Thank you for the detailed consideration of the reviewer comments from the first set of reviews at ACPD. I appreciate the checks of key data against independent instruments. I believe this article should be published after minor revisions as outlined below.
Major issues
1. The discussion of increased biogenic VOC and increased HOM, due to afforestataion, as the reason for the observed changes in the apparent formation rate of 10 nm particles is speculative. It should be labeled as a hypothesis. Currently, it is written as if it is a conclusion. It is prominent in the abstract, and in the conclusions. There are qualifications in the paper, but they are not given the prominent placement and strong language that the “conclusion” that BVOC and HOM due to afforestation are a causative agent to the features seen in the manuscript. The BVOC/HOM hypothesis, and its tie to afforestation, should be confined to the discussion and clearly labeled as a hypothesis supported by some suggestive evidence. The evidence presented is insufficient to support it as a firm conclusion.
2. The language around the increase in VOC overplays the scientific strength of the underlying data. “large increase” (line 20), “rapid afforestation” (line 21), biogenic emissions “changing significantly” (line 75), “rapid increase in BVOCs and their oxidized products as nucleating precursors” (line 94), “difference was highly consistent with the large increase in forest area” (line 365). The authors think it very important that we believe this is a large, rapid, and statistically significant phenomenon. This requires data, not words. The actual data this is based on is much more modest than the language used to describe the VOC changes – and is not actually quantitatively stated in the paper. The percentage increase in springtime BVOC emissions due to land use change is never stated in the paper. It is difficult to determine from the cited works too (discussed below).
The evidence is limited to the land use map (figure S2) where the increase in tree cover is substantial but not overwhelming, and not consistent in all directions. There are the canister measurements (see comment 3). And there are citations; but actually reading Ma et al. (2019), it is difficult to tell how much the BVOC increase was relative to baseline, where it is happening, and during what seasons it is important. Ma et al. is focused on attributing ozone concentrations during a heat wave to BVOC emission changes that are the result of a heat wave, urban forestry, and land use change. The ozone changes are extensively discussed, the relative change in VOC emissions due to land use change are much less discussed. The delta emissions are mapped in Ma et al. (2019), and appear to be minimal at the location of Mt. Tai. Wang et al. (2020) is also not that supportive. The map shows the delta of carbon fluxes most concentrated well to the south of Mt. Tai, and the time series of above ground biomass increases from 40 to about 43 over about 20 years, or about 0.3% increase per year. A large carbon sink, but not support for “rapid increase in BVOCs and their oxidized products as nucleating precursors.” Finally, in the introduction to Ma et al. (2019), another work is cited with increase due to climate change and land cover change may be 1-1.5% per year. This is substantial, and over 11 years could lead to a ~15% change in average regional emissions – I think to claim this is “large and rapid” is stretching and distracts from the strength of the paper, which is the data itself, and the careful calculation of the nucleation and growth parameters.
3. The difference in VOC concentrations between June 2006 (7.0 ± 5.7 ppb) and spring 2018 (16.1 ± 6.5 ppb) is weak and needs further discussion, probably in a supplement – or possibly removal. It is apparently by different research groups, with methods that are not only briefly presented to the reviewers. The time of day of sampling, sampling strategy, and specific compounds are not mentioned and could easily explain the difference. These need to be analyzed properly as an honest species-by-species comparative analysis to tell if there are statistically different concentrations of individual matched biogenic and anthropogenic VOCs – or it needs to be removed. Verification is needed that the samples are appropriately paired (location, time of day, air quality meteorology, season). Taking summer data for comparison to spring data is problematic. In its current form, the discussion of the VOC results seems like data cherry picked to support the predetermined conclusion of an increase in biogenic nucleation precursors, rather than an true hypothesis test.
Comment followed by questions 4-7: The exclusion of 3 channels of the SMPS for 30% of hours during the final two campaigns is a big change. I note that it decreased the condensational sink in 2018 by a factor of two. Leaving aside how such a prominent feature could escape the initial QA/QC of the team, the fact that there is now verified instrument error in the 2017 and 2018 campaigns creates an additional requirement for clarity and transparency in the handling of the data. Unfortunately, without knowing more about the root cause for the spurious intermittent counts, it is difficult to trust the remaining 2017 and 2018 dataset. I feel this is important because the 100-300 nm section of the size distribution has a substantial portion of the condensational sink. I note there is what may be a specious peak at 100 nm in Figure S4, which corresponds to the prominent peak at 100 nm in figure S8 and S9 for most of the 2017 and 2018 data. I also note that the PM2.5 vs. WPS reconstructed PM2.5 relationship degrades over time from its best case performance in 2015. The argument that we have increased nucleation rates, lack of growth of nuclei to CCN sizes, an increase in condensational sink, a substantial increase in the size distribution function at 100-300 nm, and a large decrease in PM2.5 mass – this combination is difficult to explain, even by a large increase in HOM that that fuel nucleation but not substantial growth. In my opinion, it requires a source of 100-300 nm particles – either from changes in primary emissions in the region, changes in air pollution meteorology, or instrument error. The authors argue that the time periods are climatologically representative, so that leaves only changes in primary emissions, or instrument error.
Specific questions related to this:
4. Was exclusion of three channels around 213 nm enough? Were all the needed times excluded? What was the test used to determine if a period was to have those channels excluded?
5. How is the QA/QC and the replacement of data with smoothed interpolated data marked in the files that are now publicly available? This needs to be clearly explained in the supporting data files.
6. Show, in addition to the number count vs. number count comparison of instruments (Figure S3), the size distributions functions for hours where both instruments ran collocated. Comparing the number counts rather than the size distributions can hide substantial problems. Do the size distributions match, or does the WPS have some extra peaks? This would be a strong indication of the quality of the size distributions shown in Figures S8 and S9, and the condensational sinks and other parameters calculated from them. The size distributions should be shown with no data removal, and then with the removal/smoothing of suspect malfunction channels/peaks.
7. The secondary peak at 100 nm in Figure S12 is quite striking. With a height of dN/dlogDp at 15,000 cm-3, and nearby minima at 5,000 cm-3 at 30 nm and at 250 nm, it really is a very sharp feature. Given problems at 213 nm, what checks were made to make sure this peak is real? The feature in Figure S12 is correlated with the PFGE, but abruptly disappears when instrument trouble strikes at 18:30, as indicated by the blue lines at 213 nm. There is also a faint indication of a “band” at 100 nm in Figure S4 for some 2018 data (and the data in question has acknowledged problems at 213 nm) – and it is appreciable in size, reaching dN/dlogDp at 10,000 cm-3. Such sister peaks appear in some PFGE datasets due to collocated sources of nucleation precursors with Aitken/accumulation mode particles; but such sister peaks seem (at least on average) absent from the Mt. Tai data prior to about 2017. For example, such a sister peak at 100 nm is totally absent in the 2014 figure shown (S12e).
My questions: after Figure S12 (or Figure S4) has gone through the exclusion process for the 213 nm 3-channel problem, is all the remaining data considered valid? What checks were made to make sure this 100 nm peak, growing in prominence in 2017 and 2018 (the same time as the 213 nm problem appears), is real? Do the other continuous instruments (for figure S12) support the existence of the 100 nm feature prior to 18:30. If from a primary source for the 100 nm mode, there is often correlation with PM2.5, CO2, EC, NOx, CO, and/or SO2. Is there an abrupt air mass change for S12 at 18:30 needed to support disappearance of virtually all particles? Presumably this is change from upslope (polluted) air to free tropospheric air. But now with the instrumental problems appearing in 2017 and 2018 – every opportunity to show instruments working properly and reporting valid data should be taken advantage of.
Minor issues
8. Figure S12 seems to be prior to the data manipulation around 213 nm.
9. Figures S8 and S9 should have y axis as dN/dlogDp so that they can be more easily compared to the other figures in the paper that use dN/dlogDp and to other publications. Using dN as the y axis makes the height dependent on the bin spacing.
Ma, M., Gao, Y., Wang, Y., Zhang, S., Leung, L. R., Liu, C., Wang, S., Zhao, B., Chang, X., Su, H., Zhang, T., Sheng, L., Yao, X., and Gao, H.: Substantial ozone enhancement over the North China Plain from increased biogenic emissions due to heat waves and land cover in summer 2017, Atmos. Chem. Phys., 19, 12195–12207, https://doi.org/10.5194/acp-19-12195-2019, 2019.
Wang, J., Feng, L., Palmer, P. I., Liu, Y., Fang, S., Bösch, H., O’Dell, C. W., Tang, X., Yang, D., Liu, L., and Xia, C. Z. Large Chinese land carbon sink estimated from atmospheric carbon dioxide data, Nature, 586, 720-723, https://doi.org/10.1038/s41586-020-2849-9, 2020. |
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