Review of "How atmospheric CO₂ can inform us on annual and decadal shifts in the biospheric carbon uptake period" by Kariyathan et al.

The authors have conducted a sensitivity analysis of the carbon uptake period (CUP) in the atmospheric CO₂ mole fraction to understand how changes in the CUP in net ecosystem exchange (NEE) are reflected in the observed atmospheric mole fraction. Using a series of model simulations, they examined how atmospheric transport and interannual variations in NEE contribute to changes in the CUP in the atmospheric CO₂ mole fraction, focusing on 10 observations sites across the northern hemisphere. The authors showed that interannual variations in atmospheric transport provides a significant contribution to changes in the mole fraction CUP. They found that changes in NEE are manifested as damped variations in the CO₂ mole fraction, suggesting that the use of observations of changes in the mole fraction CUP to quantify changes in NEE will likely result in an underestimate of the changes in NEE. The authors have developed an interesting approach for assessing the impact of changes in NEE on the atmospheric CO₂ mole fraction that would be a valuable contribution to the literature. However, as discussed in my comments below, these results are not surprising. I have some concerns about the observation sites that were selected for the analysis and the resulting conclusions. I would like to see the authors address these concerns before the manuscript can be considered suitable for publication.

Main comments

1. The authors are using 10 observation sites in the northern hemisphere to assess the sensitivity of changes in the CO₂ mole fraction to variations in NEE. However, the sites that were selected are those that capture mainly background CO₂. As the authors noted, the CO₂ model fraction at these background sites "represent the balance between surface emissions and uptake from land and ocean… over large spatial scales," so it is not surprising that these sites will capture a damped manifestation of the changes in NEE. At the end of Section 4.2, the authors stated that "CO₂ observations should preferably be interpreted following a formal inverse estimate of the corresponding surface NEE. It is then possible to account for the inter-annual variability, trends and delays imposed by the slow atmospheric mixing." However, inversions using the remote background sites also have difficulties in providing robust estimates of regional changes in NEE because of the influence of transport and mixing. This is one of the main reasons there has been significant effort focused on expanding the observing network. It is reasonable to ask how would the results of the study change if different sites were selected? For example, would Hegyhatsal (HUN) in Hungary be more sensitive to variations in changes in European NEE? Would East Trout Lake (ETL) in Canada be more sensitive to North American boreal fluxes? There is clearly a need to avoid sites that are strongly sensitive to anthropogenic emissions, but are the 10 sites used in this study the best sites for capturing changes in NEE given the well-known confounding influence of transport and mixing? As a modeling study, it seems to me that the authors have the opportunity to better evaluate the sensitivity of the existing observing network rather than that of what seems to be an arbitrary selection of 10 sites in the network. 
   
   
   
   Another issue is that the authors are using the temporal frequency of the flask measurements, but that is quite coarse – it is at best weekly. Some sites provide continuous measurements. Is there any benefit to using continuous data for capturing the variations and trends in NEE?
2. The analysis uses the ensemble of the first derivative (EFD) method to estimate the CUP. This approach was described in Kariyathan et al. (2023), but there is no explanation of the method in this manuscript. The reader is forced to go through Kariyathan et al. (2023) to understand what is being done. A brief description of the approach in the current manuscript would be helpful to the reader.

Other comments

1. Table 1 caption: I believe the subscript refers to the CUP_NEE, so the caption should read "subscript and superscript of the last character denote CUP_NEE and variability (V) in transport, respectively."
2. Line 90: Please change: "we used experiment ENV₀⁰ and LNV" to "we used experiments ENV₀⁰ and LNV."
3. Line 100: Please list the regions over which the fluxes were aggregated.
4. Lines 137-143: Should Figure 3 be referenced in the text here? I don't believe the figure is actually referenced in the manuscript.
5. Figure 4 caption: On the second line, change "left panel shows" to "left panels show". On the third line form the bottom, change "right panel ((d) to (f)) shows" to "right panels ((d) to (f)) show".
6. Line 218: It would be helpful to see what are the results for the other sites. Can this be presented in a separate table?
7. Lines 226-227: It is unclear that it is the trend from the IAV in transport that "leads to the asymmetry". Perhaps this should be phrased as "the trend from the IAV in transport contributes to the asymmetry."
8. Line 300: This description is confusing. Transport from Europe, Russia, and boreal Eurasia is westerly, so it is confusing when the authors say that "air mass transport is largely over the Northern Atlantic Ocean and does not extend into the continents in some years." During summer, because of the warm surface it is difficult for air transported from Europe and boreal Eurasia to enter the Arctic at low altitudes, so this circumpolar westerly transport occurs at lower latitudes, reducing the sensitivity of the high-latitude ZEP site to Eurasian air masses. I believe that the authors are trying to say that because of the lower latitude circumpolar transport in summer, the sensitivity of the ZEP site to variations in surface CO₂ fluxes in summer is confined to the Arctic and does not extend equatorward into the continents.

 Summary:

The authors present a modeling study to determine how much surface flux information is contained in the atmospheric CO2 mole fraction observations. They see how well they can recover the time duration when net ecosystem exchange is uptake by the northern hemisphere biosphere from the seasonal cycle of atmospheric CO2 mole fraction observations after running surface fluxes and anomalies through an atmospheric transport model. They show that the surface flux signal information is reduced by mixing in the atmosphere.

Major comments:

1. The authors motivate this study by a few published studies of changes in the atmospheric CO2 mole fraction seasonal cycle used to infer northern hemisphere surface flux changes without explicitly considering atmospheric transport. This feels like a strawman. The community already acknowledges the influence of atmospheric transport when linking concentrations to surface fluxes. That is why atmospheric inverse techniques were developed decades ago. Jin et al. (2022) provides an example of a study that uses an atmospheric transport model to separate the influence of surface fluxes and winds on the seasonal cycle at Mauna Loa without using an inverse approach. The references therein identify other studies that also make the point that atmospheric CO2 mole fractions are influenced by fluxes and winds. The authors’ most important sentence buried in the middle of the discussion is the main point of this study. “Therefore, CO2 observations should preferably be interpreted following a formal inversion estimate of the corresponding surface NEE. It is then possible to account for the inter-annual variability, trends and delays imposed by the slow atmospheric mixing.” I’m not sure what new perspective this study adds.
2. Furthermore, the way that the wind influence is described as “the integration of signals with varying CUPNEE timing across regions” and “variations in the timing of CUPNEE across different regions from where the signal is integrated” and in Fig 9 is confusing. They are describing the influence of atmospheric transport or winds, but making it sound like it’s a flux synchronization issue.
3. Other studies have mostly focused on CO2 seasonal cycle amplitude changes and this study’s focus on the duration of the carbon uptake period is a little unique. But this study does hypothetical forward model experiments without using the observed atmospheric CO2 mole fractions to constrain which fluxes anomalies are supported by the observations, if any. What new information about the behavior of the northern hemisphere biosphere is learned here? The authors state “Considering the {transport} reducing factor, a change of approximately 0.7 days/year might be occurring in the surface fluxes.”
4. The nomenclature for the experiments makes it difficult to look at a figure and quickly interpret which experiment combination of fluxes and winds it is comparing. The reader must work very hard to understand and remember the notation. Table 1 helps, but does it have to be that complicated? It seems the paired notation of the Experiment and Delta CUPNEE columns are needed to uniquely identify the tests, especially with ENVTo and LNVTo cases.
5. Misleading title? The finding was that obs can’t inform well on surface fluxes, without considering atmospheric transport.

References:

Jin, Y.,  Keeling, R. F.,  Rödenbeck, C.,  Patra, P. K.,  Piper, S. C., &  Schwartzman, A. (2022).  Impact of changing winds on the Mauna Loa CO₂ seasonal cycle in relation to the Pacific Decadal Oscillation. Journal of Geophysical Research: Atmospheres,  127, e2021JD035892. https://doi.org/10.1029/2021JD035892