OPEN: A New Estimation of Global Ocean Heat Content for Upper 2000 Meters from Remote Sensing Data

Round 1

Reviewer 1 Report

Comments on "A new estimation of global ocean heat content ...."

I have some fundamental doubts to be clarified:

1. Please refer P. S. V. Jagadeesh, M. Suresh Kumar, and M. M. Ali (2015). Estimation of Heat Content and Mean Temperature of Different Ocean Layers, IEEE-JSTARS, vol. 8. No. 3, pp 1251-1255, DOI: 10.1109/JSTARS.2015.2403877.

and the papers referred therein and summarise how your method is new compared to the approach described in the paper. Also, try to statistically compare your results with that given in the above paper at least for the common depths, if any. 

2.  Somewhere OHC and sometimes OHC anomaly is used. Are they used as synonyms? The equation for OHC alone is given. How do you define OHC anomaly?

3. The equation (line no 132) is for OHC, what is the equation for OHC anomaly? 

4. The above-referred equation has some flaws: Cp and roh are taken as constants. They can be brought out of the integration if they are used as constants. Secondly, it is better to use variable roh rather than constant. Argo data provides profiles of salinity from which roh can be computed at each layer. 

5. What do you mean by temperature anomaly? Do you mean the temperature difference between the boundaries of the layer? Needs to be clarified.

6. The data used in the analysis have different durations and different resolutions. How they are brought to the same duration and resolution need to be clarified. 

7. How these products OHC or OHC anomaly are extended beyond the study period, say from 1998 onward, is not clear. 

8. Very general comments: "Coefficient of determination" is the general terminology. Please give proper references following the journal format. Eg. Sue et al., Lue at al. (they should be properly referred). 

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 2 Report

Dear editor,

This is my first review of a manuscript by Su et al. titled 'OPEN: A New Estimation of Global Ocean Heat Content from Remote Sensing Data' in which the authors present a new statistical estimate of the global ocean heat content. This estimate is based on a tool that the authors have published earlier. While I find the study interesting and mostly well written, I think it lacks i) robust error estimation, ii) adequate comparison to other ocean heat content estimates, and iii) the authors should be more upfront about the limitations of the method. I think these issues are straightforward to assess (see suggestions in the comments), but might take some time, which is why I consider this a major revision. Since this is major revision, I have not commented on grammar/typos. Please see below for the detailed comments.

Major comments:

1) The study is solely based on observational data, i.e. the authors use a gridded Argo product to train their statistical model. This is valuable in the sense that they can extend the heat content estimation beyond the Argo period. However, the estimation cannot really be any better than the Argo product itself, which is likely to suffer from artifacts related to spatio-temporal interpolation. Another approach could have been to use model data for training. All models suffer from individual biases (so lon/lat information should not be used), but they should correctly represent the thermal expansion/haline contraction, and therefore be suitable for training. If the authors have global model data available then it could be relatively easy to use that in addition for training, but at least they should discuss the limitations of their current method and other possibilities for constructing the statistical model.

2) There is no error/robustness estimate in the results, yet it would be straightforward to gain one: I would suggest the authors use multiple training periods (for example overlapping 5 year periods) to form an ensemble of OHC estimates. This would allow the authors to plot an envelope around the lines in Figure 4, and for example add contours of the ensemble standard deviation in Figure 2.

3) The R2 values in Figure 3 are extremely high. Did the authors remove the linear trend before calculating the correlation? In any case the timeseries is rather short, and the OHC is globally integrated quantity, so I don’t think R2 values are the most interesting. RMSE probably tells a bit more about the quality of OPEN, especially because it seems that the method produces consistently higher trends than the Argo data alone. I think it would also be valuable to provide spatial correlations similar to Table 1 through all the years that were not part of the training.

4) The authors provide comparison to one other OHC estimate (IAP), but as they state, there are number of other estimates out there, and I think it would be very valuable to compare to at least some of them. Recently Zanna et al. (https://www.pnas.org/content/116/4/1126) published their estimate of OHC and show comparison to 6 other estimates (IAP amongst them), I would ask the authors to compare to at least few of those shown in Zanna et al.

5) There are also other methods that use statistics to combine surface and subsurface measurements. One of those is the ARMOR3D product and I think it would be valuable to compare the results to that as well https://resources.marine.copernicus.eu/?option=com_csw&task=results?option=com_csw&view=details&product_id=MULTIOBS_GLO_PHY_REP_015_002. As far as I know, the ARMOR3D uses linear regression to connect the SSH to subsurface quantities and therefore it would be very interesting to see if the neural network design that the authors use produce different results.

7) I am a bit unsure about the value of figure 7. It seems to show that 10 and 5 year trends are related, which is not really surprising. However, what it also shows is that the standard deviations deviate between the two data sets. Perhaps it would be more interesting to look at the difference in standard deviation between the data sets in the different regions/depths?

 

Minor comments:

8) The authors should clearly state early on that their heat content estimate is for the upper 2000 meters of the global ocean, excluding the polar regions. This information should probably come up already in the title, for example: ‘OPEN: A New Estimation of Global Ocean Heat Content down to 2000m depth from Remote Sensing Data’ and then in the abstract/intro point out that the estimate excludes the polar regions where there is no Argo data/no SSH data.

9) Section 3.1: the method description is quite brief and probably not very accessible for people without much experience with training neural networks. I would ask the authors to bring in some material from ref 24 here, or to an appendix so that this would be a bit more self contained manuscript. At least the basic equation for the network should be shown.

10) L132 The authors should use TEOS-10 equation of state to calculate the ocean heat content. This would mean using conservative temperature and constant heat capacity (or just directly using their product i.e. potential enthalpy), but also a varying density. Also, the equation should have a number associated with it and I would suggest using the math editor of their text editor (both MS Office and LibreOffice have one these days) to typing the equation (now it seems to be low resolution graphic).

11) Figures 2, 6, 8 and 9. I would strongly encourage moving a way from the jet/rainbow colormap and using some perceptually uniform colormap instead (should be the default in new versions of Matlab/Python Matplotlib).

12) L418 I would encourage publishing the code/trained model online for example in GitHub/Zenodo.

 

Author Response

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Author Response File: Author Response.pdf

Round 2

Reviewer 2 Report

Dear editor,

This is my second review of a manuscript by Su et al., now titled 'OPEN: A New Estimation of Global Ocean Heat Content for Upper 2000 meters from Remote Sensing Data'. I thank the authors for a quick, but thorough review. I think the addition of new data and the error estimate greatly improved the manuscript and provide a good reference for OPEN. As always, more questions arise with more data, but at this point, I think the manuscript can be published and I have only suggested some minor/editorial changed and quick check on their analysis that the authors might consider before publication.

Minor comments/Suggestions:

Figure 4 (and the similar supplementary figures) show that at a global scale OPEN is similar to ARMOR and GLORYS, except for the first ~3 years. This is very interesting because these three datasets incorporate some information about the sea level in contrast to EN4, IAP, and NCEI (which are consistent with each other). I would mention this explicitly in the text.

Figure 4 and 5: Have you low-pass filtered the data? The reason why I am asking is because it seems that there are some steep increases in the beginning/drops at the end of the timeseries which could be artifacts. I would suggest using something like scipy filtfilt method in python (probably similar in Matlab). Also, L377 you mention that there is an inconsistency with OPEN and the other methods in the Pacific. However, when you look at the Global OHC (Figure 4) somewhat similar increase to the one seen in the Pacific (Figure 5) is also visible (2014-2016). However, on the global scale it seems that ARMOR and GLORYS agree with OPEN. I wonder where that increase in the global OHC comes from in ARMOR and GLORYS if not from the Pacific?

Figure 6 and the associated text: I would avoid calling the trend an ‘Ocean heating rate’, because mostly the signal is actually a mass displacement, not ‘real’ heating. I would simply call it ‘OHC change’.

Editorial:

The manuscript reads reasonably well, but it might be worth doing a check with some native English speakers (which I’m not). In any case, here are some of my suggestions to improve readability.

#1 L53 I would say ‘internal ocean dynamics’

#2 L147 I don’t think there is a real ‘convention’ to always consider the heat content down to 300 m, 700 m, 1500 m, and 2000 m. I would just say ‘We integrate the ocean heat content down to …’

#3 L161 should read ‘is not a concern’

#4 L167 This is a bit hard to read. Here is a suggestion: ‘Each hidden layer consists of N neurons, whereas the output layer has only one neuron as our target, OHC, is a scalar.’

#5 L168 I would suggest: ‘Each neuron in each layer calculates a weighted sum of all the outputs from the previous layer, transforms ...’

#6 L183 should read ‘Considering that the...’

#7 L185 I would suggest ‘Training with 2005-2018 then yields a network for each depth with optimized \theta‘

#8 L190 I would suggest ‘… was slid through the data with ...’

Author Response

Please see the attachment for our responses. 

Author Response File: Author Response.pdf