One of the reviewers suggested further revision of the manuscript. Here is the list of the changes suggested by the reviewer.

1) Page 2, line 24-
The authors summarized previous NPF studies in Beijing well in this paragraph. However, it is not clear yet in the revised manuscript what are different from previous studies and what are scientifically new.
For example, in Page 3, lines 3-6, the authors described as follows: “sulfuric acid and/or organic vapors have been proposed to drive particle growth in different NPF events (Wiedensohler et al., 2009; Yue et al., 2010; Wu et al., 2016). Recently, the formation of NH4NO3 has been proposed as a driver of the rapid growth of newly formed particles in field studies and chamber experiments (Zhu et al., 2104; Man et al., 2015; Wang et al., 2020).” Which parts of this study are different from these previous studies? How was the understanding of NPF in Beijing advanced in this study?
Because the importance of NH4NO3 and organics has already been found in previous studies, the sentence at Page 3, lines 6-7 (“The role of NH4NO3 in the growth of newly formed particles in Beijing remains poorly understood.”) is not enough.

2) Page 5, lines 23-
The SP analysis (this part and section 4.5) should be removed. I cannot understand why the authors can say that the calculated SP is valid for most of NPF events. This analysis implicitly assumes that all atmospheric particles in Beijing are formed during a new particle formation event in Beijing. I think this assumption is unrealistic. Some aerosol particles in Beijing may be preexisting particles (e.g., primary particles, new particles formed a few days ago), transported from other cities, and/or transported from higher altitudes. Although fresh primary particles may be small enough, many particles in the atmosphere (>50 or >70 nm) are probably produced by non-NPF or non-local NPF processes.
This analysis is therefore not valid and should be excluded from the manuscript.

3) Page 6, line 9, equation (5)
Please clarify why Dpg1 and Dpg2 (median diameters) were used instead of observed particle diameters. It is more straightforward to use the observed diameters of the size distribution observations directly rather than using the Dpg1 and Dpg2.

4) Page 6, lines 16-, Section 2.3
The model simulations cannot be used to interpret the relative importance of NH4NO3 and SOA because SOA is severely underestimated. Model simulations and their interpretation should be removed from the manuscript. The main results of this study do not change even if the model results were excluded.
I think the discussion using the model simulations decreases the reliability of the whole results shown in this manuscript.

5) Page 7, line 8
NMB of -39% is probably wrong for SOA when I see Figure S7. Simulated SOA is severely (more than an order of magnitude?) underestimated.

6) Page 7, line 15
Figure S2 can be used in the main manuscript.

7) Page 8, line 8-
Line 10: Fig S3b -> S3c, line 16: Fig S3c -> S3e, line 18: Fig S3d -> S3g, line 20 Fig. S3e -> S3i

8) Page 10, line 26
Fig 2b does not show that sulfuric acid contribution is small.

9) Page 11, line 19-Page 12, line 5
These three paragraphs should be removed as I described in the comment 4.

10) Page 13, lines 5-8
This paragraph should be removed also.

11) Page 14, lines 4-12
Authors explain what was obtained but do not explain why this result was obtained.

12) Section 4.5
This section should be removed as I commented before.

Dear authors, I would like to thank you for addressing all the reviewer's comments. I have a minor comment from my side. When you calculate the survival probability (SP), you are implicitly assuming that the increment of N50-200 and N70-200 are not affected by the boundary layer height (in Fig S2 the N increment overlaps with the decreasing boundary layer height). I would suggest to the authors to comment this point and specify if the SP calculated using such increment is actually an upper bound.