Ma and others model the carbon balance of biocrusts at multiple sites with differing climatic conditions. The results provide interesting context for understanding biocrust physiology worldwide but the presentation needs work for simplicity and clarity.

Abstract: more quantitative if possible. This extends to the introduction starting especially on line 50 where the text could benefit from numeric values to help the reader understand the magnitude of C stocks and fluxes that biocrusts interact with.

Regarding 69: when environmental conditions are in an optimal range vascular plant would usually be favored, so what constitutes ‘optimal’ for biocrusts here?

92: ‘a Q10 relationship’

Regarding longwave radiation, I question somewhat the use of the ERA5 data if avoidable; were local surface temperature data available at any of the sites and if so how closely do these data align with the ERA5 data?

Reading on to 127, if surface temperature are available, avoiding ERA5 in the model would be advisable. Line 127 should be in the previous section.

On line 174, something more than a visual comparison is necessary. In Fig. 1 a-d (should be b-e because the left panel should be a), the consistent early peak in the simulated temperatures should be corrected for if possible because the heat capacity that entered the model is obviously incorrect. I’m not sure how this interacts with the discussion 188 if temperature was approximated. When is the temperature approximated and when was it modeled? Section 2.3.2 needs improvement also on line 204 regarding the negative photosynthesis rate. This could be a negative net C flux or the Rd parameter exceeding carbon uptake, but photosynthesis itself isn’t negative.

I’m not entirely convinced about the usefulness of section 2.5 and its description was rather meandering. That being said Fig. 6a is interesting but I wish that the normalization was done differently as a normalized value of < - 10 (for the case of air temperature) is difficult to discern.

How does the data driven model in 2.3 differ from LiBry in 2.6 especially given that LiBry doesn’t fit the observations well as described in 3.2? Was there an effort to improve LiBry given the results of the study?

362: not the moisture required to give them the ability to be active?

The Fig. 7 legend could use more detail. I had to search what the “fixed” and “dynamic” parameters meant. They were detailed in section 2.5, where these terms could have been more clearly defined.

422 and elsewhere: subscripting (here in CO_2) is inconsistent, used correctly here but not in other places.

For precipitation, how is dewfall and other factors that are important to biocrusts considered? In 477 and elsewhere, is vapor pressure deficit not a more physiologically consistent approach for estimating stomatal function than relative humidity and/or is relative humidity mostly a surrogate for the surface being sufficiently wet for biocrust function to proceed?

569 and elsewhere: wasn’t there just one alpine site such that a more accurate summary would be “at an alpine site”?

570: “obvious” is subjective.

GENERAL COMMENTS

This is a paper that endeavors to simulate carbon balance in biocrusts. The approach is very nice and has high potential, but the model does fail in some cases and the authors should be more up front about this. Fortunately, in my view, the places where the model fails are interesting and can be discussed. The title and abstract should reflect that a model was constructed and tested and did not work in all cases, and the reasons should be enumerated and explored. This is done for one source of uncertainty, the environmental conditions; however, it is done inadequately for what is likely the larger source of error: the physiological parameters of the biocrusts. Carbon balance numbers should be listed and emphasized in the abstract, both the believable and unbelievable ones. As the model does not always work, the claims about uncovering drivers and mechanisms should be substantially reduced to maybe a speculative hint here or there, not proffered as major claims in the title and abstract. A question I am left with is: after seeing the failure at some sites to estimate a positive C balance, does this mean the dryland ones are also wrong and giving what might be a right number for the wrong reason, or does the model genuinely work better at those sites and if so why. These things are touched on but should be the main focus of the discussion. Generally, I want to emphasize again that physiological parameters being a likely source of uncertainty needs more attention above and beyond the possible effects of seasonal acclimation. All this said, I like this study and commend the authors for an ambitious undertaking.

SPECIFIC COMMENTS

Title: going back and re-reading the title, I think it is not accurate to say 'drivers are determined' for sites where the authors later explain that some of the C balance numbers are quite unrealistic (eg -96 g/m2/yr).

Abstract

L22. 'along a climatic gradient' is pretty vague at this point in the abstract and I am having trouble following what was done. How big is this gradient?

L25. effects on what? Looks from context like carbon balance, but I had to go back to previous sentences to figure this out.

The last sentence of the abstract indicates that the key conclusions are methodological while the title and introductory section suggests there will be new mechanistic insights. The previous sentence about climate change came as a surprise since climate change was not mentioned before that and the stated conclusion in this sentence is also vague and unsatisfying. With this mix of basic system function, applied stuff like climate change, and methodological issues, the abstract leaves the impression that the study will be unfocused. [Note: upon reading the whole paper, it is more focused than I thought it would be; thus, I recommend the abstract be rewritten to reflect this.]

Having read further in the paper, making it clear early in the abstract that this paper is mainly based on a modeling approach is recommended. I recommend to include something like "While there is a lot of empirical field data on biocrusts, rarely have these been assembled into a comprehensive modeling framework. Here we use such a framework to explore factors such as biocrust C balance in contrasting climates" I recommend to say this before talking about the environmental factors and gradients and it will make more sense to readers. Also I would back way off saying the 'key drivers are determined' based on what follows.

Introduction

The first paragraph is an overgeneralized description of biocrusts and their function leaving me not sure where the paper is going. I recommend to hone in more clearly on setting up the modeling approach and discussion of the biocrust role in ecosystem C balance to set up the later material.

The second paragraph is much better, setting up the importance of long-term C balance in biocrusts.

Finally by the end of the introduction I understand what the paper is about. It is a modeling study exploring C balance in biocrusts over a range of conditions. This needs to be MUCH more clear in the title and abstract.

2.1. I recommend that instead of making the case that the sites were chosen because they are the only sites with these data in the world (a dubious claim in my opinion - I can think of several other well-studied biocrust-focused sites that probably have enough data to take a similar approach), the authors should make the case that the sites were chosen to enhance the work done by the authors at these sites, which would be an adequate justification. The one exception to this might be the innovative 'activity measurements' the authors mention. If this is the case, I recommend to be more clear about this and explain why other proxies of activity (soil moisture perhaps) could not work at other sites.

L143. Soil-surface boundary layer CO2 is often higher than this due to diffusion from soil. This should be mentioned and the ramifications considered.

L144. Were these intact biocrusted soils or were the biocrusts removed from the soil and measured in an enclosed chamber separate from the soil column? Same question for L149-160.

L153. For poikilohydric biocrust organisms, time since hydration is a big factor in how these C balance values will look. It may be in the cited papers, but it should be discussed here too. The whole conclusions of the study could hinge on differences between, say, 1 hour vs. 4 hr vs. 24 hour wet-up periods for the biocrusts examined. Whether this has been adequately taken into account or not, it should be described how this issue was handled.

Table 1. 110 mm is pretty low. I'd probably call that arid rather than semiarid. If the determination is based on something else like aridity index, that should be reported.

Table 2. 96 is a big loss of C. The dryland values are in line with what I would expect--small positive fluxes. These data are really valuable and this is a nice contribution of this study. Not a lot of people try to calculate these as carefully as done here. A selection of these numbers should be in the abstract to make the goals and findings of the study more concrete up front.

Sensitivity of the environmental factors is fine and appears to be well done, but what about sensitivity to the estimates of the biocrust physiological parameters? Those are the ones that likely have much more substantial errors in my view. The high variability in these parameters among individually measured biocrusts is even noted by the authors. What if the light response or moisture curve or temp response is misshapen, have intercepts at 0 that are slightly off, etc?

L398-407. Good discussion and I agree this aspect of the model throws really reasonable values, just from first principles. A shrubland that might be found in a 100-300 mm MAP ecosystem typically has an NPP on the order of 100 g/m2/yr and I would expect biocrusts to be an order of magnitude or two below that given their size, amount of chlorophyll, etc.

L410-413. This needs to be further unpacked. It of course makes no sense for them to lose as much carbon per year as a shrubland grows. Which part of the model is responsible for this nonsensical result?

L419. This is a key point of the paper. I recommend the authors discuss it here, not below.

L436. There are a number of field manipulations showing exactly this in Spain and USA. Could be worthwhile to cite here.

L436-504. This section on abiotic factors is long and includes a lot of speculation. For example, the paragraph on humidity goes through a lot of hypotheticals and discussion when to me the humidity didn't stick out as a huge factor in the earlier parts of the paper, with the authors saying that co2 and air temperature were more relevant.

L511. Here we get back more to what I care about: why did those estimates come out with big losses? An idea is suggested, which is that the long periods of suboptimal conditions are the problem. I would bet it goes something like this: the net C flux field/lab measurements slightly overestimate the C losses because of the timing of the respiration measurements with respect to hydration or the stresses of an incubation or a number of other factors. Plus, it's hard to separate crust from heterotrophs so you always get some heterotroph signal in those physiological measurements. Then this slightly exaggerated C loss gets multiplied by all the times when the conditions are not great (most of the year) and it looks like a ton of carbon is lost. Maybe my narrative of what went wrong here is itself quite wrong, but I think if sensitivity to physiological parameters is added and then a more complete post mortem of what happened with these calculations is done, the whole study will make more sense. I want to see a story like this, but that the authors provide to the best of their ability.

L515-525. Seasonal acclimation sure, but what about inaccurate estimates of physiological parameters? It's always a possibility. These things are very hard to measure. I see that the LiBry model is being used here as a talking point for why the numbers are not correct. I am not totally sure I buy the seasonal acclimation argument. It could be a factor but I think it is a lot more than that on the physiological side of things.

L559-560. Ok yes this is what I have been saying for the whole review! The authors are aware of this. It needs to be discussed MUCH more thoroughly throughout. It doesn't make sense to exhaustively turn over all the abiotic variables when the physiology is very possibly the biggest source of error. Ideally it would be sensitivity-tested like the environmental variables. How sensitive is the model to parameter estimates on light response curve, A-Ci curve, temp response, respiration q10, etc.

L563. This I agree with. It's a very nice approach, I think it just needs a more complete explanation for the modeling shortfalls. It is fine that it fails, it just has to be better described why, with quantitative information. The acclimation piece is a start, but I have a feeling the shortcomings of the physiological estimates are a lot greater than just lack of accounting for acclimation. Various physiology numbers are probably slightly wrong and the model is likely sensitive to this.

L569. This paper has multiple sites, but does not have an explicit spatial component so I would not use this word here.

L571. I do not find it particularly insightful to say rainfall is relevant in drylands. This is a given. Also I don't follow the argument about CO2 and question the assumed value used (400 ppm). I would focus the conclusion on where the model succeeds and why and vice versa.

L581-585. This paragraph doesn't add much and can be removed.