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: NO MOW MAY LAWNS HAVE HIGHER POLLINATOR RICHNESS AND ABUNDANCES: AN ENGAGED COMMUNITY PROVIDES FLORAL RESOURCES FOR POLLINATORS
Review round: 1
Reviewer: 2

Output:
Basic reporting: •	The manuscript is written in clear English and is relevant to its hypotheses.  Raw data is shared. Figures & tables are provided although edits are suggested.

Other comments:
•	Figures and tables should be numbered consecutively based on first discussion in the text (e.g. Table 3 is mentioned before Table 1 and 2; Figure 2 is mentioned before Figure 1).  Also, consistency in the capitalization of the first word of the table/figure title is needed, and all abbreviations should be spelled out (e.g. AIC), and in-text references to tables/figures should also be capitalized consistently
•	Table 3 isn’t needed – place the AIC values and predictors in the text; you are not presenting multiple variables as you suggest in the text
•	Make sure your table and figure legends are fully descriptive.  E.g. Figure 1 – should indicate black dots are participating homes and colours represent both areas that were surveyed and the resulting diversity levels in a heatmap.  Sample size of houses could be shown. Bee abundances could be presented as well – why aren’t they?  A different symbol for urban lawns vs greenspaces would be helpful as well.
•	And for Figure 2, is there a standard error or 95% confidence interval?  Are there significant differences? This can be shown on the graph
•	I’m not sure why you have the “NoMowMay Summary of Results” website page included here; it’s not clear if it’s a copy of your program results website, or trying to show the stats results of your analyses, or what.
Experimental design: •	The paper is based on primary research with relevant questions, and is situated in the literature (although very few papers in the literature are referenced).  Ethics was obtained for the relevant research. But a lot of the methods and the overall experimental design is missing or unclear.  I am also concerned about the comparison of non-mowed lawns to mowed greenspaces in parks, particularly without accounting for surrounding habitat.
•	Additional comments:
•	I suggest including a definition of citizen science, and more clearly explaining how the citizen scientists were involved.  I would not consider No Mow May itself to be a citizen science initiative if people are just taking an action but not collecting and submitting data (i.e. not participating in ‘science’).   Volunteers helping to collect data would be citizen scientists but not “regular” home owners.  Ditto for survey respondents.  You don’t actually try to describe this until line 265. There are a number of papers on this in the literature.
•	Line 109: how were the homes and greenspaces selected?  Also, why did you choose to compare mowed greenspaces vs lawns? Why not lawns that participated vs did not participate?  Having previously surveyed greenspaces is not a relevant reason in my opinion as you do not have previous information for the residential properties for comparison purposes.  I’m sure you could get permission from non-participating homes if you asked.  you could ask property owners for permission (these could be lawns side by side or on the same street/same community)?  It’s not a true comparison if you’re comparing urban lawns to actively managed (mowed & treated with pesticides) parks.  Also, I see from the map in Figure 1 that some greenspace/park sites were quite close to each other, while there are parks surrounded by participating homes quite a distance away that were not selected.
•	How many homes were within the same 1km of the park/each other?  Within 100m of each other? (Line 136 mentions the latter; it should be moved up to the site selection section)  Within 100m of the park?   I plotted the first three sites in your data and one was across the road from the park (so less than say 20m), another one maybe 70m away, another 150m or so; that suggests that all could be in the same foraging range of bees, and you’re double counting.  Alternatively, if you want to say you’re sampling the same population of bees at all sites, so that the population/source of the bees is the same, state that.
•	Line 111: who were the citizen scientists? What was their background? What training was provided? Were the authors/researchers out with them? Did all 8 help survey at all sites?  Did experts verify their findings?
•	Line 112: how were the plants identified? Personal knowledge, a specific identification key?
•	Line 113: were they truly randomly selected points?  E.g. you put a grid overtop the whole area and used a random number generator to select grids to sample?
•	Did you account for other vegetation in the area? There could be a big difference in visitation to lawns that are surrounded by flowering plants in formal gardens/naturalized sections of the property vs those that have only lawn.
•	Line 120: how did you come up with 150m2 for the size of park space to sample?
•	Line 120: The justification of 100m apart for grids should be referenced, and even then there is ample evidence that bees (even small solitary ones) will forage for more than 100m away from nest sites, so you could still recapture bees in nearby plots. 500m would have been a better option.
•	Line 126: so did you survey the entire “no mow” lawn area of each property?  Did you survey the entire mowed greenspace area of the parks?
•	Line 127: why only one survey period per property? What was the time period for surveys? Some species are only active at certain times of the day.  How many people surveyed at one time?  Did you only survey/collect bees that were actively visiting flowers on the lawn area vs flying by or visiting flowers that were in other locations (e.g. flower beds, planters)?
•	Line 142/survey: some of your questions are leading and do not take into account historic practices.  E.g. perhaps a home owner previously only mowed 2x/month – they do not have this option, or even the option to select ‘mow less frequently’.  They also didn’t have the option to select ‘no change’ – not everyone may have enjoyed the results or perhaps they will not have to change their practices.  Similarly, for changes post-May, they may be already doing some of these actions, which can not be captured by the survey; either they check that they ‘will’ do something based on their participation (which wouldn’t actually be based on their participation) or they do not check anything and that information is lost.  Also, did you try to clarify “yard” vs “lawn”?  I.e. differentiating between flowers growing in e.g. flower beds vs in the lawn?
•	Survey vs summary of results (external files): so were there over 500 households participating or 435? Or were over 500 homes including those deemed by the researchers to be participating but not registered (and how did they determine they were participating in the initiative vs just not mowing for whatever reason).
•	Line 152: was abundance based on all species combined?
•	Is the effect due to the urban garden resources vs greenspace resources?
•	Was there a control in the survey to account for those who already managed habitat for pollinators, etc?  Did properties with more gardens have more pollinators regardless as to how much lawn was not mowed?  Were properties with more gardens already established more likely to participate in No Mow May than those with no/fewer gardens?
•	Discuss what plants were flowering in the lawns – native vs non-native? Preference for some species of plants over others? Do you consider not cutting the grass to be the same as naturalizing?
Validity of the findings: •	The analyses were appropriate, but the underlying comparison of lawns to greenspaces is not necessarily appropriate or relevant.  Some analyses that could have been conducted were not or results were not clearly presented.  This may be best treated as a pilot study.
•	Additional comments:
•	Line 195/Summary of results (external document):  Do you have any “proof” (even personal communications with residents) that all of this “protected” “pollinator habitat” was only due to No Mow May (vs would have existed anyway)(i.e. do some residents normally not mow in May, or is based on surrounding vegetation)?
•	Line 195/Summary of results (external document): were you including the mowed greenspaces in your total amount of habitat being protected by the initiative (because they did not change management practices)?
•	Line 165: please indicate here if the list of species and abundances are being provided in a table
•	Line 175: you refer to “common and abundant” – what is commonness based on? Abundance based on?
•	Table 1: provide percent coverage for each species if you have that data, or percent of plots, or some measure of abundance and cover/forage; it is possible for one species to fill 100% of a plot or only 5% of a plot; ,
•	Table 1: why not include all plant species here?  If the list is too extensive, why not include in a supplementary table?
•	Table 1, 2: provide the scientific authorities for each species
•	Table 2: provide relative (percent) abundance for each species for easy comparison in addition to counts, and if they were present in one or both of lawns & greenspaces
•	Line 182: provide model results here, including model statistic, df, p-value (this is not presented in paper currently)
•	Line 199: provide actual results of the survey in a table (in-text or supplementary)
•	Line 265: it’s not a city wide experiment if you aren’t actually testing across the city; you focused intently in just a couple areas
•	Provide discussion about what plant species provide the most forage
•	Discuss if impacts on pollinators would be consistent or change over the course of the month.
•	Discuss the impacts of lawns being mowed after May ends (i.e. did home owners create a sink by attracting and supporting pollinators and then removing that food?)
•	Discuss the value of lawns and other areas being mowed occasionally to create a new flush of growth vs never being mowed.
Additional comments: •	Line 50: I disagree that we need to protect non-native species, particularly in urban areas that may be a refuge for native ones. Please supply references to support your claim that these species need to be protected.  You later (e.g. line 63) focus on native bees.  Native bees can provide ecosystem services, and in many cases can be better than honeybees.   Honeybees are a managed agricultural farm animal like cattle, chicken, etc. and it is important that researchers and the public understand the distinction between native and commercially produced species.
•	Line 66: remove the word “the” in “the late April”
•	Line 74,77: add a reference for the initiatives (even a URL if no reports, etc. available)
•	Line 104: add a comma after the organization name
•	Line 174: repeated “mowed areas” three times; remove repeated words and replace with correct term
•	Line 174: add in “plant” or “flower” species here if that’s what you mean (vs bee species)
•	Line 247: remove the comma after Appleton
•	Line 250: who provided the educational opportunities?  What type of reach did you get?  Relatedly, Line 269: how did you improve the general public’s understanding  of “key ecological and conservation issues” and “understanding of urban ecosystems” – did you discuss all of these items on your Facebook page?  Did you do any media outreach?  Was the messaging just about pollinators or were there others?
•	Line 270: were all >400 households invited to help collect data?  Were only 8 people from across the city interested?
•	Line 281: why are lawns easily accessible? By whom? Does that mean forests/meadows/wetlands are not accessible?
•	Line 320: who are the 3 citizen scientists not mentioned here?  At least say ‘and 3 anonymous individuals’ to acknowledge them if they don’t want their names listed.
•	Line 326: remove the word “a” before registered


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: NO MOW MAY LAWNS HAVE HIGHER POLLINATOR RICHNESS AND ABUNDANCES: AN ENGAGED COMMUNITY PROVIDES FLORAL RESOURCES FOR POLLINATORS
Review round: 1
Reviewer: 3

Output:
Basic reporting: Overall, the manuscript is well written, well referenced and thoughtfully structured.  The motivation, objectives and methods are generally clear, with plenty of context to place.  There are a few areas that could be re-written to improve readability and comprehension; or made more concise - I have identified these in the pdf annotation.

1.  The objectives included the citizen science component (i.e. how to engage and include citizens within a community programme such as No Mow May), which is an important consideration. However, it seemed at times that the process of the citizen science component overwhelmed the science component of the paper (i.e. details of council meetings and administrative process in the Methods, and parts of the Discussion). I feel like this paper would be stronger with some of these details made more concise, or included as supplementary material. I have included more detail in the PDF annotation.

2. There is a tendency of the paper to be USA focused, which may render it less relevant to international readers. Include a few more specific details of the study area (i.e. location relative to the contiguous USA on Fig 1., population, etc.). I have annotated the PDF with a few more notes.

3. The figures and the text could benefit from more consistency in the terminology between the two treatments.  Can I suggest 'Unmown' and 'Regularly Mown' to identify them.

4. I thought the referencing was a little incomplete, given the few studies on lawn management on insects generally, and bees specifically.  While many studies discuss other insect groups, e.g. Hemipterans, Scarabideae, these could be interesting to discuss in order to strengthen the central argument of the paper. A summary of these papers is presented in one of my research group's meta-analyses: Watson et al. Journal of Applied Ecology 2019. DOI: 10.1111/1365-2664.13542

In particular, the following is very relevant and should be included: Wastian, L., Unterweger, P. A., & Betz, O. (2016). Influence of the reduction of urban lawn mowing on wild bee diversity (Hymenoptera,
Apoidea). Journal of Hymenoptera Research, 49, 51–63. https://doi.
org/10.3897/JHR.49.7929
Experimental design: The research question is clearly stated and very relevant within the context of current urban greenspace management.   The methods are described reasonably well, but a few details were lacking and/or confusing (see below for more specific details). This research certainly fills a knowledge gap and this is well identified. The number of replicates seems a little low given the availability of

1. From an experimental design perspective, there is a minor problem with comparing residential yards and parks/sporting fields as the two treatments: the variety of maintenance activities in residential lawns can be quite different, whereas public lands tend to be more consistently managed but have more aggressive management, such as widespread pesticide treatment, shorter cuts, etc.  While this does not invalidate the results, I think it is worth addressing to identify this potential to the reader.

2.  I had a little difficulty following some of the methods, and identifying which variables were collected. I suggest a review of the methods section to clearly identify what was collected and how this was done. In particular, the use of '% of unmown surface' as a primary variable was not clearly defined. Is this simply a measure of the surface area of each yard, or the proportion of unmown relative to mown?  This is a critical element and needs to be clarified, then discussed in the Discussion.

3. I found the results and explanation of the post-project survey a little confusing. Specifically, many of the questions are framed as yes/no, and it is not explained that respondents have a scale on which to respond. The results of the survey (certain questions) may better be presented as a figure to clearly show how participants responded on this scale.

4. The floral diversity data could likewise benefit from a figure to clearly show the results.
Validity of the findings: The findings of the study (most notably, the bee and plant diversity components) are well designed and conducted. The data has been provided, and the statistical methods presented.  The conclusions draw together the scientific research and the citizen science findings, though for mine the citizen science discussion dominates the importance of the biodiversity findings.

1. I find the use of the models a little superfluous, given that there are few input variables, and limited discussion of why these were selected, covariation, etc. The use of AIC in this case is irrelevant as the AIC is only useful to compare the fit of models, so should not be presented in this context. Perhaps reconsider if these models are necessary, or change the way they are presented and discussed.
Additional comments: Thank you for a welcome study that supports a surprisingly small volume of research in this field.  The results of the bee diversity data were expected, but welcome - particularly to see the magnitude of increase in unmown areas.  This is really important work, and important to publish.

While I understand the motivation for wanting to include lots of detail on the citizen science component, I would encourage reducing the detail of this a little. At times it overwhelmes the bee and floral data. Likewise, some parts of the methods and results are rendered a little confusing which detracts from the overall strong results and thoughtful message of the paper - I would suggest a thorough revision of the language of the manuscript to ensure it thoroughly explains the methods and variables collected, and that the messages and arguments are presented strongly and concisely.  Picture this as being read by a global audience because it certainly will be!

Thanks again. I am eager to see more work from this research group and this part of the world.


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: NO MOW MAY LAWNS HAVE HIGHER POLLINATOR RICHNESS AND ABUNDANCES: AN ENGAGED COMMUNITY PROVIDES FLORAL RESOURCES FOR POLLINATORS
Review round: 2
Reviewer: 1

Output:
Basic reporting: •	I think the authors did a good job in responding to the earlier criticism.
•	I find Figure 1 hard to read and understand
o	you indicate that all black points/dots are no mow sites; presumably you mean all sites that had registered for No Mow May not all study sites; while I realize you probably want to highlight how involved the city was in in participating in the intiatiive, showing the other points is not applicable here and I would remove them; if you’re keeping them in, adjust the legend to clarify that the black dots are all registered households; perhaps change them to be a different symbol (e.g. star, bee, flower, etc.)
o	the size of the larger coloured circles is much larger than that of the black dots; if the coloured circle is a now mow study site, why is it is so much bigger than the dots?  Which of the dots were selected, when there are multiple per circle?
o	You can also crop the map in a lot more, to just surround the areas that were studied vs all of the outlying city area (if people want to see what the city looks like, they can google it); this will help make the points more visible, as right now they are overlapped and hard to distinguish (this would almost double the visible size of the study area)
•	Table 1: I still think you could list all plant species in table 1, otherwise indicate that these are the top x of y species found, or just the species that were found in >1 property, etc..
•	There is no reference in-text to supplemental materials, yet in the author rebuttal letter they reference supplemental materials for plant lists, survey results, and model output.  Will the authors be providing the entire Excel file as a supplemental file?  I suggest separating out and further summarizing.
Experimental design: •	In their rebuttal, the authors indicate that the comparison of mowed greenspaces to unmowed lawns is appropriate as they have done surveys of various vegetation types, which is being presented in other papers; I still do not agree with this, but understand that they did not get enough permissions to conduct surveys in mowed areas.  This should be explicitly discussed in the methods and discussion, and the possible repercussions/influences on the data. The fact that the parks have been managed consistently the same way for decades does not apply here, as you don’t have the baseline data for the mowed vs unmowed sites.  I.e. expand the discussion more about this.
•	The authors indicate in their rebuttal and line 192 in the track-changed text that “every effort was made to avoid double counting and recapturing individuals.” But didn’t explain how they did this.  Additionally, in the text (line 117 of track changed file) “Homes were selected based on remaining not mowed through the entire month, and their proximity (within 1 km) to the focal parks within each of the five neighborhoods.  Homes were separated by at least 100 meters to reduce the likelihood of resampling individual bees at multiple homes.”   but with sites only 100m apart according to your text (and in some cases, across the road and other locations <100m away, in my plotting of points), and with some specimens being released at the end of the individual household survey period, you’re still sampling the same population of bees, so the sites aren’t independent
o	Were you trying to have all no-mow May sites and mowed parks be withing the same 1km radius so they are sampling the same bee population? In that case, the no-mow sites  should be considered sub-sites/samples – clarify more.
o	In the author rebuttal it sounds like you didn’t want to collapse sites/subsites in order to keep power (i.e. “As for independence of samples, a spatial autocorrelation test with three points may not be statistically appropriate here. We got around the independence issue by sampling multiple parks around town with distances typically >2 km apart from each other. The three plots in each park show within park variability, by lumping them into a single metric our sample size and power would decrease from n=15 to n=5“; the desire to keep power/sample size is not a valid reason on its own to ignore independence though
o	Line 192 should be clarified to explain how you avoided recollecting the same bees; indeed, also discussion should be included about this and if there was any impact on lethally collecting bees from within the same study area as other homes and parks in terms of bee abundance in later surveyed areas
Validity of the findings: •	While I still have concern about the comparison of mowed parks to unmowed residential areas, the findings are of interest and valid with the expanded discussion indicated above.
Additional comments: •	There are still references to citizen/community science in this study that I believe should be removed; e.g. first line of abstract (“No Mow May is a community science initiative”) and line 131 of track changed file (“Working with city government and community scientists”): As you addressed in your overall rebuttal comments, you agreed that the act of not-mowing lawns is not a community science participation on its own.  You can say it’s a community initiative, or working with community members, or similar, but not community science.  Your discussion still brings in community science (Line 360 (having just a couple volunteers assisting researchers isn’t really the same thing as a community science program)
o	Line 365, 369, etc.: be consistent in use of community science vs citizen science
o	Line 424, 425, etc.: be consistent in citizens vs community members
•	Line 55 of tracked changed file: urban areas provide nesting and overwintering sites in addition to foraging sites; even if the emphasis of your paper is on foraging, I would include these other habitat types that can be provide here as well
•	Line 57: why specifically list honeybees here as an example species and not list examples of the other native or non-native bees?   The way you list honeybees as the sole example seems to give them more weight or importance.
•	Line 125, 163, 236,256, 399etc: be consistent in capitalization (and terminology) of No Mow May, No Mow Area  (and un mowed vs not mowed)
•	Line 200: this implies that all 435 homes participated in the survey yet earlier (Line 124) you indicated only 130 did, a 30% response; I’d either move the response rate to this section, or report based on the 130 responses you did get
•	Line 384: give a few examples of these other drivers (e.g. as reviewers had pointed out)


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: A COMPARISON OF SEX, MORPHOLOGY, PHYSIOLOGY AND BEHAVIOR OF BLACK-CAPPED CHICKADEES TRAPPED USING TWO COMMON CAPTURE METHODS
Review round: 1
Reviewer: 1

Output:
Basic reporting: I found the article's aims to be clearly stated, and well written.  It was easy to follow the methods that the authors employed and the analysis (and associated rationale) for handling the data.

Raw data was easily retrieved and and text of analysis well documented.
Experimental design: The authors compare individuals caught using two common techniques - mistnets vs baited walk-in traps - to capture chickadees, and compare whether this creates a bias in the attributes of the individuals captured.

They caught up to six birds at each of ten sights alternating between techniques - first three birds at a site with either traps/mistnets then switch until they catch the next three
birds. They used sufficient numbers of exemplars with predator model presentations to account for potential pseudoreplication issues in playback stimuli. Thy also pre-bait/train birds for Potters traps, which should reduce initial neophobic response to the platforms, so in both cases they have employed standard capture procedures.

They then compare mophometric measures (wing, weight, tarsus), physiological (baseline and induced corticosteroid response) and behavioural attributes (boldness to predator model, and neophobia to novel object in PIT tagged birds coming to and RFID feeder) of birds caught using either technique.  Analysis uses conditional inference trees to account for multiple comparisons.    They found no difference in any measure between birds caught with different techniques, and so suggest that this could alleviate fears of capture-based biases.

Methodology is very thorough, but I have several queries that warrant address by the authors.

1.  I commend the detail of data collected for physiological/behavioural comparisons, but the overall sample size of 55 birds and ten sites is rather small for the comparisons (27 vs 28 with either technique).  Given that some of the metrics, particularly behavioural assays, have a very broad data range, how does this affect power to detect differences?

2. Related to the above, we have typically experienced a marked drop off in capture rates (using single techniques) in the second half of the morning vs the first half.  Did you see this decline in rate (increasing length of time between successive captures with time of morning)?  You partially account for this by alternating between sites which of the two techniques you employed first.  However, this would result in only a 5 vs 5 comparison even if you control for order as a random variable - do you feel this is sufficient to account for this variation affecting your overall results?

3.  L190- Most procedures I have seen with induced corticosterone response recommend spinning the samples down and extract plasma within 30min - 60min.  Your methods (L244) suggest you did these within 6hrs of collection.  Did you see any difference in the amount of corticosterone with time to extract, and if so did you correct for this?

4.  L217- an 80-90dB range is huge, as dB is a logarithmic scale. Was this range variance across sites, or were all sites varying over the same upper and lower range?

5. L317 - One metric you don't measure is typical CONDITION measure - residual mass/tarsus length. What is the reason this wasn't included (instead of measuring mass and tarsus independently)?  If you do include this, I would recommend using a scaled mass index, which better accounts for the non-linear relationships between increasing mass/length than ordinary least squares residuals (e.g. Peig, J., A. J. Green, and C. Ame. 2009. New perspectives for estimating body condition from mass / length data : the scaled mass index as an alternative method. Oikos 118:1883–1891.)
Validity of the findings: The authors find no differences in morphology/physiology or behavioural assays between birds caught using either technique, which is good news for those wanting to use these as an unbiased means of subsampling the population.

There are a couple of things the authors should address:
1. L120 - the assumption is that there may be two independent motivating factors which differ between response to the two trap types - reduced neophobia to walk-in traps, and increased boldness to mist nets. This would predict that boldness and neophobia are not negatively correlated (i.e that bold individuals are also not the least neophobic). What evidence is there to make this assumption in chickadees?

2. L313-320 - One of the attributes that you suggest might affect capture is dominance rank.  However you didn't assess this attribute among your banded birds through observation of interactions.  However, you might be able to address this through proxies - both age and sex are correlated with rank.  While you found no difference of sex on capture techniques, this can also be confounded by mate protection of high-ranked females having priority access to feeders.  Did you assess whether the relative age of the birds (as assessed by tail shape for AHY/ASY or HY/SY) affected propensity to catch the birds with either technique, especially when controlling for sex?
Additional comments: Found this paper very interesting to read, and hope you can address the 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: A COMPARISON OF SEX, MORPHOLOGY, PHYSIOLOGY AND BEHAVIOR OF BLACK-CAPPED CHICKADEES TRAPPED USING TWO COMMON CAPTURE METHODS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Very good.  no issues.
Experimental design: See general comments
Validity of the findings: Valid, see below
Additional comments: This study gives all indications to be a thoughtful and rigorously carried out study that investigates gear-specific sampling bias.  They have been careful to contrast this with sampling bias more broadly, a related question, but something which is difficult or impossible to do in most instances as it requires knowing the underlying population frequency distribution.  They find no evidence of any differences in traits between the two gear types, concluding each is equally good (or bad) at sampling birds in the wild.  The MS is mostly well written, and covers relevant literature and ideas, so I don’t have substantive comments to make on that note.  More generally, I don’t have any negative comments to make in particular, but rather raise a couple issues.

I had no idea what this “conditional inference tree approach”   was, and I have never heard of it, despite being somewhat of stats nerd and have lots of statsy chats with people who are quantitatively saavy.  At lines 280-284 they justify why this method is better (than say a familiar linear model) without any citation, and to my mind these arguments are either not correct or not compelling to me.  The data are not particularly unusual in any way, don’t appear to be badly behaved, so it seems odd to me that they choose to use an analysis that likely won’t be familiar to readers.  They state they also analysed the data using familiar linear models and with mixed effects and it gives same results.  So, why not use these?  Or use a MV model?  That should be equally parsimonious as the tree approach.  I’m just trying to avoid you having a situation where some reader(s) dismisses your study in part or whole because they get hung up on the analysis.

All that said, a visual inspection of the individual plots of raw data indicate immediately that there are no differences between gear types for any trait.  In a sense, given these data in the graphs, any analysis should return a null result!  Thank you for plotting raw data, many studies do not do this most basic and crucial aspect of presenting results.

Related to analyses is one issue that I think you should acknowledge, and that is low sample size: at both the among- and within-individual levels.  Several of your traits are labile, meaning that estimating an individual’s trait value with a single assay/measure often leads to downward bias of correlations and reductions in differences (see e.g. Adolph and Hardin); related to this is the additional issue of few individuals, and potential sex differences that you don’t have any power to test for.   Behaviour and hormones are notoriously low repeatability traits (R = ca 0.3-0.4, Bell, Biro and Fanson), meaning we need both repeated measures and fairly high sample sizes (see Wolak, where he shows data needed to estimate individual mean values with precision, tho his paper focuses on estimating R, which are two sides of the same coin – if you estimate R with precision, you also estimate individual predicted mean values with precision, i.e. the blups in a mixed model.  To gain a sense of how variable a trait is when R is low (0.4), and how relatively indistinguishable individuals are even with large samples, look at graphs in Biro and Stamps.

Therefore, its possible that a difference exists, yet you did have good power to test for it in the case of behavioural and hormone traits.  Please acknowledge this in your discussion.

Signed
Pete Biro

(Adolph and Hardin 2007, Bell et al. 2009, Wolak et al. 2012, Biro and Stamps 2015, Fanson and Biro 2018)
Adolph, S., and J. Hardin. 2007. Estimating phenotypic correlations: correcting for bias due to intraindividual variability. Functional Ecology 21:178-184.
Bell, A. M., S. J. Hankison, and K. L. Laskowski. 2009. The repeatability of behaviour: a meta-analysis. Animal Behaviour 77:771–783.
Biro, P. A., and J. A. Stamps. 2015. Using repeatability to study physiological and behavioural traits: ignore time-related change at your peril. Animal Behaviour 105:223-230.
Fanson, K. V., and P. A. Biro. 2018. Meta-analytic insights into factors influencing the repeatability of hormone levels in agricultural, ecological, and medical fields. American Journal of Physiology-Regulatory, Integrative and Comparative Physiology 316:R101-R109.
Wolak, M. E., D. J. Fairbairn, and Y. R. Paulsen. 2012. Guidelines for estimating repeatability. Methods in Ecology and Evolution 3:129-137.


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: A COMPARISON OF SEX, MORPHOLOGY, PHYSIOLOGY AND BEHAVIOR OF BLACK-CAPPED CHICKADEES TRAPPED USING TWO COMMON CAPTURE METHODS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper uses professional English language that is clear for the most part.

The introduction and background were mostly well referenced and relevant. The rationale regarding the possible influences of morphology and sex on the likelihood of a bird being captured by one or the other of the methods was not well developed. Cited sources refer to problems regarding entering a trap (because an animal is too large, for example) but that should not have been an issue at all for chickadees entering a walk-in trap … and unless the mist nets had very large mesh, there is little chance that a bird’s morphology would have affect its chance of being captured in a mist net. That males and females might behave differently in the social conditions associated with trapping is plausible, but the authors did not develop thoroughly their assumptions about ow that might work.

The submission conforms to PeerJ standards regarding manuscript structure. (The Results section is, however, exceedingly brief … and it omits information that would be important for fully assessing the validity of the study’s conclusions, as noted later).

The figures are well designed and labeled: the patterns they show (including lack of differences between birds in the two capture categories) are clear.

The authors supplied the raw data via the Open Science Framework, and I was able to access the those. The raw data file provides metrics for the individual subjects in the study, but it omits information about site and sequence of capture method that preclude checking of some analyses. The file also omits some variables; regarding corticosterone, for example, the file includes only the stress-induced metric, but not the bird’s initial value (it also omits covariates such as time after capture).
Experimental design: The manuscript presents original primary research within PeerJ’s scope.

The study’s main research question—about whether behavioral or other differences among individual animals might result in sampling bias depending on capture method—is well defined, relevant, and meaningful. The authors did state that their study fills a gap in knowledge that they identified about the possibility that using a trap to capture birds for behavioral or ecological studies might result in marking of a different set of birds than one would obtain using mist nets.

The authors seem to have performed their investigation rigorously and with appropriate attention to ethical standards about use of wild birds as subjects and about management of data and reporting of results.

The manuscript includes sufficient detail and explanation about the methods to make future replication possible.
Validity of the findings: The study does not replicate any prior work involving the study species (black-capped chickadee). It parallels in some respects prior work on two other songbirds, the great tit (a close chickadee relative) and both pied and collared flycatchers.

The study reports an overall negative result: the authors did not find evidence that morphological, behavioral, or physiological characteristics differed between birds captured using one method as opposed to the other. The authors conclude that the two capture methods (both of which are used widely in field ornithology) would not produce issues for downstream studies resulting from capture biases.

This (negative) conclusion is clearly stated and linked to the study’s results. I am not familiar with the details of the statistical approach (conditional inference tree analysis) on which the authors relied, but if I understand the things correctly, the paper’s conclusions match the patterns and test results reported in Table 1.

While I do not dispute that the available data support a conclusion of a negative result, I was disappointed not to see discussion that considered questions about the power of the analyses. A main reason that the statistical analysis did not identify any factors discriminating between birds caught using the two methods was that some of the potential predictive measures (especially those concerning behavior) were highly variable among individuals, as indicated by the standard deviation values in Table 1. The manuscript does not include thorough consideration of sources of this variation and its effect on the primary conclusion (no difference depending on capture method), although the authors did mention dominance relationships (which they did not evaluate) as a potential complicating factor. Given that researchers aimed to assay behavior often considered part of an animal’s personality, more consideration about consistency of the metrics was merited. However, the study’s design precluded any quantitative consideration of consistency. Accordingly, most of the variability in the results—on which the conclusion about lack of bias deriving from the alternative capture methods largely depends—is unexplained.
Additional comments: I appreciate that while the study involved a relatively small number of subjects (28 females and 27 males), the project’s multiple elements (including especially netting/trapping at multiple field sites spread over a fairly large geographical area followed by later behavioral experimentation across that same range of sites) represented significant logistical challenges. The authors clearly put in a lot of time and effort on the project, yielding a good amount of information.

That said, I think that the authors can improve the paper in various ways. I address these in the comments below.

Title: Could and should be less vague; “differences” could refer to all sorts of things.

In the Introduction, the rationale about potential importance of morphology (lines 88-89) emphasizes mechanisms such as the physical constraints of a trap (preventing some animals from entering). However, no such constraint would be an issue for chickadees entering a walk-in trap or flying into a mist net. Testing morphology for its own sake (beyond its correlation with sex and therefore likely with dominance) needs better justification.

Similarly, the authors state the postulated effects of sex because of behavioral differences between males and females far too vaguely (“territoriality, offspring defense, and foraging). Testing for differences by sex allow inclusion of a simple comparison … but without any clear expectation of why trappability would differ between male and female chickadees. Again, the authors need to provide clearer justification here.

Figure 1: absolute measures of body size/mass not very meaningful. Why not consider body mass index (mass scaled to body size) as measure of condition? Correlated with fat score? While the data from this study don’t provide support for the idea that a bird’s condition affect its tendency to enter trap vs. get caught in net, it would be good to cite more thoroughly studies in birds (including especially tits) showing that there are connections between condition, dominance, and risk-taking.

Table 1 is problematic regarding the RFID feeder data for the post-capture behavioral assays. The rows for number of feeder visits are labeled as having the units of seconds … but should these numbers not be just counts of independent visits to the feeder? Beyond this detail, I question the value of considering duration of feeder visits—as a separate metric from number of visits—because duration of each individual visit to a feeder probably didn’t vary much at all. Maybe it did … but the authors present no data about that.

To evaluate this, I checked the raw data and found that the “duration” at the feeder during a 2-hour sample period was predicted by the number of visits (P < 0.0001, r^2 = 0.86 for the data from the control time periods and the cup presentation time periods; slight weaker relationship—but influenced by one extreme outlier (excessive duration: 437 seconds, vs. max for all others of 139 seconds; erroneous data point, or bird that became “frozen” to the perch??)—for visits during the owl presentation).

If birds did change the time they spent at the feeder during each visit (to choose a seed, or to stand on the perch surveying surroundings before selecting a seed), that would be interesting and potentially important.

This brings me to a more general comment: The results section is exceedingly short, because it omits presentation about underlying aspects of the data like those I just discussed. (The analysis includes nothing about the duration of individual visits to the feeder.) More presentation about descriptive statistics for this and other various metrics would be helpful … BEFORE moving on to focus on comparisons between the birds with respect to how they were captured. Standard deviations were very large for many of the behavioral measures. The paper needs to include more information about variation, because it relates to statistical power: was there any reasonable chance of detecting the kind of difference that the authors hypothesized given the number of birds studied and the variability in the metrics that emerged?

Additionally, it seems (if I interpreted the Methods correctly) that the authors conducted each behavioral assay only once at each site (2 h with owl one day, 2 h with novel object on the prior or subsequent day). This design provides no measure of consistency of behavioral responses for individual birds at a given site. Were there not RFID data available for other time periods that the authors could use to consider consistency of visitation (number of visits in 2-hour period; visit duration) for the control period, at least?

Without including analyses like these, the next best thing the authors could do is to review more thoroughly what’s known about the consistency of behavior measures associated with personality in songbirds, and particularly in tits (including chickadees). Including more discussion about that could reassure readers that the behavior measured was unlikely to have varied much (for the same bird) from day to day because personality-associated variables of that kind are known to be highly repeatable.

The design controlled for time of day, but not for other conditions that likely varied from day to day (e.g., temperature, wind, cloud cover). Ample prior research (not cited) has shown that those varying conditions affect visitation at feeders by chickadees … and thus there may have been a lot of extraneous variation injected that obscured any patterns (based on prior capture method) that the researchers were testing for.

Besides dominance affecting visitation at RFID feeder, it might be worth also citing studies showing that a bird’s social network position can be an influence, too (perhaps correlated with dominance, but not necessarily synonymous).

Lastly, on a general level, would the analyses have been sensitive to detecting a pattern whereby one capture method yields a set of birds whose traits represent a SUBSET of the subjects captured using the other method? The manuscript does not seem to address this possibility, as the analysis focus (only) on whether the birds caught in the two ways differ in their average traits.

Some additional specific comments:

Line 280: The assertion that “the conditional inference tree approach is preferable” merits a citation.

Lines 324 – 327 “In chickadees, we expect dominance hierarchies could influence the direction of response to the stimuli, with lower-ranked individuals being more likely to come in to the feeders during stimulus presentation, while dominants are avoiding the perceived threat.” OK ... but what is the basis for this assertion? (Citation of sources would be helpful here.)

Lines 128 & 153: “comprised of” should be just “comprising” or “comprise”

Line 167: Poor grammar to use “however” as a conjunction. Precede “however” with semicolon to link two independent phrases.

Line186: PIT tag company is now Eccel, in Leicester (no longer IB Technology in Bucks). Citing company’s new name and location would be more helpful for readers wanting to buy similar gear.

Lines 294 – 302: excessive repetition of concepts from Introduction (no new information added here).

Lines 307 – 310: largely repeats concepts and citations from lines 57 – 61 (again, no new information added).

Line 329: write out numerals small than 10 (not just because the sentence starts with a number)


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: A COMPARISON OF SEX, MORPHOLOGY, PHYSIOLOGY AND BEHAVIOR OF BLACK-CAPPED CHICKADEES TRAPPED USING TWO COMMON CAPTURE METHODS
Review round: 2
Reviewer: 1

Output:
Basic reporting: fine.
Experimental design: fine.
Validity of the findings: fine.
Additional comments: I dont feel like the authors have convinced me that their analysis method provides any realy advantages over the widely used ones - we've discussed this already, and i'm not being hard line on it, as the raw data speaks for itself anyways.

authors have addressed the concerns just fine, and i dont have any more substantive concerns to raise.


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: A LABORATORY COMPARISON OF THE INTERACTIONS BETWEEN THREE PLASTIC MULCH TYPES AND 38 ACTIVE SUBSTANCES FOUND IN PESTICIDES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well structured, with relevant figures and tables. It is self-contained with relevant results and hypotheses.

The English language is in general comprehensible and easy to read. There are several grammar mistakes throughout the manuscript though that need to be corrected. Some examples include lines 25 (no data is), 38 (assess __ behaviour), 48 (in __ European Union), 52 (debris are left), 66 (debris are more), etc. These are only some examples; please consider getting the full manuscript revised by an English native speaker.

Please review the way citations are presented: it is common practice that only the first author name is referred followed by “et al” when there are more than 2 authors – check for example lines 51, 57, 64, 67, etc. Also, when a sentence starts with a citation, it should be referred the author(s) name followed by “et al” (if more than 2 authors) and followed by the year of the publication in brackets; the authors of this manuscript aren’t following this rule – see for example lines 93 and 94: Nerin et al. (Nerín, Tornés et al. 1996) and Sharom and Solomon (Sharom and Solomon 1981). The full manuscript needs to be revised for these situations.
Experimental design: The manuscript presents a laboratory experiment where the sorption of 38 active substances of pesticides into 3 types of plastic mulch is being tested. Additionally, the authors investigated the decay of the active substances in the presence/absence of plastic mulch.
The Experimental design has been properly designed and performed and it is of relevance to the scientific community as well as to society and policy makers in general. The methods were well described and, despite minor issues, they have sufficient detail and information to be replicated by others.

I do have some questions/remarks/comments though:
1. As described by the authors in the introduction and further discussed in the discussion chapter, plastic mulch is used in agriculture and therefore it is mostly in contact with soil. Moreover, most of the used pesticides are applied in the soil, that then will be in contact with the plastic; or they are applied post emergence in the crops, reaching the plastic mulch and most probably the soil as well. This means we are in the presence of a solid(soil)-solid(plastic mulch) phase and not a liquid(incubation solution)-solid(plastic mulch) phase as performed by the authors.
1.1 How does the performed experiment in a liquid-solid phase translate to the reality of a solid-solid phase? How relevant is this experiment in a liquid-solid phase to the reality observed in the field?
1.2 Why didn’t the authors test with soil (solid-solid), which would represent better the reality?

2. It is shortly described the procedure for the extraction from the plastic pieces, but it isn’t described the procedure for the incubation solution. Was the incubation solution directly analysed without any extraction? Even if so, the authors had to include IS correct? Please give a short description on how was the incubation solution prepared for analysis in the LC-MSMS.

3. The authors followed the method of analysis of Mol et al (2008) – analysis for food/feed, and Silva et al (2018) – analysis in soils. How certain are the authors about the good extraction efficiency from the plastics? Were tests performed in plastic to verify the good extraction procedures and to obtain the recoveries from plastic? It is a different matrix from soils or food/feed, adsorption is likely to behave differently and therefore extraction might be easier or more difficult.

Ls 221 & 223: Please give the full names of the acronyms used when used for the first time (LC-MS/MS; TQ-S; UPLC)

L225: The blanks and standards were prepared in Milli-Q water? Please specify.

Ls 227 to 230: From the authors’ description, and assuming that the calibration standards were prepared with Milli-Q, it means the LOQ is based on the best scenario analysis, meaning it is based on the best signals you can obtain for your analysis. Matrix effects from the plastics extraction may have happened though. Didn’t the authors test for these possible matrix effects? How did the authors guarantee that the LOQ isn’t at a higher level due to these effects?
Validity of the findings: Conclusions are well stated and linked to the original research questions and are somehow limited to supporting results.
All data in which the conclusions are based have been provided.
The manuscript presents enough impact and novelty to be accepted for publication after major revisions.
Additional comments: 1. Consider using the term “adsorption” instead of “sorption” throughout the manuscript when referring to the adsorption of pesticides into the plastic.

2. Say what is the incubation solution composed of (10% ACN, 90% H2O) already in the abstract and also the first time you refer to it in the methods section (in L142). It isn’t nice nor good to the reader to have to wait until section “Incubation solution” to know what is the solution composed of.

3. Throughout the whole manuscript, consider substituting “square” (when referring to the piece of plastic) by “piece” or similar to avoid confusion with the square from cm2.

4. I couldn’t find any legends for the figures and tables in supplementary material, please include such.

L32: consider removing the word “square” – cm2 already has the “square” meaning on it.

L74: remove the space after “:” and lowercase the “T” of “the”.

L113: The sentence starting with “As a preliminary investigation…” should be a new paragraph.

L142: remove “a)”

L173: remove “squares”

L174, L201, L370: a sentence should not start with numbers (“3x3”, “15”, “38), rephrase the sentences accordingly.

L208: make it “quantification”

L287: use normal brackets for the presented number of samples.

L287: do the authors by “ lower DT50” mean “shorter DT50” or “longer DT50”? Consider changing to shorter or longer.

Ls 292 to297: This section on the decay reduction should be a little bit more developed. Only a comparison is made between the decay without plastics and with plastics in general. But could there be a plastic type that could affect the decay more strongly than another type? From the results presented in Fig. 3, a greater adsorption was observed for Bio plastics – did this reflect a greater decay reduction for active substances with Bio plastics as well? Consider changing Fig. 5 to show the decay reduction for each type of plastic and verify as well if there are significant differences in decay reduction between plastic types.

L301: Include references for the previous studies referred.

Ls 311-312: The authors refer that the time of incubation and temperature may have increased the adsorption to the Bio mulch due to the formation of H-bonds. This might also be true due to the fact the experiment was performed in a liquid-solid (incub. solution-plastic) phase. Would the authors expect the same to happen in reality, with a solid-solid (soil-plastic) phase?

L329: … “the pesticides sorption in soils”… Do the authors really mean “in soils” here? In general, adsorption of pesticides in soil is known. I believe the authors mean to refer something related to the plastics instead? Please revise.

L330: remove the “s” from “soils”

L350-353: The authors analysed the samples only once, 15 days after incubation (not at time 0 or at different time periods), so how certain and confident are the authors that the referred “decay” wasn’t linked to a poor extraction procedure due to strong sorption to the plastics of some compounds?

L357-366: “The decay of active substances from pesticides was supposed to be reduced by sorption.” Why are the authors saying “supposed to be”? The results presented by the authors proved that this effectively happened (assuming a good extraction performance of the method of analysis)… Please consider revising this sentence and the whole paragraph for stronger statements and based on your results. The way it is written leaves the feeling that this was not what happened in your results, which isn’t true. This whole paragraph refers too much uncertainty when studies already proved most of this (“commonly accepted”, “plastic debris may reduce”, etc).

L377: “A not-dissolved fractions” - or you remove the “s” from “fractions”, or you remove the “A” at the beginning.

FIG.1 – There is a typo in the legend: in the 3rd description it says “soultion” instead of “solution”. Please correct it. Also, again, remove the “square” and substitute it by “plastic piece” or similar. Moreover, include information on what is the solution composed of.

Table 1: include what is the incubation solution composed of.

Table S2: Include the reference(s) for the information you provide.

Table S3: Please include SD for sorption and decay results. Maybe due to the lack of a legend to the table, it isn’t comprehensible what the results presented really mean: sorption and decay after 15 days? For example, azadirachtin is shown with a decay of 100% - does this mean that this compound degraded completely? You also present negative percentages (ex: Clorimuron-ethyl, linuron, etc) – what do these negative values mean? Please find a way of making these aspects comprehensible by reviewing the titles of the columns for example. The table needs to be able to stand alone.


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: A LABORATORY COMPARISON OF THE INTERACTIONS BETWEEN THREE PLASTIC MULCH TYPES AND 38 ACTIVE SUBSTANCES FOUND IN PESTICIDES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The title requires re-structuring. In its present for, it suggests that the tests were conducted in three types of mulch. Instead, it was in three types of plastic using in mulching. Please rephrase. Some minor phrase corrections are needed, such as in the Introduction, where it should read, for example, “..year in the European Union” or “debris leads to its accumulation”, or “A laboratory single point sorption experiment was”. However, these are minor issues that do not affect the readability of the manuscript, although proof-reading is recommended.
Discussion
“Additionally, sorbed chemicals are generally assumed to be less accessible to microorganisms,
which preferentially or exclusively utilize chemicals in solution” – Please clarify.

Figure 2 – I do not understand exactly how what the authors sate in the caption relate exactly with the image, regarding the vertical black lines. Is this an interval, or are these error bars?
I believe that some listed references that are not cited in the text (e.g., Besseling et al, 2017), but I may be mistaken. Please verify.
Experimental design: The main limitation of the work stems from the fact that no kinetics can be deduced from the provided data, as the authors made single-point measurements. Although this may be understandable, taking into consideration the large number of pesticides tested, this work would have been of immensely larger significance had the authors opted to study these effects on a smaller set of representative pesticides, but included multiple measurement points. Additionally, these tests could have been conducted resorting to environmentally significant concentrations of these pesticides. The authors were careful to include types of plastics and pesticides used in intensive agricultural activities, but the concentrations used, as the authors themselves noted, are not environmentally relevant. There are also some methodological issues that need further elucidation. For example, why was an ultrasonic bath used? This certainly does not mimic real-world settings.  Also, the LC-MS/MS method needs to be better described, regarding the elution conditions. Was this carried out in gradient, or isocratic mode? In the case of the former, please provide the elution profile. In the case of the latter, please provide ratios. I certainly appreciate the authors providing the LC-MS/MS raw data, but it would have been nice to see at least an example of a typically obtained mass spectrum and LC chromatogram. Furthermore, was the described method validated? If so, data for this need to be provided. Was there any mass balance conducted, that quantifies the pesticides found adsorbed on the plastics and those that remained in the solution? This should be done.

Materials and Methods.
Please include number of scans for FTIR and the background.
3×3 cm² squares/15 days/38 – Please do not begin a sentence with a numeral.
Equipment, such as incubators, ovens, etc, need to be identified (make and model).
Validity of the findings: Please refer to other sections, in which the methodological approach is assessed as well as the associated validity issues.
Additional comments: Beriot and colleagues have submitted a manuscript in which they compare the putative interactions between three types of plastic materials and numerous pesticides. Although certainly interesting, the work carried out by the authors requires some clarifications.


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: A LABORATORY COMPARISON OF THE INTERACTIONS BETWEEN THREE PLASTIC MULCH TYPES AND 38 ACTIVE SUBSTANCES FOUND IN PESTICIDES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised manuscript has improved its quality. There are minor mistakes that still need to be corrected though.
I annotated my comments in the uploaded word document after the responses from the authors (in red, for Reviewer 1) - document named "peerj-46097-Rebuttal_Letter_04_06_2020_R1".
I also highlighted most of the necessary changes in the uploaded pdf - document named "peerj-reviewing-46097-v1_R1".
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No additional comments


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

Input:
Title: NEST-SITE SELECTION AND BREEDING SUCCESS OF PASSERINES IN THE WORLD’S SOUTHERNMOST FORESTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Generally of high quality. I mention a couple of instances in my detailed comments below where additional citations should be added to back up some of the ideas in the paper.
Experimental design: no comment
Validity of the findings: generally good.  See detailed comments where the claim that "Milvago was the main predator" needs a caveat
Additional comments: Here the authors present data on the nest site selection and nest success of 5 passerine species in a southern forest. The paper is well-written and the data analysis seems thorough. Although the sample size of nests is small for a couple of the species, there is little information currently on the reproductive ecology of such species in a southern forest so the findings stand to make a useful contribution.  As a result, most of my comments are minor:

1) lines 86-89.  Although I understand where these predictions about habitat and predation-risk from aerial predators are coming from, the eyesight of raptors is very keen and so it seems unrealistic, (does it not?) to think that the height of the canopy (trees) will be a significant limitation for raptors detecting prey below them? What is the actual variation in canopy height in your forest system and do you think this model effect is biologically real?

I was trying to get an appreciation for the effect of canopy height in the models and noticed in Figure 4 that the predicted plotted curve goes from a canopy height of 0 on the figure and rises quickly to a maximum nest survival at a height of just over 4 m.  This seems quite strange to me--certainly the average canopy tree is taller than 4m??  Yet the effect of "canopy height" seems to be operating mainly from 0-4m high which does not seem to be biologically realistic.  And within this short distance it seems unrealistic to assume that the vision of raptors is going to be limited by distance?  I'd check the raw data to see whether a few odd points of canopy height might be affecting these results.  In figure 4, it does not make much sense to plot "predicted" curves at levels of the independent variable that are not possible in nature.  At least the predictions and discussion with respect to canopy height should be better justified.

2) the predatory kite (Milvago) seems to be a generalist predator? It certainly can hunt by perch-and wait but when I was in Chile, I often observed these birds foraging from the ground, much like corvids. Is it possible they could also depredate nests from the ground? For background, I would cite some literature on the hunting techniques of Milvago..  Also, did you ever see this raptor on the ground in your forest? Perhaps the placement of passerine nests is an "average optimum" of the different hunting techniques of Milvago--e.g., if the raptor sometimes hunts from the ground and sometimes from above, the birds may have had to balance predation risk from above and below even before the introduction of novel ground predators.  This possibility should at least be mentioned.

3) Because the species of predator could not be identified in 58% of cases, you can NOT say that Milvago was the main predator in your study!  You can only say that it was the most common predator of the ones you were able to identify. You do make this distinction correctly at one point in the discussion section, but you need to change the claims you make repeatedly, elsewhere in the paper.  For example, line 52 in the Abstract should read "Milvago was the most common predator among the 42% we could identify.  Similarly, line 381 in the discussion needs to be reworded.

4) line 278. To me, presenting these predation rates as fractions is confusing.  Why not present these as straight %success and then give the sample size of nests for each species in parentheses.

5) line 432.  At what distance do the parents flush when a predator approaches?  Nest concealment could still be of benefit if a parent sits tight until the predator is quite close…

6) For the species in which no habitat variables predicted nest placement, one possibility is that the birds place nests "randomly" to avoid predators forming search images for nests. This seems to be the case for white-tailed ptarmigan and other grouse, for example (see Wiebe and Martin 1988, Animal Behavior 56, 1137–1144).


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: NEST-SITE SELECTION AND BREEDING SUCCESS OF PASSERINES IN THE WORLD’S SOUTHERNMOST FORESTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors examined two hypotheses regarding nest placement and its consequences for nest survival. This study is motivated by a recent introduction of ground predators to an island where the only native predators were raptors; thus, the study sought to identify nest predators, nest-site characteristics, and whether passerines selected nest sites that provided protection from both the native, aerial and introduced ground predator species.

Although the manuscript is clearly written and well-referenced, it is lacking context beyond this system. The authors can improve the manuscript by emphasizing how their hypotheses (nest concealment and predator proximity) fit into the context of general ecology to demonstrate the knowledge gap that exists outside this system in both the introduction and discussion sections. An additional shortcoming is that only one nest was confirmed to be depredated by a ground predator, which limits the scope of inferences the researchers can make about the risk of predation due to the recent introduction of mammalian predators. However, the authors have done a good job in the discussion to explain the caveats surrounding the interpretation of the depredation summary statistics.

The authors have described an interesting system and pose an important question that is relevant to this system but has implications for understanding nest placement generally. The analyses are well-written and appropriately applied. The raw data are shared but may require metadata to describe column headings and field entries; although, this is generally obvious. The manuscript can be improved by providing greater background for the hypotheses and placing the study in a more general context beyond that of this system.
Experimental design: The research has a well-defined question and a knowledge gap is clearly identified. The methods are clearly written, understandable, and appropriate for the study questions. The authors may consider generating random values for unmeasured nest selection variables and including the season effect as a fixed term rather than a random effect (see general comments). I particularly appreciate tables 1 and 2 that give the justification and rationale for inclusion of model variables.
Validity of the findings: The authors have made appropriate conclusions based on their results. However, the authors could improve the manuscript by considering the implications of their results outside of the study system.
Additional comments: Introduction:
L85-89: The justification for canopy cover as part of the predator proximity hypothesis needs better explanation or terms. The use of the term “canopy cover” here makes me think that this variable fits under the total foliage hypothesis (i.e., more cover = more foliage = more nest concealment). A better description may be canopy height and extent. I see that you have used canopy cover and canopy height in the table 1; perhaps add height to your sentence in the introduction.
L90-91: What about the interaction of these two hypotheses? The combination of these two habitat features likely contributes to nest success/failure.
L90-122: These paragraphs are very system-specific. You may consider removing some of this information from the introduction and moving it to the study site section of the methods.
L105-122: Instead of focusing only on evidence of predation pressure as a driver of nest-site selection in this system, you should present some general support for this hypothesis from other systems.
Methods:
L159-160: Does this mean that the cameras took three pictures with a minute between each picture whenever the camera was triggered? If so, a minute seems like a long delay; did you have any issues with missing what triggered the camera?
L189-196: Did you consider randomly generating a nest height for the paired sampling plots from a range of possible nest heights (could also do the same for concealment: 0-100%)? This could add a potentially important conclusion to your results and implications.
Statistical analyses: Good, clear description of analyses.
L231-233: Three levels is pretty low for a random effect and is likely unnecessary here (see Harrison et al. 2018. A brief introduction to mixed effects modelling and multi-model inference in ecology. PeerJ. 6: e4794. Doi: 10.7717/peerj.4794). Did you try treating year as a categorical fixed-effect term?
Results:
L277-279: The presentation of success/failure rate is not very intuitive. Why not present % successful or % failed?
L281-282: Do you think the failure to capture depredation events was due to the one-minute lag between pictures?
Discussion:
General: The discussion section is very system specific. What implications do your results have for our understanding of nest-site selection and nest survival broadly?
L333-334: It would be stronger to open with your general hypotheses and why that is interesting in the context of general ecology.
L335: word choice: “predicting” substitute with “correlated with”
L344: E. albiceps and T. falcklandii selected nest sites with characteristics that were no different than in the randomly sampled paired plots (they did not randomly select their nest sites).
L351-364: This section seems like it belongs within the nest survival section. The flow of the discussion would be smoother if this was moved elsewhere.
L406: abbreviate daily survival rate to DSR.
L466-468: The hypotheses are not necessarily mutually exclusive-nest concealment and predator proximity are likely interactive features of the environment that together contribute to nest placement and nest survival. This could also make it difficult to find support for one hypothesis over another.
Tables and Figures:
Table 1 is a nice addition for providing an understanding of your reasoning. Well done.
Table 2: It would be good to add the rationale for the last row of variables.
Table 5: Consider reorganizing this table in a way that allows you to easily see what variables are shared across species and how the estimates compare. Perhaps you could have the species as the columns and the variables listed as the rows, and the cell values could be the estimates, or something to that effect that makes reading the table a bit more systematic.


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: NEST-SITE SELECTION AND BREEDING SUCCESS OF PASSERINES IN THE WORLD’S SOUTHERNMOST FORESTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: 1. This paper is professional and the introduction is well-written. Appropriate context is supplied in the introduction to provide a theoretical framework for the study. The authors make appropriate use of references to give background information and discuss their results in a broader context.

2. One major concern centers around the clarity and presentation of the results section. Please see notes in the general comments below.

3. I also have suggestions for improving tables and figures, included in the general comments below. Please consider these comments carefully – in their current state, I do not think the tables and figures do an appropriate job conveying the results and incorporating modeling uncertainty.

4. I encourage the authors to give a close read for occasional small typos. E.g., line 56 “not”, grammar on line 472.

5. The authors switch back and forth between scientific names and common names in figures, tables, and text. Please decide on one and use it consistently.

6. Please include a .README or Metadata file defining the fields in the raw data.
Experimental design: 1.  I commend the authors for gathering an extensive dataset that provides valuable insight into the breeding biology of birds in a remote and under-studied area. The authors used an appropriate modeling framework to analyze their data.

2.  My major concern with the modeling framework centers around the model selection methods for survival models.
•	In general, the model selection methods and results lack clarity. I suggest continued work on this section to make sure that readers can clearly understand the step-by step process that you used to build the final model.
•	First, for stage 1, it is not clear in the text how the authors build the candidate model set for temporal variables. It appears from the supplement that they ran all possible combinations of variables. If so, please state this in the text.
•	Second, there is an inconsistent use of AIC between survival models and nest selection models. For nest selection models, the top model was chosen based on the smaller number of parameters. For stage 1 in the nest survival models, there is no information presented on how the top model was selected. For stage 2 in the nest survival models, the top model was chosen based on having the highest number of significant parameters. This inconsistent use of AIC selection criteria introduces inappropriate subjectivity into the model selection framework, and it needs to be corrected in the revised manuscript. Please select one criteria for selecting the best model when there are multiple models within 2 delta AIC, and use this same criteria throughout.
•	Relatedly, the inconsistent use of AIC also creates problems in lines 305-309. This is currently worded in a way that suggests a form of data dredging – i.e. bending selection criteria in an attempt to include variables that appear statistically significant after the model is run. There needs to be one selection criteria for the “best model”, applied across all models in this analysis.
•	In lines 206-207, the authors select a top model based on the fewest number of parameters. If the revised manuscript continues to use this approach, please provide evidence for why this is an appropriate method. Generally, when multiple models are within 2 AIC, researchers choose to use the model with the lowest AIC. Even if this model has more parameters, the fact that AIC remains low means that the addition of the extra parameter overcomes the AIC penalty for parameters (-2k) and significantly increases the likelihood. Thus, it may not be appropriate to only use the model with the fewest number of parameters when it is not the lowest AIC.
Validity of the findings: 1. The authors do an appropriate job interpreting their findings in the context of the results. The authors provide evidence to support both the total-foliage and the predator proximity hypothesis.

2. The authors speculate that introduced mammal predators may contribute to a disconnect between nest site selection and survival. I agree that this is a reasonable hypothesis, but there are many other potential explanations for this phenomenon. In fact, it’s actually quite common for nest ecology studies to see this trend. Please add text to the discussion to reflect this. I suggest reading and referencing the following paper in the discussion section, which reviews potential hypotheses for disconnects between nest site selection and nest survival:

Chalfoun, A. D., and K. A. Schmidt (2012). Adaptive breeding-habitat selection: is it for the birds? The Auk 129:589–599.
Additional comments: I have completed my review of Nest-site selection and breeding success of passerines in the world’s southernmost forest. I found this paper novel and interesting, and I believe the results are important to avian biology. I have included general comments below, organized by manuscript section.

Introduction

1.  The introduction sets up two hypotheses operating on avian breeding biology in this system.
•	The “total-foliage” hypothesis sounds very similar to the “nest-concealment” hypothesis that I see more often in the literature. Please provide text to distinguish how these hypotheses are different, or if they are the same.
•	Line 42: As currently worded, this sentence indicates that the two hypotheses exclude each other. Please clarify that they are non-exclusive, and perhaps even complimentary.
•	Suggested citation for framing in the introduction. This study experimentally manipulates nest height and examines predation risk.
Latif, Q. S., S. K. Heath, and J. T. Rotenberry (2012). How avian nest site selection responds to predation risk: testing an ‘adaptive peak hypothesis.’ Journal of Animal Ecology 81:127–138.

2. In order to support the claims in the introduction, more detail needs to be provide on the differences in the predator communities between the island and the mainland. Is there evidence that mammal predation is more important than raptor predation on the mainland?
•	Line 108-109: How do we know that this difference is not just due to differences in vegetation type or vegetation height?

3. Line 129-130: If the authors hypothesize that nest height has a quadratic relationship with survival, why isn’t nest height tested as a quadratic variable in the candidate models?

Methods

1. Please see the concerns in the experimental design section above.

2.  Have you considered using a random slopes model to make population-level inference? This would allow you to include all species in a single model, with a random slope effect for species. For the nest selection model, for example, this approach would estimate a population-level effect of understory cover, as well as a unique estimate of understory cover for each species. Random slopes models allow species with small sample sizes to “borrow strength” from species with larger sample sizes.

3. In table 2 and throughout the paper, I suggest replacing “biological and temporal” with just “temporal”. The current wording is confusing because habitat variables are also biological.

4. Line 245-246. I don’t understand why the choice was made to exclude this variable. If all nests above the ground were successful, this indicates a strong effect of nest height on survival.

5.  Line 200: Please clarify that a separate model was run for each species. This is currently unclear.

Results

1. Overall, I believe the results need to be substantially edited for clarity. The results are highly repetitive, inefficient, and difficult to follow.
•	Please remove areas where the results are simply repeating estimates that are already reported in tables (e.g. lines 297-299).
•	Lines 297-298: it is unclear where these numbers come from, and why some a ranges and others are not. Report these numbers in table 4, and describe overall relationships in the text. Please include CIs for all estimates of total nesting success.

2. Table 3: The intercept estimate for Austral Thrush should be reported as 0.

3. Table 4: The organization of this table is unclear. Why is the camera effect split into egg and nestling stage, and why are estimates only presented for camera=absent in the Austral Thrush?

4. Table 5: I suggest changing this table so that it has a column with coefficient estimates (with CIs included), rather than writing out the model formula. If there is a random effect, include the estimated standard deviation of the random effect distribution.
•	Please note that the notation used in this table is not intuitive for people who do not have experience using glm()-class functions in R.

5. Figures 2-6.
•	It is not necessary to give the model equation in the figure caption.
•	Please include confidence intervals on all line plots.
•	If table 5 is changed to include CIs and coefficient estimates, the coefficient estimate figure will no longer be necessary.
•	Why is a line splitting up nest stages included for all nest age plots, except for figure 5? In figure 3 and 5, why aren’t the estimates for nest stage presented as a figure. Effects of categorical variables on DSR can easily be presented as boxplots.
•	To help clean up the figures, I suggest only including figures for statistically significant parameter estimates. Readers will be able to reference the table to see parameters estimates for non-significant effects in the top model.

6. Line 270: Replace “increased by 1.03” with “increase by a factor of 1.03”.

7. Line 278: Replace success/failure rates with either successes/total or failures/total, so that results are more interpretable and match the reported rate on line 277.

8. Supplement
•	Please include captions for all tables in the supplement.
•	What are the little cross symbols next to variables in supplemental table 3?

Discussion

1. Line 344: The claim that nest selection was random is not supported by the results (e.g. there could be unmeasured variation that the birds respond to). Instead, the authors can make the claim that among the habitat variables that they measured, none had a strong effect on nest site placement.


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: NEST-SITE SELECTION AND BREEDING SUCCESS OF PASSERINES IN THE WORLD’S SOUTHERNMOST FORESTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have improved the clarity of their writing in the revised draft. The addition of examples from other species to the introduction and discussion has increased the ecological scope of the manuscript.
Experimental design: The context of the study and research questions are well defined. The methods have been improved since the previous draft and are more clear in this version. The tables and figures are also clear. Well done!
Validity of the findings: The authors have done a good job incorporating examples from outside of their study system that increase the ecological scope of the inferences. I appreciate the additions the authors have made to the discussion; however, some sections are quite long. It may be possible to edit some of the text down. I also suggest considering the addition of some subheadings to the Nest Survival section to help structure that section a bit more.
Additional comments: L78-79: Can you briefly explain what you mean by "simpler structure" in high-lat vs. tropical forests? Some readers may be unfamiliar with the structure of these forest types.

L326: comma needed after "In addition"

L327: "effect" should be plural

L360-482: This section is long with lots of references to analyses you conducted. Consider adding some subheadings to this section that correspond to the specific analysis you talk about to help cue the reader to remember the method/result you discuss.

L373-378: This is a matter of style, but the questions here read a bit informal. I would state these ideas another way for a more professional presentation.

L334, 360, 484: Make sure that the headings are consistently formatted. L334 does not match the others.


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: NEST-SITE SELECTION AND BREEDING SUCCESS OF PASSERINES IN THE WORLD’S SOUTHERNMOST FORESTS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have adequately addressed my comments on the previous version, and I feel that the manuscript is much improved. I especially commend the authors for their changes to the text in the introduction and discussion, which now frame the study in a more compelling way.

Though the writing in the results section has improved, there is still some work to be done in the last paragraph of the results. Here, the results read like a choppy list that repeats the information in the figures and tables. I realize that it is difficult to find the right balance, especially when there are results for so many species. Please spend some more time on this paragraph, re-organizing it to read less like a list. Note that it is not necessary to describe every single variable in the text – it’s okay to only focus on the ones that proved important in the analysis.
Example for A parulus: “We did not find any strong temporal or habitat effects on DSR for A. parulus (Table S4), though estimates showed a weak positive relationship with nest height and understory cover, and a positive quadratic relationship with nest age.”

In addition, some typos remain. Here are some examples:
78: “Hight-latitude”
Table 1: Understory cover: change “interfere” to “interferes”
273-274: Confusing syntax “both of these parameters had their CI overlapped zero”
289: change “nest” to “nests”
326-327: Syntax error “In addition to support previous”
Experimental design: The authors have done a good job addressing my previous concerns about model selection methods.
Validity of the findings: Much improved, but please see comments in the “results” section below on unreasonable predictions for DSR values, and suggested changes.
Additional comments: I have completed my second review of Nest-site selection and breeding success of passerines in the world’s southernmost forest. Overall, the authors have done an adequate job incorporating reviewer’s suggestions, and the manuscript has substantially improved. My remaining concern (described above) centers around the need to clearly present the uncertainty associated with the low sample sizes in this study.

INTRODUCTION
No additional comments

METHODS
203: The sentence that starts with “We considered…”  is redundant with the previous sentence.

231: “Two species with more nests” is confusing – it’s not clear here that you’re referring to sample size.

To make the methods more repeatable, please report the number of days in each nesting stage that were used to calculate nest survival rates from DSR. This could be reported either in the main text or a supplement.

RESULTS
Please see the comments above about suggested changes to improve the last paragraph.

I also have an overall concern about the DSR values reported in this study. Many of them are exceptionally low – lower than the realm of possibility for these data. For example, a DSR value of 1.4% (line 301) translates to essentially 0% chance of success. This may be true for the handful of sampled nests, but it should not be taken as a population-level estimate. DSR values in the plots regularly dip down to levels that render a population functionally extinct. For example, a DSR value of 0.8 over, say, a 20-day nesting cycle means that only 1% of nests actually fledge young. I see two potential reasons for this, and both must be clarified in order for these results to be trusted.

(1) The sample sizes used in this study are very low, meaning that DSR estimates are highly biased and include lots of uncertainty. These data are valuable and I think that the analysis is justified (a lot of hard work when into collecting these data!), but the authors need to openly and explicitly address this limitation, report that these estimates represent a baseline for an under-studied population, and perhaps state that more research is necessary to produce more certain estimates. The fact that certain variables are important predictors is all the more impressive given small sample sizes, but as an ornithologist I cannot place much faith in the intercept DSR estimates due to the sample size. After adding sample sizes to figure 3 (see comment below), I also suggest adding a short paragraph to the discussion section providing caution about these estimates and clarifying that they represent small-sample baselines.

(2) I’m suspicious that the x-values in figures 4, 5, and 6 extend beyond the range of values sampled. For example, in Figure 4, did canopy cover for E. albiceps nests actually range from 0 to 100? Did canopy height measured at nests range from 0 to 18? Forcing a model to predict outside of the range of fitted values will produce unreasonable DSR predictions (particularly for logistic functions!), like the extremely low predictions presented in some of these plots.

275: Please clarify: “none of the habitat characteristics that we measured showed strong effects on nest location”

300: Suggested change to wording. Instead of saying “larger CI”, I suggest using a phrase like “greater uncertainty around the mean estimate”.

301: This number is incredibly low and has a huge amount of uncertainty, probably due to a very low sample size. Thus, I don’t think it’s beneficial to report it in the Results section because it is likely a biased estimate that doesn't represent the general population. I think it’s fine to include estimates for species with low sample size in Figure 3, but sample size should be stated more clearly in the figure.

312: “Eggs’ DSR” is awkward wording.

Figure 1: In the bottom panel, the CIs look like they are predicting estimates above 1, which is impossible. Perhaps there is a problem with the back-transformation of the predictions from the logit scale? Please correct this error in the predictions (e.g., plogis() function in R).

Figure 3: I suggest placing the sample size for each estimate above the lines. It is clear that low sample sizes are severely impacting estimates here (e.g., A. parulus, Z. capensis), and placing the sample sizes in this figure will help readers understand why uncertainty is so high.
The caption for this figure is rather informal and could use some clarification. There are two sentences that end with “in it”. The last sentences could be clarified with wording like “… to an exponent representing the average number of days in the nesting cycle for each species”.

DISCUSSION
As suggested above, please include a paragraph discussing sample size limitations and how they affect interpretation of the baseline DSR estimates.


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: GENETIC DIVERSITY AND STRUCTURE OF THE CRITICALLY ENDANGERED ARTOCARPUS ANNULATUS, A CROP WILD RELATIVE OF JACKFRUIT (A. HETEROPHYLLUS)
Review round: 1
Reviewer: 1

Output:
Basic reporting: Six microsatellite markers were used to assess genetic diversity in five populations of
Artocarpus annulatus. Moreover, leaf material, locality information, and demographic data were collected from them.

I agree that locate and conserve crop wild relatives is critical for the conservation of crop genetic diversity and improvement. Moreover, I acknowledge that studying and conserving A. annulatus has broad economic implications. On the other hand, I observe some important limitations in the experimental design.
As observed by authors, the results show the absence of inbreeding and genetic structure among the five populations in A. annulatus.  However, this result could be afflicted by the low number of microsatellites analysed as observed for other wild species.  In my opinion, the authors should increase the number of genetic markers to assess the real genetic diversity and structure among populations. I recognize that finding or developing new SSR markers is very demanding but this is the only way to get robust results. Alternatively, the authors should use other molecular tools such as AFLP or RAD-seq, which could allow collecting more data. Instead, I evaluate very positively to analyze the genetic structure across age classes. This result could be very interesting in conservation program.
Experimental design: Methods are described with sufficient detail but the main problem is the low number of SSR analysed.
Validity of the findings: 'no comment'
Additional comments: No additional comments