discrepancy between the stickleback studies could be the choice of behavioral test. The novel tank diving test was originally developed for zebrafish which show a characteristic movement to the bottom when entering a novel deep tank. In my experience, wild-caught stickleback do not show the same ”diving response” and hence results such as increased or decreased duration in the top should be interpreted with care.
- Line 100: what do you mean with ”sojourn preference”? This is not an established term.
- Line 126: how many replicate tanks were used per concentration and temperature?
- Line 128/129: 30 fish in 10L of water is a very high density that may affect water quality. Water changes twice a week may not be enough. Please provide data on ammonium levels. Same for experiment 2 (line 152-153).
- Line 137-138 ”At 7 days post-hatch, the heart rate of 5 individuals of each control and the highest concentration tank was measured and, whenever a difference was revealed, the other treatments were also assessed.” This strikes me as an unusual procedure to collect data. The choice of measurements to perform should be made independent of the outcome of the first measurements to avoid type I and type II errors.
- Line 138-140: It seems the duration spent in each vertical section of the aquarium was assessed in the exposure aquarium. First, it is unclear how you defined the vertical sections. But more importantly, measuring vertical movement in the home tank is quite a different thing from assessment of the diving response in the novel tank diving test, and might therefore give quite different results. In the novel tank diving test, the fish is placed alone in a novel, narrow and deep tank, a stressful situation for a shoaling fish species. Species such as zebrafish usually quickly move to the bottom, while this ”diving response” is reduced by chronic fluoxetine treatment (Egan et al. 2009 https://www.ncbi.nlm.nih.gov/pmc/articles/PMC2922906/ ) as well as treatment with the anxiolytic diazepam (Bencan 2009), therefore decreased duration at the bottom (or increased duration at the top) is usually interpreted as an anxiolytic effect. In your exposure tanks, there was likely a dominance hierarchy in the group which influenced where the fish swam, and there was no additional stressor of being alone in a novel tank.
- Line 146: why was the tailfin used for citalopram tissue concentration? Bioconcentration factors differ between different tissues and the most logical choice here would be brain tissue since this is the tissue where the drug exerts its effects. See Heynen et al (2016) for a comparison of pharmaceutical concentrations in different tissues of perch. https://www.publish.csiro.au/en/en16027
- Please provide a timeline to further clarify the sampling points and tests performed in each of the two experiments.
- Line 225: Please consider rephrasing ”artificial swimming measurement device (ASMD)” to ”automated video tracking of swimming behavior” or similar. Authors familiar with ethovision then immediately know what you mean, whereas ADSM is term that I have never encountered before. The use of the term ASMD also is unclear in line 141.
- Line 225-244: The ASMD procedure is unusual since multiple fish are tested in the same small test arenas (5 larvae in experiment 1 and 3 juveniles in experiment 2) instead of fish being tested individually. Also a key anxiety-related behavior, thigmotaxis (wall-hugging), has not been measured, which is a missed opportunity since this has been more closely linked to the behavioral effects of pharmacological effect concentrations of SSRIs compared to swimming activity. The small arenas may not have enabled the researchers to quantify thigmotaxis since this behavioral variable is best measured in larger test arenas that exceed the fish length by approximately 20 times.
- Line 241: the total distance moved should be directly proportional to average velocity if tracking is perfect after manual corrections of the track (i.e. if the total duration in the arena is exactly 18 minutes for each trial). Hence there is no need to report both variables. If tracking is not available for 100% of the trial, average velocity is more reliable since it compensates for the missing part of the track.
- Line 241: The authors calculated swimming velocity and total distance moved, but these parameters are influenced by the size of the fish. Larger fish swim larger distances. Indeed the fish exposed to the higher concentration are smaller (for both temperatures) and move shorter distances. It would be helpful to calculate swimming speed in bodylengths per second by dividing the velocity in cm/s by the measured standard length of each individual (in cm). Another ethovision parameter to add to table 1 and 2 is the duration of time spent moving/ not moving. This parameter sums the time intervals that the fish spent not moving (moving less than 2 cm/s say, this threshold should evaluated using integrated visualization as described in the ethovision manual) and is independent from swimming speed.
- Line 268: please indicate which response variables were transformed, and how.
- Line 271: it is not clear what is meant with ”block”.
- Line 385-411: ”bioaccumulation” is a term that is in some parts of the literature used to describe the accumulation over the food web. Please consider rephrasing to ”bioconcentration”. Please also consider adding a sentence in the beginning of this paragraph describing the bioconcentration factors for the different treatments used, for 2 reasons. First, it makes it more clear that for egg exposure, the tissue concentrations in fin muscle tissue are still lower than the water concentrations while in larvae exposure tissue concentrations exceed water concentrations. Also it makes it easier to compare bioconcentration factors for the different exposure concentrations. The calculation of the bioconcentration factor is found in Heynen et al. 2016 (https://www.publish.csiro.au/en/en16027 ).
- Line 395: ”possibly due to the longer exposure time of about 4 weeks” : please add the number of exposure days for each temperature between brackets.
- Line 401-406: could the authors please specify what the approximate citalopram concentrations were in the effluent studies (Grabicova et al. 2014, 2017)
- Line 413: change ”induced by citalopram” to ”influenced by citalopram exposure”
- Line 416: what is meant with ”exogenous feeding in salmonids is associated with higher mortality risks”? That predation risks are higher once the yolk sack is consumed? But the exposure tanks were covered in your experiment?
- Line 424: please provide exact fluoxetine concentrations in this study.
- Line 431: but developmental exposure to 1.5 ug L-1 citalopram increased food intake in stickleback (Kellner 2017). Can the authors please discuss that other studies have reported both increased and decreased food intake?
- Line 441-442: ”In general, the test design used in the present study for this parameter is comparable with the new tank diving test.” (Please change ”new” to ”novel”.) I very much disagree with this statement. There is a big difference between measuring the vertical position in the home tank in groups of fish, and measuring the diving response of individual fish in a novel tank. Zebrafish indeed show a clear 'diving response' where the fish initially lies still in the bottom in the first minutes followed by gradual movement to the middle and top zone. The authors first need to show that brown trout have the same response. The diving test has also been verified with acute and chronic exposure to therapeutic concentrations of anxiolytics and antidepressants, that reduce this behavior. This has also not been shown for brown trout. Hence the behavioral assay used here has not been verified for the species investigated and it is unclear how ”more fish in the top half” should be interpreted. These drawbacks and the differences with the NTDT should be made clear to the reader and cannot be ignored.
- Line 453-455: ”The significant difference in sojourn in the upper aquaria part of the brown trout larvae exposed to 1 and 10 μg/L citalopram at 7°C is more likely due to the fact that only one of the three replicate aquaria was analysed and therefore a single individual has a higher impact on the relative sojourn in the upper aquaria part.” Why was only 1 replicate tank analysed? This is in direct contrast to line 215 where you write ”Nevertheless, the selection of photographable tanks was representative for the entire number of aquaria.” Please provide information on the number of tanks observed for ”sojourn in upper half of the aquarium” for each treatment in table 1 and 2.
- Line 458: ”An anxiolytic effect of citalopram ...” please state exactly which behavioral variable was measured in these studies. Did these species also spent more time in the upper half of the arena?
- Line 461-462: Please move this sentence to the next section on behavioral activity. Also, you do not mention that Kellner et al. 2017 (stickleback developmental exposure, which is more comparable to the current study) also observed lower swimming activity, which is in line with your own results from the ASMD. Please provide a balanced review of the studies measuring behavioral activity in response to citalopram, highlighting any differences in results between studies and differences in methodology that could account for these divergent findings.
- Line 469: ”This effect is exclusively due to the anxiolytic and soothing effect of the antidepressant.” The relationship between anxiety-related behavior and behavioral activity is not at all as clear-cut as the authors propose here. In general, decreased activity is usually rather indicative of an anxiogenic and not an anxiolytic effect! Freezing is a very common response to a stressful situation in salmonids, and citalopram seems to increase this anxiogenic response! Hence you see an opposite effect of exposure to low concentrations of citalopram! This might have to do with the low concentrations used, and has been reported for low concentrations of fluoxetine as well. Fluoxetine exposed musquitofish (8 or 97 ng L-1) spent longer time freezing after the drop of a cilindrical metal probe into the tank (Martin et al., 2017). Wild-caught guppies exposed to fluoxetine (4 or 16 ng L-1 for 4 weeks) remained stationary for longer, spent longer time under plant cover and were less active following a simulated bird attack (Saaristo et al., 2017). An alterative explanation is that developmental exposure of larvae to citalopram can actually cause anxiogenic effects while anxiolytic effects are seen for adults. A third explanation is that the highest concentration of citalopram actually resulted in a sedative (sleep inducing) effect, which is thought to be caused by citalopram also being a mild antihistamine. Hence the current interpretation of reduced activity as anxiolytic is problematic and this part of the discussion lacks a critical review of the available literature.
Martin, J.M., Saaristo, M., Bertram, M.G., Lewis, P.J., Coggan, T.L., Clarke, B.O., Wong, B.B.M., 2017. The psychoactive pollutant fluoxetine compromises antipredator behaviour in fish. Environ. Pollut. 222, 592–599.
Saaristo, M., McLennan, A., Johnstone, C.P., Clarke, B.O., Wong, B.B.M., 2017. Impacts of the antidepressant fluoxetine on the anti-predator behaviours of wild guppies (Poecilia reticulata). Aquat. Toxicol. 183, 38–45.
- Line 471-474: ”Table 2: Results for juvenile brown trout exposed to citalopram. Data are shown as arithmetical mean ± standard deviation. Asterisks indicate significant differences to the respective controls (*p<0.05; **p<0.01; ***p<0.001). LoD=limit of detection” This information should be removed from the discussion as it is a figure caption.
- Line 476-477: ”which basically results in a startle reflex and increased escape behaviour”: no behavioral data is provided to show that the startle reflex drove the differences in activity between citalopram treatments. Clear evidence would be increased velocity in the beginning of the trial which gradually is reduced over the 20 minutes of the trial, with citalopram exposed fish showing less of a peak in velocity in the beginning. Considering the rather low average velocities measured in this experiment (2 cm/s and 1 cm/s or lower in the high concentration) I would rather presume that the differences in activity were driven by differences in time spent freezing.
- Line 478-479: ”as they swam slower and less bustling than control fish” Again, no data is provided to show that control fish were burst swimming (not bustling) more. As discussed earlier, the movement (duration moving/ not moving) variable from ethovision might back this up, but velocity/ distance moved by itself does not give any information on whether the control fish moved with higher routine swimming speed or alternatively, whether their speed was higher because they were bursting more. Please provide evidence!
- Table 1 and 2: what do the standard deviations represent? Variation between replicate tanks? Variation between individuals?
- Figure 1: Please consider dividing up this graph into 8 bars: 4 citalopram concentrations that were directly dissected for cortisol and 4 citalopram concentrations tested in the ASMD. This will make your general point more clear that citalopram exposure did not affect cortisol concentrations, while the ASMD method was stressful to the fish.
- Please add a graph with the ASMD data: velocity in bodylengths per second over time (in minutes) per citalopram concentration.


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: IMPACT OF THE ANTIDEPRESSANT CITALOPRAM ON THE BEHAVIOUR OF TWO DIFFERENT LIFE STAGES OF BROWN TROUT
Review round: 2
Reviewer: 1

Output:
Basic reporting: Line 89: “1,5 ug/L” — should be 1.5

Line 91: “1,5 ug/L” — should be 1.5

Line 96: “2,3 and 15 μg/L” – should be 2.3

Line 85–102: It’s good to see an open discussion of the different results across studies. However, when listing the results of the different experiments it’s difficult to ascertain when results are in accordance or contrasting. Could the authors please make this clearer. Study X found a reduction in anxiety-related behaviour at X ug/L with a X day exposure, whereas Study X reported no change in anxiety at X ug/L with a X day exposure. The comparisons of studies addressing feeding were done well.

Line 140: “static three block setup to 0, 1, 10, 100, 1000 μg/L citalopram at both 7°C and 11°C” — to avoid confusion should read ‘at 7°C or 11°C’. Also, it should read three-block'

Line 244: “Small aquaria (17*17*8.5 cm)” — typically formatted with ‘×’ not ‘*’

Line 249–250: “(Basler acA 1300-60 gm, 1.3 MP resolution, Basler AG, Ahrensburg, Germany, lens: 4.5-12.5 mm; 1:1.2; IR 1/2”)” — When giving a range of number you should use N-dash (–), not a hyphen (-). For example, “1300-60 gm” should be ‘1300–60 gm”.

Line 251: “The setup” — ‘set-up’

Line 275: “3,3’,5,5” – It appears that you have used commas, as decimal points throughout. I would recommend changing this.

It is uncommon to report p-values beyond 3 decimal places. It will help readability if you reduce to 3 decimal places.

Line 332–333: “During this exposure time, fish were 43 d – 71 d post hatch which is the critical phase of complete yolk sac consumption and first food intake.” – This information belongs in the discussion or intro, not results.

You may find a recent paper on reporting disputed foraging dynamics of fish exposed to the SSRI fluoxetine useful here, given your fish also exposed in groups.
Martin, J. M.; Saaristo, M.; Tan, H.; Bertram, M. G.; Nagarajan-Radha, V.; Dowling, D. K.; Wong, B. B. M., Field-realistic antidepressant exposure disrupts group foraging dynamics in mosquitofish. Biology Letters 2019, 15, 20190615.
Experimental design: Swimming behaviour in exposure aquaria: the data gathered with this experiment is a little hard establish, as it is currently worded. Is the following interpretation correct? If so I would suggest re-wording as follows…

 ‘During the exposure, over a 10-day period, three pictures were taken daily across X tanks. For each day, an average was calculated using the three photographs, giving a total of 10 daily measures for analysis (n = X per treatment).’

I used ‘X’ tanks because I wasn’t actually sure how many tanks you measured. Please make this clear.

Line 231–232: “Nevertheless, the selection of photographable tanks was representative for the entire number of aquaria” — It is unclear what is meant by this sentence.
Validity of the findings: You need to report how much of the variation was captured by your random effects.
Additional comments: It was my pleasure to re-review this article for PeerJ. I thank the authors for taking on board previously feedback. I have made some additional suggestions to improve clarity, particularly in the swimming behaviour assay. I have also requested the addition of some statistical information, namely the variability captured by the random effects. I believe that with the following changes the MS will be suitable for publication. Excellent 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: IMPACT OF THE ANTIDEPRESSANT CITALOPRAM ON THE BEHAVIOUR OF TWO DIFFERENT LIFE STAGES OF BROWN TROUT
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: Overall the conclusions are thoroughly supported by the data. Only the newly added data on velocity and no movement over time lacks statistical analysis (see general comments).
Additional comments: In my opinion, the manuscript has been greatly improved since the first version. Especially the interpretation of the behavioral results (vertical distribution of fish during exposure and the ASMD) has been expanded and there is now also a stronger link to previous studies. I only have a couple of minor comments:
-	Line 72: change “range” to “ranging”.
-	Line 86: add “part of the” between the words “upper” and “aquaria”.
-	Line 139: “three block” is not an established term. Please consider rewriting to “a semi static setup with three replicates each of 0, 1, 10, 100, 1000 µg/L citalopram at both 7°C and 11°C”
-	Line 368-373: please provide statistical proof for these statements. In figure 1, panel B, C, E, F, H and I it is also difficult to compare the control groups with the exposed groups. Please consider converting these bar graphs to line bars with a single line per treatment connecting dots on the lines which indicate the mean per minute per treatment. The same comment holds for lines 391-394, please provide statistical proof here as well.
-	Line 473-487: the discussion of the interpretation of the swimming behavior during exposure has been greatly improved. The comparison with both the scototaxis and novel tank diving test as well as shoaling behavior has been expanded which greatly facilitates the interpretation of the behavioral results (vertical distribution) obtained from groups during exposure.
-	Line 495: please consider changing “quantity spent” to “time spent”
-	Line 508: please consider rephrasing “except of decreased acitivty” to “except for decreased activity”.
-	Line 529-536: also the discussion of the ASMD has been improved and I agree with your take-home message of a sedative effect.
-	Line 540-544 is a repetition of line 493. Perhaps simply refer to this earlier piece: “Similar to the effect on citalopram on vertical distribution patterns during exposure, behavioral changes in the ASMD were more pronounced in exposed larvae than in juveniles. As previously mentioned this might be the result of the longer exposure of larvae or differences between life stages in sensitivity (Schwarz et al. 2017).”
-	Line 586-7: Please consider rephrasing “which cannot exclusively be associated with the longer exposure time, but also different sensitivities can play a role” to “which could be associated with the longer exposure time in larvae compared to juveniles, but also differences in sensitivity between life stages may play a role”


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: REVEGETATION PATTERN AFFECTING ACCUMULATION OF ORGANIC CARBON AND TOTAL NITROGEN IN RECLAIMED MINE SOILS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The novelty of the study was “to evaluate the effects of different revegetation patterns on the SOC and TN pools in reclaimed mine soils”. is very clear.
[1]	LN 97-98: The mine encompasses a total area of 52.11 km2 , and the mine elevation is between 1025 m and 1302 m.  I suggest that you make it clear about mine elevation 1025 m to 1302m, it is from MSL or ground level or base level? Also explain, is ita plan area or undulating topography and lowest point is 1025m?
[2]	LN 108-110: I suggest, you need to change/ rewrite LN 108-110 “ In the process of reclamation, at least 1 m of top subsoil (the deep loess parent materials stripped during mining) was applied on the top of the dump and appropriate leveling was conducted to create a flat surface”.  for example, you can add “ In the process of technical reclamation, (add technical), 1m top subsoil.. leveled appropriately  .. (just change little bit this sentence).
[3]	LN 146: I suggest for better clarity of the Line No 146 “ The bulk density was then used to convert SOC and TN values from g kg –1 to kg m –2” write in the formula form so that it could be easily understood.
[4]	Add site photographs of reclaimed mine sites (RMSs), including artificially revegetated sites (ARSs ;  arbors [Ar], bushes [Bu], arbor- bush mixtures [AB], and grasslands [Gr]); a natural recovery site (NRS), and undisturbed native sites (UNSs),  if available.
Experimental design: No comments
Validity of the findings: No comments
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: REVEGETATION PATTERN AFFECTING ACCUMULATION OF ORGANIC CARBON AND TOTAL NITROGEN IN RECLAIMED MINE SOILS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The Article needs a better background about the importance of SOC and TN in soils and climate change.
Experimental design: The experimental design could be better explained. Is not clear the the topographical positions were samples were taken
Validity of the findings: The results and the discussions are well done. In some parts they are mixed, but I think they could be rearranged. To improve the validity of the findings is important the authors explain better the experimental design.
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: REVEGETATION PATTERN AFFECTING ACCUMULATION OF ORGANIC CARBON AND TOTAL NITROGEN IN RECLAIMED MINE SOILS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No MS is technically sound after incorporation of all suggestions/ corrections.
Experimental design: Satisfactory.
Validity of the findings: Good
Additional comments: MS may be accepted 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: REVEGETATION PATTERN AFFECTING ACCUMULATION OF ORGANIC CARBON AND TOTAL NITROGEN IN RECLAIMED MINE SOILS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: From my part the article can be accepted


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: PATTERNS OF CHANGE IN Α AND Β TAXONOMIC AND PHYLOGENETIC DIVERSITY IN THE SECONDARY SUCCESSION OF SEMI-NATURAL GRASSLANDS IN THE NORTHERN APENNINES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Review of Lazzaro et al. “Secondary succession of semi-natural grasslands..”

Dear authors

You study different measures of alpha and beta diversity in different successional stages within two types of grasslands. You find among others, decreasing relatedness in later successional stages, in particular in the dry grasslands. Much of this trend can be explained by the presence of Juniperus.
I appreciate that a lot of field work and data analysis went into this manuscript. But I am sorry to say - I understood extremely little in this manuscript.

First, the writing is impenetrable to me. There are likely hundreds of problems throughout the ms.  Below just as an example the Abstract, it goes on like this throughout the ms. My comments in “##   ##”. I am asking a lot of questions of comprehension. I can sometimes *guess* the response, but this is not my role as a reader. Note that I only comment on the writing, not on the content. Content was above. Note also that I have not left out anything from the Abstract. In many places you seem to have missed words.
-----
“We studied the secondary succession in secondary semi-natural grasslands (dry grasslands and hay meadows) located in the Eastern side of the Tuscan Apennines (Tuscany, Central Italy). We compared these habitats, verifying: i) the patterns in species richness, composition and phylogenetic diversity during the succession; ii) whether these changes..
 ## which “changes”? This word does not appear before.##
.. determined ..
## how can a “change determine” something?##
..different trends in species loss and species turnover in both taxonomic and phylogenetic diversity..
 ##what is a “trend in species loss in a diversity”? Other than species loss.## .
…We performed a stratified random sampling, in a full factorial design along habitat type and succession stage (60 sampled plots, 10 x 2 types of habitat x 3 stages of succession). We built a phylogenetic tree of the plant communities and compared the differences in taxonomic/phylogenetic α- and β-diversity during the succession..
 ### compared to/between what?### .
…Both habitats displayed a decrease in species richness..
 ##decrease of sr with what?##
..., with a random species assembly..
##how did you study “assembly”? A diversity measure is a pattern, “assembly” is a process## ..
..in the earlier succession stages, but a shift towards phylogenetic overdispersion characterized the deeper nodes ..
## how does “shift of dispersion characterize a node”?##
..of the latter stage of dry grasslands. As to β-diversity,..
##starter only makes sense if you had before something explicitly on alpha diversity, which you didn’t.##
.. dry grasslands resulted..
##??##
..mainly dominated by richness difference..
##??##
while hay meadows displayed a higher species replacement..
 ##between what and what?##.
Accordingly, they..
 ##who, “they”?##
..showed similar..
 ## between what and what?##
features in phylogenetic β-diversity, with a greater contribution of the difference in number ..
##how can a “difference in number contribute anything?##
..of species sharing the same lineage in dry grassland..
 ##species do not share a lineage as if lineage was something acquired. Anyway, how is many species “sharing” the same lineage different from low phylogenetic diversity?”###,
..even if this trend...
## which trend?##
...is slightly lower than expected by chance...
## by chance alone you should expect a trend with advancing succession?##
due to the a very distant..
##how "distant"? Why does a distance render a trend  weaker than expected by chance?##
..species (Juniperus communis).”
---
I understand that the above exercise might appear strange to you and the editor. I just tried to illustrate in how I literally do not succeed in penetrating this text. And it goes on like this. I fear the problem is less one of English as a foreign language (which it is also for me). For most of the sentences I commented on, I do not have the impression that any foreign-language equivalent would make sense. It is more a matter of getting your ideas 100percent straight and then using words to express them. Which is hard work for all of us. Please do not take it as an arrogance: I think you need the help of someone more experienced in this kind of work. Otherwise your hard field and stats work will be lost, which is a pity.
Experimental design: Second, why do you study these patterns, what do you learn from them?
In the Introduction or Abstract there are no biological mechanisms, let alone hypotheses. There are just descriptions of patterns, without prior proper justification of what one learns from such patterns or even predictions of patterns to be expected should a particular hypothetic mechanism operate. There is only a vague statement that we know little about some types of patterns, and that many people now say that these patterns are great to study: lines 58 ff: “Nevertheless, less is known regarding the changes occurring in the communities focusing on trends in β-diversity phylogenetic relationships, also concerning their link with changes at the taxonomic level. Indeed, according to Chase & Myers (2011) beta-diversity can provide considerable insights into the importance of deterministic and stochastic processes in generating community structure along spatial and ecological gradients. In addition, the use of molecular phylogenies may be helpful in analyzing the forces that influence patterns of biodiversity and biogeography, and in depicting the interactions among co-occurring species (Selvi et al. 2016). Indeed, in the last decades, the use of molecular phylogeny is widely increased for ecological purpose.” Etc etc.
The results present many types of analyses that are not even announced in the Introduction – so I have even less ideas what possibly these results might be good for: the CCA analysis, the SDR plots.
The Discussion then does not resolve this mystery on why studying these patterns, either.  It talks a lot about results from other studies, and about the role of Juniperus. If at the end the patterns are mainly driven by the *specific* case of Juniperus then the authors should reconsider presenting a study on *general* patterns of phylogenetic diversity. I admit that this kind of criticism may be applicable to many studies  on phylogenetic patterns. The Discussion does not conclude about any mechanism, either.

Third, given the two above fundamental problems I did not go into full details of the rest of the ms. Only  some points pop up:
- you standardized PD by species richness, but apparently not NRI or NTD. At least NTD is strongly related to species richness.
- lot of methodological info is missing on how you standardized your measure
Validity of the findings: - You argue that “loss in species seems counterweighted..” to result in some PD.ses  - but if PDses is independent of spp richness, then loss of spp is not an issue anyway

- I cannot assess whether there are some other environmental variables or spatial positions that are related to "successional stage", and that might be the true drivers of the patterns you find. You do not provide environmental information other than successional stage.
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: PATTERNS OF CHANGE IN Α AND Β TAXONOMIC AND PHYLOGENETIC DIVERSITY IN THE SECONDARY SUCCESSION OF SEMI-NATURAL GRASSLANDS IN THE NORTHERN APENNINES
Review round: 1
Reviewer: 2

Output:
Basic reporting: As far as I can tell as a non-native speaker myself, the ms is well written and I didn't have any problems following the text. However, there seemed to have slipt in small grammatical errors here and there, so I would suggest having the ms proofread by a native speaker or professional service. A few examples of this:

line 34: by chance due to the a very distant species (omit "the")
line 82: these ecological difference (differences)
line 308: many more species are loss from the community (lost)

Other than that I have no additional comments, as the relevant literature is cited (though it could be extended, see comment in section 2), the ms is well structured, graphs and tables are appropriately prepared. Raw data and calculated diversity indices are provided in the form of an excel file and the phylogenetic tree of the studied species (in Newick format). I was able to open these data files, and also able to read in the Newick tree into R. The only (very minor) thing that could be mentioned here is that the names in the vegetation data are abbreviated but full names are given in the Newick tree so that it is not 100% straight forward if one would wants to reanalyze those data.
Experimental design: The study is mainly descriptional, investigating patterns of taxonomic and phylogenetic diversity (alpha and beta) along a successional gradient in two different habitats. The study therefore implicitly fills the knowledge gap of reporting and describing these pattern for the studies system, though this is not explicitly stated. In my opinion, the study could be more hypothesis-driven, or at least add some expectations in terms of the pattern of taxonomic and phylogenetic diversity patterns observed along the succession gradient. There are various hypotheses proposed regarding how taxonomic and phylogenetic diversity should change along such a gradient, and I think the authors could provide a bit more background here. The following articles and literature cited therein should provide some basic context in which the study could be set:

Letten, A. D., D. A. Keith, and M. G. Tozer. 2014. Phylogenetic and functional dissimilarity does not increase during temporal heathland succession. Proc Biol Sci 281.

Purschke, O., B. C. Schmid, M. T. Sykes, P. Poschlod, S. G. Michalski, W. Durka, I. Kühn, M. Winter, and H. C. Prentice. 2013. Contrasting changes in taxonomic, phylogenetic and functional diversity during a long-term succession: Insights into assembly processes. Journal of Ecology 101:857-866.

Verdú, M., P. J. Rey, J. M. Alcántara, G. Siles, and A. Valiente-Banuet. 2009. Phylogenetic signatures of facilitation and competition in successional communities. Journal of Ecology 97:1171-1180.

There is one aspect of the study where I am uncertain about the meaningfulness of its inclusion, and this is the part regarding the indicator species analyses. These results are nowhere mentioned in the abstract and seem somewhat tagged on to the rest of the analyses, or at least I fail to see how they are an integrative and complementary part to the other analyses, in the light of the questions put forward.

The study relies on observational data and the sampling of the vegetation is well described and appropriate for the study questions at hand.

I have to say that I do not have experience in building a phylogeny from scratch from molecular data, so I can only comment on this part that the description given in the main text as well as in the Appendix seems very detailed and well documented.

Regarding the statistical analyses, I would suggest adding some detail that is important to understand exactly how the data was treated:

- You mention mean pairwise distance as the basis for calculating NRI, but you don't specify what exactly is calculated. One could infer it from the name, but I think it would be more helpful to describe it in a simple sentence. The same goes for MNTD (mean nearest taxon distance), which is the basis of NTI. Importantly, MPD and MNTD are actually the same as NRI and NTI, but with an opposite sign. I personally think that it makes much more sense to use MPD and MNTD (or their SES) directly, as they more logically translate into over- and underdispersion. But I realize that NRI and NTI are also often used so that it is up to the authors which they prefer.

- The null model to randomize communities (for the alpha phylogenetic diversity) is merely described as "regional" null model. As this is an essential part of any null model-based study, I would prefer to read a sentence or two that describes what this null model does, instead of just referring to a published article.
Validity of the findings: The results of the study are valid within the context of the study question (but see my above point that it would be nice to contextualize the questions with some expectations/hypotheses). Especially interesting is the influence of a single species on the results and their interpretation and the authors rightfully advise to take into account such influential species and compare results with analyses excluding such species. This also provides some support for the general difficulty to infer processes from patterns.

As mentioned in the basic reporting section, the raw data are provided. Due to time constraints, I have not attempted to reproduce the results, but it would certainly be possible with the provided data (though somewhat complicated by the mentioned mismatching of species names between vegetation and phylogenetic data).
Additional comments: The authors present a well carried out study presenting a set of interesting questions. The only main objection I have is the mentioned lack of putting forward some hypotheses or expectations connected to the described diversity patterns. I think this could even add more relevance and importance to your finding that inclusion/exclusion of particular species or clades can make a big difference for phylogenetic diversity patterns, and that linking processes to patterns is often difficult and not straight forward, as also anticipated in the recent literature (e.g. Gerhold et al. 2015).

I hope that the authors find my comments helpful and worth considering.

Lars Götzenberger

References:
Gerhold, P., J. F. Cahill, M. Winter, I. V. Bartish, and A. Prinzing. 2015. Phylogenetic patterns are not proxies of community assembly mechanisms (they are far better). Functional Ecology 29:600-614.


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: PATTERNS OF CHANGE IN Α AND Β TAXONOMIC AND PHYLOGENETIC DIVERSITY IN THE SECONDARY SUCCESSION OF SEMI-NATURAL GRASSLANDS IN THE NORTHERN APENNINES
Review round: 2
Reviewer: 1

Output:
Basic reporting: Figure 5: Allocation of panel letters seems to be mixed up in the figure caption, i.e. a and b are showing non-standardized diversities, not a and c. The same for the standardized indices.
Experimental design: You attempted to improve the description of the null model used to calculate standardized effect sizes for the phylogenetic diversity measures. Unfortunately, your description raises more questions than it answers. Firstly, it appears a bit vague that all the mentioned community properties are held ‘approximately’ constant, without saying what that means exactly. Secondly, and more importantly, it appears that this null model is based on number of individuals. However, you described a sampling scheme that records presence/absence of species. It is not clear how that is supposed to fit together. If this null model is applicable to presence/absence data than you have to describe how so. If it is not, you used a null model that shouldn’t be used, which obviously would translate into using a more appropriate null model.

Additional minor comment regarding methods and results:

Line 224f “It describes the relationship within species focusing,…”
This is somewhat misleading, as the index describes phylogenetic relatedness, not a relationship, and it does so among species, not within.
Validity of the findings: I have no additional comments compared to my initial review for the first submission.
Additional comments: I thank the authors for their efforts to revise the submitted manuscript and take into account my suggestions and comments. While I find the overall ms improved compared to the previous version, I am still concerned about some details, especially regarding some methodological details. I detailed these concerns in the "experimental design" section of this review.


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: PATTERNS OF CHANGE IN Α AND Β TAXONOMIC AND PHYLOGENETIC DIVERSITY IN THE SECONDARY SUCCESSION OF SEMI-NATURAL GRASSLANDS IN THE NORTHERN APENNINES
Review round: 3
Reviewer: 1

Output:
Basic reporting: There are a few minor things that crept into the revised parts of the text that need some final editing:

L318: "dramatic" I would refrain from using such a word in a scientific text. The same goes for "compared to what happened" in the next line (319).

L 320: vary -> varies

L321: "all patterns toward a phylogenetic overdispersion in dry grasslands clearly vanished" also sounds convoluted. I think you could simply replace it by "phylogenetic overdispersion in dry grasslands clearly vanished".

432ff: There is something wrong with the part of the sentence. "... during the succession the replacement of lineages in the communities brought to a certain degree of phylogenetic similarity between managed hay meadows and both managed and transition dry grassland" Please rephrase.
Experimental design: I thank the authors for clarifying the issues around the use of null models. I am satisfied now with the application and description of the new null model used.
Validity of the findings: No additional comments to previous reviews.
Additional comments: I appreciate the efforts of the authors in revising their ms. At this point, I have no further comments or questions that I feel need to be addressed. I still suggest a final minor revision to smooth out some linguistic bumps (see my comments in Basic Reporting section).


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: TROPHIC NICHES OF A SEABIRD ASSEMBLAGE IN BASS STRAIT, SOUTH-EASTERN AUSTRALIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Literature use needs to be improved - see comments below. Many key refs missing, too many old citations, need to include studies from beyond Phillip Island.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Referee’s comments – Fromant et al seabirds Bass St

Line 38. Surely more recent and more relevant refs than Ridoux 1994?
Lines 37 -41 – would like to see more references than 1 per aspect, and more recent refs where possible.
Line 51. Worth noting that 14.6 of 15M seabirds are shearwaters – diversity is actually low given predominance of one species.
Table 1 – prob worth including the dates of the population estimates – some of the Brothers et al surveys date back to the 1970s, 1980s and 1990s – well out of date.
Lines 60 – 64. The SASW is primarily present in the winter months when the STC moves north into Bass St or even farther north.
Line 84. Surely cite the recent surveys of Schuman rather than the national synthesis of Ross 2001?
Lines 86 – 90 – the foraging range of short-tailed shearwaters extends to the Antarctic in the summer breeding season – clearly worth citing these studies.
Line 94 – if there is no information, then no references are needed, but if there are some studies to generate “almost no” information – please cite. Text should be at line 106, not 113 – 124.
Line 106 – how were stomach samples obtained? Method and references pls. Collected at sea?
Line 140 – presumably squid beaks?
Line 214 – what is “coastal krill”? Nyctiphanes? Please provide latin names where possible in the text [I don’t have the supp material]
Line 239. Can the low variance explained by the foraging areas of the shearwaters?
Line 292 – shearwaters feed on superba – Antarctic Krill, not “subantarctic” krill.
Lines 303/304. Presumably we are talking about breeding birds foraging over Bass St/shelf. Prions and diving petrels will travel well into the Southern Ocean during non-breeding season.
Line 313 – ‘farther’ south!
Lines 320-323 – could the differences be related to shearwaters flying west from WBS colonies and east from EBS colonies? Local/fine-scale variation close to colonies?
Lines 326 – 329 – probably worth thinking about some of Ainley’s work re colony size/foraging ranges/overlaps here. Dare we suggest Ashmole’s Halo?
Line 338 – what evidence is there that the SAC water contains prey and nutrients? Any independent data to support this claim?
Line 347 – does the SAC provide the greatest volume of water into the study area in winter? What about the northward movement of the STC?
Line 387 – ‘coastal krill’ – Nyctiphanes? If so, worth looking at the role of Nyctiphanes in New Zealand (Mills et al 2008) and in SE Tasmania (Woehler et al 2014) re gulls and other seabirds.
Lines 409+ - some discussion re potential impacts of climate change on Australian seabirds has been reviewed by Chambers et al and should be included/cited in Discussion here.
Line 417 – Did Vertigan report on Bass St shearwaters?


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: TROPHIC NICHES OF A SEABIRD ASSEMBLAGE IN BASS STRAIT, SOUTH-EASTERN AUSTRALIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: This study compares isotopic values of blood from three abundant seabird species over two seasons (summer & winter) at several locations across Bass Strait to identify niche overlap between these species. It is very well written, and tables and figures are clear, although in the case of the figures I recommend the use of line styles/symbols that make it possible to distinguish between lines when copied in B&W. My comments are minor.
Methods
Lines 137 – 140. How were eroded otoliths dealt with? What proportion were still identifiable to species?
Explain why discrimination factors weren’t used for isotopic analyses.
Statistical analyses: were the same individuals sampled twice across seasons? If so, individual would have to be entered as a random factor into models.
Line 211. Re-organise this sentence so that the crustacean remains are not consuming the jack mackerel.
Lines 225 and on: Report results in past tense.
Lines 237-238: These differences are not very obvious as they are rather small.
Line 239: substitute “but” for ‘and’. I found this paragraph hard to follow.
Lines 241-242. I would prefer to see Table S4 in the main body of text, but reduced, showing only models within delta AIC values of 2. This I believe is the commonly adopted method for presenting these models.
Line 251: I found this figure really helpful and suggest it should be in the main body of text rather than in supplementary material.
Line 254: add ‘in’ before ‘all’.
Discussion
Lines 282-283: The point of the Cavallo et al. paper is that gelatinous prey is virtually undetectable without doing DNA analyses.
Line 305: At the end of this section I suggest making a statement on how conventional stomach analysis suggests substantial dietary overlap among the procellariforms, and that the isotopic analysis is able to tease apart into separate foraging niches, to emphasise the value of this dual approach.
Line 358. Specify what “this’ is.
Line 373: Please clarify how variation in the consumption of coast krill would result in substantial inter-annual variation in N15 values.
Line 381: Substitute “than” for “to”.
Line 391: Does this difference in foraging strategy explain the difference in C13 values between FP CDP? If not, what might?


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: TROPHIC NICHES OF A SEABIRD ASSEMBLAGE IN BASS STRAIT, SOUTH-EASTERN AUSTRALIA
Review round: 1
Reviewer: 3

Output:
Basic reporting: Background/Context:
To better understand your results, the reader needs much more background on the breeding cycle of the species studied and on which part of the breeding cycle your data refer to. Because seabirds are central place foragers, this information is extremely important. It could be helpful to create a figure that shows the annual cycle of each species with the period your sampling covers highlighted somehow.

Figures and Tables:
As is, tables 3 and 4 are a lot to take in. Maybe you could simplify them to make it easier for the reader to digest the key information? For example, the values for the mean and range of each isotope are better displayed as a figure (i.e., as in Figure 4). For the Figure 4 legend, please clarify whether these are data aggregated across summer and winter.
Experimental design: Animal Use Permit:
It is unclear to me whether an animal use permit was obtained for the study. Maybe this was the permit from Deakin University? Please clarify which permit process thoroughly reviewed your animal use procedure, as the methods used are fairly high impact (especially the stomach flushing).

GLMs:
It would be interesting to know whether season was a significant predictor of isotope value. Could you test models including season as a term, rather than separating out the two seasons a priori and running separate models?
Validity of the findings: Caveats
Although you do not need to go into too much detail, please provide readers unfamiliar with stable isotopes with some of the caveats of this approach. For example, your results could have been influenced by difference in TEFs among species. Furthermore, the isotope data represent diet aggregated over time, while the stomach flushing data represent a snapshot of diet.
Additional comments: Your manuscript is well written and provides useful information on the trophic niche of the four species studied. The raw data are provided in appropriate detail in the supplementary files (though they could be organized a bit better for ease of examination by reviewers/readers) and the statistical approach is appropriate. There are, however, several places where more details are necessary for the reader to interpret your findings. Furthermore, several changes could be made to improve readability.

-Lines 52-53 and elsewhere in the document, the word "which" is used where the word "that" should be used.
-Line 90 – If these references are species specific, please move them up in the sentence to follow the relevant species.
-Line 101 – Were data collected throughout this time range in each season? As noted above, please provide more context for the portion of the breeding cycle that these isotope values represent.
-Line 126 – Why weren't meals provided to the other species studied?
-Line 172 – Please provide reference for why C:N values of 3.1-3.7 do not require lipid extraction.
-Lines 210-213 – This sentence should be reworded to improve readability.
-Lines 226-231 – Do these range values include both summer and winter data? In general, summer and winter data are combined in some portions of the paper and not others (e.g., for the GLMs) and it is unclear when/why the decision to combine or not combine data was made.
-Lines 251-261 – Please provide a supplemental table showing niche overlap among all pairs of categories (each species in each season x each species in each season). You should also define niche overlap for those not familiar with SIBER – I am assuming you used: area of overlap/combined area of niches.
-Lines 251-261 – Why use fairy penguin as the species to which all other species are compared in table 3? Based on previous studies, isn't it expected that overlap between fairy penguins and the other species studied will be low (e.g., as outlined in Lines 84-90)? It might be more interesting to compare the species that feed primarily on krill to each other.
-Lines 264-265 – Please reword this sentence.
-Lines 282-284 – Is there anything from the SIA results that could be used to indicate the consumption of jellyfish?
-Line 307 – This transition feels odd because it is a continuation of the previous section where the diet of short-tailed shearwaters is discussed. Maybe the discussion could be rearranged slightly to improve flow.
-Line 371 – Please start a new paragraph and clarify what is meant by "similarly" in this sentence. What are these species consuming in years when krill abundance is low?
-Lines 380-383 – This sentence should be reworded to improve readability.
-Lines 385 – Clarify here that the data for white-faced storm petrels are from previous studies (and I am assuming, a different year? Possibly a different region?) i.e., "lower than values previously reported for white-faced storm petrels foraging in this region".
-Lines 386-388 – It's not clear that the preceding sentence indicates that krill are an important diet item for the procellariforms you studied. You could use your stomach content data to back this point up.
-Lines 386-388 – Are there any data availability for the isotope values of prey items I this region? And how variable these signatures are?
-Lines 409-421 – The transition to this paragraph feels somewhat abrupt. Maybe it should be separated out into its own section or better integrated into the rest of the discussion?


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: TROPHIC NICHES OF A SEABIRD ASSEMBLAGE IN BASS STRAIT, SOUTH-EASTERN AUSTRALIA
Review round: 2
Reviewer: 1

Output:
Basic reporting: See comments to author
Experimental design: See comments to author
Validity of the findings: See comments to author
Additional comments: Fromant and colleagues' revisions improved the manuscript, particularly in terms of providing important methodological details that were previously missing. However, there are still a several details missing from the results section and the discussion remains difficult to follow (see below).

Lines 16-17: This sentence could be restructured to improve readability. I am also unsure whether "foraging niche" is the appropriate term for this study, which focused on the isotopic niche or dietary niche. Foraging niche is often studied using data on foraging locations (e.g., tags). Isotopes provide only general insight into foraging location.
Line 22: Since you didn't sample all species in all sites/seasons years, maybe instead say "that varied among years, seasons, and regions"
Line 94: inter-annual, seasonal, and geographic variation
Line 166: Please clarify "(not sampled for diet determination)"- does this just mean that none of the individuals were sampled for both gut contents and isotopes?
Line 212: Were the stomachs without identifiable remains empty, or were the items just too digested to identify? (especially for the common diving petrels)
Line 238 and elsewhere: I know a lot of tests were run, and commend the authors for providing the raw data, but more details are needed on the results from the post-hoc tests. There is now wide agreement in the literature that p values should not be included in papers without additional information necessary for the reader to reach their own conclusions regarding the results. For example, see recent papers by Smith "Ending Reliance on Statistical Significance Will Improve Environmental Inference and Communication" Estuaries and Coasts https://doi.org/10.1007/s12237-019-00679-y. Furthermore, please provide the actual p-value when you can round it to only two decimal places (e.g. 0.71 instead of >0.70).

Line 245: It is unclear to me why δ13C was included in the model. Is the idea that δ13C might indicate different foraging locations, which would in turn influence the trophic level the individual was feeding at? Some relationship between δ13C and δ15N is often expected due to slight trophic fractionation of δ13C, but I don't see why that would be a meaningful thing to test for in the current study.

Line 249: What is the 0.2%? Variance explained by season for little penguin?

Discussion: I am still having trouble with the structure of the discussion. As noted by the authors, part of this has to do with the complicated nature of the data, especially given that different combinations of samples (isotopes, gut content) and sampling occasions (region, year, season) were collected for each species. I am not sure of the best way to simplify this to make it easier for the reader to follow. One issue is that some sections focus in detail on one species then only cover the other three species very briefly (e.g., inter-annual trophic variability section focuses almost exclusively on little penguins, with just 1-2 sentences on the other species). Maybe restructure the discussion with the three goals outlined in the introduction as the subheadings?

Lines 442-444: This seems like the major finding of the study and could possibly be used to think about restructuring some of the discussion.


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: CODON OPTIMIZATION, EXPRESSION IN ESCHERICHIA COLI, AND IMMUNOGENICITY ANALYSIS OF DEFORMED WING VIRUS (DWV) STRUCTURAL PROTEIN
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript reports expressing of three major structural proteins of Deformed wing virus (DWV) in E. coli. The codons in these protein-coding nucleotide sequences were optimised to maximise expression in E. coli. The expressed recombinants VP1, VP2 and VP3 proteins ( as well as wild-type DWV particles, and PBS control) were used to immunise mice to raise antisera. The authors demonstrated that antisera reacted with the corresponding proteins in ELISA tests. Then, the authors used investigated if incubation of DWV inoculation with antisera the recombinant DWV proteins, wild-type virus particles, of control antisera  could reduce infectivity of DWV in honeybee pupae injection tests. The levels DWV RNA and actin mRNA were quantified in the injected pupae by qRT-PCR. The pupae injected with DWV which were pre-incubated with antisera raised to DWV particles or any of the recombinant DWV VPs showed slightly reduced levels ( between 1 to 3 Ct values) compared to the control DWV injection ( virus only or non-specific antisera with virus).  Notably, after 3 days post injection bees of  all  treatment groups had high levels of DWV (i.e. higher copy number of DWV genomic RNA compared to actin mRNA), including those injected with DWV particles incubated with specific antisera (Supplementary S5 Table, Fig, 6).

MS shouldpProvide more details on how antibodies developed to DWV could be applied as therapeutics agains DWV ( lines 44-45, 459-462).

The manuscript requires extensive scientific English editing. There are many spelling mistakes (e.g. line 30: "Methods" -> "Methods", line 67: "DWV is a positive, single- and plus-strand RNA virus" -> DWV is a positive-strand RNA virus").
Experimental design: Experiment summarised in Fig. 6 does not include essential virus-free control, PBS injected pupae (without virus and without any antisera). Also, it would be preferably to include injection with all five antisera (Fig. 6) without DWV.

it is important to note that, after 3 days post injection all pupae had high levels of DWV (i.e. higher copy number of DWV genomic RNA compared to actin mRNA), including those injected with DWV particles incubated with specific antisera (Supplementary S5 Table, Fig, 6). Such high levels of DWV are normally found in there bee pupae with overt DWV infection, i.e. virus-injected bees or bees exposed to Varroa mites (see for example papers where delta Ct[DWV]-Ct[actin] metrics was used  - see for example https://peerj.com/articles/1591/ (Fig. 4).  The reported difference between level DWV in uninfected (or covertly infected) pupae  and DWV infected pupae is usually about 10 - 15 Ct units ( https://peerj.com/articles/1591/ (Fig. 4); or https://doi.org/10.1371/journal.ppat.1004230 -  (Supporting Figure S1)).   Therefore all treatment groups in Fig. 6 could be classified as "overtly" infected. Slight (between 1 and 3 Ct values,  Supplement Table S5), though statistically significant, differences in DWV loads between the groups in Fig. 6 at 3 days post injection could be a result of different proportions of virus inoculate being inactivated by specific antibodies. Such reduction in the infectious DWV units number in the inocula is likely to result in change of virus replication dynamics, specifically increasing time when DWV infection reaches highest levels.  I would suggest, therefore,  to extend experiment for additional 24 for and include 96 hr time point.

Other notes.

MS does not contain protocol for purification of DWV virus particles used for immunisation (the virus particles used to raise antiserum mentioned in lines 246-247), provide method or reference.

Figure 6 legend have to include description of all treatment groups. It is not clear what "NC" means. Also note the antisera, rather than purified IgG were used. Include explanation (Materials) how "Relative normalised DWV titer" values was calculated  - I understand that these were calculated as 2 in a power of Ct[DWV]-Ct[actin] (Suipplementary Table S5). The authors assumed that there is s a 2-fold difference of DWV concentration corresponding to each Ct unit, which might not be a case. it is possible just to use delta Ct values ( Ct[DWV]-Ct[actin]).

Figure 2.
roVP1 - explain why "anti-His6" and "anti DWV" antibodies stained  proteins protein with different molecular weight

line 70 , Reference Lamp in not correct, use Mordecai et al 2016, - those paper proposed DWV-A-B-C.
Validity of the findings: see above
Additional comments: see 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: CODON OPTIMIZATION, EXPRESSION IN ESCHERICHIA COLI, AND IMMUNOGENICITY ANALYSIS OF DEFORMED WING VIRUS (DWV) STRUCTURAL PROTEIN
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper submitted describes an interesting basic research on the capsid proteins from DWV. Most papers on this virus are very recent, with a high impact on honey bee population. The manuscript is presented in an almost clear form, with nearly good grammar. Some sentences need to be rewritten, specially in the abstract and methodology sections.

Minor concerns:
- line 30: check "MTHODS" for missing vowel E.
- line 32-34: This sentence is not clear, please check grammar.
- line 85: speculatde
- line 108: sentence in red (font color).
- line 163: needless to say "For large scale purification", as it seems that the later expression experiment was a only a preliminary experiment.
- line 251: was injected with...
- line  247-254: experiment design is not clear: 30 pupae, 7 groups, 5 pupae/group. Were there 6 or 7 groups? What was the group 7 for?
- line 303: I suggest to replace "influence of IPTG" to "induction of IPTG".
- line 303: injected.
Experimental design: In this section, the manuscript needs more attention. I have questions on the methodology that the authors followed that are not covered in the experimental design section.

Q: Which tools were used for codon optimization?

Q: Does the authors analyze the amino acid sequence for potential glycosilation sites or other postraductional processing that may alter the recognition of viral particles?

Q: Has the production of polyclonal anti-DWV on line 185 been published before? These antibodies were produced with virus particles (like the positive controls of mice immunizations) but not the roDWV proteins.

Q: Since the virus produces a single polyprotein that should be cleaved, how do the authors known the correct amino acid sequence of each VP1, VP2 and VP3 protein?
Validity of the findings: Many vendors offer the analysis of codon optimization for gblock or gen synthesis, even for E. coli or other cell systems. So, why is this step important in the context of this research?

As a proof of concept on codon optimization for VPs production, there is no evidence showed that indicates that this strategy improved obtaining the three recombinant proteins. The paper from Lamp et al. described the recombinant production of VP1 but in low levels (DOI:10.1371/journal.pone.0164639).
Additional comments: As described in literature, the virion of DWV assemble as an immature procapsid of its VP1,VP2 and VP3, that further fills up with the viral genome. It would have been interesting to see if the humoral response or protection against DWV had improved upon a synergistic injection of roVP1, roVP2 and/or roVP3.

The production of recombinant proteins from virus or animal sources in E. coli can be a problem that the authors solved. However, the methodology and results sections described more the immunogenic potential than the recombinant expression.


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: CODON OPTIMIZATION, EXPRESSION IN ESCHERICHIA COLI, AND IMMUNOGENICITY ANALYSIS OF DEFORMED WING VIRUS (DWV) STRUCTURAL PROTEIN
Review round: 1
Reviewer: 3

Output:
Basic reporting: 1. The text needs English editing. The English in the present manuscript is not of publication quality and require a significant improvement. I am attaching the reviewed manuscript (in PDF) with some suggestions for modifications. However, authors should understand that the function of the reviewers is to evaluate the quality and accuracy of the research presented, and provide some feedback to improve the clarity, transparency, accuracy, and utility of potential papers, not to serve as an English spelling and grammar corrector.

2. From my perspective the literature references provide a good background and support the evidences of this study.

3. The paper is well structured, figures, and tables are fine. One reccomentadtion is to write a more attractive and clear justification of the study
Experimental design: 4. Due to the lethal effects caused by the DWV, the study might be relevant and meaningful.

5. From my perspective the methodology described is  appropriate and accurate., Furthermore, the methods are described in detail so that others could follow the same protocol.
Validity of the findings: 6. To the best of my knowledge the literature on therapeutic strategies against the DWV is still limited. Thus, this study tested the ability of immune responses against specific targets in the virus, and may yield insights into the use of novel therapies against DWV.

7. However, the discussion section, which is the most relevant part of any study, is extremely shallow and poorly discused. In this way, authors are invited to expand the discussion. Perhaps a brief discussion on the physical blockage of the antibodies to some structures of the virus would benefit the manuscript. Authors should take some advantage of the openess of the journal to speculation, but it should be clearly stated as such.
Additional comments: From my perspective, the manuscript has the potential to contribute to solve the serious problem provoked by DWV to the populations of honey bees world wide. However,several parts of the manuscript should be rewriten so that readers are able to understand the arguments of this 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: CODON OPTIMIZATION, EXPRESSION IN ESCHERICHIA COLI, AND IMMUNOGENICITY ANALYSIS OF DEFORMED WING VIRUS (DWV) STRUCTURAL PROTEIN
Review round: 2
Reviewer: 1

Output:
Basic reporting: Revised version of MS is improved, in particular English language. Although authors did not explain how anti-DWV antisera could be directly used used as "therapeutic" agent against DWV in industrial / commercial apiculture, these antibodies will definitely be extremely valuable in DWV research. Revised version also included new interesting discussion on the potential mechanism of action of anti-DWV capsid antibodies in blocking virus entry (lines 638-652).

There are questions to the results and interpretation of "neutralisation test" experiment (lines 5127-538, Figure 6).  It is clear from Supplementary Table 5 that DWV infection did develop in the pupae co-injected with the virus and with the antibodies, while in the control group of bees injected with "5 antisera mix without virus" (lines 354-365) there were no development of DWV infection at all (undetectable DWV, line 526, Supplementary Table 5). The level of DWV in the pupae of "5 antisera only" group therefore was significantly lower than in the pupae of any other treatment groups and this must be clearly stated in Fig. 6  and in Results. It should be noted that co-injection with anti-DWV antisera therefore did not prevent development of infection, but only reduced DWV levels. Maximum reduction observed when "Virus+anti-DWV-antisera" group was compared with Virus-only" group was no more than 8-fold (3 delta-Ct units, 2^3=8,  assuming that one delta-Ct unit correspond to 2-fold difference of DWV RNA copy numbers). Neutralising effects in the case of antisera raised to the recombinant CPs were even lower. There were approximately 2-fold,  2.5-fold , and 4-fold reductions for anti-roVP1, anti-roVP2, and anti-roVP3 antisera, correspondingly. Although all these modest differences were statistically significant. It should be noted that in the case of the "5 antisera only group", the delta-Ct value should be at least 25 units if qPCR test had 40 cycles considering Ct(actin)=15. Therefore I suggest to specify the degree of neutralisation using antibodies raised to the recombinant proteins, approximately 2-fold to 4-fold (line 53).

Other notes :

Lines 523-526
"At the same time, the Ct value of the group with five antisera is not display using qRT-PCR, which shows that the virus was not detected in the mice antisera immunized with DWV. "
should it be replaced with:
"At the same time DWV was undetectable by qRT-PCR in the group injected with five anti-DWV antisera"...

Fig. 6. Specify in the figure legend how delta-Ct values were calculated. It is clear from the Supplementary Table 5 that these DeltaCt = Ct[DWV] -  Ct[actin], but this must be specified in the main text.

line 364
Specify which five antisera were mixed ( line 364), only four antisera were listed in Fig. 6 legend.
Experimental design: see comments above
Validity of the findings: see comments above
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: RELIABILITY OF THE VELOCITY ACHIEVED DURING THE LAST REPETITION OF SETS TO FAILURE AND ITS ASSOCIATION WITH THE VELOCITY OF THE 1-REPETITION MAXIMUM
Review round: 1
Reviewer: 1

Output:
Basic reporting: Meets all Basic Reporting standards, however analysis would benefit from the inclusion of citing Ormsbee et al 2019 https://www.ncbi.nlm.nih.gov/pubmed/28301439. See 3, validity of findings below.
Experimental design: Meets all Experimental Design standards
Validity of the findings: Meets standards, only one instance in which the speculation by the authors may conflict with previous findings. Specifically, on line 278-288 please see the recent in press article by Ormsbee in which they found a significantly lower velocity at 1RM among experienced bench pressers vs inexperienced (with a lower 1RM) on free weight bench press. For this reason, I think it would be a more conservative conclusion to state on line 288 (see upper case added text) that “it is not necessary to modify the minimal
velocity threshold based on the 1RM strength values FOR THE SMITH MACHINE BENCH PRESS”. Given Ormsbee and colleagues did report a different velocity between participants of different strength, this statement with my suggested modification may be more likely to be true, as perhaps the complexity of free vs smith machine bench press could make a difference https://www.ncbi.nlm.nih.gov/pubmed/28301439.
Additional comments: This is a well written, useful addition to the literature that expands what we know about smith machine bench press, variants of the bench press, and potentially improves the prescription of VBT.

I only have a few minor comments in addition to my notes in the specific sections above:

In the introduction, please indicate when discussing prior studies on the bench press when/if they used the Smith Machine in each case “bench press” is stated.

Line 260-261 this sentence reads as incomplete to me, and for clarity would benefit from revision.

Line 273 also please include that we (Helms 2017) used a “press” command to simulate powerlifting competition, so there was a brief pause on the chest which may produce a different velocity than a con-ecc free weight bench press without a brief pause.