|Second review of Wang et al.|
"Long-term relative decline in evapotranspiration with increasing runoff on fractional land surfaces"
The paper has overall improved as the authors have addressed some of
the concerns raised by me and the other reviewer.
However, at the same time important issues remain unresolved:
As pointed out in main comment (1) of my previous review,
the validation of the inferred time series against independent data such as the Fluxnet-MTE product,
and observed streamflow is not convincing.
The differences are not satisfactorily explained by the authors in their rebuttal.
Figure S11 clearly shows diverging trends in the tropics, and the author's explanation about
"different models, forcing data and time scales" does not provide evidence why their product
(and trends therein) is more reliable than the Fluxnet-MTE reference product.
Moreover, the different runoff trends between Figures 4c and S14 cannot be entirely explained with
human influence on the observed streamflow, I think, as even the large-scale patterns
differ clearly, for example in Europe and Australia.
Given that the differences between the products here are partly so remarkable I feel that
they need to be understood better in order to illustrate the reliability of the newly derived dataset.
As pointed out in main comment (2) of my previous review,
different time periods are considered during which trends from the data derived in this study are determined versus the trends from the CMIP5 data. The authors acknowledge that matching time periods would be "better, but difficult to achieve", and state that this might not be so important as the evaluation
focuses on directions of change rather than the actual magnitude. I do not agree with this.
Even the sign of change may be different in different time periods, as for example introduced
by decreasing and later increasing radiation within the global dimming and brightening periods.
Further, decadal climate variability can introduce varying trends over time.
Therefore, I think that with using different time periods, the comparison of trends between the
data derived in this study and the CMPI5 data is not meaningful.
Even though I requested this in main comment (4) of my previous review,
the authors did not explain why they chose to employ artificial neural networks
over alternative machine learning approaches.
Even though I mentioned this in main comment (5) of my previous review,
there are still many small language errors throughout the manuscript,
for example in lines 71, 77, 131, 155, 159, 196/197, 205, 224, and 249.
One additional issue caught my attention this time, sorry for realizing this only now.
The ANN model is trained with target data from flux tower sites which typically cover 5-15 years.
I doubt that CO2 in such short time periods would change sufficiently to lead to an emerging
influence of CO2 fertilization on ET or EF.
Therefore I think the reasoning of the CO2 fertilization effect on stomatal conductance
potentially explaining differences in the partitioning between ET and runoff over time,
which can be found throughout the manuscript, is not valid.
I do not wish to remain anonymous - René Orth.
lines 66-67: not clear what is meant with "boundary layer budget" and "non-linearity"
lines 70-74: The authors state that existing datasets are somewhat biased towards the (flux) data availability
which is largely concentrated in the northern hemisphere. This is true, but it is also true
for the data derived in this study even if the weather stations are more distributed,
because the model training is confined to the flux tower sites, as for the existing products.
lines 156-157: Why was exactly this combination of input variables chosen while other combinations
showed even better performance in Table S1, for example after including precipitation?
lines 165-166: What do you mean with initial tests and how did that influence the final decision?
How was this formula applied to guide these decisions?
lines 204-213: Why are there different p-value thresholds used here?
line 220: Why >12000?
lines 220-225: How are these trends computed? As linear trends? Over which time period?
line 241: Why are you using the 11-year old Fluxnet-MTE product from Jung et al. 2010
rather than the more recent Fluxcom product from Jung et al. 2019?
line 298: Which CMPI5 models are used in the considered ensemble, and how were their simulations aggregated?
Figures 3-7: How did you determine the area of the Sahara?
Jung, M., et al. The FLUXCOM ensemble of global land-atmosphere energy fluxes, Scientific Data 6, 74 (2019).
Jung, M., et al. Recent decline in the global land evapotranspiration trend due to limited moisture supply. Nature 467, 951–954 (2010).