Summary

Animals impact elemental cycling in many direct and indirect ways. Evidence from several biomes demonstrates that even after death, animal carcasses can change the biogeochemistry of ecosystems and these impacts can be long lasting. Most studies of carcass impacts on ecosystems, however, are done on small to medium (1kg to 200kg) sized animals. In this contribution, the authors investigate the effects of elephant megacarcasses on the biogeochemistry of soils and plants. The authors report significant effects of elephant carcasses on components of soil and plant elemental cycling and they discuss how these effects may be important components of spatiotemporal heterogeneity in ecosystems.

General comments

1) Overall, I found the writing good. The authors have crafted a nice narrative that makes a compelling case that megacarcasses can be important parts of ecosystems and therefore we need to learn more about the impacts of these carcasses on ecosystems.

2) I have a few questions about the analysis. The effective sample size is 10. Obviously, it is hard to find carcasses (I would have great difficulty in finding 10 fresh moose carcasses in my system!) but the authors are trying to squeeze a lot of information out of very few data points. I have the following specific questions about the analysis:

i) While I like the transect approach, the design may have been stronger if the authors had random transects (ie, transects with no known carcass) like Risch et al. work. This would strengthen inference.

ii) lines 180-183. The author’s approach to checking for normality of response data does not seem sound to me. The assumption of normality (for linear models) is normality in light of the model, i.e., investigating the normality of residuals is a more common approach to this. Either way, it is often better to avoid transforming the data and generalized linear models do allow for a lot of flexibility to fit different error distributions. For example, the gamma family in glm is very flexible and can handle log-normal data sets. Did the authors try different families of error distributions before transforming their data?

iii) lines 187-189. How many data points did the authors have per estimated parameter in the most complex model here?

iv) line 194. This is fine but I think Burham & Anderson would say that any model within deltaAIC of 2 of the null model should not be considered to be supported. In several cases, the authors interpret top models that are ranked above the null but within deltaAIC of 2 of the null as supported (e.g., lines 217-218, 218-221).

v) what R^2 are the authors reporting? In the captions of Tables S1 and S2 (thank you for providing full AIC and coefficient tables), the authors state “R^2 is the proportion of variance explained by a model”. This is unclear. These are mixed models, and the most common approach is to report the marginal R^2 and conditional R^2. Is the R^2 in these tables one of those or another pseudo R^2? This is critical for many reasons but most importantly, given the small sample size and large number of mixed-models, I would expect at least one of the models to not converge. There are many indicators when a mixed-model does not converge and one of the best is when the marginal R^2 = conditional R^2. Without having both of these pieces of information, the reader is unable to adequately assess the fit of the models. Other indicators of models not converging are coefficients estimates or errors that are very large or very small (i.e., 0 – see next comment).

vi) I am confused by the magnitude of Table S2 sodium and iron coefficients and/or the scale of reported on the y-axis of Figure 5 for these. The iron coefficients in Table S2 seem small relative to the Figure 5c ? Or am I misreading things?

3) the reporting of results could be improved. I recommend, the authors report: top ranked models (AIC + measure of independent fit like R^2). Then report effect size or relationships (coefficients). I found key statistics to be missing throughout. Statements like “Phosphate concentrations were greater in granitic soils…” would be more informative if they included the coefficient + error in parenthesis. Coefficients can be reported for the top-ranked model or from model averaged results when there are several competing models.

4) in section 3.2 I think the reader may be more interested in coefficients and confidence intervals around those relationships than p-values that are currently reported.

Specific comments:

5) I found the use of three different terms that mean similar things (nutrient flows, ecosystem processes, nutrient availability) in the introductory sentence confusing. I recommend the authors replace “nutrient availability” with “ecosystem processes” or “nutrient flows”. Surely living animals (not just carcasses) influence nutrient availability (which is just a part of a continual nutrient cycle).

6) line 83. I believe there is no “e” at the end of the citation Risch et al.

7) lines 96-111. How do these elephants die? As someone with no experience with megacarcasses, I would appreciate some insight on the causes of death. Most large herbivore deaths in my empirical systems are from predation which I assume is not the case for elephants.

8) really excellent job with clear hypotheses and nice work carrying forward these hypotheses throughout the ms – really makes the job easier for the reader.

9) lines 132-133 Why 10cm deep core? Is that mineral soil only?

10) the discussion is well done – concise and touches on all hypotheses.

11) Figure 1 is an outstanding visual!

12) in figures 2-5 I recommend the authors consider reminding the reader of the sampling resolution because the jitter of points makes it impossible to see what distances were measured below 5m.

Summary:

Reed and coauthors present a well-written study on the impacts of megacarcasses (elephants) to soil biogeochemistry after up to 2 years of decomposition. The authors examined 10 carcass hotspots with 5 carcasses each on two different soil types. They quantified soil major and trace element chemistry as well as plants associated with the hotspots to determine if carcasses influenced soil N and P chemistry and if those elements were subsequently enriched in vegetation. The current version of this manuscript does not adequately describe the methods in enough detail to make the work reproduceable. Additionally, the handling of the data for statistical analyses is strange and non-standard. The discussion needs to be re-written to better emphasize the importance of the work (as framed in the introduction). I think this work has potential to be an important contribution, but there needs to be some major revisions.

General comments:

• The importance of this study in adding to our knowledge about nutrient transfer at carrion hotspots is not emphasized clearly in the discussion. The introduction frames how megacarcasses may be “functionally different than smaller carcasses” but never returns to this aspect in the discussion, which is really where this work could add to our knowledge. Adding more to the discussion would help address this issue and would make the impact of the work clearer.
• Parts of the results belong in the discussion, and I’ve tried to highlight those below in specific comments.
• The methods need significantly more specific details, highlighted in specific comments. Additionally, there were no control soil or plant samples examined here. Please describe in the methods why there were no controls.
• The handling of the data for statistical analyses is non-standard and not clearly justified. If data were non-normally distributed (it seems like some datasets were and some were not), why not just use a non-parametric statistical test rather than log-transforming the data? It is a bit strange to log-transform some data but not all. The approach of adding 0.001 to zero values is also not correct (described below in specific comments).
• The presentation of elemental data for soil and plant composition is non-standardized throughout. Some data (i.e., iron) are presented as mg/kg (is this soil dry weight?), while others are presented as % (Ca% of what?) in the same figure (figure 5 for example). Other data are presented as mg/L (figure 2). Part of this confusion is from the missing details in the methods that clearly explain how these data were generated. In several of the figures there is a statement about back-transformed data, which is also confusing.
• I can appreciate that finding carcasses that have decomposed for the same amount of time is challenging, but 1 month to 26 months is a huge range of time (at least from what we know from not megacarcasses). The biogeochemical processes occurring at a carcass decaying after 1 month postmortem is very different than a carcass that has been decaying for 26 months (from smaller carcasses). It would be useful to see some of the data, particularly ammonium, plotted as a function of postmortem interval (months) even if that is not a variable that could be included in statistical analyses because of the small sample size. It would also be helpful to see if the postmortem interval for the 10 carcasses is evenly distributed between the two soil types or if one has more fresh carcasses and the other has older carcasses, that could help with interpretation of the results.
• I think it may be useful to add some photos to supplemental information (or even the main text) showing what the carcasses/sites looked like (maybe representative images from a fresher carcass and one that is older).

Specific comments:

• Lines 99-100: There should be more details provided on the soil type and what makes the granitic soils “nutrient poor” compared to soils developed from a basalt protolith. Because soil type becomes an important part of this study, the details of the soil types need to be expanded in the introduction.
• Line 132: Include a citation or discuss why soil samples were collected to a depth of 10 cm rather than the upper 5 cm. For decomposition studies, typically the upper 5 cm is examined, not the upper 10 cm.
• Line 145: More details are needed beyond “measurements of soil ion concentrations”. What instrumentation was used? What specific extraction protocol was followed? I’m assuming deionized water was used (1:2 soil to deionized water?), but those details are not provided. How long were samples mixed (shaking platform?), what speed, etc.
• Line 148: “mass spectrometry”—elaborate on what this means with respect to instrumentation used to analyze cations. Here and throughout the methods, please also include what standards were used for the different analysis types.
• Lines 146-150: Clarify if these analyses were conducted on the water extracts.
• Line 152: Were stable isotope analyses conduct on oven-dried soil? 10 g is an exceptionally large amount of soil—how much was actually analyzed with EA-IRMS? Were samples powdered prior to combustion?
• Line 154 (and throughout with respect to stable nitrogen isotope results): The authors refer to “¹⁵N” measurements, but surely this should be presented as the ratio of 15/14N and in delta notation? In the methods here there also needs to be more description of the standard, the materials used for linearity, and the analytical precision of the instrument.
• Line 175: More details on the ICP-MS are needed, including standards, detection limits, etc. Additionally, were these samples digested in nitric acid? Water? How long were they microwaved?
• Line 182: Adding some random number to each variable is not a standard way to handle data that are zero in your dataset (or if it is, there is no citation here and I am not familiar with that approach). Typically for geochemical data (like what was generated with ICP-MS), you can replace zero values with ½ the detection limit to remove non-zero data. There are other more technical ways to deal with zero values from a statistical standpoint, but the ½ the detection limit is the easiest and has the longest history of use. Please justify the use of your approach or re-run the analyses following a standard method for handling non-zero data in a geochemical dataset.
• Line 255: The part of the sentence that reads “…we found evidence that N from carcasses had moved from soils into plants” does not belong in the results section. This is interpretation and should be moved to the discussion.
• Lines 256-258: Similar comment as above where the content of this sentence is interpretation and should be moved to the discussion.
• Lines 295-297: I’m not quite sure I understand the logic presented here. First, soil microbial biomass was not measured. The respiration potential (through production of CO2) was measured, but heterotrophic activity (which is how respiration can be interpreted) consumes oxygen. I think the phrasing here needs to be re-worked to not imply that the soil respiration (and the communities producing CO2) are not necessarily the same that are driving nitrification.
• Lines 304-305: There are prior studies that demonstrate the impact of increased organic C during decomposition on soil microbial processes that should be cited here (see studies by DeBruyn and colleagues)
• Lines 310-311: I’m not sure that this is phrased correctly. Phosphorus (predominantly as phosphate) is considered immobile in soil partly because of low solubility because it is often sorbed with Ca, Fe, Al or organics, and the release of P is tightly controlled by soil (or fluid) pH. N does not face the same sorts of sorption immobilization constraints. I think if you rephrased it to clarify that P and N are held within different reservoirs within soils that make them behave differently (and add some citations), that would help.
• Lines 324-328: As mentioned above, because the composition of the two soil types were not included, this part of the discussion is not supported by the results. It’s unclear if the authors here are trying to say that the basaltic soils contain more nutrients after being impacted by decomposition or if the native state of the soils (background conditions) are more nutrient rich. I think if the introduction described the background chemistry of the two soil types this would be better supported. Additionally, basalt and granite contain different types of minerals and therefore additional sources of elements like P. I don’t know what the specific mineralogy is of these two rock types in KNP, but it might be worth exploring. In particular, the presence of apatite (Ca-P bearing mineral) in the granite might also be contributing to elevated P measured in the granite soils.
• Figure 5 (and others): I’m a little bit confused by the figure caption. I think it would be better to present this as selected elements plotted as a function of distance. These are not the results of generalized linear mixed models, but the selection of how to present the data were informed by the models.

This manuscript presents data on the influence of elephant carcasses on nutrient availability in South African savanna soils. It would be a surprise if a decaying elephant did not increase nutrient concentrations in the proximity of the carcass, but there are some interesting differences among nutrients in terms of the distance over which the effects extend. There are parallels with other nutrient hotspots in tropical ecosystems, including glades in African savannas (e.g. Augustine 2003) and leafcutter ant nests in tropical forests (e.g. Hudson et al. 2009) - it would be worth introducing these into the discussion for comparison. I have several questions about methodology and results that should be addressed before this manuscript could be acceptable for publication.

Line 38 – these are not graves. A grave is an excavation for burial.

Line 77 – what about the amounts of cations in an elephant?

Line 89 – cations are not micronutrients. Is there direct evidence for widespread (or any) cation limitation of growth in savanna ecosystems? 

Line 99 – please include classifications for the granitic and basaltic soils in one of the internationally recognized systems. In Soil Taxonomy these are presumably Inceptisols / Alfisols and Vertisols, respectively?

Line 138 – freezing soil has implications for subsequent measurements of extractable nutrients (e.g. Turner and Romero 2009). This should be mentioned here. Given the apparently very high values for some measurements (see below) I suspect that pretreatment had a major impact on results.

Line 145/146 – please explain the difference between phosphate and plant-available P. As written, it appears they were both measured in the water extracts. Most plant-available P tests are not conducted in water (e.g. Olsen, Mehlich, Bray, etc). 

Line 158 – was there any inorganic C in the samples? Savanna Vertisols developed in basalt can have considerable carbonate concentrations, albeit often in subsoil. Soil pH values would help indicate this possibility – how did carcasses affect soil pH?

Line 161 – was moisture standardized prior to the incubations?

Line 182 – an alternative is to set values to ½ detection limit.

Line 188 – I understand that there were insufficient carcasses to allow inclusion of carcass age in models. However, major differences would be expected between carcasses aged 1 month vs 2.5 years. Is there any way to provide an indication of the magnitude of the age effect? How would distance effects look if young carcasses were excluded, for example?

Line 228 – It is perhaps not surprising that P concentrations showed little variation with distance, given that P was measured in water extracts (i.e. the extraction is recovering a relatively small pool of soluble P).

Line 230 – how is plant-available P defined here?

Line 286 – Soil extractable nutrients should be expressed on the basis of dry soil, not volume. 

Line 286 - these very high extractable nitrogen concentrations are presumably in part a consequence of soils being frozen prior to analysis. Another factor is time between sampling and freezing - or storage prior to freezing.  Please provide a statement about sample treatment prior to analysis (time from sampling to freezing, storage conditions during this time, etc, as relevant). 

Line 308 – the high available P and tissue N:P ratios (see below) indicate that there is no P limitation here. This might limit the likely influence of carcasses on foliar P, as found here (i.e. foliar P is not a strong indicator of the extent to which carcasses change P availability in general).

Line 322 – water-extractable P represents a tiny proportion of the total soil P, so reliance on this procedure probably limits the possibility of detecting change in soil P.

Line 323- 330 – this text largely repeats results.

Line 340 - missing here is a discussion of the ecological consequences of the findings. What are the implications for plant and microbial ecology in savanna ecosystems?

Figure 2B, C – these values should be presented in mg/kg soil.

Figure 2B – these are extremely high nitrate concentrations, even out to 15 m. For example, 100 mg/L is equivalent to 200 mg/kg based on a 1:2 soil to water extraction ratio. Extractions done quickly after sampling and in 2 M KCl are in the range of 1-5 mg/kg. This seems to be a clear indication of storage effects.

Figure 2B, C – are these values as NO3/NH4 or on an N basis?

Figure 2D – please express stable isotope ratios as δ¹⁵N. This may be how the results are presented, but this is not clear from the units.

Figure 2F – these are very high available P concentrations for a natural ecosystem, although there is no mention of the method used.

Figure 4 – it looks like foliar N:P ratios are around 4 (2% N, 0.5%P) – these very low values that suggest strong N limitation. This is incompatible with the very high nitrate values presented in Figure 2. This further indicates storage problems with N measurements.

Augustine, D. J. (2003). Long-term, livestock-mediated redistribution of nitrogen and phosphorus in an East African savanna. Journal of Applied Ecology, 40(1), 137-149.

Hudson et al. (2009). Temporal patterns of nutrient availability around nests of leaf-cutting ants (Attaolombica) in secondary moist tropical forest. Soil Biology and Biochemistry, 41(6), 1088-1093.

Turner, B. L., & Romero, T. E. (2009). Short-term changes in extractable inorganic nutrients during storage of tropical rain forest soils. Soil Science Society of America Journal, 73, 1972-1979.