This manuscript discusses oxygenated volatile organic compound emissions and sources in the Berkeley/Oakland area of California. The authors tied together both flux tower measurements and mobile monitoring in this study to investigate emissions and sources of ethanol, methanol, acetone, and acetaldehyde with significant depth. They assessed the role of cooking in contributing to ethanol and acetaldehyde emissions, and the contributions of VCPs for acetone and methanol. They concluded that the total oxygenated volatile organic compound contribution to total measured VOCs was 70% of molar flux, 69% of measured mixing ratios, and 27% of calculated OH reactivity, with ethanol standing out as having the highest mixing ratio and flux of the focus chemicals. They also performed some comparisons of their flux measurements with the GRA2PES inventory and showed good agreement for ethanol sources but not with emission factor estimates for ethanol. Emission factor estimates for acetaldehyde and methanol similarly had poor agreement with GRA2PES, with the inventory generally overestimating emissions. This was a strong paper and is a good fit for the journal. I have a few minor comments and suggestions, which are listed in detail below.

Methods: Minor clarifying questions.

Line 104-105: When you say roughly the same roads were sampled for each domain, do you mean roughly the same roads daily, or across some other unit of time?

Line 218: It would help readers to provide slightly more detail about how the flux footprints were computed rather than relying too much on the cited literature, and also to potentially move this discussion closer to the occurrence of Figure 1 where the flux footprint first appears.

Line 133: Can you clarify how many times per day was the grid cell sampled (as you mention that you report the median of daily means)?

Line 139-140: Can you provide some additional justification, validation, or references for this definition of background concentration used?

Generally: How were isobaric interferences accounted for in the PTR-MS measurements (e.g., for acetone measurements, did you make any assumptions about the contribution of propanal?)?

Results and Discussion:

Line 234: Any speculation as to why there was no significant correlation between OVOC fluxes and temperature? Can you show this explicitly in a figure (perhaps in the SI)?

Figure 2: It would help to note the year on top of each bar for readability.

Figure 3: I wonder if this could be merged with Figure 4 so that the reader can directly compare the chemical fluxes in Figure 4 with the environmental parameters shown in Figure 3. This would also address my comment above with respect to line 234 (of showing temperature and fluxes explicitly together).

For the literature cited for ethanol to nonanal ratios in lines 219 to 323, two of the papers measure indoor mixing ratios and one measures outdoor. While each of these observations is valuable in constraining the possible range of ratios, what caveats need to be considered when interpreting the indoor values when considering outdoor measurements? I.e., other confounding sources of these chemicals either indoors or outdoors?

Generally: can the authors address, in a paragraph, any impacts of the flux tower and mobile measurements not being temporally aligned, and also any considerations regarding the only 12 days of mobile measurements included (and thus some commentary on how representative these are)? If possible, I wonder if some kind of figure similar to Figure S6 with the range of mobile measurements overlaid on the flux tower data would help establish the relationship between the two data sets (in terms of their relative mixing ratio ranges and relative levels between observed chemicals).

Figure 9: Can the authors provide a few more example time series to show spike correlations? Over what timescale is the co-occurrence quantified (i.e., do the peaks need to co-occur over the course of a few seconds like the SI example shows (Fig. S4)? Few minutes? And does the length of time remain consistent across spikes defined as “correlated”?)?

Line 679-680: This is a really important and big point that feels glossed over at the end (about the inventory/measurement comparison being more accurate for lower population density grid cells and potential associated issues with population density scaling). Can the authors elaborate slightly more here? This sounds like an excellent future work direction.

General Comments

Katz et al. combine a very unique long-term eddy covariance (EC) VOC flux dataset with mobile observations to investigate the sources and spatial variability of ubiquitous OVOCs in Berkeley and Oakland. This is a valuable dataset, and the combination of tower and mobile measurements provides rare and much needed insights into urban VOC emissions and the representativeness of the tower footprint for those that are locally derived with the EC method. The large contribution of ethanol to the measured VOC flux is consistent with observations from other urban areas, and the flux-based source apportionment provides an important complement to the many published concentration-based apportionment studies.

My main concern is that some of the quantitative source apportionment results are presented with more confidence than the current analysis supports. In particular, many estimates rely on inventory- or observation-derived scaling factors and source ratios without fully evaluating the associated uncertainty. The comparison with GRA2PES is also useful, but some of the apparent agreement is not fully independent, and several conclusions about the causes of model-measurement differences seem stronger than the available evidence. Overall, I think the manuscript is suitable for publication after the authors provide additional sensitivity and uncertainty analyses and soften several of the source-specific and inventory-comparison conclusions. I hope the comments below are helpful in strengthening the analysis and interpretation.

Specific Comments

Lines 98: Some more experimental methods could be helpful here. Can the authors please provide some additional information about the mobile platform and inlet, including the inlet length and location relative to the vehicle, whether the reported tubing diameter is the inner diameter, and the flow rate through the tubing.

Lines 117-118: Some experimental details should also be included here. How were zeros produced (cylinder, heat platinum catalyst, etc.), and were calibrations performed using serial dilutions with multiple concentration steps?

The text says the calibration factors and zeros were stable, but it would be helpful to provide a quantitative value for what that stability threshold was such as typical variability or maximum deviation within a sampling day.

Lines 120-121: How was the default kPTR value determined, and what compounds were used to derive it? Please also provide an uncertainty for the default sensitivity, like a range of potential values based on observed or representative species.

Lines 133-134: How was the 200 x 200 m grid cell size selected, and was the sensitivity of the spatial patterns to this choice evaluated? In other words does this resolution average over important sub-grid variability? The grid size may not strongly affect comparisons using the overall climatological footprint, but it could matter if individual averaging period footprints are considered in this analysis.

On a related note, reporting the 50% relative standard deviation in daily means is good but I also think that there should be a more quantitative presentation of the relationship between high RSD and VOC emission hotspots.

Lines 142-144: The spike-correlation analysis is interesting, but correlated signals within a short time window may represent transport of a mixed source plume rather than necessarily direct co-emission, so I suggest using “correlated” or “coincident” spikes unless co-emission can be more directly established. Is there any example figure like Fig. S4 where there are some spikes for a group of compounds with a common source and no spike for a group or VOC from a different source?

Please also clarify whether ions known to be fragments of the same parent compound were excluded from the correlation analysis, since shared fragmentation could otherwise produce high correlations that do not represent separate co-emitted compounds. It seems like correlation analyses were only used for calibrated species known not to be fragments?

Lines 152-153: While it is mentioned that additional information is available in the Katz et al. (2025) reference, some experimental details relevant to the EC measurements should be mentioned here. For example, the inlet length, inner diameter of the tubing, flow rate, and approximate inlet residence time should be provided here. Further, what was the calculated high frequency attenuation (Horst, 1997; DOI: ⁠10.1023/A:1000229130034) and random uncertainty (Langford et al., 2015; https://doi.org/10.5194/amt-8-4197-2015) for select VOCs?

Line 168: The manuscript assigns 50% uncertainty to compounds using the default sensitivity, but Katz et al. (2025) states that this value was assumed. How was the 50% value determined?

Line 171: How large was the isoprene fragmentation correction, either avg. magnitude or % correction during day and night?

Also, was interference of ethanol fragments in the acetaldehyde signal quantified? The Coggon et al. (2024b) reference goes through this correction.

Lines 189-190: Why was a 60% stationarity threshold selected rather than generally recommended 30%? If the covariance changes substantially within an averaging period, the calculated flux may combine different turbulent, footprint, or source conditions and may not represent a single steady-state period. This seems particularly relevant in a heterogeneous urban footprint with intermittent emissions. Are the main source-apportionment results sensitive to a stricter threshold?

Lines 192-193: What were the typical lag times and did this align with what was expected for a calculated inlet residence time? Were these calculated lag times still robust in the evening and early morning when covariances are typically low and approach the noise?

Line 266: The authors suggest that lower winter ethanol fluxes may partly result from enhanced wet deposition. Do the authors mean enhanced dry deposition and/or uptake to wet surfaces rather than wet deposition? Could this proposed mechanism be evaluated using exchange velocity, dew point departure, surface wetness, or another available metric?

Lines 300-305: The relationship between nonanal flux and the number of open restaurants provides useful supporting evidence, but both quantities have strong diel patterns. I think the diel profile needs to be removed or accounted for before this correlation is interpreted. For example, the authors could compare anomalies at the same hour on different days or normalize the flux using sensible heat, friction velocity, or another measure of turbulent transport. Further, was the number of open restaurants determined dynamically within each half-hour footprint or within the overall climatological footprint? Those might provide different results and interpretations.

Line 326: Did the authors mean that cooking intervals are when ethanol/benzene are greater than 0.01? I would expect cooking periods to be when ethanol is high, but benzene is low, and even then I would think it’s much more than 0.01. Please clarify this threshold.

Line 327-328: The rationale for using the lower portion of the ethanol-nonanal relationship seems reasonable, since additional ethanol sources should only move points above the cooking relationship, and the similar slopes from the 5th to 20th percentiles provide a useful sensitivity test. However, I am still not fully convinced that the lower edge necessarily gives a representative ethanol/nonanal ratio for cooking. Even if the measurement uncertainty, cooking period selection, and binning are all reasonable, couldn’t the lower edge still be influenced by differences among cooking sources or by non-cooking sources of nonanal? It would be helpful to show whether the slope is similar across different wind sectors, times of day, seasons, or reasonable cooking selection criteria, or by using quantile regression on the unbinned data. That range could then be used to show how sensitive the reported cooking contribution is to this assumption.

Line 349: The VCP+ category is calculated as the residual after subtracting cooking and vehicle emissions. As described in the manuscript, it may include alcohol consumption, biogenic emissions, unaccounted sources, and errors in the other estimates. I think there should be some presentation of an independent tracer showing that VCPs dominate this term or it should be called “other” or “residual” to avoid being misleading. The statement that these sources are difficult to quantify also seems somewhat inconsistent with presenting this residual as a quantitative VCP contribution later on in the text.

Lines 368-375: The vehicle contribution is estimated using an ethanol/benzene ratio from GRA2PES, and the resulting source apportionment is then compared with the GRA2PES source fractions. The agreement in source fractions is therefore not fully independent, at least for the vehicle contribution, and I think this should be acknowledged.

Lines 384-387: The GRA2PES ethanol emission in the lower population northern grid cell is closer to the tower observations, but I do not think this comparison alone demonstrates that the population-density scaler is overestimated. Even if population scaling is the main reason the inventory differs between these two cells, the tower does not measure the northern cell, so the comparison only shows that a lower modeled emission magnitude agrees better with the observations. I think the language should be softened unless there is other supporting evidence.

Lines 581-585: The acetaldehyde cooking estimate uses an acetaldehyde/ethanol ratio of 0.06, while the literature values span 0.03-1.33. Can the authors provide more context for this range? For example, how are the reported values distributed, and do they vary systematically with the food or cooking method? The finding that ratios above 0.1 produce more cooking acetaldehyde than the total measured flux provides a useful upper constraint, but it does not by itself establish that 0.06 is the most appropriate value. Since the reported 57% contribution depends directly on this ratio, please show how the estimated cooking fraction changes across a reasonable range of ratios and reflect this uncertainty in the reported contribution.

Lines 588-589: The combustion contribution also depends on inventory-derived acetaldehyde/benzene ratios. Please provide a reasonable uncertainty range for these ratios and show how it affects the reported 23% combustion contribution.

Lines 593-603: The correlation between the residual acetaldehyde flux and PPFD is interesting, and I appreciate the calculation and consideration of below-sensor gas-phase chemistry, but I do not think it is sufficient to identify photochemical degradation of surface materials as the source. Why was PPFD used rather than a surface UV measurement that is more directly related to the proposed process? Could thermal degradation also contribute to this process, which would be consistent with cooler surfaces in the winter? Is there evidence that ambient aerosols or urban surfaces can produce acetaldehyde under atmospherically relevant light and temperature conditions through heterogeneous chemistry?

Fig. 11: The interannual variability in both the cooking fraction and the magnitude of the acetaldehyde flux is notable. Can the authors provide some potential causes these differences? Are they related to differences in restaurant activity, wind direction and footprint, the estimated ethanol/nonanal ratio, or meteorology? This variability should be discussed because it affects how confidently the campaign-average source fractions can be interpreted.

Minor Comments/Technical Corrections

Line 186: This is a really minor comment but the text says meteorology inputs were 20 Hz but the sonic data was actually downsampled to 10 Hz before calculating the covariance, correct?

Line 191: There is an extra “all” in “All data is all on Pacific Daylight Time.”

Line 302: Please correct “they was highest” to “were highest”.

Line 355: F(EtOH,cooking) should be subtracted, not added if this is a residual.

Line 417: I know what the authors mean but it may be more straightforward to say a 200 x 200 m grid rather than “200 square meter grid” since it’s technically not 200 m2.

Lines 421-422: The sentence stating that the tower could be “missing key sources of ethanol” could be made more clear. I think the intended point is that the footprint does not include some important regional hotspots, rather than that the local flux measurement is somehow incomplete.