This comprehensive study uses dry air CO2 mole fractions measured at the Amazon Tall Tower Observatory (ATTO) and airborne vertical CO2 profiles in the CarboScope Regional atmospheric inversion system to estimate the net carbon exchange in tropical South America. They find that the biogeographic Amazon is a net carbon sink after accounting for vegetation fluxes, river efflux, and fire emissions. They note that treatment of Cerrado and Caatinga biomes in previous analyses have been historically lacking and include these biomes specifically, They further note that Cerrado and Caatinga biomes roughly offset the net uptake making the entirety of tropical South America close to neutral. The paper also addresses the role of measurement uncertainties on their results , namely water vapor corrections to aircraft profiles and low representation of measurements in the Amazon-Andes foothills. Overall, this is an important study spotlighting a key region (from both climate and ecological angles) that is underrepresented in existing carbon cycle model/measurement studies. I recommend the following minor revisions.

Specific Comments:

Title: “Combined CO2 measurement record indicates decreased Amazon forest carbon uptake, offset by Savannah carbon release”. I find the title confusing – consider rewording.  Decreasing Amazon forest uptake implies that the Savanna carbon release is doing the opposite of offsetting. That is, a weaker uptake signal in the Amazon forest combined with an increasing Savanna release means an *amplified* overall release rather than a counterbalance/offset. Perhaps you mean to say the Amazon Forest C uptake signal is diminishing in its capacity to offset the Savanna C release?

Minor suggestion – Savanna is far more common as spelling; I recommend changing from Savannah to Savanna; fix throughout (including title)

Abstract: Specify the study time period (2010-2018) in the abstract also for clarity

Abstract: uncertainties – specify whether SD, or 95%CI, or other.

Abstract: a little weak, fails to highlight main points of paper expand on this. Bring more attention to the results summarized in L423-427 re: impact of water vapor correction and L533-537. In addition, there is an information mismatch with the title-- the overall results suggest a biogeographic amazon sink (abstract L7)  … so if you also mean to say there is a diminished sink trend from 2010-2018, make that clear in the abstract. However, this “diminished sink trend” requires further analysis – and meanwhile Figure 6a and Figure A15 don’t seem to suggest a strong trend from 2010-2018 for the Amazon as a whole or by region.

L30 Assis et al. (2020) has parentheses in the wrong place…also throughout, check the formatting of citations and incorrect placement of parentheses as this happens in multiple locations (e.g., L112, L152, L153…).

L34 Inconsistency with L21 (230 PgC). Use a consistent estimate; perhaps in both places indicate 150-230 rather than 150-200.

L63 vegetation-related source

L83 Do you mean “With this we [conclude] ” ?

L84 Sentence fragment; join to previous sentence.

L86: You bring up RECCAP2, but only once in the introduction. Consider expanding more on contributions in the conclusions.

L100: “for all sites are obtained” – you mean all the aircraft sites + MAN from Figure 1b?

Methodology Sec 2.1.6: What eddy flux sites are you using to calibrate VPRM? Provide in appendix, and include in acknowledgments.

L153: This is confusing. If you are using the ATTO+NAT+Aircraft for the global inversion whose posterior is then the prior for the regional inversion (L99) you are using the ATTO+NAT+Aircraft data twice. So it doesn’t seem like this is giving you any new information (ie you’re optimizing with the same constraints twice). Wouldn’t it be better to, say, use ATTO as an NBE constraint for the step 1 process and then use NAT+Aircraft for step 2? However, I could just be misunderstanding as Table 1 suggests that all the subsequent prior fluxes for the regional inversion are based off the s10 (rather than s10sam). Can you clarify all this please?

L174: Expand -- Provide citation/justification for assumption.

L250-L251:  What is the physical basis for selecting a 0.5x scaling factor for VPRM and SiB4? Related, Figure A8 – the 0.5VPRM Prior shows a change in sign as well in large portions of the Amazon indicating you applied a scaling factor of >1 to the respiration which had a net result of 0.5xVPRM_NEE correct? What was the exact respiration scaling factor? Did you apply that SF because you expected respiration to have been underestimated by VPRM and SiB4 (rather than GPP to be overestimated)? If so, why?

L268: Expand on this methodology and discuss drawbacks/limitations. You are assuming the same scaling factor for COprior/COpost as for CO2 ? As CO/CO2 relates to combustion efficiency, it’s possible that the GFAS CO prior relates to the CO posterior in a way that is not necessarily mirrored in a CO2prior/CO2post relationship. What if you instead do a biome-specific COprior/COpost factor (with uncertainties) – that way you get a sense of combustion efficiency across a specific biome that integrates dominant plant functional types and account for the average expectation of CO/CO2 combustion efficiencies.

L300: “consistent with predominant air transport…” Can you re-phrase and/or clarify this statement? You seem to be correlating observational density and air transport which is confusing.

L319: Clarify – is the mean impact 2% or >5%? Do you mean to say that the maximum UR can be >5%?

L250-251; L338. The VPRM (and SiB4) scaling nomenclature is confusing. 1xVPRM seems like it should be just VPRM (mathematically) but I think what you are trying to say is that 1xVPRM is VPRM constrained by respiration to have a total NEE of 1PgCy-1. If this is the case, then can you change the nomenclature? Something like VPRM, VPRM_0.5Pg, VPRM_1.0Pg.

L335, Fig 3: I don’t quite follow what your main message is with these results. Are you just trying to show the spread and/or convergence among flux model ensemble members, and break that down regionally? i.e., with the Cerrado & Caatinga region, you are showing that there are two families of ensemble members, namely the VPRM family that suggests the cerrado & caatinga region have net uptake in prior and post (-0.4gCm^-2d^-1), and all other models showing neutral to net release at least in their posteriors. Can you clarify your main message here? Related, in the next paragraph you are stating the superior constraint by atmospheric data for Figs 3c-f – is this statement based on the change in the posterior distributions (ie approaching normal/biggest reduction in uncertainty) on the y axes? If so, the same can be said for Cerrado and Caatinga region but the issue there is that the VPRM family seems to be driving the bimodality in Fig 3b y and x axis. Again, clarify main message as it seems to be getting a little lost. (Your main message seems to be L350-352.)

L353: How significant are these results? South American stations are ATTO+NAT+Aircraft? Somewhere early on state that ATTO+NAT+Aircraft will continue to be referred to as South American Stations and keep that terminology consistent throughout.  How does adding more stations (and having no impact on Andes Amazon Piedmont) reinforce lack of observational constraint in that region? Are you trying to say that the stations added are irrelevant to that region, and you need more stations *within* that region?

L356: For Brazilian Shield Moist Forests, did you mean to say movement from neutral to net release of 0.03? That is clearer than “there is a shift in sign”.

Table 2: In title, add “averaged over 2010-2018”

L383: “…between these two regions”— change to ““…between the biogeographic amazon and the cerrado&caatinga”

L407: Typo – change to Figure 5b

Figure 6b: This is on average across 2010-2018? Specify in caption.

Discussion/Conclusions: With all the satellite data now available, it would be worthwhile to have a brief discussion on the value those data could add in tropical NLF constraints.

Summary: The authors use the CarboScope framework, in a two-step process, to optimize regional CO2 flux over South America generally (northern), and the Amazon basin specifically. They find that optimized fluxes are much closer to balance than initial estimates. They find that in the Amazon hydrologic basin Net Biome Exchange (NBE) is a small sink, and in drier savannah/caatinga regions to the south and east NBE is a small source.

The authors address an issue which has been the topic of sometimes vigorous debate in the community, that of water vapor in flasks and how CO2 measurements may be biased by water condensation.  They use coincident measurements of flask and in situ CO2 measurements to obtain an equation describing the CO2 bias, related to water vapor, and then use predicted values of water vapor from the ECMWF model (with STILT) to obtain water vapor predictions for locations sampled by aircraft flasks, and the bias correction for water vapor obtained from in situ CO2 measurements is applied using the predicted water vapor content.

The authors present an ensemble of prior fluxes in the inversion, and investigate multiple estimates of fire flux as well.

Review Synopsis: There is an impressive amount of work here. Unfortunately, it is presented almost as a regurgitation of work completed, and lacks organization and focus. I might describe the paper as ‘sprawling’. My recommendation needs to be that the manuscript is not suitable for publication and should be rejected. However, I believe that with reorganization, inclusion of some important context, and condensation this research would contribute to the body of work on the subject. I thereby also recommend resubmission.

The authors are passive and unclear with regard to major findings from this research. The end of the abstract leaves the reader with a bland statement about the effect of systematic uncertainty due to water vapor on flasks and a vague exhortation for more observations. Come on. There was a lot of work done here, point the reader explicitly and clearly to what they should take away from the paper and what it tells them about how the world works.

 In my reading, I find the first main point to be that the Amazon hydrologic basin (hereafter, Amazon) has a small annual sink of CO2, and the cerrado/caatinga (hereafter, cerrado) is a small source. Fine. That is known, from the work of others (e.g. Luciana Gatti). Another important finding, for me, is further support of the notion that in the Amazon the net flux is a very small residual from very large component fluxes. It is my opinion, and the opinion of several of my colleagues, that this is a very important concept that is perhaps underappreciated by the carbon cycle community at large. These are mentioned in the abstract, and in my opinion the paper would benefit from more emphasis on them.

Water vapor in flasks. Oh, boy. I understand that this is a topic of much discussion, some of it impassioned.  There is a group of people who believe that this issue calls into question some scientific results, and another group who believe that it is not that big of a deal. I am agnostic on the issue, but I see the division in the community. The authors obviously spent a lot of effort studying the issue, but after reading the paper I do not come away with any feeling of resolution. Does the water vapor issue call into question previously published results or not? If you can, make a statement one way or the other. If you can’t, then the question is still open and you might want to think about how much attention you pay to it in the manuscript.

During multiple readings, what I took from the paper is that the Amazon is a small sink, the cerrado/caatinga is a small source, and these net fluxes are small residuals from large component fluxes. The authors were able to obtain this result with a method that is consistent with yet independent of other estimates. While not earthshaking, I see that as a worthwhile result that adds to an emerging body of work and pushes forward a narrative that many in the carbon cycle community might not fully appreciate.

I can’t tell the authors what paper to write. I can say that there is a lot to keep track of in the paper as is, and it can be hard to keep focus on what is important. The reader is trying to follow information about different regions, water vapor, priors, fire, rivers, mechanisms, spatial attribution of flux signals, and more.

I believe a condensed paper with tightened focus would be beneficial and well-received by the community. A lot of material could be moved to Supplemental Information (fire, rivers) or greatly condensed. There is good material here, I look forward to seeing a revision.

Ian Baker

Cooperative Institute for Research in the Atmosphere (CIRA)

Colorado State University

Fort Collins CO, USA

More Detailed Review:

Observations: An exhortation to the community for more observational constraint is made several times in the manuscript. This mention is unnecessary, everybody knows it, campaigns are being planned even as we speak. This can be seen as an excuse, or a defense for the authors against being wrong. Make your statement with the available data and analysis. If you’re proven wrong later, write another paper describing how, and show what you’ve learned from it.

Background: A few things were conspicuous to me by their absence.

1. There is no mention of the OCO-2 Flux MIP (Crowell et al., 2019; Liu et al., 2017; Peiro et al., 2021). Inversions constrained using retrievals of XCO2 provide a nice counterpart to inversions constrained with flask data. There are published papers (Crowell et al., 2019; Peiro et al., 2021) that describe what XCO2 inversions have shown in the Amazon/cerrado. How do your results compare? For that matter, the inversion results are available on a 1x1 grid. How do these results compare with your regional partitioning?
2. ENSO (2015-2016 El Nino): Maybe this goes into the analysis/discussion, but there really isn’t anything in the manuscript about this event. What sort of ENSO response did CarboScope determine? How did that compare with other estimates (e.g. (Crowell et al., 2019; Liu et al., 2017; Peiro et al., 2021).
3. Transport: “errors in atmospheric transport” are mentioned on line 51, but nothing further is said. An analysis of different transport models (TM5 and GEOS) is described in (Schuh et al., 2019). Does the transport in CarboScope align with either of these? How might this influence results? At the very least the Schuh paper should be mentioned; if the findings of that paper are meaningful for CarboScope inversions (or not), the reader should be made aware.

Regions:  I frequently had to refer to Figure 1A to figure out what the authors were talking about. By the end of the paper, my impression is that I should primarily be concerned with the Amazon region and the cerrado region, and that there is heterogeneity in the Amazon region with regard to sub-regions (Amazon River Flat Plains, Amazon and Andes Piedmont, Guianian Shield Moist Forest, Brazilian Shield Moist Forest). I’m not sure why the other regions are included in the map or the analysis-are they adding to the scientific narrative, or just thrown. In my opinion the ‘story’ would be much clearer (and more concise) if the analysis was limited to the Amazon and cerrado regions, with discussion of Amazon heterogeneity included with regard to the sub-regions within the Amazon basin region. This brings up another point-Figure 1B suggests that there really isn’t enough surface influence in these other regions (e.g. Orinoco Savanna, Central Andes, etc) to have much confidence in results obtained there. So why include them in the paper? It adds confusion to the analysis. When the authors say “there is almost no information” that’s a pretty strong suggestion that these regions should not be included in the paper submitted for publication.

Another idea I found myself thinking about while reading about the regional analyses was this: How much information do you need to be able to partition optimized fluxes into smaller and smaller regions? In my discussions with inversion modelers, I see a tension between wanting to describe fluxes with higher and higher spatial resolution, and not wanting to overstep what the data can tell you. I’m thinking about work done by Martha Butler and Thomas Lauvaux (not sure I know the proper citations), among others. This goes back to the previous paragraph and my concern that the authors are making statements about regional flux in regions where there is not much information about the local contribution to flux. The authors should justify, even if only briefly, why they can subdivide an optimized flux into the small regions described in the paper.

CarboScope Description: I had to read multiple papers to get my head around CarboScope. I have worked with the inversion community for years, and I’m familiar with the general idea, but understanding CarboScope took some doing. Not sure I’m there yet. All this is to say that the description in Section 2.1 was not clear to me. I’m not expert enough to say exactly how this section should be modified, but I would recommend that the author who writes this section should work with someone who is not as well-versed in inversions to make sure the description is understandable to someone who does not work with inversions on a daily basis. I think this work will ultimately reach a wider audience, so the effort taken to describe CarboScope in a more ‘accessible’ manner will be well-spent.

Observational Network: I’m generally happy with this section. But I am curious: Can you justify assuming that the weekly error correlations are driven by synoptic-scale transport variability? That might make sense in extratropical regions where baroclinic systems frequently operate on something approximating a seven day cycle. I haven’t read Kontouris (2018) or Munassaur (2021), but they are both studies based in Europe. In the tropics, however, this assumption may not hold: the weather is very different, with variability imposed by convection and squall lines. If there is published literature to support treating the tropics and extratropics similarly, cite it. If not, the authors might think about what this means. I’ll leave it up to them as to how much they want to talk about this in a revised paper.

Systematic Uncertainties (flask moisture): The ‘fix’ employed here is interesting, but I’m not sure that the bias correction employed here provides a conclusive resolution. The wording in the section certainly doesn’t suggest so. If the authors think they can make a declarative statement about this issue, then make it. Some thoughts I have about this section:

• Is this a universal problem with flasks gathered in humid environments? If so, is it fair to single out research in one location (Amazon) if other regions (e.g. Southeastern USA) have the same issue?
• In figure A6 I see the linear fits, but I don’t see any statistics about tightness of fit. I don’t think I’m going out on a limb when I say that the r² is probably not a large number for either line (flask vs. Picarro, or ECMWF vs. Picarro). Is the variability explained more or less than half? What would that value suggest for interpretation, either of the initial ‘problem’ or of the ‘solution’?
• The idea as I understand it is that in humid conditions the condensation of water in flasks, and absorption of CO2 into that water, presents a persistent negative bias in flask measurements. If that is the case, what is the meaning of negative Picarro-PFP values? Is that indicative of mismatch between air ‘parcels’ (I don’t think I want to call them air masses) being sampled? Or is that an indication of uncertainty in the evaluation?
• I have not seen a time series of the Picarro CO2 samples; is the CO2 concentration fairly continuous, or does it exhibit large excursions in value over short times and distances? What about water vapor? Are there small spatiotemporal variations in humidity associated with convection, rain, updrafts/downdrafts, or is the dominant variability that associated with wet and dry seasons? Does the scale and amplitude of CO2/H2O variability have any bearing on this problem?
• The hypothesis as I understand it seems to be that the flask bias is due to a greater likelihood of CO2 absorption and low measure CO2 value as H2O mole fraction (humidity) increases. The error in the ECMWF prediction will be due to errors in transport, surface CO2 flux, and advection of long-range signal. Does higher ECMWF error with higher humidity suggest errors in cumulus transport in ECMWF? Or does it stratify along wet/dry season lines? Either way, does this suggest a ‘right answer for the wrong reason’ solution?

Priors, and Inversion Results: OK, I don’t think I understood, after reading the paper multiple times, what the benefit of using 10 priors brought to the analysis. If there is a compelling reason, other than to show that the authors did a lot of work, it escaped me. In that case the authors need to do a better job of making the reason for including them all clear to the reader. Here’s what I got out of this section:

• The uncertainty reduction is largest (Figure 2B) in the areas with the most observational constraint on surface influence (Figure 1B). Well, yeah.
• The between-model spread in the prior mean NLF is really just an indicator of model ‘responsiveness’ and bias (Gallup et al., 2021; Hoffman et al., 2014). It seems to me that the value of the optimized flux (and therefore the slope of the line) is more an indication of model-data mismatch than anything else. Is that true? The way I think about it is that every inversion has tension (Scott Denning always called them ‘rubber bands’) between the optimized flux and the prior, and between the optimized flux and the observations. A strong coupling to the prior means that the optimized flux won’t stray far from it, and a strong coupling to the observations means that it can. Some inversion systems are tightly coupled to the prior, and some can ‘move away’ from the prior more freely. In this case, I might think what is being shown in Figure 3 is more indicative of the CarboScope setup (model-data mismatch) than it is of any physical processes.
• VPRM_flat: If I remove the long-term mean, the seasonality, and the IAV from a flux product, what is left? The secular trend?
• What is the reason for changing the sign of priors (0.5X and 1.0X priors)? Is this because CarboScope can’t move the optimized flux very far away from the prior, so you move it artificially? Couldn’t the same result (much different optimized flux) be achieved by relaxing the model-data mismatch?

OK, I’ve blathered on long enough. I’ll briefly reiterate my main thoughts about the paper:

• The authors have obviously done a lot of work. Unfortunately, reviewers and readers don’t want to read about all of it. Make your main points, as briefly and directly as possible.
• The paper is written passively, with many caveats about needing further observations. If you think you can make a statement, make it and defend it.

Specific Comments:

• Check all citations: some citations that should be in parentheses are inline.
• Lines 84-86: incomplete sentence.
• Line 187-188: didn’t the in situ analyzer also measure CO2?
• Lines 353-361: Are these values even large enough to worry about? Are they meaningful?
• Lines 376-378: Does this mean that a prior flux of 0 would work as well as any of the other priors used?
• Lines 468-469: How does the issue or prior selection convolve with the water vapor issue?

References

Byrne, B., Baker, D. F., Basu, S., Bertolacci, M., Bowman, K. W., Carroll, D., et al. (2023). National CO ₂ budgets (2015–2020) inferred from atmospheric CO ₂ observations in support of the global stocktake. Earth System Science Data, 15(2), 963–1004. https://doi.org/10.5194/essd-15-963-2023

Crowell, S., Baker, D., Schuh, A., Basu, S., Jacobson, A. R., Chevallier, F., et al. (2019). The 2015–2016 carbon cycle as seen from OCO-2 and the global in situ network. Atmospheric Chemistry and Physics, 19(15), 9797–9831. https://doi.org/10.5194/acp-19-9797-2019

Gallup, S. M., Baker, I. T., Gallup, J. L., Restrepo‐Coupe, N., Haynes, K. D., Geyer, N. M., & Denning, A. S. (2021). Accurate Simulation of Both Sensitivity and Variability for Amazonian Photosynthesis: Is It Too Much to Ask? Journal of Advances in Modeling Earth Systems, 13(8), e2021MS002555. https://doi.org/10.1029/2021MS002555

Hoffman, F. M., Randerson, J. T., Arora, V. K., Bao, Q., Cadule, P., Ji, D., et al. (2014). Causes and implications of persistent atmospheric carbon dioxide biases in Earth System Models. Journal of Geophysical Research: Biogeosciences, 119(2), 141–162. https://doi.org/10.1002/2013JG002381

Liu, J., Bowman, K. W., Schimel, D. S., Parazoo, N. C., Jiang, Z., Lee, M., et al. (2017). Contrasting carbon cycle responses of the tropical continents to the 2015–2016 El Niño. Science, 358(6360), eaam5690. https://doi.org/10.1126/science.aam5690

Peiro, H., Crowell, S., Schuh, A., Baker, D. F., O’Dell, C., Jacobson, A. R., et al. (2021). Four years of global carbon cycle observed from OCO-2 version 9 and in situ data, and comparison to OCO-2 v7 (preprint). Gases/Atmospheric Modelling/Troposphere/Physics (physical properties and processes). https://doi.org/10.5194/acp-2021-373

Schuh, A. E., Jacobson, A. R., Basu, S., Weir, B., Baker, D., Bowman, K., et al. (2019). Quantifying the Impact of Atmospheric Transport Uncertainty on CO ₂ Surface Flux Estimates. Global Biogeochemical Cycles, 33(4), 484–500. https://doi.org/10.1029/2018GB006086