Bedrock geochemistry influences vegetation growth by regulating the regolith water holding capacity

Although low vegetation productivity has been observed in karst regions, whether and how bedrock geochemistry contributes to the low karstic vegetation productivity remain unclear. In this study, we address this knowledge gap by exploring the importance of bedrock geochemistry on vegetation productivity based on a critical zone investigation across a typical karst region in Southwest China. We show silicon and calcium concentrations in bedrock are strongly correlated with the regolith water loss rate (RWLR), while RWLR can predict vegetation productivity more effectively than previous models. Furthermore, the analysis based on 12 selected karst regions worldwide further suggest that lithological regulation has the potential to obscure and distort the influence of climate change. Our study implies that bedrock geochemistry could exert effects on vegetation growth in karst regions and highlights that the critical role of bedrock geochemistry for the karst region should not be ignored in the earth system model.

around the world.
The main claims are: bedrock concentrations of Si and Ca explain variance in "regolith water loss rate", which in turn explains variance in net primary productivity. Hence, Si and Ca concentrations explain variance in NPP. Finally, the relative lack of correlation between vegetation and temperature in karst terrain around the world (relative to everywhere else) is suggested to imply that lithological control on vegetation in karst terrain is widespread. **Are they novel and will they be of interest to others in the community and the wider field?
To my knowledge, the claims are novel and would be of interest to a broad swath of biogeographers, critical zone scientists, and karst region hydrologists. ***If the conclusions are not original, it would be helpful if you could provide relevant references.
To my knowledge, the claims are original. ***Is the work convincing, and if not, what further evidence would be required to strengthen the conclusions?
The work is not convincing.
Overall, I think the authors did a good job of setting up a problem worth solving, and importantly, they outlined a reasonable, testable hypothesis about the different drivers of vegetation productivity in different lithologies -specifically, karst versus silicate bedrock.
However, it's impossible to determine whether or not they have gathered the data and conducted the analyses that are needed to test the hypothesis.
First, there is no rationale given for the sites they chose. Why those sites? Is there a study design that these sites satisfy?
Bigger problem: After reading the manuscript, the methods, and the supplemental file and then studying all of the figures and tables as carefully as possible, I still do not know how the authors measured any of their key variables. NPP? RWLR? BrSi? BrCa?
There is a sense that NPP was maybe measured using remotely sensed NDVI. But how was that done? And there is a sense that RWLR is measured using remotely sensed TDVI. But how exactly? And since these remotely sensed indices are themselves calculated from different combinations of Landsat bands, doesn't that make it inevitable that they will be strongly correlated (because the same variables are used to calculate both the response and driving factors in the relationship)? And if that's the case, since the NPP-RWLR connection is a linchpin of the paper, doesn't that pretty much call the entire analysis into question.
With the BrSi and BrCa, again, I am at a loss for how these were measured. There is difficult to understand conceptual diagram in the supplemental file ( Figure S4) that seems like it may provide hints. But I just do not know. Were Si and Ca ratios actually measured somewhere?
Beyond the measurements themselves, which are not even reported anywhere in the paper or supplemental files that I had access to (making it impossible to reproduce the analysis), there is the data analysis, which is likewise difficult to follow. I go into some detail about that below, when I address the appropriateness of the statistical measures. Bottom line is, there is no rationale provided for the choices the authors made about how they chose to look for dependencies and codependencies in the data. To be honest, my sense after after digesting the paper is that they indiscriminately applied a bunch of R modules that sounded to them like they might work and then just treated the individual analyses as black boxes, without really considering whether they were appropriate or not.
In addition to my concerns about the lack of a clear explanation of how things are measured, a lack of data reporting, and a lack of rationale for why they were analyzed in the way they were, I am surprised that the authors did not spend any time at all discussing what would seem to be an 800-lb gorilla in the room on this question: land use. It seems like it would be a major confounding factor in the analysis of vegetation patterns, especially in China, where deforestation and conversion of landscapes to agriculture have completely altered the ecosystem. This is also likely a confounding factor in the global analysis, but there are even bigger problems with that in my mind.
Regarding the global analysis, the chain of inference that the authors expect us to follow here is: 1) the correlation coefficients in 16 out of 17 karst terrains they analyzed are lower than the global average for correlation between NDVI and mean annual temperature, 2) this means that NPP is controlled by lithology in these terrains. It just does not hold up. One does not follow from the other. There is the statistical issue of how much lower do the coefficients need to be? They do not look very different to me ( Figure 5). If they were reported with their uncertainties, is there overlap? We do not know because there is not a proper uncertainty analysis on these correlation coefficients.
In summary, from top to bottom -across all the analyses presented here I am unconvinced. The authors had a good idea, but I am not sure what they did to test it. If I follow them correctly, then much of what they did may be wrong, with artifactual correlations (NPP vs. RWLR) and potentially major confounding factors (land use) unaccounted for and not discussed at all in the text. ***On a more subjective note, do you feel that the paper will influence thinking in the field?
If the claims were sufficiently supported, I think the work would indeed influence thinking in the field. ***Please feel free to raise any further questions and concerns about the paper.
Overall, the writing in this manuscript is mostly OK, but needs a careful editorial pass to remove some problems like this one on line 230: "…Guizhou Province's lithology, which contains a variety of different ****carbonated**** rock types." The methods section is grossly inadequate. There is virtually no explanation here of how ANY of the main variables where measured.
For example, the method for measuring NPP -one of the two key response variables in the studyis never explained for their study sites in China. For the global analysis, it looks like maybe NDVI is used as a proxy for vegetation. Here is the text on that: "The temperature variation signal of vegetation productivity is calculated as the correlation coefficient between NDVI (obtained from Global Inventory Modelling and Mapping Studies…)." Is this how NPP was estimated at the China sites? We do not know. We do not even see a data table containing the NPP values. (At bare minimum there needs to be a data table with all of the main variables used in the statistical analyses somewhere in the supplemental file if not in the main text.) Because they do not say and they do not report the basic data needed to understand the work. And if NPP is estimated from the global NDVI data, is that even appropriate? Is it at an appropriate scale?
An explanation of how they quantified the other key response variable is also not given. The authors introduce this "regolith water loss rate" thing out of nowhere as the thing that is controlled by lithology and that in turn controls vegetation, but they never say how it is measured. Nor are values for RLWR reported anywhere. The only reference I can find to how it is measured is the quote: " RLWR is estimated by evaluating the temporal variation in regolith moisture during dry spell events at the regional scale." How is regolith moisture measured? From TDVI? But isn't that just a combination of Landsat bands? And if that is the case, is it not inevitable that there will be a strong correlation between this so called RWLR and NPP, since one is measured from TDVI and the other is presumably measured from NDVI?
There is also no explanation of how they measured Si or Ca or Mg or Al or Fe concentrations. Are there actual measurements of bedrock geochemistry somewhere? If so why are they not reported? It says soil N is the average of "N-values from the three sampling points." So the authors collected 3 soil samples from each CZU? Why is the sampling protocol not described somewhere? Maybe they also sampled bedrock? What about the N analysis procedure? How was this done? I am totally lost as to what the authors did.
The supporting information file is grossly inadequate in the following ways: First, the lack of detail provided in the methods summary was not overcome here in the supplementary information. If the authors have shortchanged the methods section in the main text because of length constraints or some other reason, it should be corrected here. But there is no additional text. Just two new poorly explained tables and five new poorly explained figures. And worst of all, they raise more questions than they answer.
The figure captions are far too short, failing in all cases to adequately explain the contents of the figure. This is especially true for the concept figures S4 and S5. For example, in figure S4, no information is given about how the supposed lithologic boundaries in the CZUs were identified. Also, precisely what was sampled at the triangles? Bedrock? Soil? Remotely sensed NDVI?
The tables also have far too little explanation. For example, it is not clear from table S2 which model is being used. GLM? Mann Whitney Wilcoxon? SEM?
It seems that one solution would be to write a brief section about each figure and table. What do the results in each of these pieces show? What part of the paper do they support? Why did you use this test versus another? What are the pitfalls if any of these techniques? ***We would also be grateful if you could comment on the appropriateness and validity of any statistical analysis, as well the ability of a researcher to reproduce the work, given the level of detail provided.
Where to start? Perhaps with the summary: The statistical analyses were largely inappropriate and unreasoned. A snowstorm of techniques was used, but there is not a clear rationale given for any of them. Why is GLM more appropriate than a more straightforward multiple linear regression model? What can we learn from these models? Isn't SEM used with social sciences datasets? Why is it useful here? What are the limitations of these approaches and why are they well suited to analyzing the data presented here (or rather not presented here, since there is no data table anywhere)? Is it appropriate to test every variable you have as a potential explanatory variable? What about the well know problem of multiple comparisons, where the overall false positive rate goes way up? By the way-because the data are not presented anywhere, it would be impossible for anyone to reproduce this work.
I am also concerned about the analysis of the global data base of karst terrain. It seems like it is reckless to espouse the chain of inference that the authors seem to want us to follow here. The lack of correlation between NDVI and T means lithology controls NPP in other landscapes? It's not a chain of inference I would be willing to put any stock in. Moreover, it is not clear that the correlation coefficients are even all that different from the "global average." An uncertainty analysis is warranted here.
Because of the lack of a clear rationale for each analysis technique, my overall impression was that the authors did not actually know what they were doing on the data analysis. Rather than follow a reasoned approach to sorting out the dependencies, including the collinearities in the explanatory variables, they threw every approach they could at the problem. It's almost as if they just decided to try everything they could find in R modules both arcane and more standard and then treated each module as essentially a black box.

Reviewer #4 (Remarks to the Author):
This is a very interesting and well-written paper that brings up new insights and challenges existing knowledge relating ecosystem productivity with abiotic factors that constraint and determine this function. This alone justifies its submission to a journal like Nature Communications. The authors propose very provoking and revolutionary hypothesis to explain and define ecosystem productivity using the critical zone concept and goes beyond current understanding of ecological processes. However, I find that to be able to solidly ground their proposed hypothesis, the authors need to be more thorough in the use of ecological theory, and provide a better theoretical explanation to their hypothesis. The authors jump very quickly to a general hypothesis from limited ecological data that relates to average climatic conditions and soil information. The authors extend their analysis to a global extrapolation, but the same problems remain in their global consideration. In synthesis, I find that the use of average conditions, as well as only a limited number of climatic and pedological descriptors precludes general descriptions of ecological processes, as these very general descriptors do not provide good explanations to ecological processes, anyway. More detailed work on ecosystem function (beyond empirical relationships) and properties would be necessary to more explicitly link ecosystem function (productivity) to abiotic factors that determine it.
For instance, no details on the selection criteria for climatic variables used in the analysis are presented; no consideration on water limitations (even if they are seasonal, and that determine ecosystem productivity to a great extent) on ecosystems is presented; similarly, MAT may not be the best predictor in a temperate system with highly seasonal precipitation regime; similar questions can be raised for the selection and descriptive metrics of topsoil and surface properties. These are just some examples of questions that be asked about the variables used to disregard the role of climate and surface properties on the dynamics of ecosystem productivity.
The authors propose that geochemistry overwhelms other abiotic factors in explaining ecosystem productivity and that it alone is enough to understand ecological processes, leading to statements related to insensitivity to climate change on carbonate-rich karstic environment. I find this kind of argument unnecessary and, frankly, potentially dangerous for ecosystem management and land-use policy. The geochemical effect that the authors describe relates, ultimately, to water-holding capacity and biogeochemical processes resulting in nutrient availability. Yet, water availability (associated with rainfall variability) is potentially the most pressing uncertainty on climate change effects on ecosystems. To hold water, the regolith needs a water input, which commonly comes from rain (or hydrogeologic fluxes). What happens if this input becomes more scarce or intermittent? if drought becomes more frequent and intense, or if seasonal variability becomes more pronounced, as predicted by most environmental changes projections and supported by observations, ecosystem productivity may be altered. I think the authors don´t need to engage in that discussion and present a dichotomy between climate and other abiotic factors. I find more useful to present their results in the shape of complementary knowledge that deepens our understanding of ecological processes in the face of climate and environmental change.
The paper would be much improved if the methods section was more explicit and detailed. On its current form, multiple aspects of the methodology (particularly those associated with the processes included in the statistical analyses) are rather vague and not straightforward. More specifically, the methods section concentrates on the statistical procedures but leaves multiple questionings about the processes that is trying to relate of describe. In addition, figure legends, both in the main text as well as in the supplementary information could be more effectively used to go beyond a mere description of the graphical elements to make a better description of the main message. The choice of visual and tabular elements in a manuscript of this kind is fundamental for conveying a message as bold as the one the authors intend to send. Perhaps a re-evaluation of the selection of elements would greatly benefit the manuscript.