General comments

This manuscript presents a valuable three-year dataset (2020-2022) exploring how heavy precipitation and the resulting YRDW influence microbial carbon dynamics in the nECS. The authors integrate satellite-based salinity, PP, HPP, and FDOM measurements with nutrient-addition bioassays. The topic is timely and relevant to Biogeosciences, addressing the interaction between hydrological forcing and microbial processes in marginal seas.

The manuscript is well organized and clearly written, and the field observations are impressive in scope. However, several aspects of the analysis and interpretation require further clarification before the conclusions can be fully supported. In particular, the paper tends to extend beyond the range of the presented evidence, and the causal links between precipitation, DOM quality, and microbial carbon partitioning are not fully demonstrated.

I outline below the main points that, in my view, require attention:

1.The paper draws a direct causal chain from precipitation and YRDW variability to microbial carbon partitioning and trophic balance. While the correlation between hydrological forcing and microbial parameters is evident, the discussion extrapolates local observational patterns to ecosystem-scale mechanisms (e.g., "enhanced microbial loop and reduced food-web efficiency") without direct process measurements of carbon transfer (e.g., respiration or bacterial growth efficiency).

The authors are encouraged to clarify which interpretations are empirically supported and which remain conceptual or inferential. This distinction will help strengthen the credibility of the conclusions.

2. The use of the HPP:PP ratio as an indicator of microbial loop intensity is informative but limited. Without concurrent measurements of respiration or BGE, this ratio reflects only relative production rates rather than the efficiency of carbon transfer or sequestration. The authors briefly acknowledge this point in the manuscript, but a more explicit discussion in the main text would strengthen the interpretation and clarify the limitations of using HPP:PP as a mechanistic indicator.

3. The manuscript would benefit from a better balance between the Results and Discussion sections. The results are presented rather succinctly, whereas the discussion is extensive and mechanism-oriented. Presenting slightly more quantitative detail in the Results—especially regarding interannual trends and variability—would make the argumentation in the Discussion easier to follow and more persuasive.

4. The study attributes seasonal variability of HPP mainly to precipitation and phosphorus limitation. However, temperature, grazing pressure, or water-column stability may also influence microbial activity. A brief discussion acknowledging these potential co-drivers would provide a more balanced interpretation.

5. The nutrient-limitation bioassay (Fig. 7) is compelling; however, the differences between 12-h and 26.5-h incubations could affect comparability. Please discuss potential bias due to unequal incubation times.

Minor comments

1. It would be helpful to clarify whether HPP and PP were measured concurrently at the same sampling stations. If not, a short note on how this may affect the interpretation of HPP:PP ratios would be valuable.

2. The authors might consider adding a simple schematic summarizing how YRDW affects nutrient stoichiometry, DOM composition, and microbial carbon flow.

3. In the Conclusion, tone down generalizations such as “greatly regulates” or “strongly enhances”.

4. The use of 0.2 μm filtration followed by a 9:1 mixture of filtered and unfiltered seawater seems appropriate for reducing grazing while preserving the original bacterial assemblage. Still, the rationale could be clarified briefly in the Methods to help readers understand the intention behind this experimental setup.

Technical corrections

The panel labels (A–L) in Figure 1 seem unnecessary, as they are not mentioned in the main text. Consider removing them or clarifying their meaning in the caption.

Baek and colleagues conducted a three-year investigation of multiple parameters of YRDW and elucidated how varying intrusions of YRDW influence heterotrophic prokaryote production and related effects. This study addresses an interesting topic and provides informative observational and laboratory data, which are clearly presented and support the authors’ conclusions. While I believe the research contributes to the field of biogeochemistry and fits the scope of Biogeosciences, certain parts of the manuscript require further clarification and revision before publication.

My main concern is that the study presents a large volume of data accompanied by some text that remains largely descriptive (somewhat lacks a line to easily follow), particularly in some of the Results section. I also recommend that the authors thoroughly revise the Abstract and Introduction to include a clear scientific question that establishes a logical narrative, making the study easier to follow and more engaging for readers. Additionally, the authors could specify what constitutes refractory DOC (e.g., humic-like substances?), as this currently lacks a clear description in the Discussion and is somewhat obscured within the detailed information. Below I also provide specific suggestions for revising the manuscript.

Line 31: climate change seems too ambitious to me.

Line 116: pls specify 1% light penetration depth.

Line 117: how did you rinse the GFF filters? These suppose to be combusted to avoid potential carbon contamination.

Line 132: T-S, temperature-salinity?

Line 153: pls also specify the depths.

Line 189: to be true, there are too many acronyms, I went back and forth for them, thus hard to follow the results. How about having an extra table to explain these acronyms?

Line 188-201: these are quite descriptive and lack a clear logical progression. I recommend revising this section to improve its flow and readability.

Line 214: pls direct specify what are the extreme conditions.

Line 226: you already defined PA, pls check the entire MS for others.