All my comments and interrogations have been addressed, and I have no further comments to make on this final version of the manuscript authored by Magrach & colleagues. This study will be a very interesting one added to the field of ecology and pollination ecology.

General comments

I would to thank the authors for their work on the revisions and for the clear Responses to reviewers file provided. Following previous reviews, the revised version is very much improved indeed.
My comments were mostly all considered, so I’ll only focus on a few remaining points that I think need to be addressed. Specifically, I have three main remaining concerns:
- are results qualitatively similar when using the same max(NODF) ‘uncorrected’ measure for all sites (instead of a new version for 13 sites but an uncorrected version for 3 sites)?
- I don’t understand how GLMM Poisson models with response variables ‘average values of fruit and seed weight’ that are (most likely) continuous (and not count-like data) can be used?
- is the effect of pollinator richness on Fruit weight and Seed weight (Figure 4) still positive and is it statistically significant (or what’s the confidence intervals for the estimates) when removing the site of maximum pollinator richness?
More details are for these main points are provided below, along with minor comments.
Also, I again had no access to the supplementary materials.

Detailed comments

Abstract
I feel like the abstract is lacking a sentence of conclusion or perspective.

Introduction
L89: change “these potential pathways” (i.e. nestedness and complementary specialisation) to “these potential attributes”?
L109: delete ‘of’ in ‘requires of the delivery’

Methods
L199: perhaps change ‘Here’ to ‘With this method,’?
L220-223: Are results qualitatively similar when using the uncorrected version of max(NODF) for all sites (not only the three not meeting the assumption of number of links > number of species)? I’m concerned about not using the same calculation for all sites.
L239-240: given GLMs were used for site-level analyses and GLMMs were used for species-level analyses, I suggest the following change at L239: “we used generalized linear mixed models (GLMMs) and generalized linear models (GLMs) respectively.”
L247-248: authors mentioned in their response that there had been an error in the first version of the MS and have corrected it. However, I still don’t see how ‘the average values of fruit and seed weight [which would almost inevitably produce decimal values, or am I missing something?] fitted to Poisson distributions’ could work.
Looking at R scripts provided by the authors (e.g. L324-330 in ‘removing out obs.R’), I see the use of package glmmTMB when modeling the response variable ‘mean.seedw’ but Poisson distribution should only work with so-called count data (i.e. positive integer), as stated for example in a glmmTMB related paper: https://journal.r-project.org/archive/2017/RJ-2017-066/RJ-2017-066.pdf.
This is an important concern here as I don’t understand how this could work and this requires a clarification.
L258-259: conversely to ‘species-level models’, here, average fruit and seed weight were modeled using a Normal distribution and I agree with this. If it was an error above, did the R code also include an error then (i.e. are the results presented from a Poisson model as in the R code or a Gaussian model?)

Results
L347-349: Was the positive effect statistically significant? I could not access Tables S7-8 (no access to spuuplementary materials). However, when looking at Figure 4, I am concerned about the influence of a single site on the overall relationships (panel A and B). Indeed, the site with scaled pollinator richness at ~2 appears well above and apart from all others and I am worried that any significant effect would disappear without this site (or even become negative in case of effect of pollinator richness on Fruit Weight).
I strongly suggest running again both models (1 and 2) for both response variables without that extreme site and check if results are robust.

Tables
Table 1: I read answers of authors to my previous comment on including or not p-values (especially from mixed-effects models) and confidence intervals. Taking the example of Centrality, the ‘large effect’ (0.46) seems also associated with large variation (SE = 0.25), and a confidence interval would help to interpret how likely the effect is (especially because SE are not so easily interpretable for non-Gaussian model).
Also, I suspect grey bands in Figure 2-4 represent confidence intervals (they often do as it’s easily interpretable). If so, if used in these figures, I think CIs could be added to tables showing model results. This was recently suggested in Conservation Letters (Fidler et al. 2018) to improve statistical transparency. So I still suggest to add 95% confidence intervals.

Figures
Figure 2:
Relative to my previous comment on panel A: points don’t go over 1 but the prediction line does. I see two issues with this panel:
1) what is the grey band surrounding the black line? I understand it describes uncertainty around the predicted effect, but is it a confidence interval and at which level (95% or 99%)?
2) given these are results from a glmm based on a binomial distribution (L245-247), neither the estimated effect (the black line) nor its uncertainty (grey band) should be predicted at values >1. For example, when using function predict() or add_ci() (package ciTools) in R on a binomial gl(m)m model, predicted values stay within the boundaries of the its associated distribution.

Reference used above

Fidler, F. et al. 2018. Improving the transparency of statistical reporting in Conservation Letters. - Conserv. Lett. 11: e12453.

The revised version has successfully addressed all of my concerns. I especially enjoyed reading the added discussion of the challenges in linking network and function empirically. I believe this paper presented important advancements on an important topic.

One last suggestion is to expand the figure captions. The current captions are too brief to be understood by someone skipping the papers.

The manuscript by Magrach et al. addresses how community-level plant reproduction is linked with pollinator visitation. The authors found evidence that visitation alone can well explain some pattern, while niche complementarity offers a mechanistic understanding of what ecological process is responsible for determining the differences in reproductive outputs. The paper is clearly written and I find the research questions to be well-defined and of broad interests. As I am a theoretical ecologist, my review would only focus on the theoretical part of the paper.

One major concern I have is the robustness of the results. As stated in the abstract, this paper has focused on community dynamics, which is a broad and complex issue. The authors have only considered niche complementarity and nestedness, and it is unclear to me why the authors picked only these two possibilities. Furthermore, nestedness, as the authors have admitted, may not be a meaningful metric for this study because of the small network size. Therefore, it is not entirely convincing that the authors have proved their main claim. I suggest the authors test other metrics as well, such as the ones proposed in 10.1101/604868. Of course, the authors are free to choose any other metrics, but the bottom line is that more metrics must be tested to convince the readers. Again, I am not doubting that correctness of the findings in the manuscript, but rather encourage the authors to run more tests.

Other major concern I have is the repetitive use of "prediction". One of the central claims of the paper is that `information on simple visitation metrics is sufficient for prediction purposes'. Yet, it falls short in two important aspects. First, regression analysis of in-sample inference does show its predictive power (which has to be based on the out-of-sample forecast). I cannot find any forecast analysis in both the main text and the supplementary material. Second, no R^2 or any other similar statistic is reported. Table 1 and 2 only show if a variable is statistically significant, but it does not show if the model explains the data well. Please correct me if I miss something,

Minor points:

• Despite the clarity in the flow of the paper, many points need more explanations. For example, What is the definition of the asymptotic number of species (line 135)? What is the Morisita index (line 159)? Please excuse me if these questions are well-known concepts in the empirical field, but I believe adding more explanations would never hurt the paper.
• Title. Maximization may not be entirely appropriate here. I think the authors found evidence that niche complementarity increases plant reproduction success, but not maximizes.
• Line 50. 10.1111/ele.13091 and 10.1002/ecy.2708 are relevant recent works on the importance of indirect interactions via shared resources.
• Line 98. I suggest to remove 'us'.
• Line 127 and many other similar places. Please specify what is the error around the mean. I assume it is standard deviation, but it does not hurt to be precise.
• Line 176-184. Recently 10.1111/1365-2656.12963 have come up with a new algorithm to compute the normalized NODF. Although the difference between the two algorithms appears to be small (10.1111/1365-2656.12964), I suggest the authors to re-compute the normalized NODF for the sake of accuracy (the code can be found in github.com/CHoeppke/maxnodf).
• Line 199. Is it "generalized" or "general"?
• Line 249. Perhaps 'small' is better than 'low'?
• Line 349. I am not sure if James et al. 2012 have claimed that nestedness destabilizes the dynamics. Instead, I think they have claimed nestedness has an almost null effect on the dynamics.

I reviewed the manuscript of Magrach et al. submitted to PCI Ecol. The authors analyze a number of network metrics and their relationship with plant reproductive success in an attempt to decipher the putative link between network theory and community-level processes. In my opinion, the authors, after extensive fieldwork provide strong evidence that some network metrics, such as centralization and niche overlap, have a significant effect on variation in fruit set and seed number per fruit. However, other metrics often calculated in network-based studies (e.g., nestedness) do not provide significant association with plant reproduction, hence lacking easy interpretation in ecosystem function. This is an interesting result.

My major concern is the complete lack of reference to classic niche and competition theory. Indeed, one can easily interpret the results by omitting network jargon and focusing on the theory developed in the 60s-70s. As I suppose network theory provides a new way to reveal and understand community patterns, I would expect that new patterns should emerge. For example, the observation that "niche complementarity is key in determining differences in reproductive outputs. Indeed, we find that communities where there is less overlap in the niches occupied by pollinator species had greater values of reproductive success, both greater fruit set values and larger numbers of seeds per fruit." (Lines338-341) is entirely accountable by niche and competition theory. Likewise, "At the community level, however, we find that niche complementarity between pollinators, a measure of the overlap in the niches of different species in terms of plant coverage, has an important effect for average fruit set." (Lines 324-327). Again, by definition the extent of resource partitioning among consumers is expected to have a substantial impact on resource dynamics and fitness.

In consequence, I would suggest that in order to improve the quality of their manuscript, the authors should try to reinforce the idea that some findings are in line with seminal advances in competition and niche theory by MacArthur, Pianka, Levin, (e.g., niche complementarity, niche overlap, resource partitioning, competition release, etc).

The paper clearly has several merits. Approaching the functioning of plant-pollination network using species and community based indices in parallel is clever. The specific objective addressed (exploring the explanatory power of community structure as opposed to more classical diversity indices) is also stimulating.

I however see several limits and needs for additional justifications.

A major limit is, according to me, the mismatch between the main objective, the results, and the conclusions. It is claimed that using community structure will help to shed light on overlooked mechanisms. Yet, those mechanisms are still very unclear after several readings. The study remains correlative and how species interact and what and how potential mechanisms contribute to increase the reproductive success is still very speculative and not really inferred from the results.

The general conclusion, therefore, is I think very expected (eg end of the abstract or L328-335). Indeed, the fact that other metrics (than simple visitation) are needed to understand community level processes is not surprising. But this does not provide in itself “a mechanistic understanding of the pathways through which pollinator diversity translate into changes in reporoductive success”. Dispersion, competition, trades off between specialization and pollination success, habitat filtering, co-evolution are few among the many processes that could be studied explicitly for such a mechanistic understanding. The metrics in itself are only tools to capture potential processes. In this respect, that additional metrics are needed to capture multiple processes is not making a very strong case.

A potentially key missing information for this framework are the environmental variables. Unless I have missed something 16 sites are described and equated to 16 networks. Therefore the pure effect of site is confounded with the network property. If an environmental co-variate both influence the plant and insect diversity, then part (and potentially most) of the results derive from the spatial distribution of this co-variate, not from any network functioning. It is likely, for instance, that altitude (Figure 1) is both affecting plant and pollinator diversity similarly, driving the correlation between the two components of the network. I was surprised that this is completely neglected.

The paper remains largely inconclusive for many relationships. More precisely, for important descriptors of reproductive success (fruit and seed weight, L282) and for community level, model 1 and 2 ie (ie including simple visitation metrics or information on community structure) are equally good (L291) or model 1 is even better for weight variables. This, together with other intriguing results (eg negative effect of pollinator diversity on fruit set) cast some doubts on the robustness of the conclusion that major gains of information and a better understanding of the mechanisms involved are provided by considering metrics of community structure. It probably does. But the results are not that clear on that perspective. My understanding is that even more confusion is produced.

Overall, it seems that this paper is a nice methodological contribution with an important message: approaching network functioning necessitates integrative descriptors. But the extent to which it helped to access to a better understanding of ecosystem functioning as claimed, is at this stage overstretched and deserve more justifications. My feeling is that the authors need to better delineate their strategy towards a more rigorous test of alternative candidate processes or develop the methodological side of the paper further. But the mixture is I think not really convincing or would deserve more nuanced conclusions and more justifications.