Mastropierro et al made the use of CMIP6 to investigate Amazon land carbon sink’s uncertainties and underpinning drivers. This is a really important topic and I think they can potentially make useful contributions to the community. Nevertheless, I have several critical concerns about the methods before I can recommend for publications.

1. Section 2.2.2. Have you removed the effects of CO2 fertilization on carbon? If not, the equations are the combined effects of eCO2 and climate impact.
2. The use of water availability: soil moisture is more relevant for plant carbon uptake than precipitation. Why the authors did not choose mrso?
3. To my surprise, why pr is negatively correlated with NEP. A drought causes more NEP, which is not feasible.

Small comments:

-  Lines 54 -57/61-63:  Water availability control on interannual variability of tropical biomes is large and could increase.

Ref:

Humphrey, V. et al. Sensitivity of atmospheric CO2 growth rate to observed changes in terrestrial water storage. Nature 560, 628-631 (2018). https://doi.org:10.1038/s41586-018-0424-4

Liu, L. et al. Increasingly negative tropical water–interannual CO2 growth rate coupling. Nature 618, 755-760 (2023). https://doi.org:10.1038/s41586-023-06056-x

- Lines 177-180. Shall we say this? The units are not same compared to NEP uncertainty. Maybe a normalized quantification of uncentainty is fair for comparisons, like spread divided by mean.

Summary:

The authors examine drivers of uncertainty in and divergence among CMIP6 model projections of Amazon carbon cycling. First, they separate the C cycle changes driven by ENSO from those driven by mean-state climate change. Then, they use regression approaches to separate the effects of mean-state changes resulting from different climate drivers, including precipitation, temperature, solar radiation, and latent heat flux. They find that changes in ENSO account for relatively little change in the Amazon C cycle relative to mean-state climate changes, which generally (but not exclusively) enhanced net ecosystem production (NEP) in the ssp585 scenario. Using the empirical approach to disentangle the various drivers of mean-state change, they further claim that most of the diversity among the models is attributable to differences in representation of C cycle responses to surface energy fluxes (solar radiation and latent heat flux in particular). Overall, while the article presents some interesting results, I think there are some major flaws that ought to be addressed.

General comments:

1) The biggest flaw, in my opinion, comes from the attribution of mean state change to specific drivers, especially the claim that inter-model differences in latent heat flux are driving differences in C cycling. Latent heat flux is not an exogenous variable but is instead itself driven by things like solar radiation, soil moisture, temperature and humidity as well as by plant responses to climate forcings. The authors use an empirical regression approach (Eqn. 4) to separate out the constituent drivers of NEP (including latent heat flux), but what if latent heat flux is not directly driving NEP but is instead being forced by the same drivers as NEP? In this case, both NEP and latent heat flux would be highly correlated with each other despite neither one “causing” the variation in the other but instead both just responding to a common external driver. Eqn. 4 would thus misattribute change in NEP to change in latent heat flux. I think this is very likely at least partly the case because NEP and latent heat flux are both affected by stomatal conductance (which in the models is affected by vegetation characteristics, soil moisture, VPD, etc.): all else being equal, higher conductance would increase both GPP and transpiration, and thus both NEP and latent heat flux, without latent heat flux itself causing any change in NEP. While latent heat flux could indeed cause (or at least reinforce) change in NEP through land-atmosphere feedbacks, I think the regression modeling approach used here, and thus the conclusions of the paper, are likely mistaking a correlation between latent heat flux and NEP via their common drivers for a causal driver of NEP by latent heat flux.

2) Related to this, elevated CO2 is almost certainly a major factor driving both change in NEP and inter-model divergence in NEP trends, but CO2 fertilization is not examined at all in this manuscript. Instead, any CO2-related changes in NEP are likely being “lumped in” with any other climate drivers that have long-term trends (like temperature). The authors claim that temperature trends positively force NEP (e.g. in fig. 5), but to me, this seems more likely to be a CO2 effect than a temperature effect. If I recall correctly (and I could definitely be wrong about this), most other studies have found that temperature on its own should *negatively*, not positively, force Amazon NEP, especially in an extreme scenario like ssp585. Because the temperature trends closely track CO2 trends in the future projections, this to me seems very likely to be a misattribution of CO2 effects to temperature effects. Previous studies (e.g. Huntzinger et al. 2017) have also shown that much of the divergence among land surface model predictions of NEP arises from differences in vegetation responses to elevated CO2.

3) A much smaller point, but for the ENSO analysis, the authors use a December-February averaging period of the Niño3.4 index but don’t really justify this choice aside from saying that ENSO anomalies tend to peak in boreal winter (which is true). However, this does not necessarily imply that ENSO effects on surface climate and vegetation peak in boreal winter. Previous studies (e.g. the Zhu et al. 2017 and Zhang et al. 2019 papers already cited in the manuscript) have shown that the lags between ENSO anomalies and vegetation productivity can vary pretty substantially over the land surface and don’t necessarily correspond to that DJF period. (Another more specific question I had about this was why Niño3.4 anomalies that already represented 5-month averages [line 124] were then further averaged to DJF.)

4) The authors mention that they obtained soil moisture (mrso) from the CMIP6 models, but they used precipitation in Eqn. 4. Both vegetation and soil microbial communities are likely responding more directly to soil moisture than to precipitation, so why not use soil moisture in Eqn. 4 instead of precipitation?

5) In general, I was a little confused about section 3.4 and the corresponding methods section (2.2.3). There seem to be some inconsistencies in how the regression coefficients were described in the text and how they appear in the figures. For example, line 332 says that the models show a negative influence of temperature, but doesn’t Fig. 5 show a *positive* influence of temperature? I also found the precipitation response confusing… the authors variously describe precipitation as being negatively correlated with NEP (lines 341-342) on the one hand, but also say that places with larger negative trends in precipitation have lower NEPs (lines 319-320). In order for a negative trend in precipitation to result in lower NEP, that would mean that NEP and precipitation would have to be *positively* (not negatively) correlated with each other, right? I’m also struggling to figure out how precipitation would be negatively correlated with NEP (or have a negative regression coefficient with NEP, as in fig. 5 and 6) in the Amazon.

Specific comments:

Line 69: is “given” supposed to say “driven”?

Line 75: Another ENSO property that could influence the Amazon carbon cycle is the spatial location of SST anomalies in the tropical Pacific (i.e., central Pacific vs. eastern Pacific ENSO events). Recent frequencies of central Pacific ENSO events are considerably above the norm based on paleoclimate reconstructions (Freund et al., 2019) and have been shown to have distinct impacts on GPP and NEP in many regions, especially in the Amazon (Dannenberg et al., 2021). Further, some studies have shown that central Pacific El Niños are projected to be more frequent under 21^st century warming (e.g., Shin et al., 2022), though some of this might result from biases in CMIP6 model simulations of equatorial zonal flows (Wang & Lin, 2023). Still, might be worth noting that this (along with increases in ENSO amplitude and vegetation sensitivity to ENSO) is another potential source of future change in the Amazon-ENSO connection that is not examined here since the Niño3.4 region mixes the two (but is mostly centered in the central Pacific). To be clear, I’m not necessarily suggesting that the authors redo analyses to explicitly examine the CP vs. EP ENSO effect on Amazon C cycling, though it could be really interesting at least for future work!

Line 92: Could using a variable number of realizations from each model cause some model overrepresentation that would bias results? For example, if Model A has five realizations but Model B only has one, then Model A would be weighted five times more than Model B in the presentation of inter-model results. For this reason, some previous studies have only used one realization per model (Diffenbaugh et al. 2018).

Lines 128-129: 10^th and 90^th percentiles seem like pretty strict definitions. That would result in only 6 events per 60 year period. Would 20^th and 80^th percentiles be a better choice? I don’t feel strongly about this though, so I’ll leave that to the authors’ discretion.

Line 148: I’m not sure I understand what the authors mean by “uniquely standardized”… could you explain a little bit more how MLR-trend and MLR-iav were obtained?

Lines 160-164: I’m confused about equations 5-8. What are the alphas in these equations? Are those alphas different for each of equations 5-8 (in other words, removing the effect of Nino3.4 on each variable individually)? If so, the nomenclature is kind of confusing.

Lines 165-169: Did the authors examine the predictive skill of their model? It could have significant regression coefficients without being a particularly skillful model. I think it would be good to do so using data withheld from calibration of equation 4.

Line 228: It’s not clear to me what “stronger inhibition of the tropical teleconnection pathway” means.

Lines 228-232: Just to clarify, is this based on a comparison of the historical ESM SST simulations to those actually observed with measurements?

Lines 274-278: This last paragraph of section 3.3 seems to give pretty short shrift to the results. Can you expand?

Lines 282-284: I’d suggest being more explicit here. What does “satisfactory” mean? What skill thresholds need to be met for it to be satisfactory? Was the assessment of model skill based on data withheld from model training?

Fig. 1 (also worth checking the other figures as well): some of the text (especially in the legend) is very hard to read.

Fig. 2: Is it possible to include confidence intervals on these?

The authors explored the inter-model diversity of vegetation productivity simulated under CMIP6 historical and SSP585 scenarios, and found out that the uncertainty in Amazon vegetation productivity in CMIP6 projections is driven by the dominant role of local mean-state climate changes and the minor role of El Nino-Southern Oscillation (ENSO). In particular, the surface energy balance components (shortwave incoming radiation & latent heat fluxes) are the main cause of divergence actress ESM responses. They also pointed out the need for phosphorus limitation.

Major comments:

1. Novelty

This paper investigates the drivers of inter-model diversity, with a focus on local mean climate and ENSO, introducing novelty in its findings. In particular, this paper goes beyond coarse climate but examines specific climate drivers and their effects on inter-model variability. 

However, some statements appear misleading, implying that it’s a new discovery, when it might not be. For example, in the result section (3.1), the authors state that “Inter-model uncertainty is much higher than intra-model uncertainty, originated by ESMs internal climate variability” (Line 176) and “This shows that uncertainty in NEP does not solely stem from photosynthesis or respiration; instead, it arises from inconsistencies and limitations in how models represent both processes” (Line 197). In fact, Heavens et al (2013) already explained that ESM predictions differ because 1) models do not agree on the details of how climate will change; and 2) land carbon models are differently sensitive to the four processes: a. varied vegetation growth in fixing carbon; b. climate change driving changes in precipitation, which drives changes in vegetation growth; c. warming climate increasing microbial respiration; and d. carbon fixation slowing as vegetation deplete soil nutrients.  I think it is ok to include those in the result section. However, the authors need to make it clear that these findings are not novel and align with previous studies to provide the necessary context.

2. Data, Method and Results

I have major concerns in this part. The method section lacks clarity/validity and the results are not consistent.

First, the way to define El Nino and La Nina might not be convincing.  The authors defined El Niño and La Niña events using the 90th and 10th percentiles of the DJF averaged Nino3.4 index time series. Citations or evidence were missing to prove why they chose 90/10th percentiles as thresholds. They claimed that they detrended the average Nino 3.4 index over Dec-Feb, by means of a 1st order polynomial and normalized (without citation and proof as well). At least they need to clarify how “the means of a 1st order polynomial” were defined and which normalization was applied (eg., Z-score normalization, or Min-max scaling). If Z-score normalization was used, I would recommend using standard deviations as thresholds to define El Niño and La Niña events, instead of percentiles.

Second, the separation of mean-state climate and ENSO effects might be confusing. According to Power and Delage 2018 (the method the authors applied), El Nino effects on climates are defined as 𝜟𝑬𝑵=(𝛅𝑬𝑵𝒔𝒔𝒑)-(𝛅𝑬𝑵𝒉𝒊𝒔𝒕)=(Essp − Nssp)-(Ehist-Nhist), where ESSP denotes climates averaged over the El Nino events under SSP scenarios and Nssp denotes the climates averaged over the neutral years under SSP scenarios.  Notably, the definition in Power and Delage (2018) is about the effects on climate, rather than effects on NEP. The author should make it clear that the effects of ENSO on climate differ from its effects on NEP. They need explain how they applied 𝜟𝑬𝑵 to get the impacts of El Nino on NEP(Fig. 3&4). If they directly used the idea of 𝜟𝑬𝑵 to calculate effects on NEP— where ESSP and Nssp denoted NEP averaged over the El Nino events and over neutral years under SSP scenarios, respectively,  𝚫𝑴𝑺 (=𝑁𝑠𝑠𝑝 − 𝑁ℎ𝑖𝑠𝑡) would be the long-term trend effects, including CO2 fertilization. The inclusion of CO2 fertilization effects can largely lead to misinterpretation of the results and may explain conflicted findings presented in the paper.

For example, Fig. 4A demonstrates that both climate and La Niña have positive impacts on NEP, which seems counterintuitive. Rising temperatures and water deficits are expected to increase stress on vegetation, and La Niña, often associated with flooding, should exhibit some negative effects.

Third, the method section 2.2.3 (Effects of climatic drivers) is very confusing. In this section, the authors used detrended climate anomalies to disentangle their effects on NEP from ENSO. But in the result section 3.4.1, they claimed that it is the long-term changes effects on NEP by using method 2.2.3. I have two questions here: 1) what are the different purposes between methods of 2.2.2 and 2.2.3? It appears to me that the two method sections are unrelated to each other, especially in the result presentations. If detrending climates in method section 2.2.3 is to remove the long-term trend effects (eg., partially remove CO2 fertilization), why did the authors use the method section 2.2.2, including CO2 fertilization?   2) Why did the authors apply a simple linear regression model in 2.2.3? To my understanding, El Niño events tend to interact with climate in impacting NEP, suggesting additive non-linear negative effects once climate tipping thresholds are exceeded. Although the linear model in the paper used the residuals of the single-climate regression model against ENSO, there is still lack of consideration of their interactive, non-linear effects. In this case, the method section 2.23 may not have fully eliminated the CO2 fertilization effects and may have overlooked the interactive effects between ENSO and climate, which can cause conflicted results as well. 

For instance, Fig. 5 shows that precipitation has negative effects while temperature has positive effects, which seems counterintuitive. Surprisingly, Fig. 7 and 8 both show temperature has negative effects, which conflicted with the results in Fig. 5. It seems that all these figures come from the method section 2.2.3.

I hope the authors can take these conflicted results carefully and report them with consistency if revision is invited.

3. Clarity

The writing in the method section can be improved and please ensure consistency between the methods and results.

Specific comments:

Figs. 5-8 Please explain what the labels represent in captions. There is no explanation in the paper for “res”.

Line 176 “Inter-model uncertainty is much higher than intra-model uncertainty”. There is no intra-model uncertainty reported in the paper. Please add the missing information.

Line 197-200 Please rephrase these sentences.

Reference:

Heavens, Nicholas G., Daniel S. Ward, and M. M. Natalie. "Studying and projecting climate change with earth system models." Nature Education Knowledge 4, no. 5 (2013): 4.

Power, S.B. and Delage, F.P., 2018. El Niño–Southern Oscillation and associated climatic conditions around the world during the latter half of the twenty-first century. Journal of Climate, 31(15), pp.6189-6207.

Zhu, Z., Piao, S., Myneni, R.B., Huang, M., Zeng, Z., Canadell, J.G., Ciais, P., Sitch, S., Friedlingstein, P., Arneth, A. and Cao, C., 2016. Greening of the Earth and its drivers. Nature climate change, 6(8), pp.791-795.