Assessing the large-scale plant–water relations in  the humid, subtropical Pearl River basin of China

Wang, Hailong; Duan, Kai; Liu, Bingjun; Chen, Xiaohong

doi:https://doi.org/10.5194/hess-25-4741-2021

Articles | Volume 25, issue 9

https://doi.org/10.5194/hess-25-4741-2021

© Author(s) 2021. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/hess-25-4741-2021

© Author(s) 2021. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 25, issue 9

Research article

|

31 Aug 2021

Research article |

| 31 Aug 2021

Assessing the large-scale plant–water relations in the humid, subtropical Pearl River basin of China

Hailong Wang, Kai Duan, Bingjun Liu, and Xiaohong Chen

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Final revised paper (published on 31 Aug 2021)
Supplement to the final revised paper
Preprint (discussion started on 29 Jun 2020)

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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SC1: 'Comments on paper by Hailong Wang et al.', Qiang Zhang, 17 Jul 2020
- AC1: 'Reply to comments by SC1', Hailong Wang, 17 Sep 2020
RC1: 'Referee review', Anonymous Referee #1, 13 Aug 2020
- AC2: 'Reply to comments by RC1', Hailong Wang, 17 Sep 2020
RC2: 'review report', Anonymous Referee #2, 19 Aug 2020
- AC3: 'Reply to comments by RC2', Hailong Wang, 17 Sep 2020

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

ED: Reconsider after major revisions (further review by editor and referees) (23 Oct 2020) by Patricia Saco

AR by Mario Ebel on behalf of the Authors (26 Nov 2020) Author's response

ED: Referee Nomination & Report Request started (17 Dec 2020) by Patricia Saco

RR by Anonymous Referee #1 (11 Jan 2021)

Suggestions for revision or reasons for rejection

The quality of the revision is not satisfactory. I recommend major revision rather than rejection mainly because of the relatively strong yearly correlation between NDVI and GRACE TWS (R2 ~ 0.59), which if carefully analyzed has the potential to lead to informative conclusion regarding regional ecohydrology in a humid area. Claiming water limitation in such a humid area needs caution. The Pearl River basin features strong rainfall that is generally higher than the potential evapotranspiration (i.e., rainfall outweighs water demand) and the river runoff is large, too. The claim about water limitation therefore needs justification and explanation. When and where exactly does water limitation come from, is there a period in each year when the water supply cannot meet the demand of plant growth? The authors have multiple datasets (both water supply and demand) available to answer these questions.

I suggest the authors use EVI and SIF both of which are easily available. The authors’ argument is problematic as most of the significant trends in NDVI occur in the central portion of the study domain where notable forest cover exists (Fig. 1c & 4b). Using EVI can avoid the saturation issue associated with NDVI. In addition, the adopted GPP products may not represent well the soil moisture constraint. Using SIF will provide an observational metric that represents GPP.

Line 20. The authors conclude that “the degree of water restriction on vegetation was higher than that of water consumption by vegetation even in this rain-abundant region.” It is still unclear to me how water restriction (which is quantified here by correlation) can be directly compared with plant water consumption (which is often quantified by transpiration).

Line 118-119. The description about GRACE uncertainty is not accurate. The leakage error depends on the specific basin of interest and needs to be calculated case by case, and I don’t think they are released by the processing centers. Wiese et al 2016 documented the recommended procedure to estimate the leakage error (although the values provided in that paper were for RL05). How did the authors quantify the leakage error for the Pearl River basin? Also note that the mascon uncertainties provided by JPL are uncertainties associated with each mascon estimate (not the uncertainty associated with a single 0.5 degree pixel). Based on the short description provided by the authors, it is difficult to assess whether the GRACE uncertainty is treated properly.

Line 175-176 and Fig 2a-c. As I pointed out in my previous comments, the TWSA depends on the choice of the reference period. The common practice is to use the entire analyzed period to represent the “normal” condition. I suggest the authors do the same because using the 2004-2009 as the reference period is not the best effort practice when longer baseline exists, unless the authors have specific reasons to believe the 2004-2009 period better represents the normal condition. This would potentially affect Fig 2a-c in the manuscript and also the classification of dry and wet years in Figs 9 and 10. The authors’ response to my original comment stressed that the reference period wouldn’t affect the trend analysis, which was obvious and not relevant to my comment.

Figure 7. It is not appropriate to calculate correlation with TWS at pixel level as the TWS resolution is intrinsically coarse (~ 3 degree) and going beyond the mascon resolution will rely on scaling factors that are not based on pure observations. This should be either noted or avoided. The basin scale results shown in Fig 6 are more appropriate.

Line 226. As I asked in my previous comment, please clarify if the seasonality has been removed when calculating correlation using the monthly time series. Note that to quantify water limitation, the seasonality should be removed from the monthly time series.

Figure 8. Is each point corresponding to a pixel? Note that this is not appropriate for TWS. See my comment as above.

Line 188-190. It is difficult to infer causality between two variables simply based on temporal lag. The drop in NDVI occurs after Nov. Is this period also part of the growing season? Is there any energy limitation? When the NDVI starts to decline, does water demand outweigh water supply?

Figure 9c-d. The range of the right y-axis is way too large for AI and NDVI. -0.5 to 0.5 is likely more appropriate.

Line 240. If the difference in NDVI between the dry and wet years is mainly attributed to the difference in the non-growing season, does that mean the growing season NDVI does not show significant difference between dry and wet years? That would indicate that water is not a limiting factor to growth in the study domain.

Line 246-247. That seems contradictory to the notion of water limitation.

Line 248 vs. Fig 10. Is it “monthly climatological mean” (Line 248) or is it “monthly anomalies” (Fig 10 caption)?

Section 4.1 As I pointed out in the original comment, this section should go to the Method (some of them should go to introduction, e.g., Line 259-261, 272-280). The discussion should focus on the scientific hypothesis that the authors aim to address. I believe the other reviewer pointed out the same issue as I did.

Line 314. The reason that I pointed out Tong et al., 2018 in the original comment is to remind the authors that there is an active human intervention in the study (with respect to land use and land cover change), which would very likely complicate the explanation of plant-water relation – in this case, the increase in growth is partly attributed to human management rather than plant response to water supply changes.

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RR by Anonymous Referee #2 (17 Jan 2021)

ED: Publish subject to revisions (further review by editor and referees) (10 Feb 2021) by Patricia Saco

AR by Hailong Wang on behalf of the Authors (14 Apr 2021) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (11 May 2021) by Patricia Saco

RR by Anonymous Referee #1 (07 Jun 2021)

Suggestions for revision or reasons for rejection

The manuscript has improved but the following two issues need to be addressed.

- The authors argue that they do not intend to estimate leakage errors following Wiese et al., 2016, because they primarily used TWSA to infer water availability changes instead of the absolute values.
This logic is flawed. Method from Wiese et al 2016 has been widely used to quantify leakage error related to TWS variability and trend. To my knowledge most studies adopt their method to address leakage error associated with trends. For this study, the region to the north of the study domain is known to have experienced sustained increase in TWS linked to reservoir filling, which makes it necessary to evaluate if any of those signals have leaked into the analyzed domain.

- The authors justify their use of 2004-2009 baseline using the following argument: (a) the 2004-2009 baseline is “suggested by JPL,” (b) calculating anomalies using the entire period as the new baseline is “more of the anomaly of anomaly,” (c) the entire period is not significantly longer than the 2004-2009 period, and (d) the newly calculated mean annual anomaly is close to zero.
I want to first stress that for the purpose of identifying anomalous dry or wet conditions, the suitability of a certain choice of baseline should be evaluated based on how normal the water conditions are during that baseline period. In practice longer baseline is often chosen to average out anomalies across different time scales.

The authors did not evaluate how normal the water conditions were during the 2004-2009 period but instead provided four problematic arguments. (a) The 2004-2009 baseline is indeed used by JPL since earlier releases of the GRACE data but claiming that the 2004-2009 baseline is suggested by JPL would be of a different nature. In fact, JPL has provided guidelines regarding how to adopt a different baseline on the same link provided by the authors in the rebuttal letter. (b) Removing the mean over the entire period do not provide results that correspond to an anomaly of anomaly; they are simply anomalies referenced to a new baseline period. (c) The duration of the entire period is more than twice as that of the 2004-2009 period. (d) This sounds peculiar. Shifting the baseline will increase the magnitude of some of the anomalies while reducing the rest.

Finally, if the authors insist using the shorter period as the baseline, they should clarify how well that shorter period represents the normal water condition in the analyze domain.

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RR by Anonymous Referee #2 (11 Jun 2021)

ED: Publish subject to minor revisions (review by editor) (30 Jun 2021) by Patricia Saco

AR by Hailong Wang on behalf of the Authors (21 Jul 2021) Author's response Author's tracked changes Manuscript

ED: Publish as is (08 Aug 2021) by Patricia Saco

Short summary

Using remote sensing and reanalysis data, we examined the relationships between vegetation development and water resource availability in a humid subtropical basin. We found overall increases in total water storage and surface greenness and vegetation production, and the changes were particularly profound in cropland-dominated regions. Correlation analysis implies water availability leads the variations in greenness and production, and irrigation may improve production during dry periods.