All reviews of published articles are made public. This includes manuscript files, peer review comments, author rebuttals and revised materials. Note: This was optional for articles submitted before 13 February 2023.
Peer reviewers are encouraged (but not required) to provide their names to the authors when submitting their peer review. If they agree to provide their name, then their personal profile page will reflect a public acknowledgment that they performed a review (even if the article is rejected). If the article is accepted, then reviewers who provided their name will be associated with the article itself.
The authors have addressed all comments from the reviewers, and the paper can now be accepted for publication in PeerJ as is
[# PeerJ Staff Note - this decision was reviewed and approved by Nigel Andrew, a PeerJ Section Editor covering this Section #]
I recommend accepting the manuscript with minor revisions. The authors need to clarify some terminology, improve explanations of their methods and findings, and address a few editorial corrections as highlighted by the reviewers. Once these minor issues are addressed, the manuscript will be suitable for publication.
I think that the manuscript is greatly improved by the revision. Ideally I would have preferred that the authors measure acoustic parameters using a more robust method than drawing a box by hand in Raven, but given that this was not relevant to the main finding of the paper and replicates results that have been found in many previous studies (i.e., elephant rumbles are individually specific), I do not think it is a huge issue. I have noted a few other minor corrections below, and if these are addressed I think that the manuscript should be published.
Note: all line numbers that I reference refer to the numbers in the revised manuscript with track changes turned on.
• Throughout the manuscript: This is a trivial issue, but Poole’s terminology was “cadenced rumble”, not “cadence call”
• Lines 250-251: what do you mean that you could distinguish between two callers even if they looked similar on the PCA axes?
• Lines 286-287. This statement about the ANOVA is still a bit unclear. You mention that it tested “whether the differences were significant”, but what does that mean? Significant compared to what? Do you mean to say that the ANOVA tested whether the mean distance to centroid differed significantly among individuals? If so, then please clarify this in the text.
• Line 337: “return” should be “returned”
• Line 392: the word “bouts” is repeated twice but should only be said once.
• Line 450: unclear if you are saying that elephants establish their own dominance ranks based on displacements at waterholes or merely that this is how you measured dominance rank in this study. I assume it is the latter, but that is not clear from the way the sentence is worded.
• Line 561: what do you mean by “the possibility of ‘language’”? How are you defining the word language in this statement? If by “language” you mean communication, that is already a certainty in male elephants, so why talk about the “possibility” of language as if it is still unknown? If you mean language in the same sense that it is used by linguists (a system of symbolic communication that can communicate about virtually any topic including things removed in time and place from the present via a system of grammatical rules), then I don’t think there is any basis to claim that your present results suggest the possibility of language in elephants. I don’t think that putting the word language in quotation marks helps here, because it is still not clear what you mean by that term.
• With a sample size of 48 kHz and an analysis window of 65536 samples, you have very poor time resolution (as noted in line 218). So how could you accurately determine where the overlap between two calls occurred? Also, how can you be confident that you measurements of call duration are accurate?
I find that the authors have sufficiently toned down the claims about the relative importance of dominance vs. network centrality, and now find no issues with the conclusions of the article.
No comment.
I have previously reviewed this manuscript. The authors have dealt with the concerns I raised in a satisfactory way.
I have previously reviewed this manuscript. The authors have dealt with the concerns I raised in a satisfactory way.
I have previously reviewed this manuscript. The authors have dealt with the concerns I raised in a satisfactory way.
I have previously reviewed this manuscript. The authors have dealt with the concerns I raised in a satisfactory way. Based on the changes the authors have made I have included some additional remarks as comments in the body of the manuscript for the authors to consider including. I have also made a few editorial changes.
The authors integrated most of my comments and improved their paper. However, there are still some small clarifications that are required. In particular, the authors need to tune down that they identified unique vocal signatures for each individual, as they do not present either the output of the PCA or the post-hoc tests after the PERMANOVA (equivalent to Table 3 in Wieruck et al. 2021). Or they can present one of these two pieces of evidence (then the tuning down would not be necessary anymore).
l. 270: change "confirm that" to "assess whether"
l. 351: change "the five acoustic parameters for the 19 individuals" to "the five acoustic parameters among the 19 individuals"
l. 490: change "we found significant differences" to "we found some significant differences"
l. 495-496: change "between individuals" to "between at least some individuals"
l. 498: add "However, further studies should focus on the extent of these interindividual differences"
no comment
Currently, as the authors state in their response to my comments, it seems that the acoustic parameters were not sufficient to identify individuals: they also needed to know the identity of the individuals present. I made a quick distance matrix based on the summary statistics of the acoustic parameters given in the manuscript (code available upon request) and it seems like some individuals are more similar than others, suggesting that these pairs may be more difficult to differentiate:
- #18 has shortest distance with #46
- #22 has shortest distance with #25
- #25 has shortest distance with #22
- #46 has shortest distance with #84
- #48 has shortest distance with #105/#69 (2)
- #61/#132 (1) has shortest distance with #65
- #61/#132 (2) has shortest distance with #105/#69 (1)
- #65 has shortest distance with #18
- #67 has shortest distance with #48
- #76 has shortest distance with #18
- #83 has shortest distance with #146
- #84 has shortest distance with #46
- #105/#69 (1) has shortest distance with #61/#132 (2)
- #105/#69 (2) has shortest distance with #146
- #118 has shortest distance with #76
- #119 has shortest distance with #84
- #146 has shortest distance with #105/#69 (2)
- Unk1 has shortest distance with #61/#132 (1)
- Unk2 has shortest distance with #119
#119 seems to be the individual most similar to others (most difficult to distinguish), while #67 seems to be the individual most dissimilar to others (easiest to distinguish).
As the authors already conducted the analysis, they should have the PCA output and/or the post-hoc tests allowing to assess which individual significantly differs from which other individuals. This would reinforce the paper.
l. 82-94: a bit redundant information; could be simplified. For instance: "Preference for older males is likely attributed to older males taking on similar roles as matriarchs (i.e. take on a mentor or leadership role): older males aid in maintaining social cohesion (Chiyo et al. 2011), mediate aggressive behaviors (Allen et al. 2021; Slotow et al. 2000), and provide ecological information about resource location and effective navigation through the environment (Allen et al. 2020).
In general, individuals within bonded social groups coordinate their behavior and activities, which serves to maintain social stability through the use of physical interactions and vocalizations (Seltmann et
89 al. 2013). While the evidence presented from photographs appears to support passive leadership in male elephant groups..."
l. 137: citation O'Connell-Rodwell et al. 2024b refers to the preprint of the current manuscript, which is weird.
l. 238: remove "(#105/#69 (1) and #105/#69 (2); #61/#132 (1) and #61/#132 (2))"
l. 248: add "The same was true for the pair #105/#69 (1) and #105/#69 (2)"
l. 335: add "By construction in this study, but for comparison with a previous study (O'Connell-Rodwell et al. 2012, the rate of rumbles..."
l. 346: change "43.73 minutes" to "60.40 minutes"
l. 456: add "In accordance with our definition, we found a significant..."
l. 540-542: change "Most of the other group members participate in the decision making process, as far as the time and possibly the direction of the departure, similar to the negotiation of family groups" to "Most of the other group members participate in the decision making process concerning the timing of departure, similar to the negotiation of family groups"
legend Table 2: change "as age class" to "an age class"
The reviewers unanimously recognize the significance and novelty of your study, which explores the vocalizations and social behaviors of male elephants, a topic that has not been extensively documented. The research provides valuable insights into the social dynamics and communication patterns of male elephants. However, the reviewers have raised several critical points that require attention before the manuscript can be considered for publication. Once the major revisions have been satisfactorily addressed, the manuscript can be considered for re-evaluation. The revised manuscript should be submitted with a point-by-point response to the reviewers' comments.
This study is very exciting, as it shows that male elephants may be more vocal and socially cohesive than previously realized. Prior to this study, let’s go rumbles were only described for female elephants, and the discovery that male elephants also coordinate group departures with similar vocalizations represents a major contribution to our understanding of elephant social behavior. The incorporation of data on male social networks and dominance hierarchies further strengthens the paper and provides some valuable insight into how male elephant social structure is organized. I commend the authors for this exciting discovery, and for providing figures, tables, and supplementary data that are for the most part very clear and informative. My main critiques of the manuscript are listed below. If these issues can be addressed, I recommend this manuscript for publication.
In the introduction you don’t really define what a let’s go rumble is. I think you should provide a more explicit description of what let’s go rumbles are (acoustic structure, associated behaviors, etc.) as described by Poole and others in the literature.
Also, Poole (2011) distinguished “let’s go” rumbles from “cadenced” rumbles. Please discuss how the rumbles you label “let’s go” rumbles relate to these two categories. It sounds like the overlapping rumbles following the initial rumble are more akin to Poole’s “cadenced” rumbles.
Finally, Poole described let's go rumbles as being very flat in frequency. But looking at the spectrograms you provided, it seems that your let's go rumbles have a more peaked frequency contour. Can you comment on this in the discussion, citing earlier descriptions of the acoustic structure of let's go rumbles in the literature? Could you compare the male let's go rumbles described in this study with female let's go rumbles you have recorded at the same study site? It would be really interesting to know if the apparent different in acoustic structure between male let's go rumbles in Mushara and female let's go rumbles in Amboseli is due to sex differences or population differences.
Minor comments for improving clarity of language:
• Line 92: “the high-ranking male” should be either “a high-ranking male” or “the highest-ranking male”
• Line 196: “or” should be “and”
• Line 280: unclear what you mean by “this case”. What case are you referring to?
• Line 288: what do you mean by “magnitude = moderate”?
• Lines 311-312: Do you mean “the assumption of homogeneity of variance was not violated?”
• Line 327: It is a little confusing to say that the keystone male initiated departure by calling 61.9% of the time and was always the first caller in the bout. If he only initiated departure by calling 61.9% of the time, then how was he “always” the first caller in the bout? Did you mean that he was always the first caller in bouts that he participated in? If so, please clarify this.
• Line 357: “who” should be “with whom”
• Line 398: please specify in what way the two periods did not significantly differ. E.g., “the departure and pre-departure periods did not significantly differ in duration”
• Line 437: should be either “so many fewer” or “fewer”, not “so fewer”
• Figure 4, panel B: what exactly is the y-axis showing? Is it the mean association index for each individual, averaged across all the dyads that include the individual in question? Presumably you don’t just have one association index for each individual, instead you have an association index for each possible dyad. So what does it mean when you say that this plot compares the association indices for individuals who participated in LGR bouts vs. individuals who did not participate?
• Figure 4 legend: you said “three of the LGR event initiators”. Did you mean “the three LGR event initiators”? From the main text it sounds like there were only 3 initiators total in your study.
• In the two data spreadsheets provided, the tab at the bottom doesn’t match the file name. The file labeled S1 has a tab labeled S2 and the file labeled S2 has a tab labeled S1.
Overall the methods seem sound and appropriate for the research questions.
However, I am a little concerned about the reliability of your acoustic measurements, given that they may be highly dependent on how close to the call the selection boxes were drawn. Did you have any mechanism for ensuring that the selection boxes were drawn in a similar manner for each call? I suggest that you do one of the following two things to make sure that your measurements are not unduly influenced by the placement of the selection box:
1) Measure the same calls with selection boxes drawn in different ways (e.g. once with the box drawn as close as possible to the call, and once with more space between the 4 edges of the call and the box), run the MANOVA on both sets of acoustic measurements, and see if you get similar results.
2) Use measurements like fundamental frequency and formants that are based on the call itself rather than a selection box. This would require using a different sound analysis program. Praat is a free sound analysis software program that many elephant researchers use for measuring f0 and formants, but it is admittedly not the most user-friendly software. Another option is the R package soundgen. This package includes two shiny apps (pitch_app and formant_app) that allow you to measure fundamental frequency and formants, respectively, in a graphical user interface that allows manual corrections to the measurements.
In addition to this, there are some areas of the methods where the language is a little unclear or where more detail is needed:
• Lines 155-158: Please state the sampling rate of your recordings. Otherwise it is impossible to determine if the analysis window you used was appropriate.
• Line 187: How can you be confident that ear-flapping alone was a reliable way to identify callers? In my experience elephants don’t always flap their ears when calling and also may flap their ears without calling.
• Line 196: it is unclear if you only used rumbles that were overlapping or if you used rumbles that occurred within 2 sec of another rumble without overlapping. There seem to be contradictory statements about this. Also, why did you choose 2 seconds as the cutoff? Didn’t you find in a previous paper with female let’s go rumbles that 1.5 seconds was the best cutoff point for inclusion in the same bout?
• Line 198: When you only measured part of a rumble due to overlap, how did you ensure that these measurements were comparable to rumbles where you were able to measure the full call? For example, wouldn't time measurements like 90% duration be heavily affected by whether you measured the whole rumble? Wouldn't frequency measurements also be affected when the frequency is not constant throughout the whole call? Did you have some kind of systematic criterion for deciding when there was too much overlap with other calls to allow measurement?
• Line 200: Why did you only use the first three rumbles in the bout? What was the purpose of excluding subsequent rumbles?
• Line 205: why did you assume that the same caller can’t rumble twice in a row? Were the calls always overlapping? I agree that it is safe to assume that the same individual can’t produce two calls that overlap with one another, but if the two consecutive calls don’t overlap, then I don’t think you can assume that they were necessarily made by different callers.
• Lines 207-211: Can you please provide more detail on how you identified individual callers using principal components? I’m guessing that you measured calls where the caller was known for certain, calculated PCA on the acoustic parameters of all the calls, clustered the calls based on their principal component values using something like multidimensional scaling, and then compared the call with an unknown caller to each of the clusters to see which caller it was closest to. But I’m not sure if that is what you did because it isn’t explained in the text.
• Lines 213-220: you don’t mention measuring fundamental frequency in this paragraph, yet fundamental frequency is included as one of the acoustic measurements in Table 2. Did you include fundamental frequency in your analyses, and if not, why not? Also, why is fundamental frequency included in Table 2 but not in Table 3?
• Line 238: I think you have done the right statistical test here, but I think you have described it incorrectly. I am not an expert on statistics so it is possible I am incorrect, but I don’t think that “high within-individual variation” has any relevance to the reliability of the MANOVA, nor do I think that this is what the betadisper() function tests for anyway. Rather, my understanding is that the betadisper() function tests whether the variance-covariance matrix is homogenous; in other words, whether different individual callers have similar variances and covariances (the actual magnitude of the variances and covariances is not important). I suggest rewording this statement to something like the following: “to test the assumption of homogeneity of the variance-covariance matrix for MANOVA, we used the betadisper() function in the “vegan” package”.
• Line 239: “followed by an ANOVA test”. I'm confused about what this ANOVA was. What was the response variable and what were the factor(s) in this ANOVA? What was the purpose of running this ANOVA?
• Lines 249-250: how did you make a binary distinction between “highly-associated” and “not highly-associated”? What was the definition of these two categories?
• Line 254: Why did you use a one-tailed test (alternative = "less")? Usually, it is recommended to do two-tailed tests unless you are only interested in determining whether there is a difference in one particular direction, because two-tailed tests are more conservative.
• Line 313: As I mentioned above, I think that you did the right statistical test but I believe your description of it may not be accurate. I don’t think that the homogeneity of variance test has anything to do with assessing whether differences between individuals are due to high between-individual variation vs. high within-individual variation, nor do I think that high within-individual variation could cause there to be significant differences among individual callers in the MANOVA in the first place. Instead, the betadisper() function tests for homogeneity of the variance-covariance matrix, essentially assessing whether the variance for each caller and the covariances for each pair of callers are similar. If this assumption of even variance and covariance across all the callers is violated, this could potentially make it seem that there are differences among callers even if this is not the case.
I think that the analyses of social network structure and dominance are a very valuable part of this paper, and commend you for collecting and analyzing these data. However, given that you only observed 4 different males initiating LGR bouts and were only able to collect dominance data for 3 of these males, I think you should tone down the certainty of your conclusions about the importance of network centrality vs. dominance in determining who initiated LGR bouts. I think you can say that your data provide preliminary evidence to suggest that network centrality may be more important than dominance in determining who initiates a let’s go rumble bout, but I don't think you can draw firm conclusions about this based on such a limited sample size.
In line 62, you stated that my recent paper (Pardo et al. in press) found that elephants can single out specific individuals with a "noun-verb combinatory call". As exciting as it would be if there were evidence for noun-verb combinations in elephants, that is not actually what we found nor what we set out to test. We found that elephants address one another with name-like calls, meaning that calls contain information identifying the intended recipient, and that elephants can determine if a call was addressed to them just by hearing it. This has no bearing on nouns, verbs, or call combinations.
This is a very interesting study that fills a gap in our knowledge about the role of communication in the social behavior of adult male elephants. I recommend publication of this work pending the authors addressing the comments I have made in the body of the manuscript and in this review.
The manuscript is clearly written in unambiguous, professional English. There are only a couple of places where I thought the authors could be a little clearer and I have mentioned these directly as comments within the manuscript.
While the article includes a good introduction and background to demonstrate how the work fits into the broader field of knowledge, at least one critical study has been omitted.
The study, Poole, 2011, documents similar behavior and calling patterns in free-ranging female elephants in Kenya. O'Connell et al describe a male initiator of a let's go rumble (LGR) followed by a "LGR bout" that is composed of overlapping rumbles by alternatively calling socially bonded males. In contrast, Poole 2011 differentiates between a series of let's-go-rumbles typically given by a single proposer and a bout of overlapping cadenced-rumbles by alternating individuals as part of what Poole proposes is negotiation on a course of action. Poole argues that the let's go rumble (with associated behaviors described as the Let's Go Stance) is a proposal given by extrovert family members that suggests both departure and its directionality ("I want to go this way, let's go together"). Whereas, the overlapping cadenced rumbles occur when negotiation related to some form of decision-making by a family of elephants needs to be agreed (e.g. when to depart, where to go and whether to remain together or to split). These patterns of calling and the associated behavior of each call sub-type is described in detail in Poole 2011 and is also available to view/hear in The Elephant Ethogram.
It is interesting that while the behavior described by the O'Connell et al is remarkably similar (given the differences between closely bonded family units and more loosely associated males) to let's-go and cadenced calling originally described by Poole, the structure of the rumbles presented in this paper are different from the structure of let's-go rumbles (Poole et al 1988; Poole, 2011) and cadenced-rumbles (Poole 2011). While the rumbles by male elephants described in this paper are slightly modulated and show a fairly even amplitude across the harmonics, the let's go and cadenced rumbles among female elephants in Amboseli are flatter and the amplitude of the F3, F4 and often the F5 are noticibly lower (almost absent) than the F0, F1, F2 and higher harmonics.
Otherwise, the manuscript includes the correct article structure and clearly legible, understandable figures and tables that are appropriately described and labelled. I did not find the raw data although the authors noted that their raw data would be uploaded as "supplemental files 1 & 2 (DataS1 and DataS2).
The submission clearly defines the research question, which is relevant and meaningful. The authors describe and fill a knowledge gap on male elephant vocal communication social group cohesion.
The investigation has been conducted rigorously and to a high technical standard. The research was observational in nature and was conducted in accordance to ethical standards.
Methods were described with sufficient information to be replicated by another investigator.
Conclusions are well stated, linked to original research question & limited to supporting results, however I would ask the authors to discuss their results in the context of the findings of Poole (2011) who described let's go and cadenced calls separately. Further, I would ask the authors to comment on the difference in the structure of the rumbles presented in this paper versus from the structure of let's-go rumbles (Poole et al 1988; Poole, 2011) and cadenced-rumbles (Poole 2011) described by Poole. Recent work by Pardo et al (unpublished) has found structural differences in rumbles recorded in the same context, but from different populations. This begs the question whether the obvious structural differences between the let's-go-rumbles produced by males in Namibia and the let's-go-rumbles produced by females in Kenya are sex or dialect related. Either way the similarities and differences in the structure, specific calling pattern and participants are remarkable and open up the possibility of further investigation.
no further comment
This study aims to show that male elephants use vocalisations to coordinate their group movements, even though the literature has long considered that these males form loosely-knit groups, with little role for communication in coordinating activities. Taking advantage of a long-term project on elephant behaviour, the study identifies calls that could potentially be used to synchronise the departure from a waterhole, particularly between individuals that are socially close. The perspective given in the introduction is relevant and the manuscript is generally well written, even if there are a few typos and inaccuracies.
Besides, a graphical representation (e.g. a timeline under Figure 2 highlighting the various bouts and the associated number of callers) of what is meant by events and bouts could be helpful.
l. 86-88: sentence unclear.
Raw data: typos in the Sheet names indicating “DataS1” and “DataS2”: the sheet names have been inverted.
However, some important issues or even flaws are currently present in the reporting or the analysis. In particular, more information is needed (inclusion criteria) on the number of gatherings at the waterhole that did not give rise to LGRs or the number of gatherings at the waterhole that did give rise to LGRs but were not analysed. This could be added around l. 165, where the authors describe events. The inclusion tree could report the total number of recorded events, the number of events for which audio recordings were not available (criterion 1), the number of events for which males did not arrive and depart together (criterion 2), the number of events for which females were present (criterion 3) and so on. The last cell of the inclusion tree would then be the 7 LGR events included in the analysis (which at first glance does not seem like a big number, but the inclusion tree could put this number into perspective). Ideally, the inclusion tree would start by the total number of visits recorded at the waterhole, as this number should have been used to construct the social network of co-presence at the waterhole.
Even though the authors refer to another paper, it would be important to have more information on the data used to establish the social network, in particular the sampling effort (i.e. number of days per season…). Reporting it could help to realise the amount of work that has gone into collecting this hard-to-collect data. Besides, using the social network of 2007 for all analyses raises the question of the stability of this social network over several years, which is not mentioned in the manuscript. L. 242-244, it is stated that this social network has “data for all individuals included in “let’s go” events”; but in Table 2, 7 individuals (#132, #76, #83, #84, #118, #119 and #146) appear that are not present in the 2007 social network. Did you consider the possibility to construct the social network over several years or does it not make sense? If so, why is using a social network from a specific year a better option?
l. 205-207: it was not clear where this assumption was coming from. After reading the associated reference, it seems that this assumption derives from the fact that most bouts have overlapping rumbles that could therefore not come from the same individual. I would thus rephrase “where it is assumed that overlapping rumbles cannot be produced by the same individual”.
l. 207-211: Principal Components visualizations are a good way to assess individuality, but only if most individuals can actually be individually identified, which is currently not justified by the results (see “Validity of the findings”).
l. 211: according to Table 2, it seems that another pair of individuals was also difficult to distinguish: #61 and #132 [#61/#132 (1) and #61/#132 (2)]
l. 248: 26 individuals are indicated, but only 25 individuals in Figure 4.
l. 249: “223 unique dyads”, out of 325 possible combinations have been observed.
l. 249-250 & 319-322: wording not very clear. What I understand is that 64 dyads involved individuals that were both taking part in LGRs, while 159 dyads involved at least one individual who did not participate in LGRs. Dyads involving two individuals participating in LGRs had higher association index than dyads in which at least one individual did not participate in LGRs.
l. 226-228: at first, it seems odd to compare the number of rumbles in the departure period to the number of rumbles in the pre-departure period, because the distinction between the two periods starts when an elephant emits a rumble and indeed no vocalizations were recorded in the pre-departure period (l. 296-297). After reading the reference l. 170, I understood that in this older study, rumbles were not always classified as LGR. But for the current study, comparing the number of rumbles in the departure and the pre-departure period seems circular due to how the periods were defined and could be removed, as well as the corresponding discussion part (l. 408-416): it seems like the comparison between male and female groups is mostly driven by how rumbles were defined in both studies (only LGR in the current study in male groups and other possible types of rumbles in the O’Connell-Rodwell et al. 2012 study in female groups). But maybe I misunderstood something and then you should explain better which types of rumbles were considered in both studies.
There seems to be a methodological misunderstanding on how to assess the uniqueness of the calls between individuals (l. 236-239). Testing the homogeneity of variances will simply assess whether some individuals in the population are more variable than others, but not if (and which) individuals differ from each other. Therefore, the associated inference l. 311-314 is wrong: the fact that the homogeneity of variances is not significant implies that all individuals appear to have similar variation across the characteristics of their rumbles. It does not say anything about inter-individual variation per se. To test for inter-individual differences in rumble characteristics, one could perform pairwise comparisons across each dyad, as has been done in Wierucka et al. (2021) Table 3, a paper that the authors cite. The most salient characteristics for inter-individual differences could also be looked for, as in Table 4 of Wierucka et al. (2021).
l. 244-247: I did not understand what these “five additional groups of individuals” were and what they were adding to the data; where can we find information about them?
l. 266-268: could be more precise: “16 individuals involved in LGRs were in the 3Q age class, with only 3 individuals…”.
l. 275: “(Fig. 1C)”.
l. 276: “and a close”.
l. 355-358: the end of the sentence does not sound correct “… recruited those who they had affiliative relationships”.
l. 398-399: “… the departure period was not significantly different from the pre-departure period…”: in which respect was it not different?
l. 420 & 445-446: I would remove all references to direction of travel, as there is little data presented about this in the paper.
l. 225, 408 & Figure 2: why “post-departure”? Shouldn’t it just be “departure”?
Figure 4: “n = 26 individuals”, but only 25 nodes on the graph. I would rephrase part of the legend, along these lines “(B) Violin plot of the association indices for dyads in which at least one individual was never observed in an LGR group (n = 159 dyads) and for dyads in which both individuals were observed in LGR groups (but not necessarily together) (n = 64 dyads)”. Individual 61 in blue, even though listed as producing rumbles in Table 2.
Table 2: why not add a column “Age category", separated by commas for individuals present over several years?
All text and materials provided via this peer-review history page are made available under a Creative Commons Attribution License, which permits unrestricted use, distribution, and reproduction in any medium, provided the original author and source are credited.