The manuscript presents the interaction of absorbing and scattering aerosol with PBL under different synoptic patterns based on the observation and WRF-Chem model simulations. It’s an interesting study that help understand how such aerosol-PBL interactions affect the PBL thermodynamics and air quality (PM2.5). This paper also discussed potential impact of synoptic weather conditions on the PBL thermodynamics. Overall, the paper is written well. But, there are some confusions or missing parts that need be clarified.

Specific comments:

1. The paper was lack of describing how aerosols optical parameters (absorption and scattering coefficient) are obtained and constrained in the WRF-Chem model in order to estimate aerosol-radiative-effect (ARE). For instance, how large are those aerosol absorption coefficients for black carbon(BC) abd single scattering albedo (SSA) used?

 2. The paper did not clearly show the PBL-height until they were given in Fig.10 in Page-19. Please describe how the PBL-height is calculated or obtained? Is it based on the Richardson number or potential temperature gradient method, or else? It might be better to display the PBLH in Fig.7 or earlier.

3. The lapse rate is used for many times in the paper. What range of the altitude is it  calculated or referred? In Line 376-377, it is referred the range between 1000 mbar and 850-mbar, but in Line 355it is referred below 1.5 km altitude.

4. Fig. 2 (d)-(e), why are there no temperature and wind data below 750-m from the aircraft observation which are critical to assess the PBL height and thermal stability? Fig. 2 (e), why do the observed wind speeds show so large fluctuations and many stratified structures below 3 –km? 

5. Fig.4, it might be better to give the horizontal wind speed, wind direction and vertical wind velocity on Jan.3 and 4 as shown for the temperature.

6. Fig.6 (a)-(c), what are those the horizontal dash lines? Fig.6, the observed aerosol number density profiles on Jan.3 and Jan.4 show very similar stratification structures below 1 km altitude except higher concentration on Jan.3. Was the aloft aerosol layer at 1.0-1.7 km altitude on Jan.4 related to  the PBL vertical mixing transport? 

7. Fig.8, How do the results show strong heating effects from BC and aerosol cooling effects in the night of Jan 3 and early morning of Jan 4 when there were lack of solar radiance?

8. Line 157, Which metric or parameter is used to quantify PBL thermodynamic stability?

9. Line 265-275, authors pointed out that the PBL thermal stability potentially related to the simulated aerosol vertical distribution in Fig.7, but there are no potential temperature and winds displayed. Please give them for better understanding the discussions in Line 265-275 if possible.

10. Fig.13, how to calculate the standardized anomaly of the wintertime boundary layer lapse rate?

11.Line 289, how do you judge “stronger vertical mixing” on Jan.4 than those on Jan.3?

12. Line 351, “….which are sensitive to the PBL thermal structure.” The phrase “are sensitive to” might be replaced with “affect”.

13. Line 389, please take out the word “systematically”. This study only shows the analysis for the two-day data.

14. The paper only considers the PBL thermodynamics and turbulent mixing related to the lapse rate and temperature variation, but ignores temperature-RH related secondary aerosols formation (SOA) on Jan.3 and 4 such as nitrate and sulfate SOA.

This work investigates the roles of the synoptic pattern, PBLH, aerosol type and vertical distribution in aerosol-PBL interactions by using aircraft measurements, model simulation. Several parallel numerical experiments are conducted to investigate the radiative effects of scattering and absorbing aerosols under different aerosol vertical distributions. Moreover, the long-term variation in PBL stability from 1980 to 2020 over the NCP region is examined. However, the current method and model settings in this work cannot well support the conclusion proposed, and need to be reconsidered. In addition, I personally think that hardly the case study for 2 days with a flawed method can be beneficial in determining which pollutants to target and achieving precise controls of air pollution.  Here list some major concerns that need to be addressed.

Major comment:

The present study focuses on the case on 3-4 Jan 2020. However, the WRF-Chem model simulation was started on 2 Jan with only 16 hours as model spin-up. As well acknowledged, the atmospheric lifetime of aerosol is more than one week. That is to say, such a short spin-up time cannot reflect the aerosol background, chemical environment (OH radical, VOC levels and etc) and regional transport at all. Thus, it is not possible that the secondary scattering aerosol like sulfate and nitrate aerosol was well reproduced. I suggest that the authors either prolong the model time or use the other model output as the chemical initial condition.

Another issue concerning the model simulation is that the model adopted a 3-km grid resolution but used an emission inventory with ~30km grid, which is not very matched with each other in spatial. Please clarify. Besides, since that NCP has experienced significant emission reduction in past years, please specify the base year of the emission inventory that was used in this work.

According to the model settings, the Morrison double-moment microphysics was utilized, which means that the aerosol-cloud interaction has been included in all the simulations. Thus, the differences in these simulations reflect not only the changes in ARE but also perturbations in CCN due to different emission scenarios, for example, EXP_WFexBC, EXP_WF20BC  and EXP_WF20Aer. I recommend the authors reconsider and reinterpret the model result and check if it can support the conclusion.

Since the respective contributions of the absorptive and scattering aerosol are compared, the validations of the aerosol components are suggested to be conducted, especially BC, rather than just evaluating PM2.5. It seems that the aircraft measurement and model simulation are totally isolated in terms of chemical profiles. How did the model represent the vertical profile of aerosols? It would be interesting and imperative to compare the model and the measurements.

As pointed out, the combination of aircraft and model simulation was not so much. I do not think that the simulation needs to confine to these two days. Hardly the case study for just two days can represent the general conditions in this small region. While investigating statistical and general characteristics of aerosol radiative effect, simulation with a longer time period is strongly suggested. Otherwise, the implication of this simulation is expected to be very limited.

Figure 12 is not a good way to show the impact of PBL and pollution. PBLH cannot well reflect the structure itself. And for CO, it is a relatively long-lived species in the atmosphere with a background concentration of around 100 ppb. The short-term perturbations of aerosol on PBL just for two days cannot substantially influence the concentration since the background concentration in the lower troposphere is way larger than the perturbation caused by ARE.

Minor issues:

Table2: NMB makes no sense when evaluating air temperature.

Correct the unit of mass concentration to µg in main figures.

In Figure 13, Label the correlation coefficient and specify the location of LR in the caption. Is b-c  the correlations between ESWM and LR, SH and LR or their anomalies? The data needs to be double-checked.

The study tries to distinguish the aerosol-PBL interaction of absorbing and scattering aerosols under contrasting synoptic patterns and aerosol vertical distributions. They use aircraft measurements model simulations to estimate the aerosol radiative effects over the North China Plain. In general, this manuscript investigated an interesting topic with ample analyses. A concept scheme is further summarized to describe their fundings. However, the significance and representative of this study should be carefully discussed. This manuscript must address several major issues, before the potential publication. 

Major Comments:

1. Based on the model and aircraft data, this manuscript presents a case study for two days. It is questionable whether the conclusions from the case study are representative. The authors even draw a concept scheme from the case analyses. I believe the robustness of the conclusions needs to be carefully discussed. 
2. Only two cases of aerosol vertical distribution are discussed. However, the aerosol vertical distribution varies greatly case by case. It may not be feasible to discuss the impacts of synoptic conditions on the aerosol vertical distribution. It may not be valid to draw a meaningful conclusion about aerosol stratifications and absorptions based on the two cases.
3. There are large diurnal variations in PBL. However, figure 6 only mentions the date. How about the specific time? As aerosol vertical distribution in figure 6 may not represent the daily condition, the authors need to address the diurnal changes in PBL and aerosol vertical distribution. 
4. After the case study, the manuscript presents the long-term variation in PBL thermodynamic stability. However, I feel this part is disconnected from the main analyses. The long-term changes in PBL are affected by numerous factors. I did not find any useful conclusion from the analyses. The analyses also cannot conclude that “the inter-annual variability of the EAWM and SH can influence aerosol vertical distribution and ARE”, which is cited from Section 3.4. 
5. Figure 14 seems to describe common sense. It is well-known that synoptic patterns, PBL thermodynamics, and aerosol vertical distribution can affect each other. What is the significance of Figure 14?
6. Figure 15 tries to summarize the impacts of aerosol on PBL under different synoptic patterns. However, the “cold/warm advection” is only one factor and cannot fully represent the synoptic conditions. Four different scenarios are discussed but do not well support by their analyses.