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


RR2
 Reviewer #1 (Remarks to the Author):
 The composite layers although not allowing for a more direct observation of the phonon recycling
 and its harvesting, is a challenging first step in that direction.
 The authors have addressed the comments of this reviewer in a relatively satisfactory manner. So,
 the publication is recommended.
 Reviewer #2 (Remarks to the Author):
Reviewer #3 (Remarks to the Author):
 In the revised manuscript, the authors have carefully addressed my concerns with additional
 experiments and calculations. Although there are some unexpected new findings on the
 dependence of the APR effect on twist angle between WS2 and graphene as well as no observable
 APR in graphene-MoS2 heterostructures, the authors explain with good reasoning. According to
 the revision, I would like to recommend this paper for publication.
  I kindly thank the authors for their in-depth response.
 As well-understood and stated by the authors, my concern is “whether the TA signal at a time
 scale much larger than 10 ps is originated from the pure crystal heating or the phonon-excited
 carriers (acoustic phonon recycling)”, which directly relates to the main claim and originality of the
 manuscript.
 Here I maintain my skepticism. I still believe that the TA signal they observe can be explained with
 pure crystal heating. In fact, using new information they provide, I will quantitatively prove my
 point. In the following I will review the 3 points the authors make in their response:
 POINT 1: I completely agree on their claim that a derivative feature in the TA spectrum is not a
 direct proof that crystal heating is occurring but can be originated by excited charge carriers too.
 Therefore, as they stated, “We need to have more in-depth analyses”.
 POINT 2: The authors make here a fundamental mistake when describing the effect that a spectral
 shift due to crystal heating would have. Indeed, for a small spectral shift, we get a TA spectrum
 that has the form of a derivative where : A) the spectral distance between the PB and PIA peaks
 relates to the width of the original absorption peak and B) the amplitude of the PB and PIA peaks
 relates to the amplitude of the spectral shift of the original absorption peak. The case where
 spectral distance between PB and PIA relates to the spectral shift is for shifts larger than the
 linewidth: this is not the case here and this would yield TA amplitudes close to unity (not the case
 here neither). Therefore, considering the data they provide (in Supplementary Figure 7a), we get
 from A) that the original absorption peak has a width around 20-35 meV, which is the typical width
 they observe in PL for the exciton lines (Figure2), and from B) that the spectral shift increases
 almost linearly with pump fluence, which is expected for crystal heating (with a coefficient around
 -0.3meV/K). Below is a quick modeling I did to better prove my point. I calculated TA spectra
 originating from a Lorentzian line (width of 20 meV, dashed curve) with different spectral shifts
 (noted dE). The typical data they provide can be quantitatively reproduced. Here the amplitude of
 the spectral shifts is below -0.05 meV, which corresponds to a rise in temperature below 0.2K.
 This lattice temperature rise is even lower than the one the authors claim to reach (up to 30K).
 This therefore points out another inconsistency in the overall work that needs to be commented (it
 can be compared to ref Nano Lett. 2017, 17, 2, 644-651, under similar conditions tens of K are
 reached only at short timescale and only few K or less remain after hundreds of ps).
 POINT 3: Here I agree with the authors that many shapes for TA spectra can be obtain when

 considering the electronic excitation, due to the large sensitivity with the materials conditions of
 the many-body effects. This corresponds well to the short timescale signals. Yet I point out that
 the short timescale signals have more variations than the long timescale signals. The latter always
 present a derivative shape, with a PIA at lower energy than the PB. This is compatible with pure
 crystal heating (see point 2) and I guess that even better matching could be obtained if
 broadening of the line due to heating, as well as the evolution (spectral shift and broadening) of
 other exciton lines (neutral and charged), would be considered.
 From this (now quantitative) discussion, a TA signal at long timescale originating simply from pure
 lattice heating cannot be ruled out and would correspond to the simplest explanation. The main
 claim about the observation of APR is therefore not sufficiently supported.
 Considering that my main concern is still open (and even strengthened with now a quantitative
 analysis), I maintain my former opinion: I would recommend NOT to publish the manuscript in
 Nature Communications. Since no better evidence for a “phonon recycling” rather than simple
 lattice heating has be shown, then the manuscript should be heavily modified to present this
 narrower claim. It would eventually transform into an interesting, well documented, study on
 thermal management in 2d heterostructures. I would then be glad to review such revised
 manuscript.