Comments to bg-2023-129

Summary

The manuscript by Novi and colleagues aims to assess the suitability of isopycnic potential vorticity (IPV*) as a tracer of oxygen content in the upper ocean (0 – 200 m). This, in view of the possible use of IPV* to forecast oxygen content in the ocean at climatological scales based on in-situ temperature and salinity data. To this end, the authors focus on the North Pacific Ocean and evaluate the relationship between IVP* and oxygen concentrations within the framework of four Earth system models. Furthermore, the impact of two important modes of variability in the Pacific Ocean (PDO and ENSO) on the IVP*-oxygen linkage was evaluated. While the topic is certainly relevant, the approach used is novel and the motivation of the study is clearly justified, in my opinion this manuscript is only marginally suitable for Biogeosciences as its focus is mostly on the physical processes responsible for the supply of oxygen to the upper ocean. I therefore think that this manuscript is much more suitable for Ocean Science (also a Copernicus journal; see subject areas there). This does not however, diminishes the merit of this manuscript which upon moderate revision should be apt for publication in the appropriate journal.         

General comments

Strengths:

The manuscript is mostly well written and the presentation of the results is of high quality. Except for a few areas that need clarification (see specific comments below), the manuscript provides an accurate account of the approaches followed by the authors to carry out their analyses. Generally speaking, the text is well structured and the connection between objectives, approach, results and the corresponding conclusions is clear and easy to follow.

Weaknesses:

After reading the manuscript it is not completely clear what is the level of uncertainty associated with the projections carried out with the different models (described as “future” in the text and figures). This should be clearly stated as it might impact the applicability of the suggested approach if it were to be employed (as suggested by the authors) with large-scale data from autonomous platforms.

While the study covers open and coastal ocean areas; from the plots it is evident that there is a limitation on the resolution in close-coastal areas. I think it would be worth stating the proximity to the coasts at which this analyses are valid, as biogeochemical processes affecting the oxygen distribution in e.g. eastern boundary upwelling systems are particularly intense within 50-150 km from the coast (do we expect the variability in near-coastal areas to be smoothed out in climatological time scales?).

The results and conclusions section are rather puzzling. While the results in all subsections are well described, the discussion is limited and at the end one does not grasp the main message until reading the whole manuscript. My impression is that most of the current text on the conclusions actually corresponds to the missing text on the discussion. I recommend the authors to revise these two sections and cut down the conclusions to a brief text in which they state whether the study’s goals (as laid out in the introduction) were achieved or not and why.   

Specific comments

l.122: replace “for which” by “in which”.

l.143: replace “its” by “theirs”

l.235: I strongly suggest changing this section to “Results and Discussion”.

l.243–244: Please elaborate on the criteria used to classify an area as “most impacted by ENSO”. 

l.252: “(…) where the variability is dominated by PDO (…)”. Same comment as above for ENSO. 

l.337–340: This sentence is long and not understandable at all. Please revise. 

l.338: Remove apostrophe after “Peru”. 

l.375–378: This sentence is long and not understandable at all. Please revise. 

l.426–437: This can be omitted or significantly reduced as this information is mostly redundant. 

l.474: Consider changing to: “pointing to an area of further investigation”.

General comment to tables: according to Copernicus guidelines, “horizontal lines should normally only appear above and below the table, and as a separator between the head and the main body of the table”. Please revise.   

Novi et al’s manuscript “Evolution of oxygen and stratification in the North Pacific Ocean in CMIP6 Earth System Models” uses a suite of experiments across CMIP6 Earth System models and ocean reanalyses to explore the relationship between oxygen and stratification, here considered through isopycnic potential vorticity (IPV*), with an emphasis on how the relationship enhances or diminishes predictability. The manuscript uses a wide variety of analyses, including Information Entropy (IE), regression of O₂ and IPV* against climate variability indices, and trends and variability in the residuals from the regression analysis. 

The method is novel and the use of IE is an interesting way to think about the predictability of poorly-observed ocean biogeochemical variables, and how physically-relevant tracers can be used to understand upper-ocean oxygen variability. The application to O₂ is highly relevant as observations of oxygen are becoming more autonomous and is interesting on both physical and biogeochemical fronts because of its relationship to ventilation processes as well as ecosystem health.

I recommend this manuscript be accepted for publication subject to major revisions. In particular, the manuscript would benefit from much more explicit signposting throughout. The analyses are impressive but are presented in such a way that they feel separate and the reader must make their own logical steps. In addition, the manuscript lacks a critical analysis of the results and their connection to existing literature on BGC reconstructions. Adding text to connect all the sections together and references to other literature will allow readers to better understand the method and its applicability to the problem of sparse observations of BGC variables, even outside of ocean oxygen.

General Comments:

• The manuscript would benefit from explicit signposting throughout its sections. The authors set out their hypotheses in the introduction but there are jumps between the results sections. The hypotheses focus on the regulation of O₂ variability by IPV* yet most of the analyses approach IPV* and O₂ separately (albeit connected by the PDO index). Additionally, hypothesis (3) seems to relate to regions where predictability is high, but in the results the identification of hotspots uses the residuals from the PDO regression, which is where predictability is low. The lack of signposting makes it difficult for the reader to understand the full implications of the previous analyses when a new analysis is introduced, and there is ambiguity as to how well the hypotheses have been answered in the conclusions section.
• I am not sure why the PDO was chosen as the potential proxy for understanding upper-ocean O₂ concentrations. A priori I would assume that ENSO would play a significant role, and the results show a connection between ENSO and predictability of IPV* and O₂, whereas when looking at the PDO alone there appears to be a limited connection. In the introduction Ito et al (2019) is mentioned but some further explanation would be helpful. Additionally, I would be interested in seeing the regression analysis using both ENSO and the PDO as predictors and seeing how the residuals depend on the climate indices used for the regression.
• There is no discussion section, and the conclusions section seems to repeat the findings of the study without any connection to the wider literature. I would recommend changing Section 5 to “Discussion and Conclusions” (or adding a separate Discussions section) and including a critical analysis on the relationship of this study to other work on the PDO and North Pacific oxygen (e.g., Ito et al 2019) or to reconstruction efforts (e.g. Sharp et al., 2022). 
• I would like to see more discussion on the use of the CMIP6 ESMs. What are the implications of using relatively coarse-resolution models in this analysis? Particularly in the higher latitudes where eddy mixing is parameterized. What are the implications of having such a broad inter-model range in the results? It is not clear to me whether the emergent relationships are consistent enough across the models to justify the emphasis between IPV*, O₂, and the PDO.
• I would like to see some discussion on the use of predictability studies for real-world reconstructions. As I understand it, the predictability mentioned in this study assumes perfect knowledge at a time t  of a specific field, either IPV* or O₂ (for Section 4.1) or sea surface temperatures (for the PDO index used in the regression analysis in Section 4.2). However, T and S profiles from Argo are still irregularly distributed, which is a nontrivial problem for ocean reconstructions of both heat and salinity themselves (e.g., Smith and Murphy 2007, Cheng and Zhu 2016) and ocean BGC (e.g., Turner et al. 2023, Keppler et al. 2023). Especially considering that each CMIP6 model has its own covariance fields and errors relative to the real world, what is the best way to understand the predictability results from the model ensemble?

Specific Comments:

Line 174: I am not familiar with this definition of extremes. Is there a reason you have not used a general quantile threshold or a distribution fit to characterize the extremes? As you use only one realization for each model, there is a nontrivial chance of “significant” changes in extremes due to internal variability. 

Line 189: Why is the depth horizon set to the top 200 m? 

Line 193: What is the reasoning behind the choice of ESM models for the ensemble? Without choosing multiple realizations for each model and using 4 models, the ensemble seems quite small relative to the available CMIP6 output. Also it would be good to know which biogeochemical models each ESM employs in Table 1, even if biological oxygen cycling is outside the scope of this manuscript.

Line 206: JRA-55do v1.4 has an anticyclonic tropical cyclone in the NE Pacific in 1959 (as well as multiple anticyclonic tropical cyclones in the Atlantic, see https://climate.mri-jma.go.jp/pub/ocean/JRA55-do/). The issue is fixed in v1.5. It would be ideal to re-run the hindcast with the corrected atmospheric forcing. If that is not possible 1959 should be excluded from your analysis, perhaps using 1960-2014 as your historical period. 

Line 238: I am not sure exactly what predictability means. Based on (1), this assumes some perfect knowledge of t=0 everywhere in the North Pacific for each of these models? What is the length of time used to calculate the IE? Perhaps I misunderstand something in the methods with these questions, but clearer definitions for predictability both here and in the methods would be helpful.

Line 244: What do you mean by “area most impacted by ENSO”? Has there been a regression analysis done for ENSO in each of the models? Figure 2 a-f seem to have quite high IE (low predictability) in the equatorial upwelling region across all the models.

Line 319-320: How do the regression coefficients stay relatively stable if the domain for the PDO evolves? Also, what is the implication about the residuals dominating the evolution of both IPV* and O₂ in terms of predictability (and, in particular, predictability related to the PDO)?

Technical Comments:

Line 119: Should xi be multidimensional?

Line 135: What is the reasoning behind the use of 4 microstates?

Line 160: Why have you not used the same years across the models and reanalysis and hindcast product for each period?

Line 162: I find the use of shortcuts like Period 1/2, Ind 1/2/3, yseasm to hinder my understanding, particularly when examining the figures. More descriptive shortcuts (e.g., \overbar{DJF_1983-2014} - \overbar{DJF_1950-1981} instead of Ind1 ) would greatly help readability

Line 186: perhaps define N² here?

Line 188: Do you mean Equation 4? 

Line 195: Which variables are used from the CMIP6 models? If T and S, it would be helpful to know which models use EOS-80 and which use TEOS-10 for their density fields.

Line 196: Do you mean SSP?

Line 207: ORAS4 could use a description in this section. Also to explain about the lack of O2 results (I presume the reanalysis has no biogeochemistry?)

Line 221: RMSE values embedded within Figure 1 rather than presented as a list would increase readability of this section.

Line 223 and elsewhere: Please use consistent units formatting with superscripts

Line 279: Is it possible to include a scaled version of the NOAA PDO time series in Figure 3 for comparison?

Line 294: Is there one b_O2 and b_IPV* for all scenarios or are the coefficients calculated for each scenario separately?

Line 335: ORAS4

Line 435: Repeat here the vertical domain (0-200m)

References: 

Cheng, L., and J. Zhu, 2016: Benefits of CMIP5 Multimodel Ensemble in Reconstructing Historical Ocean Subsurface Temperature Variations. J. Climate, 29, 5393–5416, https://doi.org/10.1175/JCLI-D-15-0730.1. 

Keppler, L., Landschützer, P., Lauvset, S. K., & Gruber, N. (2023). Recent trends and variability in the oceanic storage of dissolved inorganic carbon. Global Biogeochemical Cycles, 37, e2022GB007677. https://doi.org/10.1029/2022GB007677

Smith, D. M. and Murphy, J. M.: An objective ocean temperature and salinity analysis using covariances from a global climate model, J. Geophys. Res.-Oceans, 112, C02022, https://doi.org/10.1029/2005JC003172, 2007.

Turner, K. E., Smith, D. M., Katavouta, A., and Williams, R. G.: Reconstructing ocean carbon storage with CMIP6 Earth system models and synthetic Argo observations, Biogeosciences, 20, 1671–1690, https://doi.org/10.5194/bg-20-1671-2023, 2023.

 Novi et al. – Evolution of oxygen and stratification in the North Pacific Ocean in CMIP6 Earth System Models

Summary

Novi et al use a suite of model outputs, including those from CMIP6 Earth System Models, hindcast runs and reanalysis data, to investigate (1) the strength of the relationship between isopycnic potential vorticity, (2) what is the physical process that underpins this relationship, and (3) whether this link between IPV and O2 can be used to identify hotspots of O2 change/variability. They focus on the North Pacific Ocean, which is influenced by inter-annual and decadal variability via the ENSO and the PDO, respectively.

Clarifications to the methods for non-specialists

I am not familiar with the methods regarding data-mining tools (∂-Maps) nor Information Entropy (IE). I found the explanation of how IE was calculated very well put, and I was able to follow without much difficulty. The exception here, however, was when the authors state “the explicit dependence of the entropy quantifier on e is removed using the maximum entropy formulation”.  At this point I was not sure of what the authors were doing, since the way an explicit e is removed is explained in Ikuyajolu et al (2021) that the authors point to and I am not familiar with. Another thing, am I interpreting things correctly if the choice to use 4 microstates means that their IE calculation uses 4 probabilities of occurrence (k=4 in equation 2)? Doesn’t this mean that the authors are choosing four different e values to create these 4 microstates from the same timeseries of IPV* Euclidean Distances (Eqn. 1)? So here I am confused about how e and Eqn. 1 is actually being done.

It is also not clear to me on reading the methods how you calculate the 95^th percentile of mean, variability and extremes in Eqn. 3. For the mean (indicator 1), as an example, are you computing the differences across all years in Period 1, then calculating the 95^th percentile of these differences? But actually, this doesn’t seem to be the case, because you state that ind_1j is equal to 𝑦𝑠𝑒𝑎𝑠𝑚2 − 𝑦𝑠𝑒𝑎𝑠𝑚), where yseasm1 and yseasm2 are multi-year seasonal means in Period 1 and 2, respectively. Multi-year is arbitrary, and on first reading I am inclined to believe that its averaging across the whole length of the period. This suggests to me that ind_1j is one number, and so it is not clear to me how you then retrieve a 95^th percentile. Could you please make this explanation clearer?

Other recommendations:

I very much agree with Reviewer 2 in that the paper would benefit from more signposting throughout, and that a reader only really appreciates what they have learned from the results in the final sentences of the conclusions.

I also agree that there is probably additional studies to point to so that the work can be placed amongst the wider literature.

There is also very little discussion or mention of the other processes affecting O2. Apart from ventilation, there is also the solubility effect of warming and biogeochemical processes affecting oxygen demand. I think the paper would benefit from a discussion of how these two other factors come into play.

For the solubility effect, it is not obvious how one would separate it from the ventilation component captured by IPV, since both are driven by warming and the IPV-O2 relationship should actually encompass both the ventilation and solubility effects. I leave it to the authors to think about how the solubility effect could be separated from the ventilation effect.

However, for the biogeochemical processes, it would not be so difficult to calculate preformed O2 from the T and S of each model and redo some of your analysis. An analysis of the IPV* - preformed O2 relationship would eliminate any impact of the biogeochemical process, and then allow you to focus on predictability of physical O2 injection. I would expect substantially more predictability and over a much greater area. Similarly, you could take preformed O2 away from your O2 tracer to get AOU, and you could look at the predictability of AOU, which is likely not predictable at all from IPV? Maybe give this a try, and see if some interesting results jump out. This would at least allow you diagnose why IPV-O2 predictability falls over in some regions?

Specific comments:

• Line 182: More accurate to say “We obtain three indicators grouped into four seasons for each variable”?
• Line 214: I know gridded Argo doesn’t provide T and S as far back as your period 1, but couldn’t you compare the ORAS4 against gridded Argo in Period 2? This would then provide some measure of how much bias there is in ORAS4, with which you are then using to assess bias in the models. Case in point is that the IPSL IPV fields looks (at least by eye) the least biased. It is not a coincidence because the IPSL and ORAS4 both use NEMO as their ocean models.
• Line 221: How is it that the RMSE of the NorESM2-LM is the lowest among the models? Are you sure this is calculated correctly?
• Line 307: Maybe remind the reader here was Ind1 is.
• Figures 4 and 5: Add text to the legend stating a more intuitive way of interpreting the plots. For b_IPV* you are presenting the change in IPV* (m^-1 s^-1) per change in SST (ºC^-1), right?
• Is the MPAS-O ocean model based on some version of MOM? The correspondence between the two models is striking.

Supplementary Material comments:

• Figure S4: you’ve stated 1950-2014 twice?

Thank you for considering my input to your research,

Pearse J. Buchanan.