This study established a mass-balance inversion framework that integrates CrIS-retrieved isoprene columns into the LMDZ-INCA chemistry-transport model to constrain global, monthly biogenic isoprene emission maps spanning 2013–2020. This represents a significant scientific contribution. Overall, I find the methodology generally sound, and particularly acknowledge the author’ thorough justification of key assumptions and parameter selections. The manuscript is well-organized and clearly written. However, there are major concerns that must be addressed before I can recommend publication.

Major Concern

The validity of inversion critically depends on demonstrating whether posterior results converge when using different prior emissions inventories. The manuscript exclusively employs LMDZ-INCA land module simulations as the prior inventory. It is imperative to conduct additional inversions using an alternative emissions inventory—ideally one mechanistically distinct from LMDZ-INCA, with differing total magnitude, spatial distribution, and seasonal variation in isoprene emissions. This test would reveal whether the inferred total isoprene emissions align with those derived using LMDZ-INCA as prior, or quantify the extent to which discrepancies between the two prior inventories are reduced.

This validation using independent prior emissions is particularly crucial because the study finds that the posterior isoprene emission seasonal cycle using LMDZ−INCA as prior is entirely reversed compared to inventories such as MEGAN (Figure3). This is a new and important conclusion but has to be addressed carefully. What seasonal cycle does the prior LMDZ-INCA itself exhibit? Would using MEGAN as prior similarly yield a reversed seasonal pattern in the inversion? Without addressing these points, the scientific robustness of the posterior emissions—especially their seasonal cycle—remains limited. Given computational constraints, this sensitivity test could be restricted to a single representative year.

Other Comments

1. Sensitivity of perturbation magnitude (Lines 180–193):
   
   The authors analyze the β+25%/β-40% value, with a global mean value of 0.9, to argue that the method is not sensitive to the perturbation magnitude  and that the relationship between isoprene emissions and concentrations can be assumed linear. However, as seen in Figure S2, β+25%/β-40% ratios reveal substantial spatial heterogeneity. The manuscript should:

• Present the grid-scale variance of β(+25%)/β(−40%) in the main text.
• Further investigate how the nonlinearity reflected by β(+25%)/β(−40%) correlates with spatial patterns of OH, NO₂ pollution, or other meteorological drivers.
• Model chemistry representation:

• The chemical mechanisms governing VOCs—especially isoprene oxidation pathways—vary significantly across models and directly influence simulated isoprene concentrations and their response to emissions. The model description section should explicitly detail the VOCs chemical mechanisms included in LMDZ-INCA.
• The limitations section should explicitly address the potential impacts of using a single model framework on the results.

Review of "Global biogenic isoprene emissions 2013-2020 inferred from satellite isoprene observations" submitted by Hui Li et al.

This manuscript presents the first multiyear inversion of isoprene emissions based on spaceborne (CrIS) isoprene measurements and a global

chemistry-transport model (LMDZ-INCA). The study is ambitious (probably too much) in that it aims to derive global gridded emissions at a high resolution (1.27 x 2.5 degrees) over an extended period (2013-2020); furthermore, it investigates in some detail the temporal variability of emissions and their correlation with meteorological and other variables. The high computational cost of emission inversion for a reactive species (known to strongly impact its own chemical lifetime through chemistry) is avoided through the use of a mass-balance approach, without iteration. The manuscript is generally well-written, and the topic is of great importance for the community. The CrIS dataset is a unique, and extremely valuable dataset for assessing the spatio-temporal variability of isoprene emissions. As expected, the results show that temperature is a major driving factor of isoprene temporal variability, while other factors (LAI, radiation, etc.) contribute as well.



Although to a large extent, the retrieved emissions are (at least qualitatively) validated by comparisons with formaldehyde datasets and by the analysis of temporal variability, I have several major reservations regarding the methodology used in this work (see below). In addition, some of the plots lack clarity (color bars, size) and important diagnostics are missing, which make it difficult for the reader to fully assess the method and the results. Finally, the results of this work should be better put in perspective with previous work, and the manuscript should cite the relevant literature when appropriate and better evaluate the results against previous work.  My major comments are as follows.



1) The assumption of linearity between emissions and column densities is not verified, despite the authors' claim that the issue is really minor. The slope of the relationship between emissions and columns (beta factor) is estimated from a reference run and a run using uniformly reduced emissions, by 40%. This is compared to an alternative estimation where the perturbed run uses increased emissions (+25%). The two estimations of beta differ by about 20% over much of the globe, in particular in July (Figure S2). Although not stated explicitly, the reason for adopting the case using decreased emissions (-40%) is motivated by the significant prior model overestimation against CrIS columns over rainforests, which account for a lare fraction of the global emissions. Wherever the emission change deduced from CrIS is of the order of -40%, all is fine. But, Figure 1 shows many regions where

emissions actually increase, and sometimes quite a lot. There, the optimised emissions are overestimated. Figure 1 displays many regions where the posterior model columns are significantly higher than CrIS, most notably Eastern and Central USA, southern China, the Middle East,and large parts of Canada, Europe and North Africa. Very probably, the emission enhancements are much larger than +25% at many of these places, and the linearity assumption breaks down. It would be easier to figure this out with a plot showing the ratio of posterior to prior model columns, not just annually but for different seasons, since the emission updates varies over time. It is impossible to tell from Figure 1 whether the -40% decrease is appropriate wherever CrIS suggests an emission decrease; at some locations, the decrease might be much larger than the -40% used in the beta estimation.



In their inversion of isoprene emissions based on CrIS and Geos-Chem, Wells et al. (2020) applied an iterative mass-balance approach, i.e. Equation 2 was applied iteratively "until convergence, with the final solution obtained when normalized model-measurement differences over isoprene hotspots change by <1%". The number of iterations needed for this criterion was not mentioned, but it is safe to say that 3 is likely a minimum. I understand that iterative mass balance is more computationally demanding that the method used in this work, but I don't see the point of the high spatial resolution when the potential errors due to the method can be very large, and completely avoidable with the iterative approach. At the very least, iterative mass balance must be applied at least for one year, at least 3 or 4 iterations, so that the consequences might be assessed. I'm not even so much in favor of this option, because the issue might influence the interannual variability, at least over regions with low columns. For example, the interannual

variability of retrieved emissions over India is higher than anywhere else (Fig. 4), probably due to a combination of large CrIS errors (due to low columns) and wrong emission optimisation (due to non-linearity). To avoid such issues, areas with low columns could be simply left out of the optimisation process.



2) The LMDZ-INCA is not appropriately described. As far as I can tell from previous papers, the isoprene degradation mechanism was described by Folberth et al. (2006) and was based on earlier work (1999). Obviously, it does not incorporate the numerous mechanistic updates (e.g. OH recycling) prompted by laboratory and theoretical studies since then, of special importance at low-NOx (see e.g. Wennberg et al. 2018; Novelli et al. 2020; etc.). The consequences for the prediction of OH levels and HCHO formation are difficult to tell, but could be very large. This should be investigated, e.g. using a box model, to assess the performance of the LMDZ-INCA mechanism, in comparison with more recent ones. In absence of recycling mechanisms, the OH levels might be too low in the model at low NOx, leading to substantial overestimation of isoprene columns.



3) A description of NOx and reactive VOC emissions should be provided, given the importance of NOx for OH levels (and hence isoprene) and VOCs for HCHO. Figure S6 suggests an underestimation of NO2 modelled tropospheric columns in comparison to TROPOMI, at least over tropical regions. However, the relative underestimation over key regions (e.g. Amazonia) is impossible to tell. This is essential to figure out, given the role of NOx for isoprene emission inversions (Wells et al. 2020). Note that Figure S6 shows features (red areas over Patagonia and parts of Australia) that are almost impossible to understand, and make me wonder whether the tropospheric column is correctly calculated.



Another model aspect requiring more information is PBL mixing. How does the model perform for the vertical profile of reactive species such as isoprene or similar compounds? This is relevant to model comparison with CrIS, because of the vertical dependence of the sensitivity of the instrument (Wells et al. 2020).



4) The analysis of results is long and often repetitive, and it does not cite properly the literature. Many findings are presented as new, while they were perfectly well known from past studies. Those studies should be cited and feed the discussion. Examples: the role of meteorological variables, especially temperature, is incorporated in emission models such as MEGAN, and has been verified using satellite measurements, see e.g. the Geos-Chem studies (e.g. Abbot et al. 2003) and Stavrakou papers (e.g. Stavrakou et al. 2018). The impact of El Nino on emissions was shown e.g. by Naik et al. (2004), Lathiere et al. (2006) and others.



The inversion results should be better evaluated against relevant literature. The ORCHIDEE emissions, being used as prior inventory, deserve to be shown. The seasonal variation of isoprene emissions (Figure 3) is evaluated against MEGAN-MACC and MEGAN-ERA5. What is the point of showing MEGAN-MACC? The seasonality should be evaluated against recent HCHO-based emission inversions. A part of the discrepancy between this study and MEGAN-ERA5 can be explained by the overestimation of emissions from Oceania. Still, Figure S12 suggests a large remaining bias even when removing Oceania. Is this due to differing seasonality in key emitting regions (e.g. Amazonia), or is it due to different geographical patterns?





Minor comments



l. 18: "introducing substantial uncertainties due to complex and nonlinear chemical pathways": wrong point to make, because the isoprene-based inversion is also subject to such uncertainties. The main "selling point" of CrIS-based inversion is of course the direct observation of isoprene, whereas formaldehyde is produced from the oxidation of many other VOCs. Please rephrase.



l. 34: Is precipitation really a driver of isoprene emissions? It is correlated with cloudiness and there anti-correlated with radiation. It also affects drought stress. The causes for correlation between top-down emissions and precipitation are therefore generally unclear. Rephrase, and adapt in the discussion.



l. 43:  Delete "precipitation"



l. 47: add shrub to the land cover types



l. 73-74:  The main source of uncertainty might be that the emission factors for many plant species are currently unknown, e.g. over tropical

forests



l. 76: "spatial correlation": there is more than just correlation



l. 78-79: As explained above, isoprene concentrations are even more affected by non-linear chemistry than formaldehyde production rates.



l. 79-80: "non-zero isoprene/HCHO lifetimes that smear the retrieved isoprene emissions": rephrase, unclear



l. 83: replace "potentially" by "partially"



l. 94-95: "overcoming limitations of traditional HCHO-based...": see above, rephrase, taking into account the isoprene-based inversions have

their own limitations



l. 108: Are the monthly-mean model columns sampled as the CrIS observations (i.e. ignoring days when CrIS data are absent)?



l. 125: What version of TROPOMI NO2 is used?



Figure S3: the color bar is inadequate, please narrow it down and discuss potential differences with the corresponding distribution of beta from Wells et al. (2020) (their Figure S9).



l. 222 "indicating that real-world differences in beta are likely modest": this is absurd, the globally averaged difference is irrelevant.



l. 229 "prior overestimation": rephrase. The overestimation is far from being ubiquitous.



l. 239: The validation using PGN data shows an almost negligible improvement. Note that the number and location of the PGN stations is not ideal for this validation. Since the number of stations steadily increases, consider using 2020 for this validation.



Figure 1 is difficult to read due to the small size of the maps. The color bar leads to saturation in high-emission areas, while most other regions are very dark. Consider using a non-linear color scale to improve clarity.



l. 283: the uncertainty of 43.8% for global emissions is not compatible with Figure 2(b), which shows values well below 40% everywhere

(except >60N). Also, how can the uncertainty be so uniform in space, except for the lower values over high-column areas? Over low-column

regions (e.g. deserts), one would expect uncertainties close to the prior (117%). Please clarify.



l. 300-301: "consistent with our posteriors": not so much, the seasonal profiles are still very different.



l. 312-316: Such a long explanation... there is simply much more mid-latitude area in NH compared to SH.



Figure 3: The precipitation subplot is not useful. The LAI subplot does not bring much either.



Figure 4 (a) is not very clear, it is difficult to distinguish the lines.



Sections 3.5-3.6: I find that these sections should be shortened. Attribution of causes to the observed correlation is often speculative and uncertain, due to the co-variation of different factors.



l. 386: "amplified sensitivity" and l. 390 "enhanced temperature sensitivity": rephrase. There are other factors than temperature. Only the apparent temperature sensitivty is enhanced, not the real one.



l. 505: "with atypical vertical profiles": rephrase. Model have difficulties reproducing vertical profiles of short-lived species (not just in atypical situations). A discussion of this aspect would be needed, in light of model comparisons with aircraft data (for other species, from previous papers).



l. 515-516: the linearity clearly breaks down in many regions, not just at low NOx. This is shown by the posterior model overestimation of CrIS columns in many regions, as mentioned above.



Section 6: This section lacks substance. The "findings" (climate sensitivity of emissions, etc.) are not new. I fail to see what we really learned from the emission inversions. E.g. is T-sensitivity too weak or too strong in MEGAN in some regions? Where are biogenic emission models successful, and where do they fail?





Technical comments



l. 26: replace "surface observations" by "ground-based optical measurements"



l. 168: and elsewhere: replace "low NO2" by "low NOx"



l. 170: replace NO2 by NOx



l. 195: Impact of NOx



Figure 1, 2, 4 and in the Supplement: why is Antarctica wrongly shaped? You could limit the plot to 60S - 90N.













References





Abbot, D. S. et al., Geophys Res. Lett., 30, 1886, doi:10.1029/2003GL017336, 2003.



Folberth, G. A. et al., Atmos. Chem. Phys. 6, 2273, doi:10.5194/acp-6-2273-2006, 2006.



Lathiere, J. et al., Atmos. Chem. Phys., 6, 2129, https://doi.org/10.5194/acp-6-2129-2006, 2006.



Naik, V. et al., J. Geophys. Res., 109, D06301, doi:10.1029/2003JD004236, 2004



Novelli, A. et al., Atmos. Chem. Phys. 20, 3333, https://doi.org/10.5194/acp-20-3333-2020, 2020.



Stavrakou, T. et al., Geophys. Res. Lett. 45, 8681, https://doi.org/10.1029/2018GL078676, 2018.



Wells, K. C. et al., Nature 585, 225, https://doi.org/10.1038/s41586-020-2664-3, 2020.



Wennberg, P. O. et al., Chem Rev. 118, 3337, DOI: 10.1021/acs.chemrev.7b00439, 2018.

This study develops a global, multi-year inversion of biogenic isoprene emissions by assimilating CrIS-retrieved isoprene columns into the LMDZ-INCA chemistry–transport model, producing monthly emission estimates for 2013–2020. The approach represents a meaningful advancement in directly constraining isoprene emissions, distinct from traditional HCHO-based inversions. The manuscript is clearly structured, and the results are generally consistent with existing inventories, providing valuable insights into the spatial and interannual variability of global biogenic sources. Overall, I find the study scientifically relevant and well executed, but several methodological and interpretative aspects require clarification before publication.

Model description and chemical mechanism

A more detailed description of the atmospheric transport model (LMDZ-INCA) is needed, particularly the configuration of isoprene-related chemistry and its coupling with oxidants such as OH and NOx. Since the chemical mechanism largely governs how simulated isoprene columns respond to emission perturbations, the manuscript should specify the chemical mechanism (i.e., relevant reaction pathways and key rate constants). This will allow readers to assess the reliability and representativeness of the inversion results.

Sensitivity to NOx levels

Given that the oxidation rate of isoprene depends on ambient NOx conditions, it would be valuable to perform an additional sensitivity experiment under NO2 concentrations closer to TROPOMI observations.

Seasonality of posterior emissions

The seasonality of posterior emissions in this study appears to differ from that of existing inventories, yet the underlying cause of this discrepancy remains unclear. It would be helpful to disentangle the contributions from the prior and the observational constraint. I suggest presenting the seasonal cycles of the prior (e.g., ORCHIDEE), satellite observations (CrIS isoprene and satellite HCHO), and possibly a parallel inversion using MEGAN as the prior. Comparing these seasonal patterns would clarify whether the retrieved seasonality reflects model, data adjustments, or inherent observational features, thereby strengthening the validation of the inferred isoprene emission seasonality.

Regional contribution and structure of Sections 3.5–3.6

Section 3.5 could be more focused on quantifying and interpreting regional contributions to global variability, while Section 3.6 emphasizes the environmental drivers. This clearer separation would improve the logical flow and avoid redundancy between the two sections. Additionally, including comparisons with MEGAN or other inventories in the driver analysis (Section 3.6) would contextualize the inversion results and highlight the added value of the CrIS-based framework in capturing regional differences and environmental controls on isoprene emissions.

Specific comments:

1. Line 125: Please specify the TROPOMI NO2 version.
2. Section 3.2: In the current uncertainty configuration, the authors apply a simplified three-segment scheme for the CrIS observational uncertainty, assigning a uniform 70% uncertainty for all low-column grids. This assumption may underestimate the uncertainty gradient in regions with very low isoprene concentrations. It is recommended to refine this setting by introducing a continuous or extended scaling below the lower threshold, so that the relative uncertainty increases progressively as the concentration decreases.
3. Section 3.3: To validate the seasonality of the posterior emissions, comparison with inventories alone is insufficient. I suggest that the authors include HCHO-based inversion results as an additional reference.
4. Table S3: The left parenthesis is missing.
5. Line 301: The use of “consistent” is not precise here, as the results are not actually identical or in full agreement in Fig. S12, please rephrase.