Report on the manuscript of acp-2022-729 titled “Unbalanced emission reductions of different species and sectors in China during COVID-19 lockdown derived by multi-species surface observation assimilation” written by Kong et al.

This work estimated multiple emissions using the EnKF with the state augmentation method during the COVID-19 pandemic. Then, they assessed the unbalanced emission reduction of different species during the restriction. The manuscript is well organized and contains detailed analysis. However, the authors have some issues to be clarified in the manuscript for the final publication in ACP.

Specific comments

1. Line 91 & 285 (Weak motivation): The EnKF coupled with the state augmentation used in this study could be a more advanced method than inversed single estimation (Zhang et al., 2020; 2021, Feng et al., 2020, & Hu et al., 2022) in terms of emission estimation for multiple species. However, it could be less cost-effective. Also, as mentioned in the manuscript (line 285), it shows a similar performance with the single estimation of SO₂ (Hu et al., 2022). In other words, the inversed single estimation can be better, considering both performance and computational cost. Therefore, considering these issues, the authors need some more explanation or justify the use of your method to enhance the motivation for this work.
2. Line 126: The authors need to clarify how to consider the non-linearity between NOx emission (for estimation) and NO₂ concentration (of observation). Additionally, in-situ NO₂ observation may be based on the commercial chemiluminescent instrument. While the instrument system converts NO2 to NO through a molybdenum converter, other species, such as peroxyacetyl nitrates (PANs) and HNO3, are also simultaneously converted to NO. The other species account for a large portion of the converted NO molecules. For example, Dunlea et al. (2007) showed the interference in the chemiluminescence detection accounting for up to 50% of ambient NO₂ In other words, the observed NO₂ is almost equivalent to ambient NO_y. Also, PAN is thermally sensitive (and it is also related to the temperature shown in Figure 10). The rapid decrease in NO_x emission is strongly linked to this issue. Therefore, the authors also need to explain how to treat these issues in your calculation.
3. Line 90: Levelt et al. (2022) is not related to the emission inversion technique. The authors had better discard this paper in the manuscript.
4. Line 105: Anthropogenic and other emission inventories used in the simulations during the COVID-19 pandemic are based on 2010 or relatively long ago. These emission rates could be significantly higher than those during the COVID-19 pandemic. The higher emission rates are significantly related to the concentration of atmospheric species like O₃. Therefore, the authors need to justify the uses of such emission inventories in the simulations.
5. Line 138: The explanation of EI and MI (from both MET and EMIS change scenarios) is rather complicated. The authors need to clarify it. Tabulating or illustrating the scenarios or cases makes it easier for the readers to understand them.
6. Line 218: The authors need to define P1, P2, and P3 on Line 218, not on Line 247. Also, the authors need to add some lines for P1, P2, and P3 on the x-axis of Figure 4.
7. Line 268: The performance in the O₃ simulation is relatively poor. As mentioned in the manuscript, the lower performance is related to VOC emission. Since the VOC emission used in the simulations is made for 2010, there are some time gaps. Therefore, the authors need to compare the VOC emission rates with the recent or 2019 database and then make an additional explanation of (expected) ozone concentrations.
8. Line 289 & 303 – 304: The authors need to explain what causes increases in PM₁₀ during the P3 in Figure 4, Figure 5e, and 5f. The authors explained these are related to the sandstorm. However, the concentration of PM₁₀ during the P3 period was rather low in the NW and Central regions.
9. Line 295: The explanation is not sufficient for the PM_2.5 emission increase in the NCP region. The observation done by Dai et al. (2020) was carried out at a single site in Tianjin.
10. Line 340: The authors also need to mention that the O₃ is under-simulated in all regions (refer to Figure S6).

Minor comments

11. Line 32: measurement -- > measure or measures
12. Line 33: remove ‘both’.
13. Line 261. It is probably Table S1, not Table S4.
14. Lines 277 and 280: The authors need to confirm the numbers in these lines (and Table 2).

REFERENCE

Dunlea, E. J et al.: Evaluation of nitrogen dioxide chemiluminescence monitors in a polluted urban environment, Atmos. Chem. Phys., 7, 2691–2704, 2007.

This manuscript evaluates the changes in air quality during the COVID-19 lockdown by dividing them into meteorological and emissions parts. The authors specifically assessed the impact of emission reduction during the lockdown using a multi-air pollutant inversion system and observational data, which is a unique approach compared to previous studies. The findings from this study will be valuable in evaluating the effectiveness of emission reduction policies by policymakers in polluted regions, including China. However, to be published in ACP, the authors must address the following issues:

Line 39: During the COVID-19 period, a haze event also occurred. However, the use of the term "COVID-19 haze" may convey the notion that the pandemic was the cause of the haze phenomenon. Thus, the authors should choose terms more carefully.

Lines 128-129: Despite removing unrealistic observations through the Wu et al. (2018) method, some extreme values persist in the time-series plots (e.g., Figures 3(b), S1(b), and S2(b)). Hence, the authors should thoroughly verify that the raw data has been properly filtered.

Lines 208-242: (Section 2.4) The authors assess both the MI and EI approaches for decreasing nonlinear effects. If the extent of nonlinearity (or sensitivity) demonstrated by the two methods is documented in the paper, it can provide a helpful reference for future research.

Lines 302-304: The authors posit that the rise in PM₁₀ emissions in the NW and central regions during P3 is due to sandstorms but do not provide clear evidence. Furthermore, the simulation using a priori in the central region does not show a significant deviation from observation. Thus, the authors must provide further evidence for the sandstorm hypothesis.

Line 306: east China -> southeast China

Lines 311-312: There is a change in the values of SO₂ and PM₁₀.

Lines 313-315: The authors suggest that CO emissions decline significantly, as CO's transportation share (18%) is higher than SO₂ (5%) and PM_2.5 (6%) (as shown in Figure 4). However, the percentage decrease in emissions is insignificant (-10.6% vs. -9.7% and -7.9%, as shown in Table 2). Furthermore, while the transportation share of PM₁₀ emissions is only 2%, the emission decrease is -12.1%, which is greater than that of CO. Hence, other factors beyond transportation may have influenced the reduction in anthropogenic emissions during P2. Therefore, the authors should clarify their results.

Lines 317-318: The values given are incorrect (e.g., SO₂ is 77.6%, not 86%).

Lines 329-389: (section 3.3) The results presented by the authors, such as the significant contribution of meteorological fields to PM_2.5 during the pandemic and the titration effect on O₃, have been reported in previous studies. Hence, the authors should distinguish the difference between their results and previous studies using numerical values.

Lines 340-341: The relative overestimation of ozone is not clear. Please provide a specific value. Also, Figure 7 is not related to this.

Lines 359-361: The author's assertion that the rise in PM_2.5 levels in the Beijing region is mainly due to fireworks during the Spring Festival is not supported by sufficient evidence, as there is no evidence that the increase in fireworks emissions is unique to Beijing.

Line 441: Some subscripts are misspelled.

Lines 460-461: Is the unit for ozone also µg m^-3?

Line S36: Figure S4 -> Figure S7