General comments

This study provides novel results on OA  in the Mozambique Channel, addressing relevant scientific questions and contributing to the understanding of Global Change impacts in the Indian Ocean. The authors present recent observations from this region, contrasted with existing datasets and supported by climatologies and neural network approaches. The study design, concepts, methods, and data employed give the manuscript appropriate scientific significance.

However, several aspects require major revision to improve the quality of the research and the presentation of the results and conclusions. In particular, the manuscript would benefit from a clearer description of the study area and its main oceanographic features, a more detailed and structured explanation of the applied methodology, and a careful revision of the trend calculations. Addressing this last point is crucial to strengthen the main conclusions of the study.

Below, I provide my major and minor concerns.

Major comments

The introduction is concise and well-structured. However, it would be convenient to make explicit reference to the study area and include a description of the most characteristic processes that may act as sources of variability for the CO2 system. Alternatively, a short description could be included in the introduction, with further details provided in a Study Area subsection within the methodology.

The color code in Figure 1 does not allow interpretation. It is difficult to distinguish the tracks of each cruise, particularly the red ones (from 2010 onwards, when most cruises took place). Please consider using a unique color for each cruise to improve readability.

Line 128: How was SST measured? And salinity? What were the instrumental uncertainties? How was the equilibrator temperature corrected relative to in situ values? Even if this information has been described in previous works, it would be helpful to include it in Section 2.2 so that readers can fully understand the methodology.

Lines 299–300: “…the climatology (Fay et al., 2024) or the FFNN model (Chau et al., 2024) is coherent compared to the data.” Was any intercomparison test performed? It would be appropriate to include results of such an intercomparison, for instance, the mean difference between climatology/NN outputs and observations, and/or provide an additional figure in the Supplementary Material (e.g. time in months on the X-axis and difference on the Y-axis).

Figure 3: The criteria for selecting these specific periods are not clear, and this choice may introduce bias. The averaging of the 2003, 2004, and 2014 cruises seems to give greater influence to the earlier years . It would be more informative to present the direct observations of each cruise with distinct markers. This approach would facilitate interpretation and enable clearer comparison with FFNN and climatology results. Including error bars would also strengthen the figure.

Section 3.3 does not appear to align well with the overall structure of the paper. Although the main result derived from this section is interesting for the broader discussion, it does not directly fit within the objectives. I therefore suggest moving this section to an Appendix and including the figure as Supplementary Material.

Section 3.3.2: How were the trends calculated? Were they derived from observational data or from climatology/NN outputs? This is a critical point that needs clarification. For example, between 1963 and 1995 (line 498) a trend is reported, but only two data points exist. In this case, it would be more appropriate to report the change between 1963 and 1995 (-0.040 units) rather than describing it as an interannual trend, which would be biased without intermediate data. The same concern applies to trends reported for 1995–2019 (lines 507–509) and 1995–2022 (lines 514–515). Similarly, in Table 4 the limited number of observations in the second half of the 20th century (only in 1963 and 1995) introduces biases in trend estimation. In addition, the high variability observed since 2018 could influence the calculated trends. Under these circumstances, no interannual or decadal trends can be identified with any statistical significance; instead, it would be more reliable to compare recent values with those from 1995 to estimate the magnitude of change. These changes will require a revision of the main conclusions of the paper, as well as the abstract

Section 3.4 (line 622): The calculation applied in this section may be difficult for readers to follow. The reconstruction of past and future values and the data sources used are not entirely clear. It might be beneficial to expand on the methodological details, either in the methodology section or in a dedicated Appendix, and limit the current section to the discussion of results. Additionally, please clarify the estimation error associated with Eq. 2.

Minor comments

Lines 41–42: Is this referring to surface measurements? Please clarify.

Line 47: Replace “fugacity of CO2” with “CO2 fugacity”.

Lines 47–50: The inclusion of these trends may appear arbitrary and potentially confuse the reader, since the study region has not yet been specified in the introduction. While the Indian Ocean reference is understandable, the criteria for also including the North Pacific is unclear. As a suggestion, it may be more relevant to mention the decrease in pH using trends from time-series stations (Bates et al., 2014), noting that most are located in the Northern Hemisphere and that knowledge of OA in the Southern Hemisphere remains limited. This could help emphasize the importance of the paper and engage the reader.

Line 49: What does “TS.decade^-1” mean? Please use “units decade^-1” or simply “decade^-1” instead, and apply this consistently throughout.

Line 58: Acceleration with respect to …?

Line 135: Were only three gases used? Was a 0 ppm gas not included to zero and span the system (Pierrot et al., 2009)? If not, how were the xCO₂ measurements corrected?

Lines 160–162: Please include statistical information (e.g., RMSE and r²).

Lines 193–194: “For pH, the decrease of -0.005 over three years, i.e., -0.0017 yr^-1, is surprisingly close to what is generally observed at global scale and over several decades (-0.017 ± 0.004 per decade).” Please use consistent units when reporting both trends.

Table 2: Why do the mean SST and SSS values for CLIM-EPARSES fCO₂ and CLIM-EPARSES AT-CT not match? They should be identical if only the computation of the carbon system variables differs. The same issue appears in Table 3 with OISO-11 and OISO-31. Please clarify.

Line 316: Please specify the salinity to which CT is normalized.

Line 323: Is there a reference supporting the reported trend?

Lines 365–366: This statement would be more appropriate in the Results section.

Line 387: Consider replacing “increased” with “reinforced”.

Lines 424–425: How were eddies identified? Were satellite images used, or is there a reference?

Line 428: ΔfCO₂ should be defined as the difference between oceanic and atmospheric fCO₂ before it is mentioned for the first time.

Line 496: What does “difference of ΔfCO₂” mean? Please clarify.

Line 500: Please specify the units.

Line 639: Instead of simply stating “compared well”, it would be helpful to report the mean differences between this method and the observations, as well as between this method and the FFNN estimates/climatology data.

Lines 679–680: Please provide a reference.

Figure 9: Is it possible to add error bars?

Metzl et al. compile observations and observation-based reconstructed surface ocean carbonate parameters to assess historical and future trends in ocean acidification in Mozambique Channel. They find an acceleration of acidification since the 1990s and predict the timing of the crossing of critical thresholds for coral reefs. Given the scarcity of observations in this region, and the Indian Ocean in general, as well as the existence of nearby coral reef ecosystems, this is an important contribution to the scientific literature. However, there are several issues that should be addressed in order to clarify the methodology, reporting, and implications of the results.

Seasonality of the observations and reconstructions:

Given the significant seasonality of surface ocean carbonate chemistry in this region (Figures 3 and 4) and the desire to report trends without adequate observational coverage in all seasons, it would be useful to better align trend comparisons in the same month(s). In section 3.3.2, trends from historical observations from April-May should be compared to trends from the FFNN product from April-May rather than only April. Figure 3 shows there are significant differences in the climatology between April and May. In addition, it is unclear why August is used for the future predictions (Line 636) when the comparison is being made to July observations (639). It would be better to align those FFNN months with the available observing months or report seasonal FFNN results that encompass the observations (Jan-Mar, Apr-Jun, Jul-Sep).

In addition, it is not always clear what time period is being referred to. For example, is the FFNN trend referred to in Lines 501-502 FFFN annual or FFNN April?

Coral reef implications:

How close in space are the historical sampling locations and the coverage of the FFNN reconstructions to the coral reefs in the Mozambique Channel? It is not obvious whether surface ocean carbonate chemistry presented here overlaps at all with nearshore subsurface coral reefs. More evidence is needed to conclude that the current and projected low aragonite saturation state conditions presented here are likely to be the same conditions occurring near coral reefs in this region. In Figure 1, it would be useful to include the extent of coverage used from the FFNN products as well as locations of coral reef ecosystems. The shading in Figure 1 needs to be described in the caption, and if they represent bathymetry, a scale for that should also be included.

Other comments:

Line 18: I assume “TS” refers to pH in total scale? If yes, define that acronym at first instance in the main text (line 49) and just say in the abstract “ranging from a pH change of -0.012 decade ^-1” in the abstract. It wasn’t until I got to Figure 2 that I figured out what TS was.

Line 25: How do you define “low”? Should this be “lowest”?

Line 27: Briefly describe the two emission scenarios here.

Line 160: Even though this alkalinity proxy is described in another contribution, the uncertainty in the alkalinity proxy should be provided here.

Line 172: Similarly, a brief overview of the estimated uncertainty of reconstructed fCO₂ should be provided here. Given one season has no data for training the neural network, are there any assessments of predicted uncertainty during that season?

Line 174: This section seems to be both Results and Discussion?

Lines 322-325: Given the rapid warming in this region, have the authors considered assessing the thermal and non-thermal components of the fCO2 trend? Later in the results, values are presented that correct for the SST warming, but the method used for doing this is not presented.

Figures 2 and 3: Should FFNN-2010 be presented as gray to match the observations from the same time period like FFNN-2022?

Figure 3: Is FFNN-2022 missing?

Figure 3: Include an interpretation of what may be causing the anomalous observations in April 2018-2022. Is this due to the variability from the 2021 eddies described in Lines 424-425?

Lines 418-419: Measurement and calculated parameter errors should be stated somewhere. Are these errors a part of the standard deviations in Table 3?

Figure 6: Everything in the figure legend needs to be defined in the caption. Unclear what fCO2 and AT-CT are? Measured or calculated?

Line 564: Unclear what is meant by “ambient conditions” here.

Line 636: How is “low” defined? Is “lowest” meant here?

Line 696-697: Reference the methodology for deriving fCO₂ from pH.

Figure 9b: Define “War” in legend.

Figure 744: Is it a permanent sink given the observations from 2025? What are the potential implications of increasing marine heatwaves in this region to the CO₂ sink?