Apologies I first posted this as a community comment

Review of Tang and Riley “A reanalysis of the foundations of the macromolecular rate theory”

This paper comprises two major elements (i) the paper starts with a critique of macromolecular rate theory (one of several models of the temperature response of enzyme activity) and (ii) development of chemical kinetics theory to predict temperature dependence of enzymic reactions which includes the assumption of an equilibrium between active and reversibly denatured enzymes. It is important that we acknowledge that no ‘simple’ model will fully capture the complexity of individual enzymes and their coupled activity in biochemical pathways. There are hundreds/thousands of interacting atoms that play a role in enzyme catalysis and so we are attempting to develop much simpler models that capture the general behaviour of enzymes and biogeochemical processes in useful and predictive ways. 

The authors present a model for the temperature dependence of enzyme rates that postulates an equilibrium between native and non-native conformations of the free enzyme (, Figure 1b).  This is a variation on the “equilibrium model” of (Daniel and Danson, 2013) that postulates an equilibrium between active and inactive conformations of the enzyme-substrate complex (). This equilibrium model gave rise to macromolecular rate theory (MMRT) which captures the  equilibrium in a heat capacity term (). These three models are part of a large family of models that date back at least 70 years which try to rationalise the deviations from “Arrhenius behaviour” seen for enzymes, organisms and ecosystems and specifically capture the observed temperature optima. Thus, the current manuscript continues that tradition and testing this new model is a useful endeavour – in particular characterising the  equilibrium via experiment and/or simulation.

General comments

The model presented in this manuscript is motivated (in the title, abstract and introduction) by two criticisms/assertions (ln 36 onwards) about MMRT which are incorrect: Firstly, MMRT does not assert that the Michealis-Menten equilibrium constant, K_M, is independent of temperature. This would be to ignore the basic thermodynamic relationship between equilibrium and temperature: lnK=(‑∆G/RT).  Secondly, MMRT does not assume that the enzyme is saturated at all temperatures. MMRT models the temperature dependence of the rate constant, k, for rates at different scales (enzymes, organisms, ecosystems). For example, at high concentrations of substrate, the Michealis-Menten equation simplifies to rate = k_cat[E] and MMRT provides a model for the temperature dependence of k_cat. At low substrate concentrations the Michealis-Menten equation simplifies to rate = (k_cat/K_M)[E][S] = k₂[E][S] and MMRT provides a model for k₂ (which includes K_M). This is discussed in some detail by Arcus and Mulholland (2020). When modelling respiration rates in soil, for example, we expect that substrate concentrations are low and thus the latter simplification applies. We can nonetheless rule out K_M as the source of deviations from Arrhenius behaviour for the following reason: If the non-Arrhenius behaviour for soil respiration were a consequence of K_M then we would expect this behaviour to disappear at high substrate concentrations and this is not the case when glucose is added to soil. Indeed, the deviations from Arrhenius kinetics become more pronounced when glucose is added rather than less (e.g., Numa et al., 2021). Thus, the deviations from Arrhenius behaviour, as modelled by MMRT, are not a function of the temperature-dependence of K_M. 

Specific comments

1. While at least half of the manuscript is devoted to development of a chemical kinetics theory, this is not reflected in the title and only gets a single line in the abstract. To me, this paper is about the new model and both the title and abstract should reflect this approach. It is more than reasonable to debate relative value of MMRT in the discussion when taking into account the general comment above.
2. In the introduction, not only should MMRT be described and critiqued as a temperature dependence model but the array of other equilibrium models, and (e.g. the DAMM model) (Davidson et al., 2012), square root model etc...
3. The developed theory is only tested on data from single enzymes (Hobbs et al 2013) and not biogeochemical processes so how this work translates to a journal that focuses on biogeochemical modelling is not clear. Would this be better submitted to a biochemistry journal that focusses on enzymes? Also, see line 149 the authors state a more complex model is needed for soil, so it it not clear how the author suggest a developed model fits in biogeochemistry.
4. Ln 42 the authors should define what reversible denaturation is in their framework. As large molecules, enzymes constantly undergo large flucuations resulting in an array of conformations that bind the substrate to varying degrees. Are the authors assuming only 2 states (active and inactive) rather than a continuum of binding/catalytic states with varying Kms?
5. Ln 90 Schipper and Liang and others primarily suggested using MMRT rather than Q10 or Arrhenius functions because neither latter function resulted in a measure a Topt (and therefore Tinf).
6. Ln 205 and elsewhere (ln 79). There needs to be a clear description of the differences between the dCp for the different models. In the current paper, dCp is the change in heat capacity between the reversibly denatured state and the active state. In MMRT, the dCp is argued to be the heat capacity difference between the enzyme-substrate complex and the enzyme transition state. There is no reason that these should be the same size of sign as these are not the same processes.
7. Ln 133 enzyme denaturation was shown experimentally to have Topt without enzyme denaturation in Hobbs et al 2013. Are the authors invoking reversible denaturation here? See also ln 143 are the authors arguing for including irreversible denaturation or reversible denaturation? These are very different concepts.
8. Ln 155 why can the uncertainty ranges of the fitted parameters not be determined? This should be about the fit of the data and not the variation in data extraction?
9. Ln 180, Figure 3 Is this modelled data? The authors argue that Topt increases with decreasing substrate concentration but do not provide error bounds on Topt for substrate concentrations ranging between Ko and infinite substrate. Is this a real change in Topt, that is, do the authors believe that a modelled increase in Topt of 1C (figure 3d) or 3C (Figure 3a) is real, based on a 4-parameter fitted model? This is something that could be experimentally tested. In contrast, measurement of respiration when glucose or litter was added to soil shows decreases the temperature optima (Robinson et al., 2020; Numa et al., 2021)
10. Figure 3b why is the maximal rate of c3 (substrate 10x Ko) so much lower than when substrate is limiting c1. Would you not expect higher rates when substrate was not limiting?
11. Also figure 3d seems to have bulge in the curve at around 300 K, which is not normally seen in experimental data. Is this considered as realistic or a function of the model?
12. Ln 187 what is meant by the phyisological optimum - what concentration of substrate is this referring to?
13. Ln 197 MMRT has been used to capture differences due to changes in substrate availability on Topt in soil (Numa et al., 2021)
14. Ln 201 Is the assertion that higher Topt occurs with high substrate availability is a consequence of the developed model but not observations? Should be clearly stated. Is this extrapolating beyond the parameters used to model the enzyme in the first place?
15. Ln 206 a comparison between dCp between the model developed by the authors and MMRT is not reasonable these are different phenomena as pointed out above. In the current paper, dCp is the change in heat capacity between the reversibly denatured state and the active state. In MMRT, the dCp reported is argued to be the heat capacity difference between the enzyme-substrate complex and the enzyme transition state. The dCp for transition state binding (that is MMRT dCp) for MTAP has been measured by Firestone et al (2017)and is same as inferred by MMRT fits within 5%.
16. Ln 215 Can the authors formalise what was considered wrong with the La Mer study rather than broad statement that is was considered flawed. This paper is not referenced in the early MMRT papers (Hobbs et al., 2013) (Arcus et al., 2016)
17. Ln 221. How can the authors argue that the developed model is a “better mechanistic representation of temperature dependent biochemical rates than MMRT”? This is an inference is based on a better fit to data using a model with 4 parameters (1 more than MMRT, as noted ln 140, so not surprising that the fit is better). There is no experimental testing of the underlying mechanism proposed in their model. There is also no accounting for the addition of another parameter using, for example, AIC, which probably should be done.
18. Ln 229. Again the authors argue their model is “better” than the Peterson model simply because the Peterson model has an extra parameter and no AIC calculated between comparative models. It is unclear how the authors are considering the relative merits of different models. Is it better to consider number of fitted parameters to describe the response or mechanistic representation?

Overall, the current manuscript presents an interesting approach on the temperature dependence of enzyme-driven rates and investigation of the phenomena contained in the model warrants investigation. Our view is that this is sufficient in itself, and does not need to be prefaced by incorrect assertions about MMRT. In biogeosciences, we are seeking tradeoffs between fully mechanistic model of temperature response and those that are useful. As the saying goes: All models are wrong some are useful. 

References

Arcus, V.L., Prentice, E., Hobbs, J.K., Mulholland, A.J., Vander Kamp, M.W., Pudney, C.R., Parker, E.J., Schipper, L.A., 2016. On the temperature dependence of enzyme-catalysed rates. Biochemistry 55, 1681-1688.

Arcus, V. L. & Mulholland, A. J. Temperature, Dynamics, and Enzyme-Catalyzed Reaction Rates. Annual review of biophysics (2020) doi:10.1146/annurev-biophys-121219-081520.

Davidson, E.A., Samanta, S., Caramori, S.S., Savage, K., 2012. The Dual Arrhenius and Michaelis–Menten kinetics model for decomposition of soil organic matter at hourly to seasonal time scales. Global Change Biology 18, 371-384

Firestone, R. S., Cameron, S. A., Karp, J. M., Arcus, V. L. & Schramm, V. L. Heat Capacity Changes for Transition-State Analogue Binding and Catalysis with Human 5’-Methylthioadenosine Phosphorylase. ACS Chemical Biology 12, 464–473 (2017).

Hobbs, J.K., Jiao, W., Easter, A.D., Parker, E.J., Schipper, L.A., Arcus, V.L., 2013. Change in heat capacity for enzyme catalysis determines temperature dependence of enzyme catalyzed rates. ACS Chemical Biology 8, 2388-2393.

Numa, K.B., Robinson, J.M., Arcus, V.L., Schipper, L.A., 2021. Separating the temperature response of soil respiration derived from soil organic matter and added labile carbon compounds. Geoderma 400, 115128.

Robinson, J.M., Barker, S.L.L., Arcus, V.L., McNally, S.R., Schipper, L.A., 2020. Contrasting temperature responses of soil respiration derived from soil organic matter and added plant litter. Biogeochemistry 150, 45-59.

General comments.

The paper provides a critique of the MMRT model, concentrating on its underlying assumptions as stated by the authors. This makes for a useful contribution since MMRT has proved popular in several fields, such as soil science. Should the model be flawed or incomplete then these applications may have reduced value, particularly in the journal's subject area. The paper does not make a direct comparison with alternative models, though it refers to a number of them, collectively termed `chemical kinetics theory'. Certainly empirical models would not be of interest here, but in any case, I do not consider such comparisons are needed since they can needlessly burden a paper with material than the interested reader can seek out. 

Specific comments.

In the introduction there is a brief coverage of publications that refer to MMRT. I found this could have been more comprehensive. It could have dealt with a number of alternative models and, as noted earlier, that would burden the paper.

L20-25. The authors note that Hobbs et al. (2013), Schipper et al. (2014) claim MMRT is able to better than the Arrhenius-like functions for various ecological properties. I suggest that it may be worth adding here that while Schipper et al. (2014) compares MMRT to a Arrhenius model it does not do any more than this, in that it does not, for example, choose to compare to the Ratkowksy 2005, Corkrey 2012 models. 

L25-30. Similarly, I would add that Alster et al (1016) does the same thing, but in addition, I would add that those authors unnecessarily dismiss other models as 'empirical' when, on examination, they do not appear be (e.g.  Corkrey et al (2012), Peterson et al (2004), Daniel & Danson  (2013)). This is a point of irritation since such claims are too easily repeated. 

L30-35. Examples (e.g., Ratkowsky et al (1983)) of papers as having parameters that are not biological interpretable. This seems a little unfair since that particular model is explicitly empirical. I suggest adding in references to other models that do have interpretable parameters and/or are based on thermodynamic principles such as those listed above.

Section 2.3. I found this derivation somewhat hard to follow (though interesting). Perhaps a little more could be added to assist non-specialists?

L130-135. I stumbled over the wording 'The motivating assumption ... many observations'. Perhaps tweak this to make clearer.

Figure 2. Given the scale used it difficult to closely examine the fits. But the majority of the fits appear excellent (except Barnase?). I was expecting comparisons to MMRT fitted lines since that is the point of the paper. For that matter, I speculate that the Ratkowksy 2005, Corkrey et al (2012) models and others would do as well and could be fitted. The fits are summarised as r2 values. The authors comment (L155-160) that uncertainties were not available, and that they were hindered by an 'ill-conditioned Hessian matrix', but I don't see why resampling could not be used to obtain 99% CIs bands (although they would be very narrow).  

L210-220. I found this enlightening. Please elaborate on what was flawed in La Mer (1933).

L230-235. The point made about Ohm's law is well made. This an important point since several of the references made (e.g. Corkrey et al 2012) refer to organismal growth rates and not enzymic data. While it might be argued that the complexity of processes involved at the  organism precludes such models being successful, this has been found to be incorrect, such in the above reference. Note that Corkrey et al (2014; 10.1371/journal.pone.0096100) may be relevant here since it also refers  to multicellular strains. It is such extensions from the enzymic to large scale processes that makes the paper relevant to the journal.