Dear Authors,

I have read the manuscript ‘How does nitrogen control soil organic matter turnover and composition? – Theory and model’ with much interest. Unravelling the different processes affecting soil C – N interactions is an important topic, as is the correct incorporation of these processes in mechanistic soil organic matter models. With my contribution to the open discussion, I would like to focus on a few modelling aspects of the study. I hope my feedback helps the authors to clarify these aspects in the manuscript.

My main feedback relates to the choice of the model (CENTURY). The structure of this model is based on the humification theory, which has been criticised in the literature (Lehmann and Kleber, 2015 (doi.org/10.1038/nature16069); Kleber and Lehmann, 2019 (doi.org/10.2134/jeq2019.01.0036)) and is considered outdated. Although the names of the pools have been changed to measurable pools, as was done in previous studies, the structure is different from the general understanding of SOM cycling (e.g., there is no DOC pool, there is a direct flux of POC to MAOC, although in reality POC is depolymerised to DOC first, which can then either be adsorbed on minerals, taken up by microbes or leached from the soil, and the amount of soil microbes does not affect the rate of decomposition (although this is implemented as a scenario in the study)). However, the authors consistently refer to this model as ‘process-based’. Over the past two decades, multiple models simulating coupled soil C – N cycles using measurable pools, while explicitly simulating established mechanisms which are addressed in the present study (e.g., adsorption and desorption of DOC on/from soil minerals, the effect of microbial biomass (or enzymes) on rates of polymerisation and decomposition, microbial CUE, etc.). Therefore, I would suggest the authors to better justify their choice for this model, over other, more mechanistic, SOM models, as these explicitly incorporate many of the simulated mechanisms related to soil microbes and MAOC discussed in the present manuscript.

Related to this, in L462, the authors cite studies using models which are very similar (Chen et al., 2019; CASA CNP in Eastman et al., 2024), or more mechanistic (MIMICS in Eastman et al., 2024) to the model they used, and refer to these as ‘process-deficient’. How do the authors reconcile this with referring to CENTURY as a mechanistic model? In the same sentence, they refer to models containing multiple mechanisms as containing ‘many uncertain parameters and hence [it is] difficult to verify the relevance of each process’. However, in their study the authors use mainly default parameters for the CENTURY and FORCENT models. I would encourage the authors to explain why the parameter values in the latter would be less uncertain compared to those in state-of-the-art mechanistic SOM models.

In their study, the authors compare simulated effects of N addition to Swiss forest soils with the results from a global meta-analysis. I would encourage the authors to better (graphically) represent the differences in environmental characteristics between the Swiss sites and the sites from the meta-analyses. Related to this, the authors justify the comparison to results from global meta-analyses by stating that ‘most experiments were conducted in temperate forests’ (L330). Which portion is ‘most’? It would be good to justify why not only these experiments from temperate forests were used in the comparison, instead of also using experiments from other ecosystems.

Specific feedback

L31-32 and L637-638: You state that your result challenge the ‘common assumption that plant is the primary respondent to N’. This is a strong statement, as you (from what I understood in the manuscript) did not simulate the response of plants to N addition, or interactions between the response of plants and soil microbes. Therefore, it makes sense that without simulating the response of plants, the response of soils will be large. However, as the response of plants wasn’t quantified, I suggest to revise this statement.

L52: you state that ‘Efforts to synthesize the diverse responses into a coherent theory and model are lacking’, although many modelling studies have studied this effect, of which you cite a few. Therefore, I encourage the authors to modify this statement. In addition, as this is a modelling study, it would have been useful to summarise the outcomes of these previous modelling studies with respect to the response of soil organic matter characteristics to N addition.

L166: Was the turnover rate parameter for SOC3 adjusted based on simulations of the total SOC stock, or were measurements of MAOC stocks available? It would also be useful to mention the new value for the turnover rate parameter for SOC3 here. Is this value in line with reported turnover times of MAOC in forest topsoils?

L187: It would be good to provide references for these meta-analyses.

Section 2.3: I appreciate the authors testing many N responses. I would encourage the authors to provide graphs that show how the proposed variables and rate modifiers vary in response to the independent variables, as this is difficult to understand from the equations alone. In addition, it would be good to mention if the proposed equations are based on literature, or if the authors formulated these equations themselves.

L244: how is the ‘monthly priming effect’ defined?

L254-255: I suggest reconsidering the subscript ‘retard’

L259: It would be good to provide citations for these ‘widespread experiments’

L287 and L301: the correlation coefficient ‘Pearson r’ is not a measure for model performance, but for the proportion of explained variation. I would suggest reporting an error measure such as RMSE instead.

Section 2.5: it would be good to mention here down to which depth the simulations were performed

L307: ‘[…] until the pools were at steady-state’: for a better evaluation of the model performance by the reader, it would be good to report the simulated turnover times of the model pools, and how C was distributed between SOC1, SOC2 and SOC3.

L318-327: as the data was extracted from global meta-analyses, it would be good to report, for example, from which ecosystems these data were collected. In addition to table 2, the authors can consider a graphical representation of the environmental characteristics of the sites from the meta-analyses, overlain by the characteristics for the Swiss forests. This information is essential for the reader to evaluate the comparison that is made with the Swiss forest sites.

Related to this, on L575 the authors state the ‘environmental gradient coverage [of the Swiss sites] differs *slightly*’ from the sites in the meta-analyses, while, for example, MAT for the Swiss sites ranges from 6.5 to 9.4 °C, while this is between 1.0 and 21 °C for the sites from the meta-analyses. This statement thus seems misleading, and a better representation of these differences seems necessary to inform the reader, as the comparison between the simulation results obtained from the Swiss sites and those from the meta-analyses is at the core of this study.

L354-358: It seems that the base model was not able to accurately simulate total SOC stocks for the Swiss forest sites (Fig. 3b). The authors justify this by stating that ‘a close quantitative match of C stocks may not actually be desirable […]’. However, I encourage the authors to better justify why they thrust results of a model that is not able to simulate total SOC stocks accurately, and to better explain why this was the case. For example, why were the model parameters not calibrated to match the conditions in Swiss forests? To evaluate the model results, an even more important aspect of the model outcomes is the simulated distribution of SOC and N over the different model pools, and the simulated turnover times of these pools (e.g., which portion of simulated SOC was present in SOC1, SOC2 and SOC3). I would encourage the authors to also report this information.

L368: It would be good to report the value for the ‘low SOC3 parameter’ here

Fig. 5a: while the regression line looks fine, a large portion of the simulated data is overestimated (y-values between 13-16), while another portion is underestimated (y-values between 7-9). This does not seem in line with the statement of ‘the models capturing MAOC:N reasonably’. I would suggest the authors to revise this statement.

L461-465: instead of dismissing previous modelling studies as ‘process-deficient’ or ‘containing many uncertain parameters’, it would have been worthwhile to summarize their findings in the introduction as a background to the modelling study that is presented here.

L485: ‘enhanced SOC3 turnover’: I would suggest to report this turnover rate and evaluate if this is in line with previously reported turnover rates of MAOC in forest soils.

L509: what is meant by ‘simplistic’ decomposition?

Tables and Figures

Fig. 1: It was not clear to me what the y-axis label ‘Labile C:N’ means. Can this be clarified?

Table 1: In the second row under (2.), should it be ‘increasing N limitation?’, instead of decreasing?

Fig. 3: a unit needs to be reported for the RMSE

Fig. 7: it would be good to provide more information about this figure in the caption.