the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 17 Jan 2022
Stochastic Generation of Multisite Streamflow for Future Water Resources Vulnerability Assessments: Application over South Korea
Abstract. Stochastically generated streamflow time series are increasingly used for various water management and hazard assessment applications. The sequences provide realizations, preserving the temporal and spatial characteristics observed in the historic data. However, the simulations are further desirable to represent nonstationarity to account for past and future interannual oscillations. This study proposes an approach for stochastically generating future multisite daily streamflow to evaluate future water security conditioned on a national-wide relationship between annual daily maximum temperature and annual streamflow. The approach is attractive since it can avoid limitations and uncertainties introduced during realization and bias correction processes for climate model-based rainfall information. Alternatively, this approach relies on high projection skills of temperature variability. While the approach is developed by coupling annual and daily simulations, it includes (1) a wavelet decomposition-based autoregressive simulation to impose the signal of regional climate covariate; (2) clustering-based spatial pattern recognition and simulation; and (3) block bootstrapping and vine copula-based simulation for multisite streamflow simulation. The approach is applied as an example to multiple basins in South Korea. Results show that the generated sequences properly preserve many of the historical characteristics across basins. For future streamflow simulations, significant decreases in streamflow are projected, likely resulting in nontrivial impacts on regional water security. Finally, we conclude with a discussion of possible improvements to further refine the approach.
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Interactive discussion
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RC1: 'Comment on hess-2021-576', Anonymous Referee #1, 18 Jan 2022
A small note for everyone before we get to the nitty-gritty. This paper was submitted to JoH previously and got a rejection. I was the one who requested it. As luck (let’s call it luck) would have it, the paper was submitted to HESS and came to me. Again. What are chances? Are there so few people in this field? Anyway, I dug through my previous reviews and compared this manuscript to the one that was submitted to JoH. To my surprise they are exactly the same. I had heard about authors submitting to other journals upon rejection but never experienced it firsthand. I must say the feeling is not nice mainly because all the effort that I put the last time was a waste. Nobody cares. What am I to do? Submitting my old review is what I do. It’s only fair. Cheers.
General comments:
I regret to say that I am very unsatisfied with the contents of this paper. The various approaches and assumptions used here are not backed up by proper evidence. Vine-copula construction is very flimsy. Using temperature as a covariate to predict discharge is not tested properly before used for simulations. The results show considerable bias almost everywhere. Finally, I do not find the results of this study to be of any importance for this journal given how much is done already on the effects of climate change on the future. Regardless, the constructions used here are unacceptable, in my opinion. The data points are too few. Complex spatial correlations require more than a regional average and a transition matrix for representing them.
I was going for major revisions but given the results of this study, even after the revisions, we won’t be seeing anything useful. I mean, we have been hearing about the effects of climate change for what? The past 30 years? Tell us something that we don’t know. Hence, a rejection. My comments will seem harsh. That is because I felt that I was wasting time writing this review. Seriously, much more effort should be put in to preparing a good manuscript. The whole time it seemed like methods from here and there were stitched together without giving any thought to the outputs and their meaning. I (almost) never reject a paper but this one took the cake (again).
Specific comments:
L180: Just out of curiosity, do we know for sure that components can be modeled using an AR process? Shouldn’t there be a test of some sorts? AR processes are useful if the dependence is normally distributed i.e., follows a Gaussian copula. And I have yet to see a natural variable that is anything remotely close to Gaussian.
L191-194: I don’t know about Ahn (2020), but daily discharges have long memories i.e., more than 1 day. In my experience, mesoscale catchments can have memories of more than 1 week (around two weeks is the norm and the annual and seasonal cycles are always there). This should be taken in to account. BUT, if first order is justified then please show it. Citing another study as a justification (in this case) is a bit weak in my opinion. It could be that the decomposed series have no/short memories but we don’t know this for sure.
L242-277: All of this would be correct if calibration and validation on independent datasets showed good results. Which are not mentioned this far in the text. According to Joe (2014), we can do a range of complex dependencies, but how do you know if the construction is correct? How many copulas were tried here?
L333-336: Is the South-Korean climate similar to that of Australia? Based on Fig. 3 alone, I won’t call it a strong relationship. For example, for a scaled Tmax of zero we can have a range from about 500 to 1200 mm. Quite a range, I think. And this is the best case?
L402-406: For Node (1,2), there is just one value that is mostly influencing the trend. I would hold the judgment that the lows have significantly changed for this node. Also, the sample size is extremely small to make the call that flows are trending downward. Do we know for sure that the stream flows are free from anthropogenic influences? I have heard that South Korea is very active in water-resources-related projects.
L408-420: Dear Lord. Fig. 6 looks bad. Pardon the nit-picking but the standard deviation, skewness and maxima are way off. What was the point of fitting the distribution when the simulations never ever went out of the observed bounds anyway? It would be okay if the simulations extended to both sides of the 1-1 line but always being on the same side represents bias. And a big one in this case. How could one say that “overall, the results describe that the stochastic simulations properly represent…including daily average”. The daily average looks acceptable but the higher-order statistics are off. The phrase “although there are some underestimations” took a whole new meaning here. The simulations underestimate the skewness massively and yes, there is bias. That has to be corrected.
L422-431: Coming to Fig. 7, the skewness seems to be doing its own thing here as it is always the same regardless of the basin considered. Except for the mean, the rest looks pretty biased too. The lower figure is acceptable.
L433-443: Based on what is considered acceptable in this paper, I don’t know what to believe now. Fig 8. shows consistent bias. Some of the cross-correlations look pretty good but many have bias in Fig. S1.
L445-458: Why is the difference of medians considered? Discharge is (to a large degree) exponentially distributed that means that the median will be a very low value as compared to the rest that make up the larger sum of the runoff. I don’t know what to make of this figure. The authors could at least consider total volume error. As an example, consider rainfall. Median rainfall is going to be very close to zero but that is not something that brings river flow, does it? It is the upper tail. Same thing for discharge but to a lesser degree. Compare the Lorenz curves of discharges, maybe?
L460-476: Regarding Fig. 10 (right), the chosen sample is way too small to make a solid judgment. Also, there is no proper explanation about why the partial model did not show a significant change? Regardless, the sample is too small.
L528-529: The approach used here is not compared to any other method, then how can one say if it is good or bad? How do we know that a simpler approach may have sufficed in the first place? Or any other existing one? I wonder now, how do you see non-stationarity in a series? I know about the long-term waves but how big are those compared to the rest of the time series? I didn’t see any figure for that. It was just assumed that non-stationarity is there. It is always there, I guess.
L530: I don’t find the simulation results to be “proper” at all.
L535-552: The new approach proposed is tested here on one region only. The results are not impressive by any means and no comparisons or validations are provided that show a decisive improvement. Just claiming that such an approach is not used before by combining various methods from here and there is rather weak. If I had a dollar for every time I heard this justification, I would have a few hundred dollars. Using such a short period of observation as input is not enough to account for non-stationarity. There are wet and dry years.
L554-568: Ah, shift the burden of validation to the future generations. Let them deal with the matter of the approach being right or wrong. But hey, at least we have a paper. When you already know the short coming that the Gamma distribution leads to an underestimation then why wasn’t a better one searched for? You could try the Pareto distribution. Nothing too complicated to test. The results of fitted distributions are also not shown anywhere.
L570-590: Instead of using higher temporal resolution data, I am more concerned about the length of the time period. 23 or 8 years is too short to predict long-term future.
Citation: https://doi.org/10.5194/hess-2021-576-RC1 -
RC2: 'Comment on hess-2021-576', Anonymous Referee #2, 02 Feb 2022
Review for manuscript “Stochastic generation of multisite streamflow for future water resources vulnerability assessments: application over South Korea”
Authors: Sukwang Ji and Kuk-Hyun Ahn
Journal: Hydrology and Earth System Sciences
Summary
The authors introduce a model for the simulation of multi-site streamflow under non-stationary conditions. The model relies on a three-step approach which combines an annual with a daily simulation approach. The approach is evaluated for 12 catchments in South Korea and applied to assess reservoir system performance under future temperature scenarios.
General remarks
The study introduces a simulation approach for the simulation of multi-site steamflow under non-stationary conditions using a temperature covariate to simulate annual streamflow. However, I think that the paper lacks a clear problem statement and research questions and that the method description needs to more clearly introduce the individual modeling steps, several among which seem unclear to me. In addition, the model seems to not capture extreme events very well, which needs to be fixed.
Major points
- Title: a vulnerability assessment does not seem to be part of the analysis and I therefore suggest to rephrase the title.
- The introduction introduces the new modelling approach but it is unclear what actual research gap the study addresses. It is important to clearly state the actual research questions.
- The first part of the introduction is a bit heavy on highlighting the disadvantages of GCMs even though streamflow is usually simulated using downscaled data as an input to a hydrological model. I think that l.62-69 and l.77-81 are not needed and that instead a short statement about different uncertainty sources involved in hydrological modeling of future streamflow is sufficient (see e.g. Clark et al. 2016; https://link.springer.com/content/pdf/10.1007/s40641-016-0034-x.pdf) before highlighting the need for computationally more efficient alternatives such as stochastic modelling. Instead, a more comprehensive introduction to different existing modelling approaches and their advantages/disadvantages should be provided.
- The methods section needs a lot of clarification, as many steps remain unclear to me. For example:
- how are the regions defined for averaging (l.172)
- how exactly is the covariate computed (l.180)?
- how was the order of the AR model determined (l. 192)?
- how exactly are the different SOM nodes selected (are these the same as classes, l.200-209)?
- how do you ensure that the temporal dependence between spatial patterns is retained (l. 211-213)?
- why six spatial patterns (l. 222)
- what do you bootstrap from (l. 226)?
- it remains unclear why the copula is needed (l. 243-254). To extrapolate, would it not be sufficient to use an extreme value distribution?
- what is a ‘pivot’ variable (l.260)?
- the coupling step (l. 280-284) also needs clarification.
- how does this bias correction procedure work (l.322)? - The model evaluation shows that extreme values are not well captured (Figure 6). This problem might be resolved by using a 3-parameter extreme value distribution instead of the Gamma distribution to model streamflow. Statements such as the one on l.415-416 or the one on l. 423 need to acknowledge the lack of performance in terms of extreme flows.
- The reservoir performance analysis (l. 505-512) comes as a surprise. This aim is neither mentioned in the introduction nor is the approach described in the methods section. What is the goal behind this part of the analysis?
- Conclusions: Based on the results presented in Figure 6, I disagree with the statement: ‘Second, compared to climate model-based projections, our simulated streamflows properly reproduce the primary characteristics observed in historical records’. There are two problems with this statement: first, the paper does not show any results for climate model-based projections and second, the model performance is rather bad in terms of extreme events. The discussion section should critically reflect this last issue.
- A discussion section should discuss the generalizability of the approach to other regions and larger datasets as well as the limitations of the approach. That is the fact that extremes are not simulated very well.
- Careful language editing is recommended to improve the reading flow.
- The figure design could be improved. Figure 1: indicate different workflow steps and better establish link to text. Figure 4: unit of legend missing, Figure 5: legend missing, Figure 6: legend missing, Figure 7: legends missing for upper panels, Figure 8: legend missing, Figure 11: legend missing.
- Figure 12: only include this analysis if problem is part of introduction and related to one of the research questions to be phrased.
Minor points
l. 128-131: statement is not necessarily true in all climate zones.
l. 306-308: rather belongs to introduction
l. 565: ‘precipitation’ -> ‘discharge’?Citation: https://doi.org/10.5194/hess-2021-576-RC2
Interactive discussion
Status: closed
-
RC1: 'Comment on hess-2021-576', Anonymous Referee #1, 18 Jan 2022
A small note for everyone before we get to the nitty-gritty. This paper was submitted to JoH previously and got a rejection. I was the one who requested it. As luck (let’s call it luck) would have it, the paper was submitted to HESS and came to me. Again. What are chances? Are there so few people in this field? Anyway, I dug through my previous reviews and compared this manuscript to the one that was submitted to JoH. To my surprise they are exactly the same. I had heard about authors submitting to other journals upon rejection but never experienced it firsthand. I must say the feeling is not nice mainly because all the effort that I put the last time was a waste. Nobody cares. What am I to do? Submitting my old review is what I do. It’s only fair. Cheers.
General comments:
I regret to say that I am very unsatisfied with the contents of this paper. The various approaches and assumptions used here are not backed up by proper evidence. Vine-copula construction is very flimsy. Using temperature as a covariate to predict discharge is not tested properly before used for simulations. The results show considerable bias almost everywhere. Finally, I do not find the results of this study to be of any importance for this journal given how much is done already on the effects of climate change on the future. Regardless, the constructions used here are unacceptable, in my opinion. The data points are too few. Complex spatial correlations require more than a regional average and a transition matrix for representing them.
I was going for major revisions but given the results of this study, even after the revisions, we won’t be seeing anything useful. I mean, we have been hearing about the effects of climate change for what? The past 30 years? Tell us something that we don’t know. Hence, a rejection. My comments will seem harsh. That is because I felt that I was wasting time writing this review. Seriously, much more effort should be put in to preparing a good manuscript. The whole time it seemed like methods from here and there were stitched together without giving any thought to the outputs and their meaning. I (almost) never reject a paper but this one took the cake (again).
Specific comments:
L180: Just out of curiosity, do we know for sure that components can be modeled using an AR process? Shouldn’t there be a test of some sorts? AR processes are useful if the dependence is normally distributed i.e., follows a Gaussian copula. And I have yet to see a natural variable that is anything remotely close to Gaussian.
L191-194: I don’t know about Ahn (2020), but daily discharges have long memories i.e., more than 1 day. In my experience, mesoscale catchments can have memories of more than 1 week (around two weeks is the norm and the annual and seasonal cycles are always there). This should be taken in to account. BUT, if first order is justified then please show it. Citing another study as a justification (in this case) is a bit weak in my opinion. It could be that the decomposed series have no/short memories but we don’t know this for sure.
L242-277: All of this would be correct if calibration and validation on independent datasets showed good results. Which are not mentioned this far in the text. According to Joe (2014), we can do a range of complex dependencies, but how do you know if the construction is correct? How many copulas were tried here?
L333-336: Is the South-Korean climate similar to that of Australia? Based on Fig. 3 alone, I won’t call it a strong relationship. For example, for a scaled Tmax of zero we can have a range from about 500 to 1200 mm. Quite a range, I think. And this is the best case?
L402-406: For Node (1,2), there is just one value that is mostly influencing the trend. I would hold the judgment that the lows have significantly changed for this node. Also, the sample size is extremely small to make the call that flows are trending downward. Do we know for sure that the stream flows are free from anthropogenic influences? I have heard that South Korea is very active in water-resources-related projects.
L408-420: Dear Lord. Fig. 6 looks bad. Pardon the nit-picking but the standard deviation, skewness and maxima are way off. What was the point of fitting the distribution when the simulations never ever went out of the observed bounds anyway? It would be okay if the simulations extended to both sides of the 1-1 line but always being on the same side represents bias. And a big one in this case. How could one say that “overall, the results describe that the stochastic simulations properly represent…including daily average”. The daily average looks acceptable but the higher-order statistics are off. The phrase “although there are some underestimations” took a whole new meaning here. The simulations underestimate the skewness massively and yes, there is bias. That has to be corrected.
L422-431: Coming to Fig. 7, the skewness seems to be doing its own thing here as it is always the same regardless of the basin considered. Except for the mean, the rest looks pretty biased too. The lower figure is acceptable.
L433-443: Based on what is considered acceptable in this paper, I don’t know what to believe now. Fig 8. shows consistent bias. Some of the cross-correlations look pretty good but many have bias in Fig. S1.
L445-458: Why is the difference of medians considered? Discharge is (to a large degree) exponentially distributed that means that the median will be a very low value as compared to the rest that make up the larger sum of the runoff. I don’t know what to make of this figure. The authors could at least consider total volume error. As an example, consider rainfall. Median rainfall is going to be very close to zero but that is not something that brings river flow, does it? It is the upper tail. Same thing for discharge but to a lesser degree. Compare the Lorenz curves of discharges, maybe?
L460-476: Regarding Fig. 10 (right), the chosen sample is way too small to make a solid judgment. Also, there is no proper explanation about why the partial model did not show a significant change? Regardless, the sample is too small.
L528-529: The approach used here is not compared to any other method, then how can one say if it is good or bad? How do we know that a simpler approach may have sufficed in the first place? Or any other existing one? I wonder now, how do you see non-stationarity in a series? I know about the long-term waves but how big are those compared to the rest of the time series? I didn’t see any figure for that. It was just assumed that non-stationarity is there. It is always there, I guess.
L530: I don’t find the simulation results to be “proper” at all.
L535-552: The new approach proposed is tested here on one region only. The results are not impressive by any means and no comparisons or validations are provided that show a decisive improvement. Just claiming that such an approach is not used before by combining various methods from here and there is rather weak. If I had a dollar for every time I heard this justification, I would have a few hundred dollars. Using such a short period of observation as input is not enough to account for non-stationarity. There are wet and dry years.
L554-568: Ah, shift the burden of validation to the future generations. Let them deal with the matter of the approach being right or wrong. But hey, at least we have a paper. When you already know the short coming that the Gamma distribution leads to an underestimation then why wasn’t a better one searched for? You could try the Pareto distribution. Nothing too complicated to test. The results of fitted distributions are also not shown anywhere.
L570-590: Instead of using higher temporal resolution data, I am more concerned about the length of the time period. 23 or 8 years is too short to predict long-term future.
Citation: https://doi.org/10.5194/hess-2021-576-RC1 -
RC2: 'Comment on hess-2021-576', Anonymous Referee #2, 02 Feb 2022
Review for manuscript “Stochastic generation of multisite streamflow for future water resources vulnerability assessments: application over South Korea”
Authors: Sukwang Ji and Kuk-Hyun Ahn
Journal: Hydrology and Earth System Sciences
Summary
The authors introduce a model for the simulation of multi-site streamflow under non-stationary conditions. The model relies on a three-step approach which combines an annual with a daily simulation approach. The approach is evaluated for 12 catchments in South Korea and applied to assess reservoir system performance under future temperature scenarios.
General remarks
The study introduces a simulation approach for the simulation of multi-site steamflow under non-stationary conditions using a temperature covariate to simulate annual streamflow. However, I think that the paper lacks a clear problem statement and research questions and that the method description needs to more clearly introduce the individual modeling steps, several among which seem unclear to me. In addition, the model seems to not capture extreme events very well, which needs to be fixed.
Major points
- Title: a vulnerability assessment does not seem to be part of the analysis and I therefore suggest to rephrase the title.
- The introduction introduces the new modelling approach but it is unclear what actual research gap the study addresses. It is important to clearly state the actual research questions.
- The first part of the introduction is a bit heavy on highlighting the disadvantages of GCMs even though streamflow is usually simulated using downscaled data as an input to a hydrological model. I think that l.62-69 and l.77-81 are not needed and that instead a short statement about different uncertainty sources involved in hydrological modeling of future streamflow is sufficient (see e.g. Clark et al. 2016; https://link.springer.com/content/pdf/10.1007/s40641-016-0034-x.pdf) before highlighting the need for computationally more efficient alternatives such as stochastic modelling. Instead, a more comprehensive introduction to different existing modelling approaches and their advantages/disadvantages should be provided.
- The methods section needs a lot of clarification, as many steps remain unclear to me. For example:
- how are the regions defined for averaging (l.172)
- how exactly is the covariate computed (l.180)?
- how was the order of the AR model determined (l. 192)?
- how exactly are the different SOM nodes selected (are these the same as classes, l.200-209)?
- how do you ensure that the temporal dependence between spatial patterns is retained (l. 211-213)?
- why six spatial patterns (l. 222)
- what do you bootstrap from (l. 226)?
- it remains unclear why the copula is needed (l. 243-254). To extrapolate, would it not be sufficient to use an extreme value distribution?
- what is a ‘pivot’ variable (l.260)?
- the coupling step (l. 280-284) also needs clarification.
- how does this bias correction procedure work (l.322)? - The model evaluation shows that extreme values are not well captured (Figure 6). This problem might be resolved by using a 3-parameter extreme value distribution instead of the Gamma distribution to model streamflow. Statements such as the one on l.415-416 or the one on l. 423 need to acknowledge the lack of performance in terms of extreme flows.
- The reservoir performance analysis (l. 505-512) comes as a surprise. This aim is neither mentioned in the introduction nor is the approach described in the methods section. What is the goal behind this part of the analysis?
- Conclusions: Based on the results presented in Figure 6, I disagree with the statement: ‘Second, compared to climate model-based projections, our simulated streamflows properly reproduce the primary characteristics observed in historical records’. There are two problems with this statement: first, the paper does not show any results for climate model-based projections and second, the model performance is rather bad in terms of extreme events. The discussion section should critically reflect this last issue.
- A discussion section should discuss the generalizability of the approach to other regions and larger datasets as well as the limitations of the approach. That is the fact that extremes are not simulated very well.
- Careful language editing is recommended to improve the reading flow.
- The figure design could be improved. Figure 1: indicate different workflow steps and better establish link to text. Figure 4: unit of legend missing, Figure 5: legend missing, Figure 6: legend missing, Figure 7: legends missing for upper panels, Figure 8: legend missing, Figure 11: legend missing.
- Figure 12: only include this analysis if problem is part of introduction and related to one of the research questions to be phrased.
Minor points
l. 128-131: statement is not necessarily true in all climate zones.
l. 306-308: rather belongs to introduction
l. 565: ‘precipitation’ -> ‘discharge’?Citation: https://doi.org/10.5194/hess-2021-576-RC2
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Sukwang Ji
Kuk-Hyun Ahn
This preprint has been withdrawn.
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(1642 KB) - Metadata XML
-
Supplement
(790 KB) - BibTeX
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