Tang and Riley: The SUPECA kinetics for scaling redox reactions in 1 networks of mixed substrates and consumers and an example application to aerobic soil respiration
This is a revision of this paper. The initial reviews were mixed, with reviewer #1 admiring the conceptual elegance of the model, but feeling that the nature of the assumptions meant that it wouldn’t likely be taken up and used by many biogeochemists—this reviewer stated “From a soil ecology standpoint, some of assumptions were very constraining, while others were unrealistic.”
Reviewer #2 was much more critical but the authors argue that this reviewer “largely misunderstood our development and analyses.”
Frankly, I can’t blame reviewer #2 for misunderstanding major aspects of the paper. The math is complex, and I’ll have to take the authors’ and other reviewers’ evaluations of the derivations.
But much of the English description is largely inexplicable. I’m not a mathematician, but I have worked with biogeochemical models and chemical kinetics, and when I read statements like: “This contrasting requirement on parameters, as we will show later, fails the DM kinetics to achieve a consistent scaling of substrate-consumer interactions for generic biogeochemical modeling” I’m really at a loss for understanding what it’s supposed to mean.
At a conceptual level, I can clearly see the value of this work. Soils are a complex network of chemical reactions that we usually treat as an aggregate mix, rather than as a network of separate independent chemical reactions. This approach takes a conceptually appealing approach to treat soil organic matter turnover as a network. By the author’s arguments, this approach is better, more robust and more accurate than other approaches to formulating multi-reaction networks of organic matter reactions.
However, the paper suffers terribly from a lack of connection to real data to show us that all of this elaborate math really does offer an improvement over other approaches. There is limited comparison to other model approaches to show how it works. Yes, it compares it to the ES and simple SU approaches, but these are both complex conceptual approaches as well. There is no comparison to more traditional approaches, or evaluation of whether adding a suite of additional variables and parameters really creates a more statistically robust approach. I see no mention of real materials or real reactions in the paper. The model is parameterized with “dissolvable organic carbon” as the substrate and honestly, I consider this a major weakness—why go to this vast level of mathematical complexity but to still use a chemically undefined substrate? I don’t know what dissolvable organic carbon is! It’s not just what’s in solution and since if you extract a soil multiple time you keep getting more dissolved material out—hence I don’t even know how I’d measure it.
Additionally, the authors compare the model to one experimental data set, and argue that it fits the data well, but honestly, it really doesn’t. Yes, the model kind of matches the observed data, but I have two issues. First, I have to take my glasses off to convince myself that the model lines match the data well (and my vision without glasses is pretty terrible). Is this better than you would get with other modeling approaches? Is it really better than applying a response function to a Century-type model? And second, actually, the match doesn’t seem very good anyhow—the data seem flatter than the model lines; higher at low relative saturation and slightly lower than the model predictions at high relative saturation. The scatter in the data makes that less than perfectly clear, but that’s what I’m seeing. So if I had to ask whether the model did a great job of capturing the data, at best I’d have to be pretty equivocal. All this work and we still have a relationship that is going to misrepresent respiration at low water contents?
And that leaves me wondering again whether this is really better than simpler model approaches? This model approach involves huge complexity and heavy parameterization—could a less complex model do as good a job of matching the data? The authors don’t show that and hence I am left wondering about the real value of this enormous exercise. Reviewer #1 was impressed with the mathematical exercise but worried whether this model had a chance of ever being picked up and used by a broader community that just Tang and Riley (who presumably understand it).
So I’m left with a conundrum in what I should recommend as a reviewer. A) I don’t have the expertise to fully evaluate the math or derivations. I know Tang and Riley’s skills so I feel comfortable in trusting that they performed the math reliably. But I remain thoroughly unconvinced by the paper that the exercise was really worth the effort or that it has substantial value to the broader biogeochemical modeling community. The paper doesn’t do an adequate job of showing me how I would apply this model in “the real world” and the one comparison to data isn’t very impressive—it doesn’t convince me that the effort was worth it. How do I apply this to real soil and real substrates? I agree with reviewer #1 that the model makes some assumptions that are either excessively constraining or perhaps unrealistic. How do we apply it?
Specific Comments:
9: I could accuse CENTURY of “explicitly representing microbial processes”! The processes are explicitly microbial, even if the model formulations don’t explicitly include microbes as drivers.
4: 1-4: we contend that readers should not misunderstand our discussion of scaling below as an attempt to do ecological aggregation (e.g., Iwasa et al., 1987; 1989). Rather we are presenting a methodology to improve the consistency in formulating the microdynamics for ecological aggregation.
Is this supposed to be clear? If so it fails. Perhaps because I’m not a mathematician, I don’t know the ins and outs of “ecological aggregation” and so this section derails the development for me. The distinction between “ecological aggregation” and “the microdynamics for ecological aggregation” is unclear to me and suffers from a major case of “curse of knowledge”: you have to know a lot to capture the half described nuance here. Inserting this to defend against a reviewer who you argue completely misunderstood the work seems a poor idea. Additionally negative arguments are almost always challenging. Don’t tell us what this is not—instead just tell us what it is, and do it clearly enough that it is obvious what it isn’t.
5: 7 & 9: You don’t need “the” in front of “two substrate” and “multi-substrate.”
6: 1: You do need a “the” in front of “consumer-substrate complex.” I’m now getting annoyed. I understand that Jim Tang may not speak English as a native, but Riley does and I can only conclude that you didn’t read this carefully enough.
6: 15: “which are mathematically identical”
6: 15: Oh, come on: “is mathematically identical” is then followed by “and they”? Why has this not been adequately proofread for English?
24:8: Langmuir isotherm. I’m uncomfortable with having to do this. But that is the authors’ point—for SU kinetics it appears necessary. Hence the problem with SU kinetic modeling. This is mixing equilibrium and non-equilibrium processes. The very reason for developing a kinetic model is because soil is a wildly non-equilibrium system. Extracting the “free substrate” concentration by assuming its in equilibrium via the Langmuir and then applying kinetic modeling seems questionable to me. Will the SUPECA approach avoid this problem?
23: 15: “We evaluated the accuracy of SUPECA” How do you evaluate the “accuracy” of a model when it is only being run with theoretical values? Doesn’t “accuracy” imply that there is a real, defined target that you are trying to match? This shows up on the page 24 where the authors state “The SUPECA kinetics is more accurate in terms of both goodness of linear fitting and RMSE.” In analytical chemistry, accuracy is defined by how close you come to the actual value of an analyte, while precision is the tightness of fit of your different replicates, regardless of whether they are accurate or not. So this seems closer to an estimate of precision than of accuracy in a chemical sense. I guess that the measure of “accuracy” is really that the SUPECA model much more closely matches the EC model prediction—but there is no absolute target here. This is still all theory and so there is no defined “correct” here to measure accuracy, is there?
25: 14: “uniformly distributed across the soil pores” Well, how likely is that? This seems one of the questionable assumptions mentioned by Reviewer #1.
25:13: Is DOC “dissolvable” or “dissolved” organic C? The normal is to consider it “dissolved”—i.e. in solution. There is much C that can be dissolved but which may not be in solution. In classic studies, Jerry Qualls showed that if you extracted a soil sample multiple times, you kept getting more and more C out. So what is DOC? By the standard definition, it would only be what is in solution; by this terminology, it could be all of that potentially extractable material.
27: 5: Is “prognosed” a technical term in modeling or is it just a really weird word choice? Since this is the first time in my life I can remember seeing it used as a verb, instead of the original noun form of “prognosis” from medicine, I find it unclear and jarring.
27:23: “Such a result strongly contrasts with the popular approach in existing soil BGC models (e.g., Koven et al., 2013; Tang et al.,2013), which apply a soil moisture response function as a multiplier on an unstressed rate.” I don’t understand this concern. I would argue that many response functions in 1st order BGC models actually represent emergent functions that reflect an integration of biotic and abiotic factors. So how is this criticism different from anything else?
28: 9: “Figures 6 and 7 demonstrate that soil aggregates may have profound influence on soil carbon decomposition rates.” I think we already knew that.
Fig. 4 caption. It would be nice if the caption identified what the graph showed—there is no mention of which reaction system this applies to. I’m also concerned that the approaches give concentration ranges that differ by a full order-of-magnitude. It’s also notable that the SUPECA approach doesn’t fix the scatter above the line (thought it reshapes it and the scatter is greater in the middle of the range, rather than growing with EC prediction). Notably, the SUPECA approach seems more to put a lower limit on the scatter—it can’t go much below the EC prediction but can go way above. |
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