Dear Author,

The reviewers assessed your manuscript as follows:

- Scientific significance: fair, good
- Scientific quality: poor, fair
- Presentation quality: good, fair

I concur with this assessment and would like to insist on 3 points:

- Methods should be provided comprehensively, especially because some of the literature cited is in Japanse.
- Lumping together surface and 10 m data could very problematic in shallow estuaries as pH can be vastly different, even 10 m apart.
- pH scale: I understand that early monitoring was on the pH scale but I wonder why it is still measured this way. Both a glass electrode (NBS) and spectophotometric (Mosley et al., 2004, Marine Chemistry) method could be used during 1 year and then all measurements subsequently made on the total scale. If the spectrophotometric method cannot be used, one could also calibrate the glass electrode using seawater buffers, although it would less satisfactory.

The reviewers' assessment is well below the bar for Biogeosciences papers. I am particularly concerned about the scientific quality: such low scores should lead to rejection. However, both reviewers recommended major revision and I will follow their advice. I urge you to carefully consider their comments when preparing the revised version as the risk of rejection of the revised version is high. Of course, the revised manuscript will undergo a second round of review.

Best regards,
Jean-Pierre Gattuso

Dear Author,

Thank you for sending a revised version of your manuscript. As you will see, it is still not acceptable for publication in its current form.

Referee #1 recommends acceptance subject to accepted subject to technical corrections. Please look at his annotated manuscript "bg-2019-150-referee-report.pdf" attached.

Referee #2 advised that the manuscript should be reconsidered after major revisions. I am appending below his comments which you will find useful for revising the manuscript.

Please revise the manuscript accordingly and reply carefully to the comments. The revised version will be send to referee #2 for a third round of review.

Best regards,
Jean-Pierre Gattuso



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Referee #2 comments

This is my second time to read this paper. The concept of studying the coastal ocean acidification have great merit. I can tell that this version was improved especially by stressing the water depth issue. However, there are still some unclear things that need further clarification from authors.

1). First, the study ignores some basic inorganic carbon concepts. For example. The CO2 system is the dominant acid-base buffer, the statement from Lines 148 to 153 and Lines 337 to 346 in session 4.3 is not accurate. Kwater does vary but variations of K1 and K2 values of CO2 dissolution should be greater. The description of solubility pump was also inaccurate in Line 345. I still have difficulty in understanding why the authors assumed the Tmax (or Tmin) matched with pHmin (or pHmax). If you check your reference Bate et al 2014 (Fig. 2g), the summer pH was not consistently lower than the values in other seasons. Can the authors draw a scatter plot to show the relation between pH values and temperature? If there was strong negative correlation, it can clear this concern. Again, the authors should also remember that pHmin may come from subsurface water (Tmin) whenever interpreting the pHmin trend and should avoid using summer pHinsitu to represent pHmin (Line 437).

2). As the authors also agree with that removing the sites with high variability (from 1127 to 289) actually removed a big fraction of sites that have large local process (for example, heavy phytoplankton bloom, or freshwater discharge change). With this data treatment, the discussion part (in my opinion) is circular logic because the only process left is global process (warming and anthropogenic CO2 intrusion) after removing the local process. Then the authors discussed and found that global process can explain the pH trends. Even though the authors want to keep the current strategy, this impact of QC process 3 should be included in discussion part to remind the readers.

3). Lines 348-353, the explanation is still very weak. Do you divide the water column (inside one site) into autotropic or heterotrophic by depth: surface is autotropic, while subsurface is heterotrophic? Your definition of autotropic and heterotrophic condition should be included in text. Otherwise, the readers will feel puzzled as what happened to me when trying to understand why the negative correlation between pH and TN trends can show the metabolic state.

4). Discussion part did not really discuss what processes should be responsible for the observed basification rate (~25% sites).

5). Fig. 8 is one of the key take home figures. Can you change the colormap order? I mean to put the insignificant trends in the first layers, and largest trend on the top. The insignificant trends should also be marked in the figure. The authors should also note in the MS that XX% of the trends are insignificant.

6). Equation 3 is wrong. Please check through whether your pH25 was correctly calculated.

7). Lines 316, how did you get the percentage of 10 m? If you can pinpoint the 10 m depth value, why do not you remove this data and see what the trend is?

Some minor comments
1). Line 34, what is the “large deviation”?
2). Lines 194-198, not only biological process, other physical process may be more sever in summer than winter.
3). Lines 201- 203, unclear. The purpose of Fig. 5 in unclear. A good correlation should also be there if you paired pHmin and pHmax or whatever two parameters.
4). Lines 422-423, unclear. Where did the -0.003 yr-1 or -0.005 yr-1 come from? Fig. 7 e-f has no this information.
5). Linea 60-61, Please change into another easy way to understand the sentence. The same with Lines 77-78. Please check through the MS to avoid this kind of description.
6). Line 447, how many sites were heterotrophic based on your definition?
7). Line 446, pH insitu TREND.

Dear Author,

Referee #2 is now happy with your manuscript which reached the minimum level of quality required for publication in Biogeosciences. I am very grateful for the help and constructive comments that the two referees provided. Your manuscript improved a lot in the process and I am glad to accept it for publication in Biogeosciences.

Please consider the two comments of referee #2 who recommends to add Fig. A (in your reply to his comments) as supplementary material and "and temperature" on line 343.

I look forward to seeing this paper published and thank you for considering Biogeosciences to publish your results.

Best regards,
Jean-Pierre Gattuso
BG Editor