General Comments:

This manuscript presents one of few studies investigating the value of joint constituent inverse analysis of satellite observations in verifying and improving the accuracy of CO2 emissions estimates. This paper is therefore relevant for publication in this journal. However, there are sections of the manuscript that need further clarification and elaboration (both methodological and interpretation of results). For this reason, the reviewer recommends minor revisions for this manuscript. Please see specific comments for details of these concerns.

Specific Comments:

1. The analysis performance on CO emissions (chem and trans) is unclear. Is the fit to CO observations also improved? Are the adjustments in posterior CO reasonable? While Figure A3 is informative, it would strengthen the paper if some discussion is added on this aspect. It is also not quite apparent whether the state vector includes grid-scale scaling factors for each sector (CO2: combust, trans, bio; CO: combust, trans, chem). Also, at what horizontal grid resolution are these state vectors (0.25deg x 0.3125deg or 2 deg x 2.5 deg or 0.5 deg x 0.625 deg)? Please clarify. How many elements are in the state vector xb and data  y_obs?
2. Is it not clear why the off-diagonal elements of R is generated? As stated in Line 202, R includes the errors from our forward model and observations. Can R be explicitly calculated from the ensemble?
3. While the authors acknowledge that assuming 100% error correlation for CO2:CO is a gross estimate, it is not realistic, and results are therefore not useful and perhaps can be misleading.
4. The paper states: “The satellite observations (CO2-only) do not show significant combustion emissions changes from our a priori estimates, whereas when we use in situ CO or CO2 and CO satellite observations, we see greater divergence from the a priori emissions.” Can this divergence be due to model issues related to representing vertical mixing processes as well?
5. Also, the paper states: “improvements in model-observation fit are small and we do not see significant reduction in uncertainties compared to our a priori estimate."  Is this because of lack of information content in the data (accuracy and precision)? Or as the succeeding statements alluded to, that the errors specified in the a priori is already low in the first place. What about biomass burning, which has relatively larger uncertainties for both CO2 and CO?
6. What is the basis of the following statements:

• Line 122. “We consider the atmosphere to be well-mixed when the standard deviation of CO2 concentrations across the lowest five vertical model levels is smaller than 0.3 ppm.” Why 0.3?
• Line 208. “We generate the off-diagonal covariance for 3 based on the spatial and temporal proximity of observations following an exponential decay with spatial and temporal length scales of 100 km and 4 hours, respectively.” Why 100 km and 4 hours?
• Line 221. “We use an assimilation window of two weeks and a lag window of one month?” Why 2 weeks and 1 month?
• Line 224. “We perform our inversion sequentially, using the a posteriori scale factors for a given assimilation window to update the a priori scale factors for the next lag window over the same date range.” Is the prior error covariance also updated?
• Line 226. “We apply a 10% error inflation when we update the a priori state vector.” Why 10%? Is it possible to show Chi-Square statistics?
• Line 229. “We localize by distance so that each state vector element that represents a grid-scale variable is only influenced by observations within a 1000 km range.” Why 1000 km? And does it mean that >1000 km has zero influence? Is there a smooth function that is applied?
• Line 253. “Our state vector also includes scale factors for transport of each species (i.e., allowing adjustment of our assumed background concentration), and
• for CO we include a vector with two scale factors for the chemistry terms (x_CO^chem).” Why 2 for chem?
• Line 260. “For our first two approaches, we assume an a priori uncertainty of 20% (relative standard deviation) for the combustion scale factors x^combust). We use an a priori uncertainty of 50% for the non-combustion scale factors x_co2^bio), and 5% for the atmospheric transport and chemistry scale factors.” Please justify the choice of these numbers.
• Line 276. “We call this our TNO approach because we use estimates of the uncertainties in the TNO emission inventory to create our error covariance matrix (Super et al., 2024). We increase the provided uncertainties by a factor of 3 to make them more comparable with our other simulations. This results in a mean grid-scale CO2 combustion uncertainty of 18%, though there is greater variability in grid cell uncertainties compared to our other approaches. We expect higher correlation between CO2 and CO gridded emissions in regions where the same spatial product is used to distribute emissions for both species (e.g., road network maps) and that spatial product has high uncertainties.” What are these spatial products? Please elaborate.
• Line 699. “The influence of neighboring grid cells decreases with distance following an exponential decay with a length scale of 100 km.” Is this assuming isotropy?” If so, is this justifiable?

This study presents a novel CO2 inversion framework that leverages CO and CO2 measurements to estimate CO2 combustion emissions. The framework employs an ensemble Kalman filter technique that incorporates the covariance between CO and CO2 emissions. The integration of CO observations improved the agreement with CO2 observations, and more accurate results are achieved by accounting for grid-scale CO2 error correlations. While the topic is highly relevant and the methodology is sound, the study falls short of demonstrating substantial and statistically significant improvements or changes in emissions at the country scale. The paper would benefit from additional explanation and discussion of both methodology and results. Major revisions are required to address these issues.

Specific comments:

NO2 has been extensively used to estimate CO2 combustion emissions. It would be beneficial for the authors to discuss in detail the potential advantages of using CO instead of NO2, including any specific scenarios or conditions where CO may offer better insights or accuracy.

Validation of posterior CO concentrations is important to determine the success of CO inversion. The authors should include this validation to justify the impact of adding CO and to provide more credibility to the inversion framework.

The paper lacks spatial maps of prior and posteriori CO2 concentrations and comparisons against satellite and in situ observations. Such maps are necessary to visualize the differences and improvements obtained. Furthermore, while the regional comparisons show slight improvements due to the TNO methodology, a more detailed validation, including a time series analysis at each in-situ observation site, would provide more insight into the performance of the methodology.

The term Relative Standard Deviation (RSD) is not defined in the manuscript. The authors need to clarify whether this RSD is based on the analysis spread in the EnKF approach for emissions or concentrations. Due to the different prior uncertainties and inflation applied, careful consideration should be given to the interpretation of the RSD. The authors should discuss whether the RSD provides a meaningful measure of uncertainty reduction in their context.

The study reports very small changes in CO2 combustion emissions in general, which raises questions about the accuracy of prior emissions and the effectiveness of the inversion process for Europe. The authors should discuss whether this small change represents a very accurate prior emissions or a potential shortcoming of the inversion methodology.

Given the small changes in CO2 combustion emissions at country scale, it would be insightful to compare their impacts at the sectoral level, especially with the TNO approach. This comparison could highlight any sector-specific discrepancies or improvements.

Also, given the small change in CO2 combustion emissions at the national level, it would be more informative to compare the impact of the TNO approach at the sectoral level. This comparison may highlight improvements needed in bottom-up inventory.

The overall impact on non-combustion emissions is also very small, except for France. The authors need to explore whether the results a high accuracy of prior biospheric fluxes and whether it is consistent with previous inversion studies that adjusted biospheric fluxes only. In addition, an explanation is needed for the large changes in non-combustion emissions in France.

Line 84: The statement “few studies have focused on using these data to constrain CO2 flux estimates over mainland Europe or the UK” requires appropriate references to support the claim.

Line 122: The assumption that the atmosphere is well-mixed when the standard deviation of CO2 concentrations across the lowest five vertical model levels is smaller than 0.3 ppm may not be robust. More meaningful results could be obtained by accounting for potential errors in chemical transport model mixing and by including, for example, PBL height from meteorological data as an additional parameter. Potential errors associated with this assumption should be discussed.

Line 168: “We use the CAMS fields at their provided temporal resolution (3-hourly) and re-grid to the GEOS-Chem horizontal spatial resolution of 2° x 2.5°”: The study uses the regional nested domain of GEOS-Chem with the CAMS fields for lateral boundary conditions. The authors should clarify whether a global domain in GEOS-Chem is required and also describe the performance of the CAMS data as the results presented in this study may be significantly affected by these boundary conditions.

Line 204: “For CO2, we use an a priori model error of 1.5 ppm for the satellite inversion (Feng et al., 2017) and 3 ppm for the in situ inversion (within the range of Monteil et al., 2020 and White et al., 2019). For CO, we use an a priori model error of 15 and 20 ppb for the satellite and in situ inversions, respectively (Northern Hemisphere CO column and surface mole fraction model- observation differences from Bukosa et al., 2023)”: I believe the model errors in the ensemble Kalman filter are estimated from ensemble model simulations. The authors should clarify whether these errors were estimated from something else.

Line 207: “For the observations, we use the errors as provided for the satellite or in situ network, averaged to the model resolution.”: When using the errors provided for satellite or in situ networks, it is important to consider any error correlations. The manuscript should address whether such correlations were considered and their potential impact on the results.

Line 201: “We use an assimilation window of two weeks and a lag window of one month, accounting for the impact of historical emissions on our assimilation period.”: The choice of a two-week assimilation window and a one-month lag window could significantly affect the inversion results. A more thorough discussion of the sensitivity of the results to the window size and lag is needed.

Line 229: “For our inversions using in situ observations, we localize by distance so that each state vector element that represents a grid-scale variable is only influenced by observations within a 1000 km range.”: The manuscript mentions localization by distance for in situ observations but does not clarify if a different setting was applied for satellite observations. This needs to be addressed to understand the methodology.

Line 236: Applying the scale factor implies the assumption that the location of CO2 sources is perfectly represented by the prior inventory. The authors should provide a more detailed discussion of this assumption and its implications for the inversion results.

The dimension of the transport scale factor (Eq. 9) is not clear. It should be clearly stated whether it represents only one boundary value or a 3-dimensional distribution.

Line 260: “For our first two approaches, we assume an a priori uncertainty of 20%...”: The balance of adjustments for transport, chemistry, and combustion uncertainties in the obtained results has not been discussed. This could have a significant impact on inversion results and requires careful consideration.

Line 276: “We increase the provided uncertainties by a factor of 3 to make them more comparable with our other simulations.”: There must be a clear justification for this increase. The authors need to explain the rationale for this adjustment and its impact.

Line 278: “This results in a mean grid-scale CO2 combustion uncertainty of 18%, though there is greater variability in grid cell uncertainties compared to our other approaches.”: Inclusion of spatial patterns of these uncertainties would be useful in visualizing their distribution and impact on CO2 emissions estimates.