This paper uses real atmospheric observations of ¹⁴C (from flasks) and CO (in situ) that infer ffCO2 values, and convolves them in an atmospheric inversion framework to test the ability of the observations to constrain ffCO2 in an urban area. They demonstrate that even though the ¹⁴C-based ffCO2 observations are more precise, the low sampling density is insufficient to produce robust inversion results.  In contrast, they show that CO-based ffCO2 values with larger uncertainties but far denser observations can produce robust inversion results.  The paper also acknowledges some of the challenges for urban-scale inversions and presents some interesting variations on the atmospheric inversion framework to deal with these.  This includes allowing the inversion to scale only total emissions rather than allowing the inversion to induce spatial variability, and fixing the large point source emissions which are expected to be quite well known.

This is a very nice study and I thoroughly enjoyed reading the paper.  I have a few suggestions for clarification in the text, and my main comment is that the Discussion and Conclusion sections are overly long and largely repeat what is already stated in the Results section.  I recommend shortening and combining the Discussion and Conclusionsections.  I recommend acceptance with these minor revisions.

Specific comments:

Language and grammar: Please check throughout for language and grammar.  I noticed a number of minor errors that should be corrected.

Page 5, line 140.  As we aim to investigate…. This sentence is confusing and should be rephrased.

Page 6 Line 155, last sentence of paragraph is confusing.  Suggest rephrasing to: Times for the hourly-integrated ∆ffCO2 observations are reported as the start of the hour e.g….

Page 6.  Line 170-174.  Is there a possibility of inducing bias by excluding the two sigma outliers?  It is likely that the outliers represent some specific atmospheric conditions such as low wind speeds, which might also imply cold inversions that could have different emissions than other meteorological conditions. 

Page 10.  Lines 246-252.  It is not clear from what is written how the authors can be confident that the a-posteriori flux variabilities must indicate the inversion is wrong, versus the priors being wrong.  Please clarify.

Page 11.  Lines 293-295.  Does this aggregation of observations apply to the following section 3.2?  Or to the previous section?  Please clarify, and if this aggregation applies to section 3.2, I suggest moving this text into the start of that section.

Page 12.  Lines 303-323.  This section awkwardly splits between two paragraphs of discussion in the main text, and referring to figures that are only presented in the appendix/supplementary material.  I suggest substantially reducing the text in the main document and including the longer discussion in the supplementary material.  Alternatively, move the figures into the main document to match the text (although this will make the paper even longer).

Page 13.  Line 356-357.  This sentence needs grammatical correction.

Page 18.  Lines 500-502.  This analysis required guessing what the seasonal cycle might be, which is reasonable for this study.  But would it be realistic to construct a seasonal cycle in the ∆CO/∆ffCO2 ratio by estimating the seasonal contributions of each ffCO2 sector and it’s characteristic ratio?  I’m not suggesting this needs to be done for this study, but it would be a useful recommendation in the conclusions if indeed it is feasible.

Page 16 – 20.  As noted in my general comments, the discussion and conclusions largely repeat each other, and repeat much of what was said in the results section.  I suggest substantially shortening the discussion section and merging with the conclusions section.

Review of Maier et al, 2023, submitted to ACP, by John Miller

“Potential of 14C-based versus ΔCO-based ΔffCO2 observations to estimate urban fossil fuel CO2 (ffCO2) emissions”

General comments:

This paper presents very promising results showing that continuous CO data, when ‘calibrated’ with discrete D¹⁴CO₂ measurements to produce ‘pseudo-continuous’ fossil CO₂ mole fractions (and then averaged over a week to a month) has great potential in estimating urban fossil CO₂ emissions.  To me, this is the most important result from the study and could be emphasized a bit more.  I was impressed by the breadth of sensitivity tests that were conducted, which provide a lot of confidence in the results.  The figures were clear (although I have a few small suggestions, and the writing was generally good; I have included some inline comments to help with clarity and English usage.

I am recommending 'accepted subject to minor revisions', because I don't think that at present any single suggestion I'm making is major, but in totality there are a lot of suggested/requested revisions.  Additionally, as noted below and in the annotated .pdf I am interested to understand why formal random error was not estimated (or at least presented) in this study.  I don't know if incorporating that information would constitute something 'major'.

In addition to my overall positive impression of the paper, I list below numerous general and specific aspects that could (and in some cases need) to be improved.  In no particular order, some general issues:

1. The Discussion section repeats much of what is said just above in the Results section. I personally prefer integrated results + discussion, because I think it is more efficient and (as is the case here) there are inevitably elements of 'discussion' in the results section. Sticking with current format is fine, of course, but the paper would be improved greatly by removing redundancy and focusing the discussion on new ideas and analysis.  As just one example, I would be interested to learn more about what difference between Figs. 3 c and d tell us.  On a related note, it would be interesting to see if you can derive some quantitative results from the large number of sensitivity results run, e.g., sensitivity of posterior to prior uncertainty and some estimate of posterior uncertainty given that this is not otherwise done.

2. There is a lot of faith placed in the TNO inventory without having demonstrated (or discussed this). It implicitly serves as a truth metric. I would feel more comfortable with this if you discussed this explicitly saying that you do in fact treat TNO as a truth metric but also saying why it should be treated as such, especially with respect to its seasonality.

Additionally, there are numerous cases where the interpretation of results assumes the point source emissions to be perfectly accurate (all mismatch being assumed to result from transport uncertainty) and also the assumption that the spatial pattern of the area sources is perfectly known.  These key assumptions need to be acknowledged more clearly, and the fact that they are not perfect assumptions needs to be recognized in the interpretation of results.

3. In general, there is a need for more detail to be included in the paper. A thorough list is provided in line as comments in the marked up .pdf, but I’ll mention some items here as well.

a. I think it’s important to quantify how different versions of the inverse model fit the observations. Reduced chi-squared, std. dev, and mean bias (please separate sd and bias instead of using RMSE which blends these) are important and easy to calculate metrics.  These are especially important when trying to demonstrate things like overfitting.  On a related note, it doesn’t appear to be the case, but were any observations withheld for cross validation?

b. A brief mention of how the non-fossil parts of the radiocarbon budget are treated in the construction of atmospheric CO2ff, especially the nuclear reactor flux of ¹⁴CO_2, would be useful.

c. The inversion methodology deserves some description, mainly basic aspects such as that it is not an ‘analytical’ inversion (i.e. an exact solution to the cost function minimum).

Given the small size of the state vector (the discretization of which would be good to explicitly describe) I would expect an analytical solution would be entirely possible just via a basic matrix inversion.  Is there a reason this approach was not used and the more complicated R2005 approach was?  The main significance is that a fully accurate posterior covariance could have been calculated allowing for presentation of analytically exact random error and also estimation of degrees of freedom, correlations over time, etc.  And even in R2005 (according to my reading of it) a reasonable posterior covariance approximation should be available but none of these results are presented.

While the sensitivity tests address quite a few systematic error issues, it’s unclear why the random errors were not presented.

4. While a small point, I think it’s important to clarify that the Delta(CO)-based method is actually based on both CO and 14C. Without this, readers may think CO and CO₂ alone have the capability to constrain fossil CO₂.

Specific comments are embedded as comments inline in the .pdf.