Review of Zhao et al.

This manuscript proposes a new approach to estimating Fractional Vegetation Cover (FVC) across China using the MultiVI algorithm, which integrates multiple remote sensing data. The results generally have good accuracy and spatial coherence, validated through field measurements. The manuscript is well written, and the methodology is well presented. The only major issue is that this dataset is for the year 2014.

General comments:

Limitation of single-year data. How representative can the use of single-year data (in 2014) be for the interannual variability in vegetation and soil properties? Why didn’t the authors expand the methods to more recent years?

Specific comments:

L27: should briefly introduce the reasons for using these three regions (e.g. for validation purposes), otherwise the readers will be confused as to why only compare to these regions.

L30: ‘free access’ to ‘publicly available’

L30: should add what year is the data for

L93: remove ‘flexibly’

L113: need more details about the choice of 55 and 60 degrees.

L272: A moving window of 330x330m might oversimplify the spatial heterogeneity, how does it affect accuracy?

Figure 6: I suggest changing the colors by using darker colors to indicate larger differences (e.g. dark blue for -0.3~-0.2, light blue for -0.1~0)

L335: why compare the mean (of MultiVI) with the median (NDVI)? Why not mean with mean or median with median?

L348: add what ‘the bias’ represents (it is already in Figure 8 legend, better to have it in the main text)

Figure 9: there seem to be seasonal patterns for some sites by eye, and it is worth further exploration.

L457: usually invalid values should be marked as nan, not 0 to avoid confusion with actual 0 values.

Review of ESSD-2024535 Normalized Difference Vegetation Index Maps of Pure Pixels over China’s mainland for Estimation of Fractional Vegetation Cover, by Zhao and others.

The authors have addressed an important issue in the use of NDVI for monitoring foliage cover.  The end members of the linear transform from NDVI to cover need to be specified and this is commonly ignored.  A robust method for routinely identifying these end members across diverse ecosystem types is needed, and is provided in this work. The Vv and Vs data generated will be valuable.  The methods for generating the 500 m version of these variables are sound; the methods for downscaling these to 30 m need improvement.  Further, the methods used by the authors for validating these surfaces are not robust and also need to be revised.  I recommend a major revision.

A significant concern I have is with the downscaling of Vv and Vs.  The method for calculating 500 m Vs and Vv are sound and the 500 m data are an excellent product.  The logic of the downscaling step, and uncertainty about how this downscaling was performed, significantly weakens the quality of the 30 m product.  The downscaling introduces the assumption that Vv and Vs are the same within a given land cover type (line 249).  This assumption rarely holds true as soil types (the main driver of Vs if one ignores the effects of soil moisture) can vary within single landcover types, or, conversely, different landcovers can share the same soil type.  This assumption opens the authors up to the same criticism that they have applied to traditional statistical methods (line 395).

Further, it is difficult to understand how this downscaling was performed as the methods do not currently describe a proper unmixing method.  Equation 8 apportions Vs (or Vv) solely according to landcover type proportion, regardless of which landcover type occupies that proportion.  As currently described, for a hypothetical 500 m pixel with a calculated Vs value and which has 10% area of forest and 10% bare ground (in the surrounding 3x3 window), the method would apportion the same Vs value to the forest and bare pixels.  Can the authors better explain the method used?

I have two significant concerns about the data used to validate/assess their products.  The first is the rather unsophisticated way the authors have applied the ‘statistical’ method.  They have only used 3 years of data to derive statistics about Vv and Vs.  What if that period was continually wet, or continually dry, or was fire affected?  The derived statistics cannot be assumed to be representative of that site.  The authors have the ability to use a much longer time series and should do so.  Also, the authors have applied the method with the expectation that it will work everywhere, which it is known not to.  The method cannot return reliable Vs values in heavily vegetated areas nor Vv in sparsely vegetated areas.  While the authors acknowledge this in the conclusion, this knowledge hasn’t been applied in their design of the derivation of the statistically derived Vs Vv data.  And so it is no surprise that this product performs poorly in these respective situations.  This led the authors to conclude that (line 442)

Traditional statistical methods are impractical to achieve this goal due to their reliance on pure pixels.

This is not universally true.  More sophisticated implementations of the statistical method can be quite effective.  Can the authors at least provide some more context to the reader about the simplicity of their approach relative to alternative approaches?  Or maybe the authors could restrict the application of their statistical method to where it is known to be valid and hence avoid reporting values where it quite rightly doesn’t work.  None of this will change the excellent result that the multi-VI method is superior.

The second concern I have about the data used to validate/assess their products relates to how the field data at Heihe were derived.  In scaling the field observations from 10 x 10 m to 90 x 90 m, the authors have effectively turned the field observations into a modelled product with its own errors.  I would expect that a direct comparison between the 10 m field data and the 30 m Vs Vv data would provide a more robust comparison than upscaling the field data.

One last comment is that some recent work is of direct relevance to this Mutil-VI paper (Donohue and Renzullo, 2025; https://doi.org/10.1071/BT24060).  I expect this would have been published after the current manuscript’s submission; however, it may be of interest to the authors.  In making this statement I should also disclose that this is my paper (it’s Randall Donohue here).

Lines 42 and 49.  The VI-based mixture model referred by the authors is specifically the NDVI-based mixture model.  It is not a generic model that can use any vegetation index.

Line 173.  Doesn’t look like the UAV data were used for anything at the Hebei site.  Do they need to be mentioned at all?

Line 200.  It is a misconception that the NDVI has a saturation effect.  When compared to foliage cover (which it what is has been shown to be linearly related to) there is no ‘saturation’.  This misconception arises when NDVI is incorrectly expected to bear some relationship with leaf area.

Line 229.  Calling the values derived from a single year (2014) the ‘historical’ values is counterintuitive.  They are not representative of site history. 

Line 229.  How much does using statistics derived from only one year of data (2014) limit the accuracy of the method when applied to other years?  I would think it important to derive these ‘historical’ values from as long a time series as possible (which would be 23 or so years for MODIS).