General comments:

The study by Giraud et al. (2025) presents a novel modelling framework that enables to simulate plant growth and related C and water flow within the plant, in interaction with a soil model simulating the interactions between C inputs from roots and soil microbial dynamics. Using this new and exciting framework, the authors have investigated in silico the effect of drought on soil C dynamics in the rhizosphere of a young hypothetical cereal plant, taking into account the effect of dry spells on root C inputs and on their dynamics in the soil. Considering this impressive piece of work, authors have already done a good job in synthetizing the main features of the coupled models and of their simulation outputs, although the manuscript remains quite dense and demanding for a reader not familiar with the original models. Besides the detailed comments below, here are my main remarks:

• The present work is built on two main models described in Giraud et al. (2023) and Sircan et al. (2025), which have been further improved and coupled here. Given that both previous articles have already tackled some of the issues described here (e.g. effects of water stress on plant growth and exudation, C dynamics in the rhizosphere), I would recommend the authors to try to focus more on the benefit of the coupling when describing the simulation results or discussing them, i.e. to focus on the effect of drought on root-derived C and their effects on SOC dynamics in the rhizosphere, while reducing the length of other, less important parts of the manuscript.
• Only few details are given in the main manuscript regarding the soil model, although some are indicated in Appendix. I think it is especially important to mention in the Material & Methods which soil processes have been taken into account or not in the model (not necessarily the equations), and how soil water content and soil temperature may affect microbial activity, so that the reader is able to better interpret the simulation results. In particular, I understood that the dynamics of the bulk soil organic matter is not represented, but only the dynamics of dissolved C. In this regard, the discussion on rhizospheric priming effect is interesting, but may be limited if all the “native” soil organic matter is not included in the model but only its labile part.
• The study focuses on the effect of drought, but here and there a change in temperature is mentioned during the drought period, without information about this in the Material & Method. If temperature changed over time or among the scenarios, this should be clearly stated; if not, this should also appear explicitly in the M&M.
• I keep struggling to understand the link between macroscale voxels and microscale domains of root segments or outside root segments… As it seems to be an important feature of this work and could be inspirational for other similar modelling frameworks, I would recommend authors to illustrate this a bit more clearly in Fig. 1, using realistic volume dimensions and showing which volumes/segments are included within which types of voxels.
• Given the number of variables investigated, crossing three scenarios of drought with three sets of soil parameters makes it quite challenging to get a clear picture of the main results in the end. An idea to clarify things for the reader could be to formulate some hypotheses about the effects of drought on root-derived C inputs to the soil and their dynamics in the rhizosphere, and to use the simulation results to validate or invalidate them.

Detailed comments:

Title: “carbon stabilization by plant” is a bit confusing. Also, authors have only investigated the dynamics of root-derived C (not aerial residues). Maybe something more neutral: In silico analysis of carbon and water dynamics in the rhizosphere under drought conditions?

Abstract:

L8 (and throughout the text): I am not familiar with the use of “biokinetic” in this context; I would suggest only using “kinetic”

L11-13: The reader may also wonder whether the drought experienced in the soil affected soil microbial activity, independently on the indirect effect of drought on C input by roots

Introduction:

L18: “and as an intra- and inter-domain signalling carrier” is not very clear to me, please explain/rephrase

L23: A comma is missing after “exudation)”

L37: “Plants can also exert direct feedback effects on themselves (e.g., aboveground-belowground feedback)” : this could be rephrased and simplified

L41: What about nutrient concentration gradients in the rhizosphere?

L76-79: This study extends the work of Giraud et al (2023) that focused on water and C flow within the plant. It would therefore be useful to state a bit more explicitly that this new study focuses on the root-derived C dynamics in the rhizosphere, taking into account the previous modelling framework of Giraud et al. for integrating the retroaction between water flows and C inputs in the rhizosphere, and coupling it to another model of rhizospheric soil C dynamics. Also, stating here at the end of the Introduction some hypotheses linked to water spells that will be verified with this new modeling framework would help the reader to focus a bit more on the originality of this work.

M&M:

L100: Meunier et al. (2017). Rephrase “and the coupled the stomatal”.

L123-124: This could be mentioned earlier on in the Introduction.

L126-137 and Fig. 1 & 2: After reading this several times, I am still not sure that I really understood the spatial scheme. There are macroscale soil voxels that may or not contain microscale root segments. However, both appear with the same size on Fig. 1. The terms macroscale and microscale are perhaps misleading? And what is then the perirhizal zone described as microscale in Fig. 2: one full voxel containing at least one root segment? Perhaps this could be clarified in Fig. 1, e.g. if showing a spatial description of the 3D root segments and the voxelization around it with realistic dimensions, and explaining where materials are actually exchanged and where specific reactions may - or not - take place.

L175: I don’t understand what Ω\∂Ω means

L219: For simplicity

L225: It would be useful to remind to the reader what ξ is, even if it was introduced a few equations ago

L289: Remove bracket

L329-332: If a new calibration was introduced to better reproduce expected trends, this should be emphasized more in the discussion, e.g. if authors choose to discuss the validity of hypotheses from their simulation results.

L347: Again, an illustration of all these different scales in Fig. 1 would really help the reader to understand more quickly how these scales are interconnected

L373: I don’t think that oligotrophic and copiotrophic have been defined anywhere. For a reader not familiar with soil microbial ecology, it would be useful to define these terms, and explain what are the expected behavior of these two microbial pools.

L380: It would be worth adding to which class these tresholds correspond to Poeplau and Don, i.e. 0.65 (threshold between degraded soils and moderate soil quality), 0.83 (moderate/good soil quality) and 1.16 (good/very good soil quality). It would also be important to state that the pedotransfer function used here was developed for German soils. One may also wonder whether this study from Poeplau and Don at field scale across Germany is really relevant to identify hotspots of C in the rhizosphere, this could lead to additional comments in the Discussion.

Results:

L405: “an increasing concentration” compared to what or according to what?

L408-432: For brevity, I would remove this part. If these simulations results have already been presented and explained in Giraud et al. (2023), shouldn’t the focus be here rather on the exudation and mucilage secretion in response to drought, starting at L433?

L449-450: Shouldn’t this sentence be mentioned earlier in the paragraph, before showing the actual results for each soil parametrization?

L456-458: I am not sure this is a very important simulation result to emphasize, given that the variation of this maximum exudation rate per cm2 among the scenarios is quite small.

L464-465: I don’t understand. If there are fewer roots, why is there a higher maximum C concentration?

Fig. 8: I would suggest to increase the size of the figures and to add a title to each sub-graph with the name of the variable detailed in the caption

L492: I still struggle to understand the meaning of a variable perirhizal truncated volume among the treatements... Please try to better explain why it is important and which biological or physical information it actually brings.

L499 and after: Please give the full meaning of each concentration when used in the main test, and not only its symbol, as reading and understanding this part is quite challenging…

L519: “the negative effects of the low soil θ on microbial activation” - but this relationship was not introduced in the Material & Method. It’s really necessary to better explain how the SOC model works and how it depends on soil water content and soil temperature.

L531: “the relative volumes of the SOC hotspots” - I continue to be lost…

L540: cycling

L564: “can cause a the”

Discussion:

L598: for further optimizing

L616-617: “the virtual plant’s starch pool can be interpreted as representing both actual starch reserves and newly synthesised wall material”. I am not sure that I fully understand the conceptual difference between biosynthetic growth and expansion. Is the second type of growth independent on C? I thought that root growth was explicitly included here in the C balance. If so, why would a part of the root growth be included in another term with starch?

L645-647: Now I understand why authors developed the description of such results at L408-432. The present statement could therefore be made earlier, at L408.

L679: a ratio of dormant oligotrophs and what other variable?

L707: “and organic C-dependent soil hydraulic parameters” - I guess that the benefit of having simulated specifically mucilage secretion in this study would be linked to this s feedback on plant water uptake. Maybe it is worth explaining this?

L709-719: I find this paragraph very interesting. However I am surprised that authors do not link this heterotrophic respiration by soil microorganisms to root respiration simulated during the dry spells, as the modelling framework enables to do this, which is rather unique. Looking at how the ratio between the two sources of CO2 evolves over time and how the resulting total basal respiration evolves over drought may reveal interesting features.

L735-736: “The lateDry scenario led to the lowest plant growth but to a higher SOC hotspot volume, indicating a more resource-efficient root system exudation.” Why would an increase in the number of rhizospheric hotspots be considered more resource efficient? Do authors suggest that SOC hotpsots are associated to a better feedback for the plant (e.g. in terms of water or nutrient uptake)? Please explain.

L870-871: This definition of microbial pools is really needed in the main text.

This work presents a technically ambitious and novel coupling of a three-dimensional functional–structural plant model (CPlantBox) with a microbial-explicit soil model (TraiRhizo) implemented in DuMux. The work addresses an important frontier—dynamically linking plant architecture, rhizosphere processes and microbial functioning to jointly simulate carbon and water fluxes across scales—and the overall concept and coding effort are impressive. The authors produce a rich set of scenario simulations that suggest compelling interactions between the timing of dry spells and microbial trait syndromes that can drive either net carbon retention or accelerated mineralization in the short term. The coupling and the multi-scale analysis framework are valuable contributions for modelling communities interested in rhizosphere processes and plant–soil feedbacks. To be honest, at 76 pages this is the most extensive review I’ve undertaken — it required a careful, time-consuming read to assess the modelling choices and their implications.

While the modelling effort is significant and presents useful, hypothesis-generating insights, the manuscript sometimes over-asserts ecological conclusions that the simulation scope and temporal extent cannot robustly support. Statements implying durable soil carbon “stabilisation” are particularly strong and risk overstating the results. The manuscript should consistently use language that reflects the model’s temporal and mechanistic limits (e.g., “short-term net C balance shifts,” “suggested potential for transient C accumulation,” or “conditions that promote reduced short-term mineralization”), and explicitly frame the findings as model-derived hypotheses that require empirical validation over longer timeframes. Recasting conclusions in this way will preserve the impact of the study while avoiding claims that require organo-mineral interaction processes or multi-decadal validation that the current simulations do not include. My detailed comments and suggestions are described below.

Abstract

Soil carbon stabilization is a long-term process involving complex organo-mineral interactions. Your model, as described, likely simulates microbial turnover and short-term respiration. To claim "stabilization" is a strong overstatement that must be tempered. The conclusions must be carefully rewritten to reflect exactly what the model outputs: namely, net C flux (input vs. respiratory output) and short-term C storage in microbial biomass or slow pools. The model may suggest a potential for stabilization, but it cannot conclusively prove it without validation against long-term experimental data.

Define what you mean by “earlier” versus “later” dry spells using absolute timing or plant phenological stages (e.g., days after sowing or leaf-stage) and by how much. Are these linked to specific phenological stages? What are the specific "soil biokinetic parametrisations"? Briefly state the difference between "reactive" and "less reactive" communities (e.g., differences in maximum growth rates or substrate use efficiencies).

Introduction

The introduction convincingly argues that coupled water–C dynamics at the soil–plant–atmosphere continuum are important under climate change, and it highlights the rhizosphere and microbes as key players. However, the justification for this specific modelling effort (why extend CPlantBox with TraiRhizo, why in DuMux, and why the chosen coupling is required now) is not tightly argued: the reader is told the model is useful, but not why existing tools cannot already answer the questions posed.

The introduction begins with very broad, textbook-level concepts (e.g., "water is a resource," "C is a building block") and takes too long to narrow its focus. The necessity of your work—integrating a specific microbial-explicit soil model (TraiRhizo) into a specific FSPM (CPlantBox) to address a specific gap—is buried and needs to be the central thread from the outset. The justification is currently implicit. For instance, the authors list several gaps (few models consider both water and C; many rhizosphere models ignore microbes; many FSPMs don’t simulate soil C), but they do not synthesize these into a single crisp gap statement that maps to the paper’s aim. The gap therefore reads as a set of related deficiencies rather than a targeted problem the paper will solve.

The text mentions updates (implicit time-stepping, updated multiscale coupling) but does not explain why these matter (stability? computational efficiency? ability to run larger/longer scenarios?). State concrete advantages and differences from prior CPlantBox couplings and from existing tools (e.g., TraiRhizo, SpatC).

The necessity of your specific approach (coupling CPlantBox with TraiRhizo) is not sufficiently justified. Why is this particular combination of models the best solution to the problem you've identified? A brief comparative sentence on the strengths of each model and the synergy of their coupling would be very effective.

Fix small typos and duplicate words:

“to to the soil” -> “to the soil”;

“unterstanding” -> “understanding”;

“ans pore scales” -> “and pore scales”.

Methods

The work described is highly sophisticated and represents a significant computational effort to integrate complex, multi-scale processes. The ambition to dynamically couple a 3D FSPM with a 1D microbial-explicit soil model is commendable.

Section 2.4.5: The definitions of the four different scales for analysis are innovative and thoughtful. The need to add a large, constant SOC_slow pool post-simulation because the model outputs were "almost always in the lowest SOC class" and "significantly below" measured values suggests a potential issue with the model's initial conditions or its fundamental ability to represent realistic background C levels. Adding SOCslow = SOCtheoric − SOCsimulated_init effectively injects an artificial, immobile C pool to match literature SOC. This is pragmatic, but it changes the meaning of “hotspot” thresholds and may bias hotspot fraction metrics. The assumptions and potential consequences must be clearly discussed and sensitivity tested. This requires a strong justification.

Section 3.2 Why were the two one-week dry spells chosen at days 11–18 and 18–25 after sowing? Are these phenologically relevant for the virtual plant? Provide biological/ecological justification.

The phrase "warmer and drier atmospheric conditions were simulated" is too vague. Precisely which driving variables were changed (e.g., VPD, radiation, temperature) and by how much?

Results

The results presented are complex and stem from a highly sophisticated modelling effort. The multi-faceted analysis across different scales (plant, bulk soil, perirhizaltrunc, microscale) is a particular strength, providing a comprehensive view of the system's behaviour. However, the results are presented as absolute truths from the model without any acknowledgment of uncertainty or variability. Phrases like "we observed," "we found," and "led to" are used throughout, but the reader has no way of knowing: Are the differences between scenarios (e.g., earlyDry vs. lateDry) and parameter sets statistically significant or just numerically different? For instance, line 431-432 is is a key finding but is stated without any statistical test to back up the word "significant."

The connection between root architecture and C concentration peaks is well-described. However, the comparison between scenarios and parameter sets is again purely descriptive. A quantitative measure of the difference would be much more impactful.

Strictly report what the model output is in the results section. Move all speculative explanations for why a pattern occurs (e.g., competition, rhizosphere overlap) to the Discussion section.

Many statements are given as percentages or qualitative (“strong increase”, “higher”, “lowest”) but without absolute units or baseline magnitudes. The authors could replace qualitative descriptions with quantitative percentages, effect sizes, or other measures where possible.

Section 3.4, line 497: The claim that copiotrophs reach 580 µmol/cm³ is alarming high — show where and how large volumes have these concentrations (absolute volume in cm³) to contextualise (i.e., are hotspots tiny or spatially extensive?).

Line 399: “FSPM model of Giraud et al. (2023))” double parenthesis.

Line 433: respectivelly -> respectively.

Discussion

The section 4.2 is overly long and reads more like an extended results section or a review of plant physiology. While comparing model outputs to literature is valid, the level of detail on biosynthetic growth, osmotic adjustment, and specific exudation rates from various papers is excessive and distracts from the paper's central focus on soil-plant-microbe feedbacks. This entire section should be drastically condensed. The key point—that the model qualitatively captured known dynamics despite its simplifications—can be made in a few paragraphs.

The introduction implicitly promised insights into how dry spell timing and microbial reactivity interact. While this is addressed in 4.3, the discussion does not explicitly return to frame the findings around the initial objectives. A strong discussion should begin by stating how the results have addressed the original knowledge gap. Additionally, Section 4.3 contains the most valuable discussion points but is buried. The insights about scale-dependency, microbial "starving-survival lifestyle," intra-microbial competition, and the rhizosphere priming effect are excellent and should form the core of the discussion.

Several sentences imply general ecological truths (e.g., “the model showed… making a 3D evaluation relevant”), while the work actually shows model-based scenarios for a single soil/site/plant parameterisation set. Rephrase to emphasize that findings are model-derived insights that suggest hypotheses for empirical testing.

The authors added an immobile SOC_slow pool to align simulated and literature SOC. This affects hotspot classification and interpretation. Discuss explicitly (a) how SOC_slow modifies hotspot thresholds and (b) whether the “stabilisation” conclusions hold without SOC_slow.

Some paragraphs are long and mix methods/results/discussion. Keep the Discussion focused on interpretation, implications, limitations, and future work; move implementation details back to Methods or an Appendix.

Please check multiple typos and grammar issues:

“Expending” -> “Expanding”;

“compaired” -> “compared”;

“diurnal cylcing” -> “diurnal cycling”;

“hostpot” -> “hotspot”.

Conclusion

The conclusion provides a brief and accurate summary of the work performed and correctly identifies the core findings. However, for a paper of this complexity and ambition, the conclusion is significantly underdeveloped and fails to adequately synthesize the study's full contributions, limitations, and broader implications. It reads more like an abstract than a conclusion. It should answer the "so what?" question. What is the broader significance of finding that C vs. water limitation in microbes dictates the soil C outcome? How does this advance the field of plant-soil modelling or inform future experimental work?