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Thanks for making those final changes.
[# PeerJ Staff Note - this decision was reviewed and approved by Dezene Huber, a PeerJ Section Editor covering this Section #]
The reviewers were all very positive about the changes that you made, but have suggested just a few very small revisions. If you can make those and resubmit I will be happy to accept the paper for publication.
I reported this in the earlier version.
I reported this in the earlier version
I reported this in the earlier version
I am satisfied with the author's revision. They have addressed most of my concerns. I recommend acceptance of this manuscript but with minor revision. In lines 232-238, the author still needs to include some sentences on why it is acceptable (or justify) to have differences in the time period of averaging for the Sahel and Willow Warbler.
See below
See below
See below
Overall, I am satisfied with the authors additions to this manuscript. My concerns have been address. I have only a few minor suggestions below.
General: I believe the terms used for the different AA periods in the supplement (which uses AA1.4_15.5, etc.) were not changed to reflect changes to those terms in the main manuscript (which uses MP1, etc.). I suggest making sure these are coherent.
L 125: Note lat/lon Bukowo and note that it is in Poland
no comment
no comment
no comment
The authors have made a great effort to revise thier manuscript considering the reviewer's comments and suggestions. They have satisfactorily and in great detail replied to all points raised by the reviewers, and have made changes accordingly. I particularly appreciate that in this new version of the manuscript the authors are more cautious with their interpretation of results, presenting alternative explanations. Moreover, they have tested and taken into account possible confounding effects, and have excluded those analyses and parts of the discussion that were inconclusive (e.g. the analysis of wing length). Thank you to the authors for giving background information on pied flycatchers and common whitethroats migrating through Bukowo, which allowed me to better understand their reasoning.
I was asked to take over the handling of your paper, as the previous Editor was unavailable.
The three reviewers have been very constructive in their comments, and all agreed that the manuscript has been much improved. However, all reviewers have identified a number of major issues that compromise the conclusions that can currently be drawn from the research. In particular Reviewer 1 and 3 have highlighted some remaining problems with the limitations of the data that have been used and the approach taken to analyse that data. In noting these issues, the reviewers did feel that they can hopefully be addressed, and that will result in a more insightful study. Please engage very thoroughly with all of the comments raised by the reviewers in your revised version.
Comments attached!
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Overall, I find both the text and figures to be much clearer, compared to this initial submission. I applaud the authors on their efforts here and in addressing concerns (from myself and the other reviewers) with the previous version of the manuscript. I found the _1yr notation and renaming of the ‘periods’ (early, mid, late) to be particularly helpful. While this paper is quite long, a substantial amount of information is presented here (both in the main text as well as in the supplement). Detailed explanations of the effect of each predictor are given, which may be useful for some readers. Some points could be conveyed more succinctly throughout the text, though I don’t think this is a major point of concern.
My remaining comments focus primarily on the readability of the manuscript. After addressing these issues, I feel this manuscript would be suitable for publication and make a nice contribution to the existing literature in this area.
The general questions and approach used to answer these questions is sound.
After addressing previous concerns from myself and other reviewers, I found assertions to be support by the findings of the authors' analyses.
This is a resubmission. I reviewed the initial submission of this manuscript as well.
More detailed comments on the manuscript:
INTRO
Fig. 1: I find the ‘migratory divide’ to be somewhat confusing – this is seemingly used to separate the two subspecies breeding ranges, but also separate Ph. t. tochilus pre- vs post-Bukowo migration. Suggest removing dotted lines associated with ‘migratory divide’ (particularly since there are already two types of dashed lines in the figure).
Fig. 1: I’m confused as to what the months indicate. The caption states those months are when birds occur in various regions. But if that were the case, why is there any _1y?
METHODS
General: Best not to refer to the ‘nominate subspecies’ for those not familiar with which subspecies is, in fact, the nominate subspecies. This term is used throughout the manuscript.
L 320: Just as a note, normality of the predictors isn’t a necessary condition for linear regression. The focus should be on the normality of the residuals (deviations between the linear predictor [e.g., regression line] and data points). Transformations are typically applied to the response variable. This transformation of the predictor may serve to curb the influence of ‘outliers’ though and I don’t think the analysis necessarily needs to be rerun.
RESULTS
Fig. 3: Lettering for figure panels needs to be fixed. B and C should be swapped, based on how they are referred to in the text (e.g., L331-334).
Table 3: It seems there is something missing after p < 0.0 in the caption.
Table 3: It seems the _1y is missing from the variable names in the table.
Fig. 4: While not a formal analysis, I like the exploratory nature of this figure and think it conveys valuable information to the reader.
Fig. 5: The x-axis appears to be the standardized square roots of number of juvs rather than the
square-root of the standardized number of juvs (as noted in the figure).
DISCUSSION
L 499-509: The addition of these points strengthens the argument here.
No comment
No comment
The authors have thoroughly revised the manuscript and replied to all of my comments. They have followed my suggestions to test some of their central assumptions. Despite this effort, however, they could not concinigly demonstrate differential passage of the two warbler subspecies, which winter in different areas in Africa. Although this conclusion is plausible, and their analyses and data do not contradict them, it is not supported by the results of the additional tests they have conducted:
Neither do their ringing recoveries show that P. t. acredula migrates earlier than P. t. trochilus at their ringing site (see, below), nor does the analysis of species wintering exclusively (or predominantly) in the wintering areas of the two willow warbler subspecies, i.e. western and eastern Africa, give clear results. While the results for Sylvia curruca are in line with the results predicted, the analyses of Ficedula hypoleuca and Sylvia communis are not (see, table R1). The authors explain the discrepacy (i.e the influence of IOD on migration of birds wintering in western Africa) by the observation that individuals of these species breeding in northern and eastern Europe may winter in eastern Africa. However, to my knowledge, most pied flycatchers winter in western Africa. Thus, if the author’s interpretation of results is true, the IOD should not significantly influence migration of this species. How could we then interpret the strong effect of IOD on the migration phenology of this species?
Furthermore, the author’s conclusion that the fact that wing-length decreases over the season supports the assumption that P.t. acredula migrates earlier than P.t. trochilus (lines 515-517) is not convincing. As they discuss in the paper (517-520), this decrease in wing-legth could be due to differential migration among sexes, females, which have shorter wings than males, migrating later. This could also be due to juveniles, which also have shorter wings, migrate later than adults. Can you exclude that during spring passage you catch a significant number of juveniles on passage? The fact that juvenile numbers in autmn significantly explains annual annomaly in spring passage (figure 5), could be an indicator that the proportion of juveniles in spring strongly affects spring phenology. To control for this pontential source of error you should include this variable in all the models, even if you need to eliminate some 1-2 years from the analyses. Would this change your results?
The discussion of the effects of different climatic indices (lines 536-731) is way too long and speculative, particularly when it refers to the potential effect of climatic effects on different populations, which presumably winter in different areas in Africa (as deduced from the differential effects of different climatic indices). I would suggest shortening this part and omitting speculative interpretations of the results.
Specific comments
Lines 499-509: Is there any evidence that Ph. T. acredula migrate along the coastline instead of crossing te Baltic Sea? Please, give reference.
Lines 510-517: The ringing dates do not support the assumption that Ph. t. acredula migrates earlier than Ph. t. trochilus. The only presumptive record of the acredula subspecies was ringed later than 8 of the 9 presumptive Ph. t. trochilus individuals you caught. Therefore, these data, if considered informative, rather suggest the opposite of what you expect: Ph. t. trochilus migrating earlier than Ph. t. acredula. Of course, the value of these few records is limited, since you do not have data on sex are age, which could confound any result. Since these data are not conclusive, I would suggest that you either delete this paragraph or revise the interpretation of results.
Lines 515-534: The overlap in wing-length between the two subspecies is considerable (Fig. S6). Therefore, I don’t think that you can use wing length to separate them. Moreover, Fig. S6 shows that the largest wing lengths are not found in individuals that are trapped very early in the season, but in the middle (between, April 20 and May 7). The same hold true, for the willow warblers with the shortest wings. Considering that males have longer wings than females and adults longer wings than juveniles, any change in the composition of subspecies, sexes or age-groups will cange the distribution of wing lengths and of arrival dates. You should explicitly state this limiation in your dataset and the interpretation of results.
Im conclusion, I think that this is a interesting study with new and relevant results. However, considering the limitations of the data and the ambiguity of the results of the tests I suggested, the authors should be more cautious with the interpretation of results and discuss in more detail the shortcomings of the study and alternative interpretations of the results.
Please pay special attention to several methodological issues raised. First, you need to be much more specific about the large-scale climate indices you use, specifics of how they are calculated, and a stronger roadmap for your reader to be able to follow. I found Fig. 1a to be helpful, although very busy - and adding panel b to it simply made it more busy. It was not clear why those results were there (they seemed more appropriate for the results section) and I also found it very difficult to keep track of all the sub-periods (3? 8? 11?) and climate variables (9? 13?) and make sense of the results.
Attend carefully to the cautions laid out about what conclusions you can draw that were highlighted by reviewer 3. This reviewer also provides an idea to make an independent test of these ideas and so you should consider the tractability of that.
Overall, please consider how you can make the analysis, presentation of the analysis, and your conclusions more clear. Do not rely so heavily on the previous paper - this paper should stand alone.
All the authors agreed that this was an interesting paper but they each had concerns, largely coming from three different perspectives. Addressing these concerns will substantially strengthen this paper.
[# PeerJ Staff Note: Please ensure that all review comments are addressed in a response letter and any edits or clarifications mentioned in the letter are also inserted into the revised manuscript where appropriate. It is a common mistake to address reviewer questions in the response letter but not in the revised manuscript. If a reviewer raised a question then your readers will probably have the same question so you should ensure that the manuscript can stand alone without the response letter. Directions on how to prepare a response letter can be found at: https://peerj.com/benefits/academic-rebuttal-letters/ #]
Comments attached!
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Overall, I found the work to be well cited, putting this work in the context of previous work to come before it. I do, however, think that there are areas that could be more concise, which would improve the readability (and hence, accessibility) of the work. I found some sections to be somewhat repetitive.
The general questions and approach used to answer these questions is sound. More detail is needed in areas to more clearly describe what was done. See detailed comments in 'General comments to the author' section.
Some additional work is needed to clarify what was done and some additional tweaks to analyses are needed. For instance, there are areas where p-values are presented that probably should not be. There are other areas where multiple comparison need to be controlled for if presenting p-values. Other times I was unsure what was done, making it difficult to assess the appropriateness of the approach used. Those areas are noted in the detailed comments below.
General comments:
This study makes use of a long-term dataset to attempt to better understand what drives the migratory phenology of a long-distance migrant. The approach is interesting and does go beyond what was previously done. The suggestion that these various indices influence arrival at different periods of time is interesting, as is the notion that one sub-species arrives before another on the Baltic coast (the opposite of what is seen on the breeding grounds). Overall, however, I think there are a number of points that need to be addressed before this work is ready for publication. See below for more detailed comments on the manuscript:
INTRO
L 74: I don’t think “Previous life stages” is the best term here. Something like ‘at overwintering grounds’ would be more appropriate.
METHODS
Fig. 1: The x-axis in B-J is difficult to interpret. I think this caption could also be more succinct. Also, I think all subplots should have the same y-axis range.
L 179: So number of juvenile captured for a given day was actually number of juveniles captured for a given day / total number of birds captured throughout the entire season?
L 193: Again, I’m not sure that ‘life stage’ is the best language here and overwinter period would be better. How were these months selected (the reader should not have to refer back to the previous paper for this)? From Fig. 1, it looks like the NAO has an effect ranging from Europe down to western Africa, above the Sahara. Are these birds only arriving in this region of Africa in April? It also isn’t clear which of these are ‘lagged’ (from the previous year) and which are not. This needs to be presented in Table 1. At the moment is looks like NAO in the Jun-Jul was used as a predictor of arrival in May of that same year (I don’t think this was what was done, but it is presented this way in the table).
L 197: The reader should not have to refer back to the previous publication for this information.
Fig. 2: The labeling of these period is not very intuitive, making it difficult to follow and interpret the figure as a reader. The larger windows represent 1/3 of the total area under the cross-year average curve. How were the smaller windows selected?
L 229: What does this mean? It was stated previously that they were standardized. Is it that they were modeled as a linear function of AA rather than as a polynomial, etc.?
General: If the question of interest is what drives migration, I’m not sure including year in these models is appropriate. There could be one models looking at trends over time and a set of models exploring the influence of climatic factors on phenology. In reading further down, it seemed like year was not included, but then in the Discussion it’s clear it was. I think what needs to be done needs to conveyed more clearly.
L 234: Please explain what this is. I assume this means that AICc was calculated for every subset of the full model (all covariates).
L 245: Somewhat odd to refer to ‘successes’ here. Suggest removing.
L 254: For which model were these pR calculated from? The full model? The “best” model?
L 265: How large? Is the possibly due to changing migration corridors from year to year?
RESULTS
Table 2: The best models are presented here. Typically models within 2 or 3 AIC of one another are considered equivalent. I see that more results are presented in the supplement which is helpful. I wonder if presenting something like the weights of each predictor (climate index) would be helpful here (basically, a metric how often each variable shows up weighted by the AIC of the model). Also, I find it somewhat odd to present p-values with these many models. Better just to present the r squared values, in my opinion (given that many models are fit in this type of analysis and multiple comparisons are not controlled for).
Fig. 3: The text is very small in the figures. It would be helpful to increase the font size.
Table S11: If anything about statistical significance (i.e., p-values) is going to be presented here, multiple comparison need to be controlled for (using something like a Benjamini-Hochberg correction), as multiple statistical tests inflate the possibility of false positive (incorrectly saying there is an effect with there is no effect).
S12: Multiple comparisons should be accounted for here as well.
L 345: What does SCAND having an effect have to do with the relationship between breeding success and timing? I think it is interesting to look at the effect of (a proxy of) breeding success, but I don’t understand the logic here.
DISCUSSION
General: I found the Discussion to be somewhat repetitive, with statements made multiple times.
L 362: Which indices were related to what areas? Please be explicit. It seems that SOI is representative of conditions in both southern and western Africa. How do you disentangle the effect of SOI on western vs. eastern migrants? How was it determined which geographic areas each index affected most strongly?
L 391: Temperatures on overwintering grounds? Breeding grounds?
L 407: I don’t think it makes sense for year to be included in the ‘full model’ used for model selection, as noted above.
L 412: Earlier in the paragraph, it’s stated that some indices showed trends over time and not others (L 401). Now it’s mentioned which indices these are. I think the writing could be more concise here, simply stating which ones changed. I think this could also improve the readability.
L 432: Are they actually under weaker pressure to arrive early? Is there evidence to support this? Females still need to breed at a time that matches favorable environmental conditions, even if they aren’t establishing territories.
L 592: This is SCAND the previous year, is that correct (given that birds have already migrated through the area by the time June comes around)? The Discussion makes it seem otherwise. I’m unclear on what was done here.
L 628: How was effort controlled for? What about pop size (number of adults, since more adults will = more juveniles without having higher breeding success)?
L 637: Wouldn’t they be second year birds (i.e., one year old) if they are arriving the spring after they were hatched?
L 651: I’m not sure this paragraph is necessary
General: Somewhat surprised that no mention of the potential role that future tracking efforts might play in confirming the proposed ecological explanation for the varying temporal effects of these indices (i.e., that one sub species arrives earlier than the other along the Baltic Coast).
no comment
In this manuscript, the authors use the same dataset and the same methods used in a previous paper (Remisiewicz & Underhill 2020; DOI: 10.7717/peerj.8770) to address a similar question. The main difference to the previous study is here the authors analyze the effect of climate indices on three main sub-periods of passage (early, middle and late) and another 8 “minor” sub-periods. Furthermore, in this study, they consider the effects of juvenile counts in autumn, as a proxy for breeding success, on spring passage.
I find the manuscript interesting, since it presents a new approach using the effects of different meteorological conditions on the trapping patterns of willow warbles during different periods of passage to identify different populations of birds wintering in different areas in Africa. Although there is some overlap with the previous manuscript, this new approach and the novelty of results would justify the publication of this manuscript. Although I find the manuscript well and clearly written, I find it too speculative for the reasons outlined below.
One problem with the study system used, is that neither birds from different subspecies can be identified, nor can first-year birds be separates from adults, or males from females. Differential migration is found in most European passerine migrants, whereby adults migrate earlier than juveniles and males earlier than females. Differential effects of climate change on the timing of spring arrival and breeding in male and female, and juvenile and adult willow warblers were found by Hedlund et al (2015). Since there is evidence for differential migration in this species, the effects of age, sex and population are potentially confounded. Because of this, you should interpret your result with caution. How could changes in the age and sex composition of the willow warbler population on passage have influenced your results? You should discuss these effects as a potential source of error.
Although, I find the explanations for some of your different results plausible (e.g. for why P. t. trochilus migrates later than P. t. acredula, lines 465-474, or why SCAND and the number of juveniles in autumn delayed migration in late spring, 588-649), they are speculative since they lack empirical evidence. I would ask you to provide some empirical evidence for your explanation: e.g. ringing recoveries from your station that indicate that birds recovered in, or from, southern Sweden (or Norway) migrate through your station later in spring than birds recovered in northern Sweden (or Norway), Finland or Russia. If you do not have such data, you should explicitly state on which assumptions your explanations are based, and which data would be needed to test them.
The reason given for subdividing the migration period is that you assume that birds migrating though Bukowo at different periods in spring have wintered in different areas. Thus, they should experience different wintering conditions and different conditions during migration. This, however is an untested assumption. In principle, the effects of different climatic indices could be indirect, e.g. through correlation with other indices or meteorological variables in other areas, or due to interactions with species, which are affected directly by these indices, during migration. The main problem of the subdivision of the migration period used is that it is somehow arbitrary, and that it is not based on actual knowledge of differences in the timing of passage between willow warblers originating from different breeding populations. Although you justify the subdivision into the 3 periods by practical criteria (lines 651-673), and the results obtained further justify your choice (667-671), a validation of results would be needed.
To demonstrate that your approach yields reliable results and that your conclusions on willow warbler migration are correct you would need to test your main assumptions, i.e. that differential effects of different climatic indices on passage reflect different wintering areas. A conclusive test would be repeating your analyses with a species exclusively wintering in western sub-Saharan Africa - the wintering area of Ph. t. trochilus – (e.g. Acrocephalus scirpaceus), and a species wintering exclusively in southeast Africa, the wintering area of Ph. t. acredula (e.g. Sylvia curruca). If you found that in these species the same climatic indices, which had an effect on the presumptive spring migration passage of the two willow warbler subspecies, then you would very convincingly demonstrate that (1) with your method you can identify different wintering areas and (2) that the climatic indices affecting these areas have an effect on spring migration of trans-Saharan migrants.
Specific comments:
Line 305: In table 2 the variance explained is 30.7% not 24.9%.
Lines 450-453, 465-473: According to Hedenström & Pettersson (1984) P. t. trochilus arrives about 2 weeks earlier that Ph. t. acredula in central Sweden. Is it plausible that willow warblers would need more than a month longer to fly to central Sweden via the Baltic States, Russia and Finland than directly via Denmark or crossing the Baltic Sea? You may estimate the time it takes if you know how much longer this route is and you know the approximate migration speed of willow warblers in spring.
Line 631: Can you exclude that populations change migration routes from year to year (e.g. because of winds)? If they did, this could explain the unexplained peak of juveniles in 1982.
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