Peer review of: Acoustic phonon recycling for photocarrier generation in graphene-WS2 heterostructures (2020)

RR3
 Reviewer #3 (Remarks to the Author):
 I appreciate the careful consideration of my comments by the authors. The following discussion
 will account for the 2 response letters they provided (on the website and later through direct
 communication with the editor), as well as the revised manuscript and supplementary materials.
 First, I acknowledge my mistake in the quantitative relation between the lattice temperature rise
 and the transient optical signal. I do agree that a 1-2 meV redshift can account for the reported
 experimental signal. What I want to point out is that this shift would correspond to a rise in lattice
 temperature of around 10K which is the one evaluated by the authors from their thermal
 relaxation model. In this view, pure lattice heating is enough to explain this one specific transient
 spectrum (Suppl Fig7).
 I do agree with the authors on their claims : “it is impossible to distinguish the lattice heating and
 phonon recycling effect simply from the shape of TA spectrum” and “an antisymmetric TA
 spectrum cannot provide much information about the underlying mechanism”. But it works both
 ways: the authors cannot use a specific shape of a TA spectrum to completely rule out lattice
 heating. In particular, lattice heating not only induces a redshift, but also a broadening (see Nano
 Lett. 2017, 17, 2, 644-651 for example). Therefore, a spectrally non-antisymmetric transient
 signal does not rule out lattice heating, in contradiction with Point 3 in authors’ response.
 Now I focus on the later received letter. The main point here is that the experimental long
 timescale optical signal is dependent on doping. The authors claim that only phononic excitation
 can account for such a doping dependence. I disagree. Here I point out that neutral excitons and
 trions have a slightly different temperature induced redshift (see https://doi.org/10.1038/s41598-
 017-14378-w in MoS2). More specifically, trions (A- dominant at +50V) have a stronger redshift
 with temperature, and therefore a stronger transient antisymmetric signal, than neutral exciton
 (A0 appearing at -50V). This is in qualitative agreement with the data reported in Figure2 of the
 letter. Therefore, lattice heating alone can also explain the data. Here we end up in the similar
 situation as before where “it is impossible to distinguish the lattice heating and phonon recycling
 effect simply from the shape of TA spectrum” even with a gate dependence (in contrast to what
 the authors claim).
 Finally, the case with MoS2 might be the most convincing one and is treated as is in the
 manuscript (discussion page 7 and Supplementary Section 4 and 8). Yet what is shown is that in
 this specific case there is no crystal heating visible nor phononic excitation effect (explained here
 by the neutral doping). It is quite indirect and stretched to extrapolate this one case for all the
 studied samples. But I acknowledge that this is an argument supporting phononic excitation.
 Let me be clear, I follow the authors in their thermal model which leads to a quantitative
 evaluation of the delayed temperature rise in the TMD lattice after graphene excitation. On itself it
 is already an interesting study given the many systems and configurations they explored. From
 this lattice temperature rise in the TMD, I do not doubt that there is a change the carrier density
 following equation 1 in the manuscript. What I doubt is the authors’ claim that this contribution
 dominates the transient reflection signal. And hence that their results show such a clear evidence
 for acoustic phonon recycling.
 I wish the authors to reflect these elements of doubt in their manuscript.
 I would suggest to slightly modify the discussion in page 7 of the manuscript and in
 Supplementary section 4 following the remarks I made. Also, given the fact that the temperature
 rise is evaluated from their model, and that the related bandshift and broadening is known from
 literature, a fare discussion in Suppl section 4 would be to plot the expected transient signal
 considering only the pure lattice heating. Then the reader could make its own opinion on the
 relative importance of the other electronic effects. If the authors plan to integrate the data and

 discussion in the second response letter (about gate dependence) in their manuscript, I suggest to
 mention the arguments I presented in my answer above. Also, in lines 247 and 308 of the
 manuscript, I do not agree with the formulation “confirms the APR effect” and “undoubtedly
 demonstrates the APR process”. In the related discussions, only a good agreement between the
 calculated temperature rise and the optical signal is demonstrated. Since both lattice heating and
 phononic excitation signals are proportional to the temperature rise, the authors cannot use these
 arguments to support APR only. Finally, the discussion around line 343 about the electrical
 response contribution is quite interesting, yet it is correct only if the optical reflection signal would
 directly indicate the number of carriers that can be extracted from the system. This is not
 straightforward (considering lattice heating can participate in the optical signal) and should be
 clearly mentioned. A study where actual photocurrent is extracted (similar to DOI:
 10.1038/ncomms12174) would be the one way to measure this contribution (and to completely
 rule out my concerns about lattice heating over phononic excitation : I sincerely advice the authors
 to go in this direction for further works since a positive result would have a major impact in the
 field).
 If the authors were to modify as follow their manuscript, I would support the publication of their
 work in Nature Communications.
 If the authors would not follow the lowering of their claim, then it would be on the editor decision
 to accept or not this manuscript.