This manuscript presents a valuable and comprehensive dataset on particulate organic matter bulk concentrations and stable isotope compositions from summer brash ice across a broad spatial extent of the Indian sector of the Southern Ocean. As current knowledge of sea-ice biogeochemistry is largely based on studies of spring fast ice, this investigation of degrading summer brash ice provides important insights into the composition, transformation, and potential export of organic matter during the seasonal melt period. The authors' estimation of the contribution of sea-ice-derived POC relative to regional primary production represents a particularly noteworthy contribution.

However, the manuscript has several key limitations, including a lack of alignment between the title and abstract and the broader context presented in the Introduction; an ecological interpretation that places considerable emphasis on zooplankton food-web dynamics without supporting evidence from direct zooplankton observations. Addressing these issues would substantially improve the coherence, scientific rigor, and overall impact of the manuscript.

Major Comments

1. The title can be made concise and eye-catching.
2. The title and abstract explicitly position stable isotopes as a primary tool and the focus of this study. However, the current Introduction is heavily skewed toward lower-trophic-level synchronization, phytoplankton blooms, and physical sea ice retreat. There is almost no conceptual background establishing the biogeochemical framework of stable isotopes in polar environments. The authors should dedicate 1 paragraph in the Introduction to framing why isotopes are necessary here.
3. The sea-ice dataset is impressive, capturing 102 samples across 24 stations over a four-year period (2016–2020) across a massive geographical range. In contrast, the comparative seawater POM dataset is highly restricted, sampled only twice daily during a single cruise in a single month (January 2019, UM18-08 cruise). The authors must explicitly discuss this limitation in the Discussion and exercise caution when making direct statistical or variance comparisons between the two distinct sample matrices.
4. The Introduction builds an extensive narrative around filter-feeding zooplankton communities, copepod/krill life cycles, and trophic structures. Because the manuscript does not measure actual zooplankton tissue isotopes or grazing rates, the ecological conclusions are entirely speculative based on estimated flux. To avoid over-promising, the text in the Introduction and Discussion should be re-scoped to focus tightly on characterizing the supply and quality of the organic matter source itself, rather than framing the manuscript as a direct investigation into zooplankton feeding ecology.
5. Line no. 229 “Sea-ice POM δ13C and δ15N ranged from −35.1‰ to −3.1‰” are correct values, but they do not match with Table 1 and Figure 2.

The observational dataset presented in this manuscript is highly valuable and fills an important gap in measurements of summer brash sea-ice BGC in the Indian sector of the Southern Ocean. Such observations are relatively scarce, and the dataset provides a useful contribution to our understanding of sea-ice BGC and the potential role of melting sea ice as a source of organic matter to the upper ocean. The manuscript is generally well written and the figures are clear. However, I have a several concerns regarding the justification of some methodological assumptions and the strength of several interpretations. In particular, the estimation of ice algal carbon, interpretation of POC:Chl a ratios, and several interpretations based primarily on correlation analyses would benefit from additional clarification and discussion of their associated uncertainties. Addressing the comments below would substantially strengthen the manuscript.

Specific comments

Line 25 – Remove “this”.

Line 31- Seawater mean and SD aren’t given in main text.

Line 32 – “indicating” seems a bit strong given that these are correlations rather than direct measurements. Perhaps consider changing “indicating” to “suggesting”, particularly for the inference regarding decomposition.

Line 54 – Include a reference here for seeding theory such as van Leeuwe et al 2022. Also, similarly for stratification influences and iron supply as there are papers on this.

Line 67 – Remove “and accumulate data.”

Line 68 – Does PN include both organic and inorganic N? If not, would PON be more appropriate for consistency with particulate organic carbon (POC).

Line 80 – I am not sure what is meant by ‘when fast ice and pack ice floes are well established to land on ice’. please rephrase for clarity.

Line 105-106 – Were all cores (even for bio) stored at -20 before analysis and approx. how long was this frozen period? Or was this only on physical cores – clarify.

Line 108 – What was the seawater filtered through GF/F’s for… POC/N?

Line 123-124 and 130 are a repeat of description for filtering for Chl a, choose one to keep.

Line 149-150 – Did you use the sea ice nutrient data from these papers? The data aren’t cited then, rather they are used/sourced? Rephrase.

Line 154-155 – Brine convection and exchange also influence bulk concentrations and doesn’t necessarily dilute nutrients. This process may also be worth acknowledging here.

Section 2.6 – I found the calculation of IAC somewhat unclear. Could the authors clarify exactly how IAC was estimated and where the IAC:Chl a ratio originates? Line 166 states that this ratio was estimated from "field observations", but it is not clear whether these observations come from the present study, a previous publication, or a larger independent dataset. If the IAC:Chl a ratio is independent of the present dataset, please clarify its source and justify its applicability to the samples analysed here. Given the known variability in algal C:Chl relationships with species composition, physiological state, and environmental conditions, it would be helpful to discuss the uncertainty associated with applying a single mean conversion factor. As this conversion is applied in several subsequent interpretations, additional justification and discussion of its limitations would strengthen the subsequent interpretations.

Line 170 – Define F.  Is this the mean IAC:Chl a 54.4?

Line 179 – What is the resolution for thickness data? I’d also add in a short sentence about the low sea ice concentration influencing why you don’t have DSF for some stations. I see it’s in the caption of Table 1 but would be good to state in this section 2.7.

Results & Discussion

Line 228 – Add specific panel you reference… ‘a’ to Fig 2.

Line 234 – Add maximum value found at St S35.

Figure 2 – Include regression coefficients on the figure panels a-c, if significant like Fig 6.

Figure S1, S2, S3 – I would add that the panel labels “B, C, D, KH20-1, RAS, CD2” are station names in the captions to be clear for the reader.

Section 3.5 heading – suggest removing “production in the”.

Table 2. What is ‘b’? I would also suggest re-arranging the footnotes alphabetically. I assume ‘e’ is supposed to be ‘b’.

For the meltwater calculation, where does the time unit come from?  Table 2 reports a mean ice melt thickness of 0.82m, yet the resulting POC input is expressed as mg mg^-2 yr^-1. Is the Komatsu et al. estimate an annual cumulative sea-ice melt thickness? If so, reporting this as 0.82 m yr^-1 (or stating explicitly what it represents) would make the calculation much clearer.

Line 269: The reported value -24.6 and -24.4 for δ13C differs from the value in the abstract. Please check for consistency.

Line 313 – Does the 27.9 Tg yr^-1 MIZ value account for both open water and ice, or just ice-derived primary production? I couldn’t find the value in the Arrigo paper. Are you taking a SIZ calculation and applying it to only the MIZ? I see in the footnotes in Table 2 it contains MIZ and MIZ shelf… do you consider this to be equivalent to the SIZ?

Line 339 – should be “Fig. 3c, b”.

Line 329-330 – Could the authors clarify/expand why higher DSF is interpreted as indicative of greater light limitation? As ice ages and decays, floes may become smaller and more fragmented, potentially increasing light exposure.

Fig 4. The C:N ratio appears higher than redfield ratio. It may be worthwhile assessing whether this could reflect the accumulation of carbon-rich matter over time (e.g., EPS, lipids, fatty acids), nitrogen limitation or other factors influencing orgranic matter composition.

Section 4.4 acknowledges the potential influence of seasonal sampling on the regional POC estimate. The discussion could acknowledge additional assumptions underlying this first-order regional calculation, such as the representativeness of the sampled brash ice, the use of a regional mean melt thickness, and the comparison of POC supply with primary production estimates.

Line 456 – The value of 924 mg m-2 yr^-1 is different in Table 2. Since Ackley et al. estimated carbon input using Chl data, would it be more appropriate to compare that estimate with the calculated ice algal carbon?