The author presents the potential TROLL 4 model performance in Amazon forest sites, this manuscript is clear while still need some improvement before I recommend this to be published. Here are my detailed comments:

Line 103: write typo: each tree belongs to a species

Line 104: what's the meaning of recruitment, some explanations

Line 119: why you select six parameters for calibration? These parameters are sensitive to what? Any sensitivity analysis?

Line 137: I disagree with the parameter values you used in this model, for example the leaf minimum conductance from literature. I read this paper and found that this value depends on the spices why you set it as 5? Also please state why giving the values to other parameter? This is very important!!

Line 138 why other parameters are assumed site independent.

Lines 164-165: Again, if these parameters are not used in your model previously at the same ecosystem, i think you should calibrate them instead of directly using the literature values.

Line 224: i don't think its an exhaustive search, more parameter sampling is needed

Line 229: I'm confused why convert SIF to GPP for validation there are several GPP data can be used

Please state the statistical indicators of consistency between simulations and observations in figures 1 to 10

If the results are statistical significant or not in Figure 11 and 12

Lines 473-475: I don't think so for basal area, I noticed there are obvious deviations between your model simulations and field observations.

General Comments: I think the discussion part is too long and didn't combine with your results closely. Reorganize this part is recommended.

This manuscript evaluates the new TROLL 4.0 model at two Amazon sites with trait, census, flux tower, and remote sensing data. Specifically, the study evaluates forest structure with census and lidar data, composition with species abundance, phenology with litter and LAI seasonality, and carbon and water fluxes with eddy covariance tower.

Calibrating and evaluating the species abundance and tropical phenology are very novel to me and it is good to see that GPP and ET seasonality generally matches the tower observations. Please see below for my comments.

Overall, it is very surprising to me that the study does not evaluate demographics (growth/mortality) of the model at the two sites. Given TROLL 4.0 is an individual-level model to predict forest community and ecosystem dynamics, it is easy and critical to benchmark growth (e.g. growth-size relationship) and mortality, and biomass changes. I believe both sites have multiple census data for such comparison?

In addition, given the novelty of the version is to better represent plant water stress and phenology, I would recommend to conduct a simulation at a drier site. For example, in the ED2.2 GMD paper (Longo et al. 2019), both Paracou and Brasilia are tested to evaluate model behavior and performance under different degrees of water stress.

Some more detailed comments

L 44, 'canopy height distribution' is a vague term to me. How exactly is this distribution calculated? Based on the manuscript, I believe leaf/plant area density is more accurate?

L 48-49 it would be helpful to report the magnitude of overestimation in addition to RMSEP, which includes both difference in mean and variability.

L 119-120 related to my comments for the Part I manuscript, it would be helpful to show model sensitivity to these global parameters.

L 126, what are the physiological interpretation of a_T,o, b_T,o and detla_o? How are they related to different phenological strategies? This is related to my confusion in the phenological module in the companion manuscript.

Line 133, Table 1, is Soil Organic Content/Bulk Density/CEC/pH used in TROLL 4.0?

Line 150-153, I like the efforts to capture inter-specific variation in height allometry. I wonder what's the correlation between a_h and h_lim with other functional traits. One editorial comment, superscript is not shown properly in the equation and sentences.

Line 162, Fig. A1 shows that over 2000+ traits are imputed based on 100+ trait data. I am a little concerned about the disproportionally large fraction of imputed data...

Line 173-175, A minor comment, ERA5 rainfall data is likely not trustworthy at daily scale in the tropics. CHIRPS data might have better performance in my personal experience.

Line 210-213, This calibration approach assumes the forest dynamics is in equilibrium. I am fine with this assumption since we don't have much better alternatives when disturbance history is unknown. Meanwhile, this means the calibrated m includes the average disturbance rate of each site (i.e. it is not just ageing and biology).

 

Line 216, this equation basically assumes equal weights between (1) AGB, (2) total stem density and (3) stem density in each size class, which seems arbitrary to me. Why not check the best trait combinations for each metric and see whether these 'posterior' trait combinations overlap?

Line 246, same as above

Line 315-316, the m values makes sense to me (2% baseline mortality + 1.5~2% disturbance rate). The big difference between a_CR and b_CR is interesting... These values mean the crown radius is *200%* higher for a 10cm tree at Tapajos compared with Paracou and the crown radius difference increases with tree size... Is this supported by canopy observations at the two sites? Given airborne lidar can identify crowns, does crown size show such big difference between the two sites?

Line 323: Fig. 1, given the large size-related variation in abundance, I suggest log-transform abundance before calculating correlations otherwise the correlation will definitely be high even if models might have large relative biases for big trees, which are important for ecosystem-level carbon/water fluxes.

Line 335-336, this (and Fig. 3) is likely because the model does not have light-driven plasticity. See my comments to the companion manuscript.

Line 339 Fig. 2, Given the model underestimate small trees in both basal area and abundance, I wonder why the model has good match in understory density (fraction of voxels with leaves/branches) when compared with lidar data? I would expect the model has lower density than observations... Or could the lidar data is problematic for the understory, especially at 1m resolution due to occlusion? 

Line 355-356, species rank comparison is cool and interesting. I wonder whether the species in the observation and simulation are paired? i.e., is the most abundant species in the model also the most abundant in the observation? I am interested in a scatter plot of species rank in model vs observations. If they are close to a 1:1 line, that means the trait-based approach and 3D simulation can explain a large part of biodiversity.

Line 382, litter mismatch might be because leaf aging is not considered

Line 410, Fig. 8. It seems there is no consensus of leaf age cohort seasonality between observations. How should we interpret this modeling results, which are constrained by the Wu et al. PhenoCam data ight? 

Line 425, Fig. 9. Could it be that the model is not sensitive enough to VPD (based on Fig. 11) If so, the model might overestimate GPP more in the midday/afternoon. It would be helpful to compare the dry/wet season average diurnal cycle of GPP between tower data and TROLL simulations.

Line 441, Fig. 10, I am curious about the evaporation/transpiration partitioning as well as soil moisture dynamics in the model. These are new components of the model and they should be reported and discussed and they are important to understand the process-level accuracy of the model.

Line 457, Fig. 11, given the high collinearity between VPD and temperature and PAR, why not using multivariate regression or other techniques to separate partial sensitivities? The gross correlation/regression is not really informative (e.g. GPP increases with VPD) A good reference is the analysis in Bloomfield et al. 2023. Based on the current analysis, VPD limitation in the model is too weak. I wonder whether it is because of the usage of Penman-Monteith in calculating and constraining stomatal processes. It will be helpful to plot and analyze key intermediate variables in photosynthesis-stomata process (e.g. gs, VPDs, Ci, etc) to diagnose the problem.

L. 480-482. I disagree, I think it is mainly due to lack of trait plasticity (check Xu et al. 2017 and Lamour et al. 2023)

Xu, X., Medvigy, D., Joseph Wright, S., Kitajima, K., Wu, J., Albert, L. P., Martins, G. A., Saleska, S. R., & Pacala, S. W. (2017). Variations of leaf longevity in tropical moist forests predicted by a trait-driven carbon optimality model. Ecology Letters, 20(9), 1097–1106. https://doi.org/10.1111/ele.12804

Lamour, J., Davidson, K.J., Ely, K.S., Le Moguédec, G., Anderson, J.A., Li, Q., Calderón, O., Koven, C.D., Wright, S.J., Walker, A.P., Serbin, S.P. and Rogers, A. (2023), The effect of the vertical gradients of photosynthetic parameters on the CO2 assimilation and transpiration of a Panamanian tropical forest. New Phytol, 238: 2345-2362. https://doi.org/10.1111/nph.18901

Line 499-504: If a homogeneous seed rain is likely to be the main cause of the model-data mismatch in species composition (and this mismatch is quite large), then it might be helpful to include some sensitivity tests to see the effect of a more heterogeneous seed rain.

Line 520-522. If this is true, why the model-data discrepancy only occurs at one site? Are there not any Cecropia at Tapajos?

Line 526. You can check the anomaly in trait/species abundance against seed trait to evaluate this hypothesis, if this is the main reason, there should be a correlation between the model-data mismatch with certain seed traits.

Line 592-94. With the current analysis, it is hard to tell whether the daily responses are realistic or not. Partial sensitivity comparison is critical

Line 620-636: in addition to the overestimate of GPP per se, the model also consistently overestimated the sensitivity of GPP to environmental factors, particularly in Tapajos. What are the potential causes of this overestimate? 

This paper presented a comprehensive model calibration and evaluation of a new model TROLL 4.0.  It is a thorough evaluation of model performance and the paper is well written.  I do have a few concerns on the paper. The authors used a sequential calibration scheme. Namely, it first calibrates the aboveground biomass and density. The best ensemble member is then used to calibrate the phenology leaf parameters. One concern on this scheme is that the interactions among carbon parameters and phenology leaf parameters could interfere with each other and thus the sequentially calibrated parameters might not give the best results. Second, it is not clear to me how the authors capture the uncertainties in data. The authors only used the best fit from ensembles: however, there are always uncertainties in data and there is ‘never’ a single realization of parameter values that could give the ‘best’ prediction. It would be better to use an ensemble of parameter values that best fit into the range of plausible range from observations. Third, it is not clear to me if the authors consider the potential correlation between parameters. The orthogonal design assumes independence among parameters. Based on this assumption, is it possible  that the calibrated parameter sets could be unrealistic? 

Please see below some specific comments:

TROLL 4.0: representing water and carbon fluxes, leaf phenology,  and intraspecific trait variation in a mixed-species individual-based forest dynamics model – Part 2: Model evaluation for two Amazonian sites 

Line 101: What is the abbreviation for TROLL, which has a meaning of ‘ a person who intentionally antagonizes others online by posting inflammatory, irrelevant, or offensive comments or other disruptive content’. This does not resonate with me well for a model name. 

Line 126: − 0.01 × ℎ − 𝑏𝑇,0, not sure the meaning of this term. It would be better to explain it without referring to the companion paper. 

Line 141: why species should have a maximum diameter at breast height and set it as 95th quantile of species diameter from observed data?  It is contradictory based on the definition and use of the 95th quantile of species diameter. My understanding of the system is that there could be a maximum height, but trees could continue to get ‘fatter’.

Line 150: can you give some scientific background on the equation without going to the modeling companion paper?

Line 174: For Tapajos, rainfall data from FLUXNET 2015 is not reliable due to issues with rain gauges and the authors used rainfall data from the ERA5-Land reanalysis dataset. I understand the strategy here but it will be nice to know how much the coarse resolution ERA5 data create a difference compared to FLUXNET 2015 data based on site Paracou, as it might be useful to see how much difference between calibrated parameters across these two sites are from climate driver data source differences.

Line 198: Might be good to point out the time to reach equilibrium in the model and how the climate driver is cycled.