Peer review of: Cathode engineering with perylene-diimide interlayer enabling over 17% efficiency single-junction (2020)



RR2
Reviewers' comments:
Reviewer #1 (Remarks to the Author):
  After revision, several critical scientific issues in my previous review have been explained in the
 revised manuscript, including the demonstration of the chemical interaction between Y6 and PDINN,
 reasons for the enhanced FF acquired by PDINN devices, and the device stability issues. There are
 only a few minor modifications remaining to be done before the paper being formally published, which
 are as follows.
 (1) The authors mentioned that ‘This phenomenon is likely related to the hydrogen bond formed
 between the secondary amine in the aliphatic amine groups of PDINN with the active layer surface as
 suggested by the variable-temperature and titration 1H NMR experiments conducted with PDINN and
 Y6 in solution (Supplementary Figure 6). The 1H NMR signal at δ1.54 (assigned to hydrogen in the
 secondary amine) broadened and downfield shifted, which provide a clear evidence that PDINN forms
 a stronger hydrogen-bond with Y6 in the solution’ (page 7, line 140-145). In fact, the 1H-NMR signal
 at δ1.54 in Supplementary Figure 6a may be assigned to the trace H2O in solvent CDCl3. While adding
 small portion of PDINN in the Y6/CDCl3 solution, signal at δ1.54 broadened and shifted to low field,
 this could result from the Hydrogen bonding either between PDINN and trace H2O or between PDINN
 and Y6. So, it is better to combine the following (ATR) FT-IR measurements and 19F NMR spectra
 characterizations to draw the conclusion instead of directly drawing conclusion like that in (page 7,
 line 140-145).
 (2) The (ATR) FT-IR measurements and 19F NMR spectra characterizations in the revised manuscript
 (page 7-8, line 146-160) is positive to prove the possible chemical Hydrogen bonding between PDINN
 and Y6. I would thus suggest the authors directly comparing the FT-IR spectra of PDINN and
 PDINN:Y6 in the Supplementary Information to more clearly demonstrate the difference and to prove
 the possible chemical Hydrogen bonding PDINN and Y6.
 (3) The authors added that the air stability of PDINN-based devices were much more superior to their
 PDINO counterparts (page 20, line 386-389), please explain a little bit about this phenomenon. Also, it
 is better to give the detailed test environment of the air stability in this paper, such as the
 temperature and relative humidity.
 (4) Among the top electrodes mentioned in this manuscript, Al electrode-based devices show the best
 performance when adopting PDINO as CIM (Supplementary Table 4), while Ag electrode-based device
 stand out when using PDINN CIM (Supplementary Table 5). These intriguing results still lack
 reasonable explanations. This issue has been pointed out as Q5 in my previous review comments, but
 was not reasonably explained in the revised manuscript.
 Reviewer #2 (Remarks to the Author): Regarding the response 2-1),
  Contrary to the PDINO, the PDINN has enhanced adhesion even with the strong polar substituents and
 this factor seems to be the most important in your report. Therefore, you need to show exact
 quantitative or numerical data on the adhesion degree of PDINO and PDINN. The adhesion is
 correlated to surface tension as you mentioned. You can get ‘work of adhesion’ using ‘Owens-Wendt
 model’ [1].
 [1] L.Q.N.Tran et al., Understanding the interfacial compatibility and adhesion of natural coir fibre
 thermoplastic composites, Compos Sci Technol 80, 23-30 (2013).
 
This reviewer was satisfied with the other responses. Thank you. Reviewer #3 (Remarks to the Author):
Reviewer #4 (Remarks to the Author):
  I read the response letter and feel that the authors have addressed the comments from previous
 reviewers.
  The authors did a great job in taking into account most of the issues raised by the reviewers.
 Therefore, the manuscript may be suited for publication in Nature Communications provided that a
 remaining issue can be properly addressed.
 I am still not convinced by the description of the TA experiments and the conclusions drawn from
 these experiments for the following two reasons.
 Assignment of the transient absorption spectra: According to the newly added Figure S14, the
 transient absorption spectra consist of two spectral regions where the pump increases the
 transparency of the sample (at 600 nm – 670 nm and between 820 nm and 880 nm), while there is a
 pump-induced decrease of the transmission in the remaining part of the spectrum. It is often proposed
 that an increased transmission is due to a ground state bleach (GSB), which is expected to show its
 maximum signal where the ground state absorption is largest. This may explain the strong positive
 signal at ca. 637 nm (where PM6 shows a strong absorption) but not of the second positive peak at
 850 nm (because Y6 has its absorption maximum at 800 nm). On the other hand, a photoinduced
 decrease of transmission is by the absorption of newly created photogenerated species, such as
 excitons, polarons etc (excited state absorpton, ESA). The text assigns the peak at 633 nm to a
 charge separated state and that at 770 nm to “the ESA” signal. What exactly is meant with charge
 separated state and why does it cause the peak at 637 nm. Why did the authors chose to plot the ESA
 at 780 nm, and why is the temporal decay of the ESA (apparently) different at e.g. 950 nm? The
 authors are asked to extend the discussion of the spectral features in the TA spectra and their specific
 decay properties.
 Interpretation of the transient properties: The transient data in Figure 3b,c and in Figure S15 display a
 continuous decrease of the signal over several microseconds, and this decrease becomes accelerated
 at higher fluence. I agree with the authors that this long term decay is dominated by bimolecular
 recombination. But what is not clear to me is the sudden (early) decay of the transient signal in the
 sample with PDINO. The authors propose that this decay is due to trapping of charges at surface traps.
 I see two problems with this interpretation. First, if the signal at 633 nm stems from the ground state
 bleach on PM6, why would trapping of charges (by e.g. impurities and surface defects) restore the
 original PM6 absorpton properties. Instead, trapping would slow down the return of the
 photogenerated electron back to the polymer backbone, thereby prolonging the signal decay. Second,
 the timescale of this early decay is 10-30 ns. If this decay would be due to charge carrier trapping at
 surface states, a considerable fraction of photogenerated electrons and/or holes must be able to travel
 to the surface. Since there is no electric field applied, this motion must be due to diffusion. I strongly
 doubt that the diffusion of electron and holes in the PM:Y6 blend is fast enough to allow them
 travelling to the surface within few tens of nanoseconds. Therefore, the authors need to carefully
 reconsider their interpretation.