the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 13 Jan 2022
A reexamination of the dry gets drier and wet gets wetter paradigm over global land: insight from terrestrial water storage changes
Abstract. The “dry gets drier and wet gets wetter” (DDWW) paradigm has been widely used to summarize the expected trends of the global hydrologic cycle under climate change. However, the paradigm is challenged over land due to different measures and datasets, and is still unexplored from the perspective of terrestrial water storage anomaly (TWSA). Considering the essential role of TWSA in wetting and drying of the land surface, here we built upon a large ensemble of TWSA datasets including satellite-based products, global hydrological models, land surface models, and global climate models to evaluate the DDWW hypothesis during the historical (1985–2014) and future (2071–2100) periods under various scenarios. We find that 27.1 % of global land confirms the DDWW paradigm, while 22.4 % of the area shows the opposite pattern during the historical period. In the future, the DDWW paradigm is still challenged with the percentage supporting the pattern lower than 20 %, and both the DDWW-validated and DDWW-opposed proportion increase along with the intensification of emission scenarios. Our findings will provide insights and implications for global wetting and drying trends from the perspective of TWSA under climate change.
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RC1: 'Comment on hess-2021-645', Anonymous Referee #1, 07 Feb 2022
General comments:
This study reexamine the “dry gets drier and wet gets wetter” (DDWW) paradigm from the perspective of terrestrial water storage anomaly (TWSA) using a large ensemble of GRACE reconstructions, global hydrological models, and land surface modes. Based on the proportional percentages of different patterns, the results showed the consistent/opposite pattern with the DDWW and then the authors claimed that the paradigm faces challenge in both history (1985-2014) and future (2071-2100).
The topic is interesting and this study potentially provide a new perspective. However, I do not see the methods are convincing and the results are robust. First of all, I want to say that the dryness/wetness change itself contains different models, so it is not surprising to find the change models that do not follow the "DDWW" paradigm on a global scale.
(1) My largest concerns are: Can GRACE observed TWS be used to estimate land surface dryness/wetness trends? How well (sensitive) can TWSA represent long-term trends in dryness/wetness across land surfaces? Is it better than traditional drought indices (e.g., the SPEI, PDSI or other methods)? There is no authoritative study demonstrating the suitability and applicability of the GRACE observed TWS in capturing surface dryness/wetness trends, especially on a global scale. Please note that, generally, the GRACE observed TWSA is applied to monitor changes in groundwater, land-ice evolution, and drought/flood events which occur on a short-term scale (see References). Hydrological processes are complex, but indices are often based on a relatively simple calculation. I take an example to show my understanding here. In glacier-covered mountains, as the climate warms, ice/glaciers are degrading with an increase in runoff/soil moisture (moisten the land surface). Meanwhile, as the mass decreases (water flows away), what GRACE observes is a decrease trend in gravity (drying). TWSA estimated trend and the real surface dry/wet trend can be absolutely opposite. Thus, changes in TWS do not equal to changes in surface dryness/wetness. Right?
Let’s continue this topic and look at the Figure 3a. Over the past few decades, glacier melting and increasing runoff/wet trend in the southwest of Tibetan Plateau have been reported (e.g., the Fig. 4b of Yang et al., 2019), but the TWSA detect a drying trend in historic period. This clearly shows that the use of TWSA to estimate surface dry/wet trend is not robust.
In addition, terrestrial water storage anomaly contains the information of changes in groundwater. With increasing human activity, large-scale pumping reduces groundwater (i.e., TWS observed a decrease trend) whereas the groundwater pumping and agricultural irrigation can moisten the land surface. I feel that the subtle effects of pumping and agricultural irrigation on dryness/wetness changes also cannot be captured by the TWSA. Therefore, I cannot confirm how valuable the perspective proposed by the author is for the capture of surface dry/wet changes.
(2) My another question is why the authors confirm that an ensemble way is more reliable than a single way? This draft does not show the individual results of different methods, nor does it compare the differences in these results, so I can't be sure that the way of ensemble is reliable. In the Figure S2, there are gaps between gravity satellite observations and climate model simulations. Besides, why the authors use the GRACE observation to correct the CMIP6 historical simulation? Do you think the simulation of CMIP6 is unreliable (relative to GRACE)? Why? How to define and calculate the TWS in hydrological models, CMIP6, and land surface models? Are they talking about the same thing (and same with the GRACE’s TWS)? How different are the estimated TWS between these methods? I don't think simply integrating the various outputs is a right path, because of the inherent scale differences between climate models, hydrological models, and satellite observations, and I think the TWS in these methods is not the same object.
(3) I found a fault in the fundamental calculation. The presented area percentages are calculated by the number of grids, which are not the real area of the Earth sphere. Such calculation can greatly reduce the proportion in the tropics, but we think the “wet-wetter”paradigm is generally well followed there.
(4) The titles of section 3.1 and section 3.2 are the same, i.e., “Global trends of dryness and wetness”. How rough! Despite an admirable effort by the authors to process data and conduct calculations, the manuscript lacks discussion and more is showing calculation results. Uncertainties regarding to the new methods and results should be fully discussed.
For the above reasons, I do not support its publication in the HESS. There are also minor issues in this manuscript (see below).
Specific comments:
- Line 13-14: Why the sum of the patterns is 27.1% plus 22.4% (not 100%)? What about other patterns?
- Line 20: What’s the meaning of “fresh availability”?
- Line 25: What do you mean “enhance”? What do you mean “vice versa”?
- Line 26-27: “in hydrologic cycle under climate change in both regional and global scales”. Is this expression a bit exaggerated?
- Line 29-30: “rational”-->“rationale”. Do so many references really question the rationale of DDWW?
- Line 40-41: “The uncertainties within previous studies are mainly sourced from different choices of measures and datasets”. However, this study do not reduce such uncertainties, and there are also great uncertainties, as there are various data sources and interpolation methods.
- Line 45: It is true that “neglect the hydrological process on the land surface”, but the TWSA used for estimating dryness/wetness is also an index and neglect the hydrological process.
- Line 47: “merely highlight differently single aspect of the water cycle, lacking the complete representation of the terrestrial water storage (TWS) ”. Why do you think a complete representation of TWS would be better than a index regarding single aspect of water cycle? I think there are already comprehensive drought/wet indices.
- Line 50: “TWS consisting of water storage in surface water, soil moisture,groundwater, snow and ice, and canopies can physically provide integrated information...” But groundwater pumping reduces groundwater (TWS is decrease) and makes the surface wet.
- Line 93: What’s the meaning of offline physically based?
- Is it necessary to carry out regional studies according to the IPCC? The zoning studies make no sense in fact. They are just another display for the same results.
- The conclusion section is not well written. What new things the manuscript provide? It is recommended to summarize from two aspects: method and finding. How well does the new method/perspective works and what is the scientific value of the results in this study?
- Figure 1: Which method was used to calculate the slopes in the left panel? Which method was used to analyze the significance of trends? Which level?
- Figure 2: What does the fan shape in the map means?
- Figure 4: I cannot figure the fan shapes and their meaning clearly.
Citation: https://doi.org/10.5194/hess-2021-645-RC1 - AC1: 'Reply on RC1', Shenglian Guo, 01 Mar 2022
-
RC2: 'Comment on hess-2021-645', Anonymous Referee #2, 09 Feb 2022
The authors present a re-examination of the dry gets drier, and wet gets wetter paradigm over global land, based on terrestrial water storage estimates from different sources. They make use of GRACE reconstructions, global hydrological models, and land surface models, as well as CMIP6 models for the future perspective. They conclude that the DDWW paradigm is challenged both in the historical period but also in the future.
I think that the topic is interesting and fits well the journal, and the use of the complete terrestrial water storage for the analysis of the DDWW paradigm adds another perspective compared to previous studies. However, the paper currently lacks some important information and has a substantial methodological issue which requires major revision.
My main concerns are:
- The use of percentage of grid cells for the presentation of many of the results is not appropriate and hinders the proper interpretation. It’s necessary to present the corresponding numbers as percentage per land area (i.e., by weighing the grid boxes according to their effective km2 area) in order not to give excessive weight to higher latitudes. This will most likely have impacts on the overall conclusions of the paper.
- The choice of the eight CMIP6 models in not transparent. Why didn’t the authors choose a larger model ensemble based on the CMIP6 archive? Based on which criteria were these eight models selected?
- Also, given the large uncertainties between the CMIP6 models on the one hand, but also within the DATASET ensemble (cf. Fig. S8), the impact of the applied ensemble mean approach on the results should be discussed in more detail.
Specific comments:
Line 20: “and freshwater availability” instead of “and fresh availability”
Line 83/84: Which of the available meteorological forcings for these reconstructions did you consider (MSWEP, GSWP3 or ERA5)? Did you take the mean over the three forcings for each of the two calibrations?
Line 125: Based on which criteria did you select these 8 models?
Line 136: “to match the observed data” instead of “to match the observed results”
Line 144 (Equation 1): The dash in TWS – DSI could be confused with a "minus". I suggest changing it to an "_" or at least a short dash.
Line 152: “all the land area except for the Greenland and Antarctica”
Line 157: “CMIP6 archive” instead of “CMIP6 achieve”
Line 168-170: Why poorer performance when NRMSE is lower?
Line 180: “greater” instead of “slighter”? The fluctuations of CMIP6 are larger than the ones of DATASET (Fig. S4).
Line 180: “the effective bias correction performance” Why effective? CMIP6 deviates more from GRACE than DATASET.
Line 212: Here and throughout the results the use of percentage of grid cells is not appropriate and needs to be changed to percentage of land area for proper interpretation.
Figure 2: Nice plot, however quite crowded. The region names are often barely readable. You could just refer to the Supplementary Figure 1 for the definition and naming of the regions. The same applies to Figure 4.
Line 234: There's no stippling on these figures? Please revise the caption and also explain the meaning of the pie charts.
Line 235: Same title as for Section 3.1. I guess this is an oversight.
Line 257 and following: I assume these percentages are again based on the grid cells only, not based on the actual area?
Conclusion: The conclusions need to be extended. What's new compared to previous studies? What are the implications?
Citation: https://doi.org/10.5194/hess-2021-645-RC2 - AC2: 'Reply on RC2', Shenglian Guo, 01 Mar 2022
Status: closed
-
RC1: 'Comment on hess-2021-645', Anonymous Referee #1, 07 Feb 2022
General comments:
This study reexamine the “dry gets drier and wet gets wetter” (DDWW) paradigm from the perspective of terrestrial water storage anomaly (TWSA) using a large ensemble of GRACE reconstructions, global hydrological models, and land surface modes. Based on the proportional percentages of different patterns, the results showed the consistent/opposite pattern with the DDWW and then the authors claimed that the paradigm faces challenge in both history (1985-2014) and future (2071-2100).
The topic is interesting and this study potentially provide a new perspective. However, I do not see the methods are convincing and the results are robust. First of all, I want to say that the dryness/wetness change itself contains different models, so it is not surprising to find the change models that do not follow the "DDWW" paradigm on a global scale.
(1) My largest concerns are: Can GRACE observed TWS be used to estimate land surface dryness/wetness trends? How well (sensitive) can TWSA represent long-term trends in dryness/wetness across land surfaces? Is it better than traditional drought indices (e.g., the SPEI, PDSI or other methods)? There is no authoritative study demonstrating the suitability and applicability of the GRACE observed TWS in capturing surface dryness/wetness trends, especially on a global scale. Please note that, generally, the GRACE observed TWSA is applied to monitor changes in groundwater, land-ice evolution, and drought/flood events which occur on a short-term scale (see References). Hydrological processes are complex, but indices are often based on a relatively simple calculation. I take an example to show my understanding here. In glacier-covered mountains, as the climate warms, ice/glaciers are degrading with an increase in runoff/soil moisture (moisten the land surface). Meanwhile, as the mass decreases (water flows away), what GRACE observes is a decrease trend in gravity (drying). TWSA estimated trend and the real surface dry/wet trend can be absolutely opposite. Thus, changes in TWS do not equal to changes in surface dryness/wetness. Right?
Let’s continue this topic and look at the Figure 3a. Over the past few decades, glacier melting and increasing runoff/wet trend in the southwest of Tibetan Plateau have been reported (e.g., the Fig. 4b of Yang et al., 2019), but the TWSA detect a drying trend in historic period. This clearly shows that the use of TWSA to estimate surface dry/wet trend is not robust.
In addition, terrestrial water storage anomaly contains the information of changes in groundwater. With increasing human activity, large-scale pumping reduces groundwater (i.e., TWS observed a decrease trend) whereas the groundwater pumping and agricultural irrigation can moisten the land surface. I feel that the subtle effects of pumping and agricultural irrigation on dryness/wetness changes also cannot be captured by the TWSA. Therefore, I cannot confirm how valuable the perspective proposed by the author is for the capture of surface dry/wet changes.
(2) My another question is why the authors confirm that an ensemble way is more reliable than a single way? This draft does not show the individual results of different methods, nor does it compare the differences in these results, so I can't be sure that the way of ensemble is reliable. In the Figure S2, there are gaps between gravity satellite observations and climate model simulations. Besides, why the authors use the GRACE observation to correct the CMIP6 historical simulation? Do you think the simulation of CMIP6 is unreliable (relative to GRACE)? Why? How to define and calculate the TWS in hydrological models, CMIP6, and land surface models? Are they talking about the same thing (and same with the GRACE’s TWS)? How different are the estimated TWS between these methods? I don't think simply integrating the various outputs is a right path, because of the inherent scale differences between climate models, hydrological models, and satellite observations, and I think the TWS in these methods is not the same object.
(3) I found a fault in the fundamental calculation. The presented area percentages are calculated by the number of grids, which are not the real area of the Earth sphere. Such calculation can greatly reduce the proportion in the tropics, but we think the “wet-wetter”paradigm is generally well followed there.
(4) The titles of section 3.1 and section 3.2 are the same, i.e., “Global trends of dryness and wetness”. How rough! Despite an admirable effort by the authors to process data and conduct calculations, the manuscript lacks discussion and more is showing calculation results. Uncertainties regarding to the new methods and results should be fully discussed.
For the above reasons, I do not support its publication in the HESS. There are also minor issues in this manuscript (see below).
Specific comments:
- Line 13-14: Why the sum of the patterns is 27.1% plus 22.4% (not 100%)? What about other patterns?
- Line 20: What’s the meaning of “fresh availability”?
- Line 25: What do you mean “enhance”? What do you mean “vice versa”?
- Line 26-27: “in hydrologic cycle under climate change in both regional and global scales”. Is this expression a bit exaggerated?
- Line 29-30: “rational”-->“rationale”. Do so many references really question the rationale of DDWW?
- Line 40-41: “The uncertainties within previous studies are mainly sourced from different choices of measures and datasets”. However, this study do not reduce such uncertainties, and there are also great uncertainties, as there are various data sources and interpolation methods.
- Line 45: It is true that “neglect the hydrological process on the land surface”, but the TWSA used for estimating dryness/wetness is also an index and neglect the hydrological process.
- Line 47: “merely highlight differently single aspect of the water cycle, lacking the complete representation of the terrestrial water storage (TWS) ”. Why do you think a complete representation of TWS would be better than a index regarding single aspect of water cycle? I think there are already comprehensive drought/wet indices.
- Line 50: “TWS consisting of water storage in surface water, soil moisture,groundwater, snow and ice, and canopies can physically provide integrated information...” But groundwater pumping reduces groundwater (TWS is decrease) and makes the surface wet.
- Line 93: What’s the meaning of offline physically based?
- Is it necessary to carry out regional studies according to the IPCC? The zoning studies make no sense in fact. They are just another display for the same results.
- The conclusion section is not well written. What new things the manuscript provide? It is recommended to summarize from two aspects: method and finding. How well does the new method/perspective works and what is the scientific value of the results in this study?
- Figure 1: Which method was used to calculate the slopes in the left panel? Which method was used to analyze the significance of trends? Which level?
- Figure 2: What does the fan shape in the map means?
- Figure 4: I cannot figure the fan shapes and their meaning clearly.
Citation: https://doi.org/10.5194/hess-2021-645-RC1 - AC1: 'Reply on RC1', Shenglian Guo, 01 Mar 2022
-
RC2: 'Comment on hess-2021-645', Anonymous Referee #2, 09 Feb 2022
The authors present a re-examination of the dry gets drier, and wet gets wetter paradigm over global land, based on terrestrial water storage estimates from different sources. They make use of GRACE reconstructions, global hydrological models, and land surface models, as well as CMIP6 models for the future perspective. They conclude that the DDWW paradigm is challenged both in the historical period but also in the future.
I think that the topic is interesting and fits well the journal, and the use of the complete terrestrial water storage for the analysis of the DDWW paradigm adds another perspective compared to previous studies. However, the paper currently lacks some important information and has a substantial methodological issue which requires major revision.
My main concerns are:
- The use of percentage of grid cells for the presentation of many of the results is not appropriate and hinders the proper interpretation. It’s necessary to present the corresponding numbers as percentage per land area (i.e., by weighing the grid boxes according to their effective km2 area) in order not to give excessive weight to higher latitudes. This will most likely have impacts on the overall conclusions of the paper.
- The choice of the eight CMIP6 models in not transparent. Why didn’t the authors choose a larger model ensemble based on the CMIP6 archive? Based on which criteria were these eight models selected?
- Also, given the large uncertainties between the CMIP6 models on the one hand, but also within the DATASET ensemble (cf. Fig. S8), the impact of the applied ensemble mean approach on the results should be discussed in more detail.
Specific comments:
Line 20: “and freshwater availability” instead of “and fresh availability”
Line 83/84: Which of the available meteorological forcings for these reconstructions did you consider (MSWEP, GSWP3 or ERA5)? Did you take the mean over the three forcings for each of the two calibrations?
Line 125: Based on which criteria did you select these 8 models?
Line 136: “to match the observed data” instead of “to match the observed results”
Line 144 (Equation 1): The dash in TWS – DSI could be confused with a "minus". I suggest changing it to an "_" or at least a short dash.
Line 152: “all the land area except for the Greenland and Antarctica”
Line 157: “CMIP6 archive” instead of “CMIP6 achieve”
Line 168-170: Why poorer performance when NRMSE is lower?
Line 180: “greater” instead of “slighter”? The fluctuations of CMIP6 are larger than the ones of DATASET (Fig. S4).
Line 180: “the effective bias correction performance” Why effective? CMIP6 deviates more from GRACE than DATASET.
Line 212: Here and throughout the results the use of percentage of grid cells is not appropriate and needs to be changed to percentage of land area for proper interpretation.
Figure 2: Nice plot, however quite crowded. The region names are often barely readable. You could just refer to the Supplementary Figure 1 for the definition and naming of the regions. The same applies to Figure 4.
Line 234: There's no stippling on these figures? Please revise the caption and also explain the meaning of the pie charts.
Line 235: Same title as for Section 3.1. I guess this is an oversight.
Line 257 and following: I assume these percentages are again based on the grid cells only, not based on the actual area?
Conclusion: The conclusions need to be extended. What's new compared to previous studies? What are the implications?
Citation: https://doi.org/10.5194/hess-2021-645-RC2 - AC2: 'Reply on RC2', Shenglian Guo, 01 Mar 2022
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