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Thank you for your responses. I continue to think that, given the use of a Bayesian framework, the entire analysis could be done in a single model, but that does not mean that the current results are invalid, so I'm happy to accept the current version.
Thank you for your careful revision and response letter. One of the original reviewers and I have re-read the paper and find it much improved. We both have additional comments about the analyses, however, and I would like to see them addressed before I make a final decision.
First, I remain confused about how the different analyses relate to one another and concerned that what could be a fairly simple analysis has become overly complicated with multiple techniques overlapping one another. Maybe it is because I am not very familiar with all of the methods you are using (i.e., TITAN), but I’m having trouble understanding the relationship between the hierarchical Bayesian model described in the paragraph starting on line 160 and the subsequent analyses. Is it that you are only using this model to obtain adjusted values, then drawing (adjusted) values from the posterior distributions for use in subsequent analyses? And, if that’s the case, am I correct that the subsequent analyses are not Bayesian? If I am right about this, then I’m unclear why one would not simply add the potentially explanatory variables (forest loss, compactness, etc.) to the Bayesian model and do everything in a single analysis. Please do not hesitate to explain if I am just misunderstanding the approach you have taken. But, the apparent approach of using one analysis to adjust the dependent variables, then another to look for thresholds, then yet another to look at the relative importance of different variables, seems unnecessarily complex.
Second, the reviewer brings up a related point in their comments on multiple model comparisons. Please address this concern either by using a model comparison approach, as suggested, or by providing a detailed rationale for not doing so (e.g., in a fully Bayesian model it may not be necessary, depending on how the model is set up).
Please also address the additional comments below and the other comments from the reviewer. I have also attached a pdf with some minor wording edits.
Line 24: I don’t find this definition of compactness to be as helpful as it might be, because it just begs the question of what is “clumpiness”. Please define in terms that explain the spatial patterning. Maybe something like this “… as a measure of how clustered exurban development was in the area surrounding …”
Line 29 (and 33): “Landscape” vs “local” are relative terms that will likely vary in their meaning among species with different home range sizes. I would suggest “compactness at the larger spatial scale …” instead. In the body of the paper itself, the terms are formally defined, so the change is less important there than in the abstract.
Line 30: I’d suggest “although the proportion of forest in the surrounding landscape had” instead, though please check that this is what was meant.
Line 141: Although the BBS data are familiar to many, I’d suggest adding a sentence to explain the basic structure – some readers might otherwise not know what comments like “every fifth stop” refer to. Something along the lines of “BBS routes involve 24.5 mile-long road transects, with 3-minute point count surveys conducted at stops every 0.5 miles.”
Line 162: It’s not clear to me how this statement corresponds to the variables given in the full model. In particular, where are the habitat features and environmental conditions in that model (in other words, is it really a full model, or is it a base model to which potentially explanatory variables were added)? And what variables were chosen, and why? Related to this, is “Noise” (in the equation) a measure of environmental noise … or is it, as I first assumed, a synonym for error. (Note that my questions about this part of the analysis may be irrelevant depending on your response to my general question about the analysis, earlier in these comments.)
Line 316. I’m not sure I would say that the change points are similar to forest species. If I’m reading the figure right, it looks as though both groups have change points that just span a wide range of compactness values – i.e., there is no real pattern in either group. I think that is perhaps what you are suggesting, but the wording implies something else.
Line 328. I think it might be clearer to say “indicating that there were not sharp threshold responses to compactness of …”.
In the legend to Fig 4 please give the actual acronym definitions rather than just referring to the AOU. Also in this figure it is not clear to me what circle size indicates.
Overall the manuscript is greatly improved. I have 2 line comments:
Line 89-91: “The aim of this study was to assess forest bird response to changes in the spatial pattern of exurban development, and to examine species response when also forest loss, and forest fragmentation.”
Line 189: Add “compactness”, e.g., “The compactness index…”
Line 347: “the effect of compactness was reduced…” how is the reduction in effect size determined?
No new comments.
The 1, 2 approach of first looking at compactness index and then looking at compactness with forest variables is interesting. Contemporary approaches to model fitting would suggest a form of multi-model comparison rather than fitting a full model only. Also, there are formal ways to assess the relative effects of different factors fit in the same model beside p-value alone. An example given the full model approach would be to standardize variables so they have the same basis for comparison, and then comparing the size of estimated coefficients. Other approaches exist, e.g., odds-ratios, that formalize the differences among variables.
I commend the authors for incorporating suggestions and conducting additional analyses per suggestions. This was no small feat, and as a result the manuscript is greatly improved. I did find it interesting that the new forest analysis did not take advantage of contemporary approaches to multi-model comparison. There are several approaches available, AIC (akaike's information criterion), DIC (Deviance information criterion), and BIC (Bayesian information criterion) being the most common ones in ecology. I recommend using one of these to evaluate a suite of models that includes compactness and forest variables separately and together. Doing so will greatly improve the strength of inference regarding factors affect birds in forested environments.
This is an interesting paper and both reviewers saw value in the work. Reviewer 2 outlines some additions to the current analysis, that I think are necessary in terms of knowing how to interpret the results. Below I outline some comments based on my own read of the paper.
Line 123: Although the method used here might reduce the risk of autocorrelation, there could still be spatial structure in the data. Is there justification for subsampling at this scale (e.g., analyses done with these routes, or other work using BBS data)? If not, either testing for autocorrelation or adding it into the models would be helpful.
Line 163: I would specify the pixel size. Many readers will know, but it might be helpful for those unfamiliar with the imagery.
Line 215: Please specify the R package. (I assume this analysis is not in base R and package titan doesn’t look right …)
Line 238: Why give only examples in Fig 3? Since space is not limiting at PeerJ, I see no reason not to provide the results for all species.
Also, perhaps I missed it, but did you directly compare these models to linear alternatives. What evidence is there that the nonlinear models provide better fit to the data?
Line 242: I concur with reviewer 2 in my uncertainty about what is meant here. Is it that you mean only 1 of 6 forest indicator species were both significant and reliable (i.e., SCTA, WOTH, etc. are forest indicators)? If so, maybe you could just drop the word "indicator" throughout the paper, since it creates confusion given its variable and often ambiguous use in the literature. If the intended meaning is different, please clarify.
Line 252: By which forest species? There was a range of values for these measures across the forest species.
Line 258-9: Maybe I am misreading the table, but it looks like 3 of 10 cases involve opposite results at the two scales. Moreover, could the situation for some of the other cases be unclear because of uncertainty in the estimate of z (I don’t see that uncertainty reported); i.e., can you be sure that those cases do not also have a difference that went undetected? For the 3 cases with differences, SCTA and EATO are more reliable at the 400-m scale, while WOTH is more reliable at the 1-km scale. My interpretation does not seem to match what is written in this paragraph. Am I just not understanding Table 2?
Line 274: Were these areas increasingly intact (i.e., through regrowth). If not, I’m not sure how they could account for an increase in forest bird abundance. Simply remaining intact would only account for a lack of decrease.
Line 282: The logic behind this argument is unclear to me, because the forest interior species described in this study are not the same species that come into feeders, plantings, etc. and that account for the increase in richness with low level development. I agree with reviewer 2’s suggestion that other variables may be confounding the analysis and that forest loss and fragmentation should be considered as covariates.
Also, the data for the species in Fig 3 suggests that any biological change over the compactness scale has a pretty low magnitude, in relation to the variation in the data. This suggests that the biological effects are very small. Given the other things that potentially affect bird densities, I wonder how biologically important such effects are? Evaluating their importance in light of other things known to affect forest birds would thus seem especially important.
Line 293: Indigo bunting declines in the eastern US are also almost certainly attributed to forest regrowth, which has reduced the shrubby habitats that they tend to use. Note that there is a big difference between catbird and indigo buntings. The former are frequently associated with suburbia, whereas the latter are not.
Fig. 4. Putting species names on both vertical axes seems potentially confusing given that you have two panels side by side. Since you clearly indicate direction of effect with the symbol, I would put them all on the left axis. Alternatively, you could stack the panels on top of each other.
My comments are focused on the use of clear and unambiguous text in the manuscript. A quantitative metric such as compactness and how it changes over time and at different scales does not lend itself to an intuitive interpretation of how, what or why birds might be responding in certain ways within the landscape. Because the language used in the methods section was quite technical, it was challenging to interpret if and how each test was designed to address a potential biological change or a mechanism driving avian response. Although the authors may wish to retain this technical language, statements relating methodological approaches to the biology of how or why birds might be expected to respond to changes in compactness or overall level of development would be helpful. This would also help the reader develop a deeper understanding of the potential mechanisms driving the results, which were contrary to the authors’ predicted response.
In the discussion session, it would be helpful if you could place your results within the larger landscape context. What changes in land use cover are happening at the regional or flyway scale that could be contributing to your results? Are there any limitations or biases associated with BBS survey data that could influence your results that the reader should be aware of?
Figure 4 – the caption for this figure is quite long and includes information that should be limited to the methods section. Or, possibly there was a formatting error? There are two paragraphs in my version, one that is quite brief, the other quite long.
As relates to the knowledge gap being filled and how this study contributes to filling that gap, I was surprised that the authors failed to mention the large body of work that Dr. John Marzluff and his students and collaborators have produced on the subject of avian responses to urban development, including exurban development. By not referencing this body of work, I’m concerned that the authors might have missed an opportunity to place their research in the context of the current state of knowledge on the subject.
This study contributes to a growing body of work documenting avian response to exurban development, identifying threshold responses for species at difference scales of interest. For species that were predicted to decline in response to increased compactness but instead had a positive association, these results suggest that further research on the topic should focus on the specific elements of the landscape that birds are responding to, e.g., increased food availability, human development pressure in surrounding areas, etc., and that it is important to consider multiple scales when assessing avian response to landscape change.
If the authors are interested in promoting the application of these results in land use planning it would be helpful if they could provide a more straightforward interpretation of how this research might guide the development of more bird-friendly suburbs and exurban areas.
The article is written well with respect to structure and flow. Some terms require additional or revised explanations to improve clarity, e.g., Compactness index, indicator taxa, indicator response taxa, and indicator response.
Line 180-183: Compactness index. I re-read the description several times, and dwelt on figure 2. I’m having a hard time lining up the text with figure 2. The best I can interpret from the figure, the compactness index is:
MSPA all other classes / (MSPA islet + MSPA all other classes)
Which would make low values for compactness when MSPA all other classes is low proportion of the landscape. This is not what the text says. Please clarify.
Line 242: Term “indicator taxa” – after reading this statement and going back to the description in lines 193 – 202, I’m still lost as to what “indicator taxa” and “indicator response taxa” and “indicator response” means. Coming from the conservation arena, I read indicator taxa and think indicator species, meaning a species whose presence or abundance is representative of certain environmental conditions. Please re-write the explanation of these terms with the goal of moving them from jargon to technical terms.
The experimental design is sufficient for the question at hand. My comments primarily seek clarification of the methods.
Line 143 and 146: I see Cit as count for species at stop i at time t, but I don’t see where Cit is in the model statement on line 146.
Line 156: Was classification accuracy assessed? How? And what are the results?
Line 167: Which imagery was classified with MSPA? Was it the (pre-processed) Landsat 5 TM images? The classified Landsat 5 Tm images from the previous paragraph?
Line 167: I’m familiar with MSPA and have used it in analyses myself. This is a clever application. I see why the edge width of 1 cell (30m pixel) was used – to grab only the isolated cells – and why only certain MSPA classes were considered exurban. Nicely done. A question though, how sensitive is compactness to a change in the edge definition? In the discussion. Lines 313 to 321, the literature suggests edge effects extend much more than 30 m. Where any other edge definitions (e.g., 60 or 90 m) explored?
Line 202: negative (z-) and positive (z+) indicator response taxa…it’s not immediately clear that z is the “effect” of interest and the sign indicates the direction of the effect, e.g., (–) means the species has a negative response to increasing compactness. In Table 2 and Figure 4, is it appropriate to say “Direction of effect” and use the sign, omitting z?
My primary concern is in the validity of the findings in light of alternative explanations for the patterns observed here.
The authors examined forest and forest-edge bird response to compactness of housing development. The definition of exurban is good, as are the methods to identify it after addressing clarifying comments.
However, I’m curious as to how factors known to affect forest birds – forest loss, forest fragmentation, and forest degradation – are treated in the analysis. It seems to me that exurban development may be confounded with forest loss (the houses were built on something, likely forest?) and with forest fragmentation (decrease in patch size, increase in edge without change in forest area).
Without accounting for loss or fragmentation in the analysis, an alternative explanation for the results is that minimizing forest loss (increasing compactness) or minimizing forest fragmentation (increasing compactness) are beneficial for forest birds.
Please address forest loss and fragmentation in the analysis. This might be done by incorporating the information from Table 1 in the analysis of species responses to compactness. The introduction should also provide a brief literature review on forest loss vs fragmentation, and the discussion revised to place the results into the broader context of exurban development in forested environments.
Overall, this is well-written, well thought-out study addressing a highly relevant question: does compact exurban development reduce negative impacts on forest birds?
The statistical approaches to address this question are top notch, though not complete. Please address how forest loss, forest fragmentation, and forest degradation may be confounding factors in the compactness analysis. This may be accomplished by incorporating the information from Table 1 in the analysis of species responses to compactness.
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