The authors have presented an impressive analysis of interest to how global ocean oxygenation levels are changing. I believe that this study will be of broad interest for not only the detection of climate change, but also in motivating further community research activities. My recommendation is that the study be accepted for publication after only relatively small/minor changes that are detailed below.

Line 220:

Where the authors say “…that does not always capture the phasing of observed variability”, can they say instead: “nature climate variability that in general does not reproduce the phasing of observed variability”?

Fig. 4b: 

Can the authors point out how much larger these spurious signals (mapping error) are than Pinatubo etc.?

Given that the authors have collective familiarity and experience in working with large ensembles, even without doing any additional analysis, how would natural variability uncertainty measure up against any of the stories emphasized here?

And again without needing to perform additional analyses, it would be good if the authors can comment in a few sentences on the relative importance of anomalies in AOU versus O2SAT in determining the observed trend in O2 for the real ocean. As a related question, if globally extrapolation/mapping were to be performed using AOU and O2 separately on density horizons, would that make a difference?  Or even if O2 itself were to be mapped on density surfaces, do the authors believe that this other aspect of mapping is an issue in producing spurious errors?

Minor editing points:

Throughout the text, the authors should replace “northern hemisphere” by “Northern Hemisphere”, I believe, to comply with the convention (same for the Southern Hemisphere)

Also, I believe that “Earth system model” should be used instead of “Earth System Model”.

Line 48: change to:

“WOD represents an international collaborative effort among…”

Lines 56-57: change from “Without any measurements nearby…” to 

“For regions without any nearby measurements…”

Line 58: change to

“… the OI method will underestimate the declining trend…”

Line 76:  change “to valid the model” to

“For the evaluation of the model…”

Line 175: change “reconstructed model output” to

“…reconstructions fr subsampled model output”

Line 177: change “…outputs for the historical simulations to…” to

“…outputs for their historical simulations to…”

Line 179: change “The bilinear” to “A bilinear”

Line 181: Change “…as the observations” to “..as with the observations”

Line 198: Change “…similar to previous studies…” to “..similar to those in previous studies…”

Line 203: change “…in the south of Greenland” to “…to the south of Greenland”

Line 330: change “There are two regions, the Subpolar and Subtropical…” to “There are two regions, namely the Subpolar and Subropical…”

Line 332: change “bracket the observation where some models” to “bracket the observations whereas some models…”

Line 341:  change “indicating that the OI method” to “indicating where the OI method”

Line 386:  replace “gap-filling method used” with “gap-filling method used with observations”

Line 394: replace “least square sense assuming the Gaussian” with “least squares sense assuming a Gaussian…”

Line 396: replace “wide-spread” with “widespread”

Lines 425-426:  replace “at the spacial scales of 10-100km and timescales of several months” with

“With characteristic spatial scales of 10-100km and characteristic timescales…”

Ito et al. provide a good try to use synthetic data to understand an objective interpolation method (i.e. Ito et al. approach). They find that the global O2 change might be under-estimated using Ito’s objective interpolation approach, which makes sense because the approach infills climatology (no data, no signal) into data-sparse regions. The use of synthetic data is also a good approach I believe. Generally, the paper can be published. But I have some major concerns, mainly on the interpretation and presentation of the results. I hope these concerns can be addressed before publication.

Major:

1. The first concern is that the results are all specific to the particular OI approach proposed by Ito et al., and can not be generalized to all OI approach. This is very important because different groups (even all using OI) have different settings and considerations/assumptions, such as influencing radii, covariance etc., and the performance would be fundamentally different. Therefore, I would strongly insist on being more specific in the paper title and in the Abstract that the “underestimation” is for Ito et al. OI approach.
2. The sub-sampling strategy has to be more clearly introduced, e.g. how do you re-sample data if a 1X1 grid box has more than 1 observation? How do you deal with the difference in land-ocean masks (models differ from the real-world, for sure)? How do you construct the climatology: are you doing this based on re-sampled data over which time period?
3. The over-simplification of the approach has to be stated clearly in the abstract: e.g. no sub-grid variability is considered (observations do have all scales of variability, but your resampled profiles only contain variability >1 grid and 1 month), and no instrumental errors and potential biases are considered. Thus, this current approach is more “conceptual” than you can definitely quantify the “underestimation”. I believe the current study is over-confident in the quantitative numbers of the overestimation. I strongly suggest the authors take this more seriously.
4. Comparison between model results, and subsampled results with “Observations of Lto et al” (black line in Fig. 4) should be more careful. The so-called “observation” itself is biased by the conservative error (as investigated in this study) and it is more problematic because it also contains sub-grid variability and instrumental problems. Thus, please to be more careful to compare the models and subsampled results with this observation. It makes more sense to remove the black line in Fig.4, and also combines the right and left columns (e.g. full-model in solid lines and subsampled models in dashed lines at the same panels so they can be directly compared). So the focus is on the sampling issue. I have similar concerns about Fig. 5 and 6. I don’t even believe “observation” (as you argued in this study, it is problematic in many places because of the sampling/interpolation issues)
5. 7: because of the area difference with latitudes, doesn’t it make more sense to define the coverage by area instead of number of cells?
6. 5/6, I would be more keen to see the real spatial pattern (1X1 grid trend), instead of the box averages. It will be more straightforward to show the dynamic regimes.
7. 8/9 and section 3.4, with these analyses, I guess the authors want to have an “empirical” correction to the OI approach. But as I said in my 1-3 major points, the quantifications are useless because of the oversimplification of the approach. I don’t see the value of doing this analysis.

Overall, I do see the value of this study, but the interpretation and presentation of the results need to be revised in a substantial way to make it a more rigorous study (also leave room for more improvements in the future).

Minor

1. Abstract “more than 80%”, I don’t think it is trustable, because the values are apparently model-dependent, and also depend on subgrid-variability and instrumental errors.
2. Line 105: it is a strange choice, because if you remove Argo because of the precision, then CTD and OSD have different accuracy as well. To me, including Argo is valuable because you just want to test the sampling issue. You do nothing with the precision/accuracy in this paper with a synthetic data approach. I understand the authors might not do the things all over again, so a clear statement on the caveats is a necessary.
3. Line 185: just to confirm, is IPSL-CM6A-LR a Earth System Model?