General comments:

This study uses the JULES model to simulate carbon fluxes across the Amazon basin. Five parameters for the tropical broadleaf evergreen tree plant functional type were optimized by comparing JULES simulation to data from four eddy covariance sites; an additional eddy covariance site was withheld for model testing. Then, those four sites were used to create a relationship between canopy height or leaf area index and the optimized parameter in order to make spatially-varying parameterization for JULES across the entire Amazon basin. Results demonstrate the parameter tuning improves NEE prediction at the eddy covariance sites, and suggest that while the Amazon as a whole acted as a carbon sink in 2021, parts of the region were a carbon source during that year.

Overall, the motivation for this study is compelling. The Amazon is climatically and floristically diverse, and efforts like this to characterize that diversity are needed. The approach taken here is novel, however, I have some concerns about generalizations drawn from the limited eddy covariance training data.

First, the authors acknowledge that the availability of eddy covariance data is limiting, but a more comprehensive assessment of how representative these sites are of the region would make it easier to see if/where extrapolations go beyond the training data. For example, because canopy height and LAI products are used to predict model parameters, it would be useful to know to what extent these four sites cover the range of variation seen across the Amazon.

Second, given that the parameter tuning at the eddy covariance sites did not reproduce observed seasonal flux patterns (stated in line 326 and shown in Figure 4), I was surprised that seasonal patterns were so widely highlighted in subsequent Amazon-wide simulations (Figures 6, 7, discussion lines 496-507). The earlier results did not seem to support that JULES is appropriate for investigating seasonal patterns.

Last, it was not clear to me whether the K83 validation exercise was conducted with in-situe meteorological data or the ERA5 meteorological data. It would be helpful to whether using ERA5 data decreases data-model agreement for all eddy covariance sites.

Specific comments:

• Lines 55-57: For a general audience, I think it would be helpful to describe JULES more broadly. For example, I see that JULES can be run either as a “big-leaf” or a “multi-layer” approach. From the supplement I see that the multi-layer implementation was used here, and I think a couple sentences about this should also be included in the main text.
• Lines 139-142: I am somewhat surprised that GEDI-based products were not used for this task, as GEDI’s sampling is now denser in this area (https://doi.org/10.3334/ORNLDAAC/2339). It would also be helpful to see what the Global Forest Canopy predictions are for the eddy covariate sites, perhaps in the supplement. It is somewhat hard to tell from Figure 1.
• Line 150: Please provide a summary of the basis of European Carbon Tracker estimates, as is done for FluxCom-X.
• Line 202: Please describe the scale factor for dark respiration.
• Lines 293-295: Why was only the area around the ATTO tower used—were data from other areas used for predictions for other areas?
• Line 363-364: The relationship with canopy height and alpha is poor. How important is this?

Technical corrections:

• Line 34: I think this reference should be (Brienen et al., 2015), but I don’t see the full citation in the reference section.
• Line 69: I suggest rewording “having as reference to Eddy-covariance towers in different regions of the Brazilian Amazon biome” to something like “using as references to Eddy-covariance towers in different regions of the Brazilian Amazon biome”
• Line 94: Perhaps “seasonally dry tropical forest” instead of “tropical wet and dry forest”
• Figure 1: I don’t see the black symbol for the validation tower?
• Line 326: Reword to “The seasonality of the carbon fluxes was not captured by any of the model simulations”
• Line 334: Reword to “direct relation”

Summary of work

This study uses five Amazon basin flux sites to derive relationships between two spatially well-observed variables (canopy height and LAI) and several JULES model parameters that are poorly observed spatially (tupp, alpha, f0, fd).  The parameters are selected from a longer list based on the sensitivity of modelled NEE to them.  One site was omitted from the fitting exercise and used as independent validation that the new functions produced parameters that improved the performance of modelled GPP, Reco and NEE at the site-level.  The study then uses the new functions in a gridded JULES run for the year 2021, effectively using a bespoke tropical broadleaf PFT in each gridbox.  This run produced a total Amazon basin NEE carbon sink of -1.34 PgC for 2021, but with notable spatial variation across the basin.

Main comments

• Overall I found this study to be an interesting way to use the limited flux data that are available for this region to address the problem of models like JULES relying on poorly constrained and abstract parameters in their formulations.  This work reminds me of efforts in recent years to base model parameters and parameterizations on observed vegetation traits rather than abstract variables.  I was slightly surprised to see such limited data produce such well behaved functions, which I think was likely down to the sensible methods the authors chose.
• The study only uses single years, with little discussion about why this was done or how useful it is (eg, how large is NEE interannual variability).  Presumably, these flux sites have data for more years, so why was this not used?
• The organisation of Section 2 is difficult to follow.  It would be clearer to put JULES model description (S2.4) before JULES model inputs and ancillary data (S2.2) and JULES model forcing data (S2.3).  The resulting description of the model the paper is very short (six sentences and no equations).  The authors should bring some relevant information out of the SI and into the main paper.  For example, the paragraph at L209 mentions several equations that should be in the main paper, particularly showing how maintenance respiration depends on canopy height, which isn't obvious from Eq 14 in the SI.
• The authors never mention model initialization or soil moisture spin-up: how was this done?  At some points is sounds like the model was run separately for individual months (eg L270) and a full year run was made after the shorter runs (eg L459 "After... the model was run for the entire year").  If so, why was this done and how was the model initialized?  The manuscript would benefit from a table describing the set-up for simulations run in this study (eg duration, forcing, parameter source).
• I'm disappointed to see no uncertainties reported in this paper, as they are really required for comparing points estimates.  For example, the authors omit the uncertainties when quoting from Chen et al (2024) and from the calculation of their headline NEE value of -1.34 PgC/y.  Similarly, I would expect to see uncertainty estimates on the fitted parameter values in Table 4.
• The authors only quote the annual total NEE for the run using new parameters (-1.34 PgC/y) and not for the runs with default or mean parameters.  This seems like an odd omission given that the default parameter run forms a baseline for comparison with other values (eg, TRENDY).  I feel that those annual results should be reported and discussed.
• Data and code availability: the results here depend on many JULES input options that it would not make sense to report in the manuscript, but which should be made available to readers.  The minimum I expect these days is for the input namelist files to be made available to readers via Zenodo or similar.
• Generally, the manuscript needs more work for clarity and readability, and typographical mistakes need fixing, particularly in the SI (eg, PFT changes to LFT, changing signs on NEE values, Sitch et al 2022 should be 2024).

Other comments

• L58 "The model includes up to nine land cover types containing five PFTs".  JULES can have any number of tiles/PFTs, but common configurations are five PFTs (HadGEM3), nine PFTs (Harper et al 2016), or 13 PFTs (UKESM1).  This line is also inconsistent with the model description in S2.4 (L165) that mentions nine PFTs being used in this study.
• L67-71: Description of the content of this manuscript could be improved.
• L97: "The tower K83 was used...".  Only later in the paper (L266) is it mentioned that K38 was chosen "at random".  The reason for choosing K83 should be mentioned here in the methods S2.1.
• Table 3: Four of the sites have sm_crit > sm_sat, which is very unusual and possibly inconsistent with other model assumptions.  With JULES sm_crit and sm_wilt are usually diagnosed at standard hydraulic pressures (-33 and -1500 kPa respectively) from sathh, b, sm_sat and the hydraulic equation being used.  Could the authors explain this apparent discrepancy?
• L137: Why did the authors choose to resample from 0.25 to 1.0 degree?  The former is a common resolution of land surface modelling (eg ISIMIP) and is inexpensive to compute for a limited region for single years.
• L148: "...used to assign a PFT for each model grid...": This description isn't clear.  I think from reading later in the paper that the LAI values were simply assigned to the BET-Tr PFT
• L183: "...fixed with the default values": The default values for the 21 parameter used in the sensitivity analysis should be reported.
• L185: "Grub's test": Isn't Grubb's test (note the spelling) used to detect outliers from random errors, such as spurious observations?  A model doesn't have random errors, so the authors should describe what conditions they are attempting to catch with this test.
• L193: Eq 1 for MAD: This is not the common definition of mean absolute deviation, which is SUM(ABS(ymax_i-ymin_i))/N.  The equation that's written describes a "mean root sum of square deviation", so it's not the RMSD either.  Is there a typo in this equation?
• L211: "...high sensitivity of NEE": Another reason for the sensitivity could be because the roughness length is also linearly related to canopy height, which will affect the carbon fluxes.  Can the authors rule out this as a significant factor in the sensitivity?
• L277: "C4 grass... canopy height": This is a confusing detail to include as no other information about C4 grass is included, and it makes it sound like the authors used the grass height to derive parameters from Eq 5, which I understand was only used for the BET-Tr PFT.  Could the authors clarify?
• L326: "...not captured by none...": Accidental double negative?
• L359-367: Is the comparison with C4 grasses in this paragraph relevant to the parameterization fits that are specifically for BET-Tr trees?  The fits are over tree heights between 27 and 36 m, so extrapolating down to a different vegetation class with heights of 0.15 m seems to me a poor comparison and not very meaningful.
• Table 5 and Figure 5: I note that the K83 parameter values are similar to the default values from Table 4 (possibly with the exception of alpha).  Presumably that means most of the improvement at K83 in Figure 5 is because of the canopy height value directly, which was prescribed from satellite data.  Could the authors elaborate on how much of the model improvement was because of the parameters in Table 5 rather than the prescribed values of canopy height and LAI?
• L418: "Table 2": Presumably the authors mean different table?
• L470: Figure 8: Couldn't "10^-12 Pg C" be simplified to "kg C"?  I understand the wish to keep it consistent with other uses of Pg C in the paper, but those are usually area totals, which are not easily compared with these per unit area values anyway.
• L492: "...water stress and nitrogen...": Perhaps more importantly, JULES accounts for factors such as radiation and humidity, which are strongly connected with the alpha an f0 parameters, respectively, that the authors show are influential.  Could the authors comment on this aspect too?
• L508: "-0.205 Pg C m-2 yr-1": This should be kg rather than Pg.  Also, isn't is unsurprising that the mean NEE for a region (from Lian et al) lies roughly in the middle of the range of extremes of spatially resolved values from this study?