the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 16 Dec 2024
Analysis of spatio temporal geophysical data using spatial entropy: application to comparison of SST datasets
Abstract. Efficient data analysis techniques are urgently needed due to the large amount of data continuously generated by Earth modeling and monitoring systems. We show that the spatial permutation entropy (SPE) is a valuable technique to characterize spatio-temporal geophysical data, allowing detailed analysis at different scales. Specifically, we show that SPE is able to uncover differences in two sea surface temperature (SST) products, in two relevant geographical regions: the equatorial Pacific (Niño3.4) and the Gulf Stream. SPE is calculated as the entropy of the probabilities of occurrences of symbols that are defined along two orientations, west-east (WE) or north-south (NS), and either in consecutive grid points, or separated by a lag, δ. We find substantial differences between the analyzed datasets, for the WE orientation with δ = 1, that gradually disappear as δ increases. We also identify two transitions, one in year 2007 when ERA5 changed its sea–surface boundary condition to OSTIA, and the second one in 2021 when NOAA changed satellite, from MeteOp–A to MeteOp–C. These transitions were not detected when using conventional data analysis tools, which demonstrates that SPE is a valuable tool for the analysis of 2D geophysical data.
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RC1: 'Comment on esd-2024-37', Anonymous Referee #1, 16 Jan 2025
The manuscript introduces a permutation method, together with the computation of the associated entropy, to analyze Sea- Surface Temperature (SST) datasets in two regions of the world, the Gulf stream region and the El-Nino region. Two datasets are used for the analysis, the NOAA optimal interpolation and the ERA5 with a monthly sample. The Indices of changes in the datasets are reported related to changes in the sources of observations used. It is claimed that these are not detected with other methods. I think that the method has merits but the work is at a very preliminary stage, and I cannot therefore recommend publication. My points follow:
- As the focus is on the introduction of a method of detection of changes, a proper statistical test should be designed. This is not performed and the indices of changes are guessed based on eye evaluation. The claim that it is better than other methods is not substantiated. Other even simpler methods could be designed for that purpose (for instance taking averages of certain fields in these regions). This is a necessary step if the purpose is to detect changes.
- The number of points in the datasets is very small (probably around a few hundreds of values at each grid point). The authors are using permutations of 4 symbols, leading to 24 different bins for the estimation of the probabilities. It means that a number of events falling in each bin is small, and therefore the estimates of probabilities and the corresponding entropy is affected by large uncertainties. This aspect is not evaluated and no sensitivity test is made. This is also a necessary step to clarify the usefulness of the method.
- Figure 3 is probably the most interesting as illustrating the potential long term changes in the dynamics of the climate system (that could be also detected with other methods). But the interpretation of the trends (and the possible implications of the entropy changes) is left for future study. In view of the weakness of the development of the method discussed in the two previous points, it would have been important to provide a deep and detailed analysis of the origin of these trends in the entropy. This exercise is not done and therefore the conclusions of the work on the physical aspects is weak.
Overall, I think that the work is too preliminary. A more extensive development of the testing method (and associated uncertainties) is necessary as the method has already been introduced some time ago, and a detailed and more extensive analysis of the physical origin of the trends is necessary.
Citation: https://doi.org/10.5194/esd-2024-37-RC1 -
AC1: 'Reply on RC1', Juan Gancio, 04 Mar 2025
We thank the reviewer for his/her comment on the merit of the method we used; However, we do not agree with the reviewer’s opinion that our work is in a very preliminary state because, as detailed in our response below, we have performed a detailed characterization and interpretation of the SST changes detected in the two data sets analysed, in the two regions considered. However, this comment gave us the opportunity to improve our work, and, if we are invited to resubmit a revised version of our work, in the revised manuscript we will include the results obtained with a popular algorithm for change point detection in time series: the Pruned Exact Linear Time (PELT) method (Killick et al., 2012).
Response to specific comments:
- As we explained in the abstract and in the introduction, our goal is to demonstrate that SPE is a reliable and versatile tool for characterizing spatio-temporal geophysical data, allowing detailed analysis by adjusting spatial scales. We willrevise the manuscript to further clarify our main objective. However, to take into account the reviewer’s comment, in the revised manuscript we will also use a Change Point Detection algorithm, PELT (Killick et al., 2012). We have already tried this method, and we found that the change points detected by the algorithm are the same as our original assessment, so no modifications in the discussion of results or in the conclusions were needed.
- We believe that the reviewer did not fully understand how we define the symbols. He/she says "The number of points in the datasets is very small (probably around a few hundreds of values at each grid point)", and therefore we believe the reviewer is referring to the number of points in each time series, recorded at each spatial grid point. In this sense, we agree with him/her that if we use a short time series to calculate the probabilities of 24 symbols, the number of events falling in each bin will be small.
However, we define the symbols as the values of SST anomalies at different grid points, at a given time.
Since there are 8000 grid points in the ElNiño3.4 region, and 3600 in the Gulf Stream region, we are confident we can properly estimate the probabilities of the 24 symbols. In the worst case, which corresponds to the analysis of the Gulf Stream region using a long spatial lag to define vertical symbols, e.g. lag=8, we can define 1440 symbols from the values of SST anomalies in the different grid points. In the revised manuscript we will make this point clearer. - We agree with the referee on the importance of Fig. 3; however we don’t understand the reviewer’s comment "that could be also detected with other methods". This figure shows the spatial permutation entropy computed from symbols defined with a long spatial lag, and two different orientations (NS and WE). We are not aware of an alternative methodology that can be used to identify the trends seen in Fig. 3.
Moreover, a clear and concise interpretation of the trends was presented in the manuscript, and not delayed for future work. Starting in line 75 in the original manuscript, it reads: “In Nino3.4 region, $H_{WE}$ has a negative trend, which can be due to SST variation over the equatorial Pacific, since it warms in the west and cools in the east (Wills et al., 2022), which means there is a westward large-scale gradient over the Niño3.4 area that can make symbols that represent trends more prevalent, decreasing the entropy (that is maximum when all possible symbols are equally probable)”. Line 83 reads: “In the Gulf Stream region, which is also heating due to global warming (Seidov et al., 2017; Todd and Ren, 2023), $H_{WE}$ and $H_{NS}$ in ERA5 and in NOAA present a positive trend, which reveals a loss of spatial structure (as the different symbols become more equally probable), and this fact is consistent with the homogeneous heating of this region”. Finally, line 117 (in the Conclusion section) reads: “Moreover, the different SPE trends found on the equatorial Pacific and Gulf Stream regions in the last decades are consistent with different responses to greenhouse gas forcing (uneven warming/cooling and homogeneous heating respectively)”. Therefore, we believe we have provided a compelling analysis of the origin of the trends found in the spatial permutation entropy.
Citation: https://doi.org/10.5194/esd-2024-37-AC1
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RC2: 'Comment on esd-2024-37', Anonymous Referee #2, 28 Feb 2025
The authors propose a novel use of spatial permutation entropy on the sea surface temperature field. They apply this metric on two domains, Niño3.4 and the Gulf Stream, and show differences between two different reanalyses. They then observed the emergence of differences in the computed entropy time series at certain times. In the case of Niño3.4, such differences are attributed to changes in the boundary conditions of ERA5. In the case of the Gulf Stream region, such differences were attributed to updates in the background error covariance.
I like the proposal of spatial permutation entropy to analyze differences in climate datasets. However, I do feel that this analysis is at its very first stage and not ready for publication. Additionally, while the authors present differences across two datasets, the interpretation of why they are different is also only preliminary. Further analysis of the statistical significance of such methodology should be added. In general, while the analysis is promising, the interpretation of results is incomplete at the current stage.
I can suggest the authors my opinion on how to build on top of this initial results. At the current stage, climate models are inputting a large amount of data. Methodologies such as the one proposed here could really help in further simplifying the analysis of the modeled dynamics. The authors could check the robustness of these ideas for an ensemble of simulations as given by the CESM Large Ensembles or the MPI Large Ensembles. Provided robustness of the (average) inferred entropy across trajectories of the same models, this information could be used to compare climate models ensembles. What can we learn from these differences about the climate system? Are these differences larger than the one observed for the ERA5 and NOAA OI vs dataset (I would hope so)? My main point is that the current application of the proposed methodology does not add a lot on what we do know about the climate system: the differences across the two reanalyses are indeed interesting, but then reasons about why we see such differences should be clearly explained.
If the authors will resubmit with new analyses I will be happy to review again.
Citation: https://doi.org/10.5194/esd-2024-37-RC2 -
AC2: 'Reply on RC2', Juan Gancio, 04 Mar 2025
We thank the reviewer for his/her comment, and we include below our response to the specific comments.
I like the proposal of spatial permutation entropy to analyze differences in climate datasets. However, I do feel that this analysis is at its very first stage and not ready for publication. Additionally, while the authors present differences across two datasets, the interpretation of why they are different is also only preliminary. Further analysis of the statistical significance of such methodology should be added. In general, while the analysis is promising, the interpretation of results is incomplete at the current stage.
We are glad that the reviewer liked our proposal, and we agree on the need of including, in the revised manuscript, a statistical significance analysis (using appropriated surrogates such as IAAFT surrogates).
However, we don’t understand why the reviewer considers that the interpretation of our findings is only preliminary. We believe that we have provided plausible, convincing arguments of the mechanisms that may underlie our findings. Even if our interpretation may, in the opinion of the reviewer, be “only preliminary”, we believe that the main contribution of our work to the community is a practical and flexible tool for the analysis of climate data and for performing model inter-comparisons, and we hope that our results will motive other researchers to test this methodology on their own datasets.
I can suggest the authors my opinion on how to build on top of this initial results. At the current stage, climate models are inputting a large amount of data. Methodologies such as the one proposed here could really help in further simplifying the analysis of the modeled dynamics. The authors could check the robustness of these ideas for an ensemble of simulations as given by the CESM Large Ensembles or the MPI Large Ensembles. Provided robustness of the (average) inferred entropy across trajectories of the same models, this information could be used to compare climate models ensembles. What can we learn from these differences about the climate system? Are these differences larger than the one observed for the ERA5 and NOAA OI vs dataset (I would hope so)? My main point is that the current application of the proposed methodology does not add a lot on what we do know about the climate system: the differences across the two reanalyses are indeed interesting, but then reasons about why we see such differences should be clearly explained.
We are indeed very thankful to the reviewer for these ideas that highlight the great potential of the methodology we are using, and we fully agree with the reviewer that research on these directions is the natural continuation of the present work. But we insist on clarifying which is the main goal of this work: to demonstrate that SPE is a reliable and versatile tool for characterizing spatio-temporal geophysical data, allowing detailed analysis by adjusting spatial scales. Of course, we also want to “add a lot on what we do know about the climate system”, and we argue that we are offering a methodology able to extract new information from observed data and model data. In this way, we believe we add a significant contribution to advance our understanding of the climate system.
If the authors will resubmit with new analyses I will be happy to review again.
If we are invited to do so, we indeed plan to resubmit a revised manuscript, which will include 1) a quantitative identification of the change points and 2) a statistical significance analysis of those changes, and we hope that our revised manuscript will be re-considered for publication.
Citation: https://doi.org/10.5194/esd-2024-37-AC2
-
AC2: 'Reply on RC2', Juan Gancio, 04 Mar 2025
Status: closed
-
RC1: 'Comment on esd-2024-37', Anonymous Referee #1, 16 Jan 2025
The manuscript introduces a permutation method, together with the computation of the associated entropy, to analyze Sea- Surface Temperature (SST) datasets in two regions of the world, the Gulf stream region and the El-Nino region. Two datasets are used for the analysis, the NOAA optimal interpolation and the ERA5 with a monthly sample. The Indices of changes in the datasets are reported related to changes in the sources of observations used. It is claimed that these are not detected with other methods. I think that the method has merits but the work is at a very preliminary stage, and I cannot therefore recommend publication. My points follow:
- As the focus is on the introduction of a method of detection of changes, a proper statistical test should be designed. This is not performed and the indices of changes are guessed based on eye evaluation. The claim that it is better than other methods is not substantiated. Other even simpler methods could be designed for that purpose (for instance taking averages of certain fields in these regions). This is a necessary step if the purpose is to detect changes.
- The number of points in the datasets is very small (probably around a few hundreds of values at each grid point). The authors are using permutations of 4 symbols, leading to 24 different bins for the estimation of the probabilities. It means that a number of events falling in each bin is small, and therefore the estimates of probabilities and the corresponding entropy is affected by large uncertainties. This aspect is not evaluated and no sensitivity test is made. This is also a necessary step to clarify the usefulness of the method.
- Figure 3 is probably the most interesting as illustrating the potential long term changes in the dynamics of the climate system (that could be also detected with other methods). But the interpretation of the trends (and the possible implications of the entropy changes) is left for future study. In view of the weakness of the development of the method discussed in the two previous points, it would have been important to provide a deep and detailed analysis of the origin of these trends in the entropy. This exercise is not done and therefore the conclusions of the work on the physical aspects is weak.
Overall, I think that the work is too preliminary. A more extensive development of the testing method (and associated uncertainties) is necessary as the method has already been introduced some time ago, and a detailed and more extensive analysis of the physical origin of the trends is necessary.
Citation: https://doi.org/10.5194/esd-2024-37-RC1 -
AC1: 'Reply on RC1', Juan Gancio, 04 Mar 2025
We thank the reviewer for his/her comment on the merit of the method we used; However, we do not agree with the reviewer’s opinion that our work is in a very preliminary state because, as detailed in our response below, we have performed a detailed characterization and interpretation of the SST changes detected in the two data sets analysed, in the two regions considered. However, this comment gave us the opportunity to improve our work, and, if we are invited to resubmit a revised version of our work, in the revised manuscript we will include the results obtained with a popular algorithm for change point detection in time series: the Pruned Exact Linear Time (PELT) method (Killick et al., 2012).
Response to specific comments:
- As we explained in the abstract and in the introduction, our goal is to demonstrate that SPE is a reliable and versatile tool for characterizing spatio-temporal geophysical data, allowing detailed analysis by adjusting spatial scales. We willrevise the manuscript to further clarify our main objective. However, to take into account the reviewer’s comment, in the revised manuscript we will also use a Change Point Detection algorithm, PELT (Killick et al., 2012). We have already tried this method, and we found that the change points detected by the algorithm are the same as our original assessment, so no modifications in the discussion of results or in the conclusions were needed.
- We believe that the reviewer did not fully understand how we define the symbols. He/she says "The number of points in the datasets is very small (probably around a few hundreds of values at each grid point)", and therefore we believe the reviewer is referring to the number of points in each time series, recorded at each spatial grid point. In this sense, we agree with him/her that if we use a short time series to calculate the probabilities of 24 symbols, the number of events falling in each bin will be small.
However, we define the symbols as the values of SST anomalies at different grid points, at a given time.
Since there are 8000 grid points in the ElNiño3.4 region, and 3600 in the Gulf Stream region, we are confident we can properly estimate the probabilities of the 24 symbols. In the worst case, which corresponds to the analysis of the Gulf Stream region using a long spatial lag to define vertical symbols, e.g. lag=8, we can define 1440 symbols from the values of SST anomalies in the different grid points. In the revised manuscript we will make this point clearer. - We agree with the referee on the importance of Fig. 3; however we don’t understand the reviewer’s comment "that could be also detected with other methods". This figure shows the spatial permutation entropy computed from symbols defined with a long spatial lag, and two different orientations (NS and WE). We are not aware of an alternative methodology that can be used to identify the trends seen in Fig. 3.
Moreover, a clear and concise interpretation of the trends was presented in the manuscript, and not delayed for future work. Starting in line 75 in the original manuscript, it reads: “In Nino3.4 region, $H_{WE}$ has a negative trend, which can be due to SST variation over the equatorial Pacific, since it warms in the west and cools in the east (Wills et al., 2022), which means there is a westward large-scale gradient over the Niño3.4 area that can make symbols that represent trends more prevalent, decreasing the entropy (that is maximum when all possible symbols are equally probable)”. Line 83 reads: “In the Gulf Stream region, which is also heating due to global warming (Seidov et al., 2017; Todd and Ren, 2023), $H_{WE}$ and $H_{NS}$ in ERA5 and in NOAA present a positive trend, which reveals a loss of spatial structure (as the different symbols become more equally probable), and this fact is consistent with the homogeneous heating of this region”. Finally, line 117 (in the Conclusion section) reads: “Moreover, the different SPE trends found on the equatorial Pacific and Gulf Stream regions in the last decades are consistent with different responses to greenhouse gas forcing (uneven warming/cooling and homogeneous heating respectively)”. Therefore, we believe we have provided a compelling analysis of the origin of the trends found in the spatial permutation entropy.
Citation: https://doi.org/10.5194/esd-2024-37-AC1
-
RC2: 'Comment on esd-2024-37', Anonymous Referee #2, 28 Feb 2025
The authors propose a novel use of spatial permutation entropy on the sea surface temperature field. They apply this metric on two domains, Niño3.4 and the Gulf Stream, and show differences between two different reanalyses. They then observed the emergence of differences in the computed entropy time series at certain times. In the case of Niño3.4, such differences are attributed to changes in the boundary conditions of ERA5. In the case of the Gulf Stream region, such differences were attributed to updates in the background error covariance.
I like the proposal of spatial permutation entropy to analyze differences in climate datasets. However, I do feel that this analysis is at its very first stage and not ready for publication. Additionally, while the authors present differences across two datasets, the interpretation of why they are different is also only preliminary. Further analysis of the statistical significance of such methodology should be added. In general, while the analysis is promising, the interpretation of results is incomplete at the current stage.
I can suggest the authors my opinion on how to build on top of this initial results. At the current stage, climate models are inputting a large amount of data. Methodologies such as the one proposed here could really help in further simplifying the analysis of the modeled dynamics. The authors could check the robustness of these ideas for an ensemble of simulations as given by the CESM Large Ensembles or the MPI Large Ensembles. Provided robustness of the (average) inferred entropy across trajectories of the same models, this information could be used to compare climate models ensembles. What can we learn from these differences about the climate system? Are these differences larger than the one observed for the ERA5 and NOAA OI vs dataset (I would hope so)? My main point is that the current application of the proposed methodology does not add a lot on what we do know about the climate system: the differences across the two reanalyses are indeed interesting, but then reasons about why we see such differences should be clearly explained.
If the authors will resubmit with new analyses I will be happy to review again.
Citation: https://doi.org/10.5194/esd-2024-37-RC2 -
AC2: 'Reply on RC2', Juan Gancio, 04 Mar 2025
We thank the reviewer for his/her comment, and we include below our response to the specific comments.
I like the proposal of spatial permutation entropy to analyze differences in climate datasets. However, I do feel that this analysis is at its very first stage and not ready for publication. Additionally, while the authors present differences across two datasets, the interpretation of why they are different is also only preliminary. Further analysis of the statistical significance of such methodology should be added. In general, while the analysis is promising, the interpretation of results is incomplete at the current stage.
We are glad that the reviewer liked our proposal, and we agree on the need of including, in the revised manuscript, a statistical significance analysis (using appropriated surrogates such as IAAFT surrogates).
However, we don’t understand why the reviewer considers that the interpretation of our findings is only preliminary. We believe that we have provided plausible, convincing arguments of the mechanisms that may underlie our findings. Even if our interpretation may, in the opinion of the reviewer, be “only preliminary”, we believe that the main contribution of our work to the community is a practical and flexible tool for the analysis of climate data and for performing model inter-comparisons, and we hope that our results will motive other researchers to test this methodology on their own datasets.
I can suggest the authors my opinion on how to build on top of this initial results. At the current stage, climate models are inputting a large amount of data. Methodologies such as the one proposed here could really help in further simplifying the analysis of the modeled dynamics. The authors could check the robustness of these ideas for an ensemble of simulations as given by the CESM Large Ensembles or the MPI Large Ensembles. Provided robustness of the (average) inferred entropy across trajectories of the same models, this information could be used to compare climate models ensembles. What can we learn from these differences about the climate system? Are these differences larger than the one observed for the ERA5 and NOAA OI vs dataset (I would hope so)? My main point is that the current application of the proposed methodology does not add a lot on what we do know about the climate system: the differences across the two reanalyses are indeed interesting, but then reasons about why we see such differences should be clearly explained.
We are indeed very thankful to the reviewer for these ideas that highlight the great potential of the methodology we are using, and we fully agree with the reviewer that research on these directions is the natural continuation of the present work. But we insist on clarifying which is the main goal of this work: to demonstrate that SPE is a reliable and versatile tool for characterizing spatio-temporal geophysical data, allowing detailed analysis by adjusting spatial scales. Of course, we also want to “add a lot on what we do know about the climate system”, and we argue that we are offering a methodology able to extract new information from observed data and model data. In this way, we believe we add a significant contribution to advance our understanding of the climate system.
If the authors will resubmit with new analyses I will be happy to review again.
If we are invited to do so, we indeed plan to resubmit a revised manuscript, which will include 1) a quantitative identification of the change points and 2) a statistical significance analysis of those changes, and we hope that our revised manuscript will be re-considered for publication.
Citation: https://doi.org/10.5194/esd-2024-37-AC2
-
AC2: 'Reply on RC2', Juan Gancio, 04 Mar 2025
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