Review of

Effects of a biased LAI data assimilation system on hydrological variables and carbon uptake over Europe

by Scherrer et al.

General comments:

This is a rather technical paper investigating the impact of preprocessing LAI observations before integrating them into the Noah-MP land surface model (LSM). Three data assimilation (DA) experiments are conducted over a Euro-Mediterranean domain from 2003 to 2019: “bias-blind”, “CDF”, “seasonal”. In the “bias-blind” experiment, LAI is assimilated as is. In the other experiments, LAI is rescaled in order to match the model climatology. The impact of the assimilation on GPP, ET, river discharge, and surface soil moisture is assessed using independent gridded datasets. In situ observations are used too. It is shown that assimilating the original LAI observations (bias-blind DA) has more impact, and a more positive impact overall than trying to precondition LAI observations to reduce the model bias (CDF and seasonal DA). So far, so good. Unfortunately, there is a serious logic issue and a serious scope issue.

• Logic: the Authors recommend dropping their most efficient bias-blind LAI DA option using specious theoretical arguments.
• Scope: both Abstract and Conclusion sections present results that are specific to the Noah-MP model and DA framework as if they were valid for all models and DA tools. Much different conclusions could have been obtained using other tools, and probably more logical conclusions. The title is also too general.

Basic hypotheses on the validation data used to perform the analysis of results are disputable, especially over semi-arid areas around the Mediterranean where the model tends to overestimate LAI. Over such areas, SIF is probably not proportional to GPP (the Authors assume that SIF is proportional to GPP) and the ESA-CCI soil moisture (SM) product has shortcomings (not mentioned in the current version of the paper).

The main problem I see in the Noah-MP DA system is that a partial (incomplete) analysis of the state variables of the soil-plant system is made. Root-zone soil moisture (RZSM) is not analyzed from the assimilation of LAI. Like LAI, RZSM changes relatively slowly. This is why RZSM needs to be analyzed together with LAI. Ignoring this tends to weaken the theoretical arguments used to criticize the bias-blind approach. The “negative effects” of the bias-blind approach are due to the incomplete use of the assimilated LAI data. Rescaling observations to the model range of values is relevant when units are different or when background model-dependent parameters affect the range of values. When model errors, model forcing errors, and model process uncertainties are responsible for the bias, the incorporation of the "true" observed values should improve the model simulations. In this case, artificially removing the bias is counterproductive and reduces the information content of the observations. This is particularly true for LAI. The exact value of this variable governs the biological regulation of soil moisture. Model LAI and RZSM biases can be due to model parameterization errors but also to biases in precipitation for example. ERA5 can present marked seasonal precipitation biases. The same difficulty would occur in irrigated areas since the Noah-MP model version used by the Authors does not represent irrigation. How can DA compensate for the impact of these biases if their influence on LAI is artificially removed? A solution is to analyze RZSM through the assimilation of the original LAI values. In the model you use, does LAI depend on RZSM? Is RZSM analyzed when you assimilate LAI? This is not clear in the present version of the manuscript and should be made clear.

Recommendation: major revisions or reject.

Particular comments:

- L. 80 (Noah-MP): More should be said here on the representation of phenology and LAI in the version of Noah-MP used by the Authors. For example, is the day-to-day change in LAI impacted by RZSM? If yes, RZSM could be analyzed through the assimilation of LAI. Is this done? If not, conclusions are only valid for this model and DA system and have no universal significance.

- L. 120 (CGLS LAI): this product has several versions/options. Which one is used in this study?

- L. 130-135: “land surface state” is too vague. What are the analyzed variables? Is RZSM analyzed? Please list the analyzed variables.

- L. 223: I guess that another reason for not using RMSD is that you do not simulate SIF. Correct? Please clarify.

- L. 231 (ESA-CCI SM): For which soil layer? Is it surface soil moisture? Please clarify.

- L. 267 (temperature): Do you mean accumulated precipitation?

- L. 283 (section 2.6): This is a bit obscure. Probably not that interesting for a majority of potential readers. I suggest moving this part and the corresponding results to a Supplement.

- L. 331 (Figure 4): I had a hard time understanding Fig. 4. Why are CDF and seasonal simulations missing? In the caption of Figure 4 I suggest replacing:

"SIF and "scaled OL" have been rescaled to have the same maximum as "bias-blind DA""

by

""scaled SIF" and "scaled OL" correspond to rescaled SIF observations and OL simulations presenting the same maximum as "bias-blind DA", respectively".

- L. 332 (deterioration of the agreement of SIF and GPP in regions with a large bias): I disagree. Regions with large bias correspond to semi-arid areas commonly affected by droughts. SIF is not linearly correlated to GPP in all conditions. In very dry conditions, this correlation disappears. See Martini et al. (2021) for example https://doi.org/10.1111/nph.17920

- L. 343 (sawtooth pattern): why should "sawtooth pattern" be considered as a problem? This is a sign that DA does its job of pulling the model closer to the observations, and that increasing the number of observations would improve the simulation.

- L. 349 (GLEAM ET): Can GLEAM ET be considered as a reference dataset? Why should it be better than the simulations performed by the authors?

- L. 361-362: These regions are also those for which microwave derived SM is more uncertain because of subsurface scattering in dry conditions (see Wagner et al. 2022, https://doi.org/10.1016/j.rse.2022.113025 )

- L. 394 (Figure 9): CDF LAI is much larger than both OL and observations from January to April. Seasonally rescaled LAI is much larger than both OL and observations from April to July 2016. How is this possible? Rescaled LAI should be somewhere between the OL and the observations. Correct?

- L. 399: replace "suppressing" by "reducing".

- L. 401 (Figure 10): Why is the number of curves/dots in Fig. 10a different from Fig 9a? This not logical.

- L. 404 (strongly decreases SM2): is this because RZSM is not analyzed?

- L. 409 (section 3.6): Move this section to a Supplement.

- L. 440-442: … and possible seasonal biases in ERA5 precipitation

- L. 494: For the sake of clarity, it should be written here that rescaling LAI observations has a negative impact on DA efficiency.

- L. 496: Are "standard assumptions" valid in a context where key variables (such as RZSM in this study) are not analyzed?

- L. 521: Do you mean that RZSM has no impact on the simulated LAI? This is far from the state of the art. Is there a more advanced version of Noah-MP able to correctly simulate LAI?

- L. 550: I completely disagree with this recommendation. I would instead recommend paying attention to the consistency between LAI and RZSM in the LSM, and to the “fitness for purpose” of the Noah-MP LSM.

This study explored the bias-blind and bias-aware LAI data assimilation approaches using the Noah-MP land surface model for Europe and evaluated its impact on the corresponding water, energy and carbon fluxes including GPP, ET, runoff, and soil moisture. The paper is well organized and made great efforts to discuss and reveal some of the critical problems in the data assimilation field. However, I have two specific concerns on the analysis and presentation of discussion/conclusion that I would very much like the authors to address/clarify. I provide below a list of comments for the authors to consider.

Abstract

1) I think both the abstract and conclusion do not fairly reflect the results and discussion sections. Benefits and pitfalls have been discussed for both bias-blind and bias-aware approach and the bias-blind approach leads to greater improvements for most of the variables and most of the metrics. However, the abstract/conclusion leads to the recommendation of the bias-aware approach, which is partly inconsistent with the message sent from the result and discussion section. I would recommend the authors to reconsider making the key points that can better and fairly reflect the content.

Introduction

2) L48-49: "It is possible that other processes (e.g., transpiration) are only represented well for a biased model climatology". If that turns out to be true, isn't it right for the wrong reason? I think such side effect should be fixed by improving the model physics instead of regarding as the weakness in the "bias-blind" DA approach.

Data & Methods

3) The spatial resolution of the simulation is coarse while there are evaluation reference datasets from in situ observations. The scale mismatch is not well considered in the metrics and comparisons in this paper, which may provide biased assessments. Would it be possible to conduct the simulation at a finer spatial resolution if most of the input datasets and the LAI observations are available at finer scale?

4) L102 - 105: What is the spatial resolution of these input datasets as well as the ERA5 forcing datasets? Please clarify in the text.

5) L106-108: I didn't quite understand why the model interprets the evergreen broadleaf forests as tropical rainforests. And what land cover type does the UMD data assign to for these locations? Are there any references that can justify the substitution of UMD data is more realistic?

6) L116: Is there a specific reason to use a spatial resolution of 0.25 degree? Why not bring it to a finer resolution since your CGLS LAI product is at such a fine resolution.

7) L125: Is there a particular reason not using the temporal interpolation method? If this can better deal with the sawtooth issue, why not apply it?

8) L163: For the seasonal scaling approach, how does the phase of seasonality look like between the LAI observation and the model simulation for the study domain? For instance, what does the spatial map of the peak month in LAI observation compared to the OL simulation? The vegetation scheme in Noah-MP has weakness even in reasonably estimating the magnitude and phase of the seasonal cycle of vegetation growth. It may introduce additional bias if rescaling observation based on the modelled climatology. Any comments on this?

9) L247: Considering the coarse spatial resolution of the model set up, the scale mismatch much be an outstanding issue when comparing the gridded soil moisture value to the in-situ observations. A simple nearest neighbor matching between ISMN stations and model grid might be troublesome. Have the authors considered the representativeness of the ISMN data for a model grid? Please comment on it and potentially discuss the uncertainties. I think simulation performed on a much finer scale might be better if one were to directly compare the in-situ observation to simulated values for a model grid.

10) L260 -262: Why not use the dam and irrigation specific datasets to mask out the basins that are heavily affected by these factors? I think directly masking out the basins based on the correlation threshold of 0.4 is biased because it is impossible to justify that such low correlation is surely due to the unmodeled processes. Such selective results may mislead audience in terms of the DA performance. I would recommend the authors reconsider the approach.

Results

11) L308 & L402 -403: I wonder if the case of Nile delta may not simply because of the lack of irrigation representation in the model. How does the LAI time series look like for the full study period compared to the time series of precipitation? Did you see consistently low LAI regardless of dry and wet years? I wonder if the representation of vegetation in response to water stress factor or the mismatch of soil types may play a role in the dynamic vegetation model that limits the growth of vegetation for this area? There are multiple reasons that the model may underestimate/overestimate vegetation growth just as the author discussed in section 4.4, I strongly recommend the authors take a closer look at the data and elaborate more on the discussion in terms of the factors at play. The analysis presented here does not justify that the lack of irrigation forcing is the main reason.

12) L315 - 317: This explains places where bias-blind DA leads to LAI decrease and soil moisture increase. I wonder how would the authors interpret places where bias-blind DA indicates an LAI increase, while there is no soil moisture decrease?

13) L324-325: The anomaly correlation of GPP improves a lot for places where LAI bias is large. Isn't it persuasive that the raw LAI observation plays an essential role in constraining the interannual changes in vegetation growth? The bias-aware approach may limit such benefit.

14) L334: It is not clear to me what area has been covered in the "southern part of the domain". I would suggest mark it out in Figure 3 or simply provide a mask map along with Figure 4 to highlight area of analysis.

15) ET comparison: Considering large uncertainty in ET products, would it be valuable to include a few other ET datasets for comparison besides GLEAM ET?

16) Figure 9: The seasonal cycle of the LAI observation would be very different if scaled by CDF or seasonal factors. I highly doubt whether such scaling reduces the value of using LAI observation to constrain the model performance. Scaling the observation to a model climatology that is further away from the truth is another form of bias. This might explain partly that the two bias-aware DA does not lead to better improvements for GPP as compared to the bias-blind DA.

17) L387: About the Majadas site: I'd suggest informing where the site is located in Figure 5.

18) L375-378: Repeated sentence. And I think such sawtooth pattern could be taken care of if enables the temporal interpolation to the observations.

19) Section 3.4: Again I have concerns in the scale mismatch in the modeling space vs. the observation. Without consider such effect, the conclusion may be biased. Would it be possible to conduct a sensitivity analysis regarding the spatial resolution of the model? Alternatively, is it possible to collect more in situ observation sites that can better jointly represent the condition for a 0.25 degree grid cell?

20) L405-408: Good point! How does the other two bias-aware DA perform in this case?

21) L426-427: True but the seasonal scaling may introduce additional bias to the scaled observations if the modelled climatology is further away from the ground truth. I think this is probably a larger flaw as compared to the bias-blind DA approach because at least the later remains the true temporal variation of what has been observed.

22) Section 4.2 - 4.3: I agree that if large bias exists then the bias-blind DA may lead to misuse of Kalman filter; but I also think that the rescaling of observation based on a biased model is a big issue, it may create even bigger problem if the seasonality is deteriorated. I think the benefit and pitfalls for both approaches should be elaborated and discussed in a more comprehensive manner before it gets to section 4.4.