The authors present a thorough and well-described study of saturation treatments in soil monoliths (i.e., 3D soil columns) collected from agricultural field sites. The overall manuscript is very well-written, and the description of data analyses is particularly thorough and of high quality: nicely done! However, there are some areas where it is not clear that the focal concepts and hypotheses align with the study design or expectations, leading to a need for some careful consideration of the relevance of cited literature and the justification for hypotheses/interpretations. Specifically, much of the background information and explanation of relevant processes is tied to the idea of Fe-SOC associations driving mobilization of DOC and higher CO2 mineralization. However, there is a key distinction between prolonged saturation and frequent saturation cycling, because the saturation cycling is likely the mechanism for changes in Fe reducibility and subsequent reduction/release of DOC. Further, the importance of this mechanism is contingent on a measurable amount of the SOC in a system being stabilized via Fe associations to begin, and much of the related work has been done in tropical soils or acidic podzols with very high reactive Fe content. In this study, I would characterize the saturation pattern as one relatively short-term but consistently waterlogged within the treatment periods, so the design does not invoke the mechanism of cyclic saturation underpinning many of the related studies (which is acknowledged in the Discussion), and it is not clear whether initial Fe-SOC interactions are a major contribution to SOC stabilization in this system. While I think the overall conclusions and insights from the study are interesting and important, some reframing of the conceptual underpinning is needed to justify the design and interpretations, and some of the known considerations mentioned in the Discussion need to be introduced more directly early on. These points are explained in more detail below, e.g. on comments on lines 25-26, 56-58, and 428-429.

Specific Comments on Scientific Content:

Line 25-26: A key factor related to waterlogging is the cycling of saturated conditions, in addition to the absolute duration. From the abstract alone, this seems like it was repeated waterlogging events over a seven-week period, but it is not completely clear; from the text, it seems that it is continuous waterlogging for a 7 week duration. Suggest more directly describing the timing and duration of waterlogging (i.e., repeated events vs. one continuous 7-week waterlogging condition) here, as it is important context for the subsequent interpretation of results (see later comments, e.g. on lines 56-58).

Lines 26-27: As described, it is unclear whether the same half of monoliths received both overwinter cover crop and waterlogging treatments. As described in the text, these are a factorial design; please clarify here.

Line 33: “both soils and plant treatments…” Wording is unclear: please revise for clarity. In addition, how the plant treatments overlap with waterlogging treatments is not yet clear, as mentioned above.

Lines 56-58: An important overarching consideration for this work in the context of "temporary" waterlogging is the frequency of saturation cycles, in addition to the total duration of saturation. The process of Fe-associated OM destabilization is described nicely below, but one of the additional mechansims underpinning some of the observations in the cited studies is the progressive increase in overall Fe reducibility from repeated dissolution/precipitation processes; e.g., as discussed in Ginn et al. (2017) (https://pubs.acs.org/doi/full/10.1021/acs.est.6b05709) and mentioned in the Discussion section. Prolonged vs. fluctuating saturation is one important factor conceptually distinguishing short-term but consistent waterlogging (in this study) from in-situ or manipulated variable moisture conditions, and relevant literature.

Lines 90-92: While I agree that many of the more targeted experiments have been conducted in laboratory scale incubation, there have been field studies evaluating fluctuating water conditions related to OM mobilization, e.g. Possinger et al., 2020 (cited in the Discussion). However, field-only observations also have limited ability to have controlled comparisons across treatments, for example. Thus, the value of a middle ground between controlled lab incubations and in-situ studies could be more clearly identified here.

Lines 97-98: An important assumption underpinning the Fe-C hypothesis is that a significant proportion of mineral-stabilized C in this system is actually associated with Fe to begin. Are these soils abundant in redox-active Fe-rich mineralogy? Note that many (not all) of the cited studies were conducted in tropical soils with high Fe oxides (e.g. much of the work by Aaron Thompson et al.), acid forest podzols dominated by Fe- and Al-C complexes, etc. While the more detailed soil description and characterization is more relevant for the methods, the justification for the overall hypotheses and study design/concept is important here, and sets up the subsequent interpretations. See also comment on lines 608-609 in the Discussion on the importance of this assumption and related interpretations.

Lines 112-113: More detail and justification for soil hypotheses related to Fe-C stabilization is needed. (1) In my opinion, “tentative” classification is insufficient: how was this assigned (by soil maps)? Do these soils align with characteristics of the assigned soil types? (2) Building on the comment regarding soil Fe abundance and Fe-OM associations, neither of these orders are archetypically associated with especially high Fe abundance or Fe-dominated OM stabilization to my knowledge. This isn't to say that they do not have abundant reactive Fe, but providing the reader some context for the oxalate-extractable Fe and Al presented in Table 1 would help to justify that there is significant contribution of these phases to OM stabilization in this system. (3) Is there a fundamental difference in the saturation regime between the Stagnosol and Cambisol/Umbrisol? In addition to texture, this seems a key factor that could influence interpretation of subsequent response to waterlogging and should be clarified here.

Lines 121-122: This is a minor point and mostly a difference in usage/terminology, but a monolith in my understanding is a 2D representation of a profile surface, rather than a 3D cylindrical core. I would interpret the soil systems as described as soil columns or mesocosms. I would suggest describing once early on in the text that you're referring to columns; e.g. "soil monoliths (i.e., 3D soil columns)..." or similar.

Lines 162-164: How was waterlogging maintained after full saturation was reached throughout the 54 and 50 day periods, especially between cover crop and no cover crop treatments? If the columns were watered subsequently, did partial drying occur during watering events?

Line 214: With high TDC solutions, freezing can sometimes induce coagulation/flocculation of organic solids which do not always resuspend following thaw. In addition, I am not familiar with the efficacy of freezing alone for DIC, which is sensitive to exposure to atmosphere. Could you comment a bit further on the preservation approach and potential limitations, if any, for TDC/DOC/DIC analyses?

Line 215: The data analysis and statistical approaches are very thorough. Nicely done! In some cases, they could be slightly trimmed down for readability when discussing conversions (if standard to the field), e.g. in the section on DIC change calculations.

Lines 229-230: Can you expand a little more on this interpolation? What is the linear part of the interpolation based on (between two sampling dates)? I can guess at how na.approx might work for this, but it's not immediately clear how this would be done with a sequence of measurements over time. It's not a major point, but a little clarification would be helpful for replicability of the method.

Lines 239-241: A sentence before explaining the overall approach for using a modeled CO2 efflux would help provide the reader some context (e.g., to compare measured and modeled efflux to test XYZ...).

Line 432-434: Figure 2 caption: While the modeling procedure was explained in the text, it would be helpful to remind the reader what "monitored monoliths" means here - it's not immediately intuitive and adds a degree of confusion that may not be needed. In addition, the importance of the difference between Cycle 2 and Cycle 3 is highlighted by having them in two separate panels, but how these experimentally-induced cycles relate to important experimental conditions/phases (e.g., the removal of biomass in Cycle 3) isn't really clear in this figure or how the results are presented in the text. Some additional labeling/timeline explanation in the figure would be helpful to follow the results as presented in the text.

Lines 380-382: It is interesting to see the change in DIC accounting for the main change in TDC. Given the question about storage and sample preservation mentioned above, just as a check: do these values align with typical ranges of DIC in these soil types (especially the values close to or slightly higher initially than DOC in the silty clay soil)?

Lines 428-429: Following my comments on the introduction, it's great to introduce the distinction between prolonged vs. fluctuating anaerobosis here, but I would suggest accounting for this distinction earlier in the text with respect to relevant literature and expectations for the experiment, as it did not apply fluctuating saturation and the related implications for increasing Fe reducibility are less applicable (e.g., see Ginn et al., 2017: https://pubs.acs.org/doi/full/10.1021/acs.est.6b05709).

Lines 433-434: Given the dependence of anaerobic response on soil type as mentioned above, initial characteristics of the soils are critical for interpretation of differences (or lack thereof). For example, though these soils do differ in Fe oxide content, it is not clear from the presented soil information whether Fe oxides in general are a major contributor to overall soil mineralogy in either soil, and further if they contribute meaningfully to SOC stabilization in this system. While the absolute values for the extractable Fe oxides are presented and the reader could convert the mmol per kg values and look up ranges for other soil types, it would be helpful for the reader to have it stated upfront (before or as part of the hypotheses) that these soils are appropriate for testing the hypothesized response due to the contribution of Fe oxides to SOC in this system.

Lines 463-465: Here and throughout, it would be helpful to have a little more guidance in the text about what the reader should take away from statements about observations in a certain study cycle. The meaning of the reference to the second and third study cycle is not immediately understandable in terms of what that means for the conditions of the experiment; in other words, what are the critical differences between these phases relevant to the target processes? It seems to me that in the third cycle the monoliths have already experienced waterlogging in the first and second cycles, so that is one important difference, as is the removal of biomass, but it's a little bit challenging as a reader to follow these processes.

Lines 608-610: In line with comments above, this take-away is stronger if the experiment were targeting Fe-associated SOC stabilization and dissolution: i.e., with relatively high contribution of Fe-associated SOC (which is unclear from the data presented) and fluctuating conditions that result in subsequently higher Fe reducibility. Consequently, some nuance regarding this take-away might be needed.

Minor Editorial Suggestions:

Line 198-199: The detail of CO2 flux conversion can be omitted, unless there was a non-standard conversion used.

Line 275: "similarly than with..." Awkward wording here, suggest rewording for clarity.

Lines 288-289: Suggest clarifying that this refers to "higher than the non-saturated treatment."

The manuscript submitted to Biogeosciences presents an interesting experiment aimed at investigating the effects of temporary waterlogging on CO2 (and CH4) production and release from mineral soils. To achieve this, waterlogging episodes were simulated in the laboratory using soil cores from two sites with contrasting soil textures (silty clay and sandy loam). The authors argue that CO2 production is sustained during waterlogging, while enhanced CO2 release during drainage suggests that diffusion plays a key role in regulating the emission of CO2 previously accumulated in the soil profile. Overall, the study concludes that waterlogging did not significantly alter cumulative CO2 fluxes.

The manuscript is well-written, with a clear structure and easy-to-follow narrative. However, I have identified several general aspects that could be improved, which I outline below. Additionally, I have included specific comments further down

General comments:

I recommend simplifying the hypotheses and focusing on testable statements. Explanations for why specific behaviors are expected belong in the introduction and/or discussion. If these explanations are not directly tested, they should not be part of the hypotheses.

I recommend the authors to reconsider what is the role of the CH4 fluxes for your story. CH4 is mentioned in the abstract, and one hypothesis addresses it, but the manuscript provides almost no results or discussion on the effects of waterlogging on CH4 fluxes. I recommend either dropping CH4  entirely or fully integrating it into the study. The latter would require introducing the topic in the introduction, presenting results, and discussing potential mechanisms behind the observed patterns.

The results section is currently too lengthy and includes elements of discussion. I suggest moving discussion points to the appropriate section and succinctly describing only the results relevant to the study's argument. Additionally, I had difficulty locating some referenced tables and figures (e.g., Fig. B1, Table A3). Please ensure all references to figures and tables are accurate and consistent.

Finally, I consider that several treatments are not significantly different between them due to the large heterogeneity in the fluxes and within the replicates, but there is room for a detailed interpretation of these trends, while keeping caution in the formulation. In Figure 6 (cumulative fluxes) I do see a trend towards: 1) higher CO2 emissions in <FC compared to saturation; 2) higher CO2 emissions in the silty clay compared to the sandy loam and 3) higher emissions in CC (for the third waterlogging).

Specific Comments:

• L105: Hypothesis (b) includes two separate hypotheses (one about CO2 and one about CH4). The first part is overly complex and involves causation mechanisms that cannot be tested with the current setup. I suggest simplifying the hypothesis to focus on what can be tested. For the CH4 component, ensure the topic is introduced in the introduction (see general comments on CH4).
• L158: Please clarify which depth was used as a reference.
• L162: This section is unclear. What exactly is meant by "events"? How long did they last? While it is stated that all monoliths were irrigated with up to 23 mm, it is not entirely clear if this was consistently applied.
• L174: Replace "speeds" with "flow rates."
• L175: This information does not align with L169. Given that the cross-sectional area is constant and the height varies by a factor of 2, why does the volume vary by a factor of 3.5? Please clarify.
• L180: How were leakages observed or identified?
• L190: The term "visual inspection" is misleading here, as this describes a numerical comparison.
• L192: This sentence is unclear. You mention discarding data with R2< 0.84 (0.6% of the data). If this threshold was applied, the fluxes below it would be discarded regardless of the reason. Please clarify the purpose of this analysis.
• L200: What is the purpose of differentiating aboveground and belowground CO2 fluxes in the context of this study? Additional context would be helpful.
• L204: What is the temporal resolution of these measurements? This information is missing.
• L227: It is unusual to inspect assumptions visually when established statistical tests are available. Consider using these tests instead.
• L240: Four references seem excessive here. Consider reducing them.
• L291/Figure 2: Why were the results for water content not presented? I suggest integrating them into Figure 2. Additionally, fine-tune the figure by removing the area with negative time values.
• L331: Remove the word "statistically."
• L336, Table 2: Do you have a statistical test to show whether differences in Q10 values between cover crop and no cover crop are significant?
• L342, 344: What is Fig. B1?
• L352, 355: What is Table A3?
• L415/Figure 6: While the authors claim no significant differences between FC and saturation, there is a clear trend toward higher emissions in <FC, which should be acknowledged. Additionally, why are there one and two asterisks in the same panel (upper left-hand panel)? Finally, I suggest avoiding the term "respired fluxes" for cumulative fluxes, as this could be misleading.
• L425: This sentence and its references are confusing. The authors state that their results align with several studies (which ones?) but contradict conventional model assumptions (which ones?). Separate the references to clarify who found what.
• L433: See general comments. There is a trend suggesting a soil type effect that should be discussed.
• L452: Either remove "in determining" or add "considering" before "the following drying period." Avoid using "soil C budget" in this context; instead, use "soil CO2 efflux" or a similar term.
• L454: This paragraph relies heavily on a previous publication, and the lack of detail in the CH44​ results suggests that it might be better to drop CH4 from the manuscript entirely.
• L462-480: I would welcome a discussion on why the models work or fail and how this could be addressed. This likely relates to the integration of soil moisture in the models. However, instead of discussing water content changes, the focus is on Q10, and the paragraph concludes that the experimental design is not appropriate for this purpose. The take-home message is unclear and should be streamlined.
• L463: The term "conventional CO2 efflux model" is mentioned several times. Please define it clearly.
• L488: Highlight the important idea that there is a transport process between CO2 production (respiration) and CO2 release (efflux).
• L507: This section overlaps with L462-480. Consider streamlining the discussion to avoid redundancy.
• L539: Was this process captured by your experimental setup?
• L579: Were these results presented in the results section? If not, they should be included.
• L595: The study does not appear to address C stability. Instead, it focuses on DIC and DOC, which are more related to C accessibility.
• L608-613: The mismatch between models and results likely stems from the neglect of diffusion processes rather than the sole reliance on aerobic processes. Regarding the effect of cover crops, see my earlier comments, as I suspect some marginal differences are being overlooked.