Peer review of: DIP/Dpr interactions and the evolutionary design of specificity in protein families (2020)



Reviewers' comments: 

Reviewer #1 (Remarks to the Author): 

My comments from the first round of review have mostly been addressed. 

However, if I understand the newly included explanation of the experimental error analysis 
correctly, then the reported Kd values are misleading. Very small errors are reported that are the 
fitting error from two technical replicates from re-measuring *the same samples* (in reverse 
order). This does not provide an estimate of measurement error. I.e. this error estimate does not 
account for any pipetting error in constructing the concentration series, error in sample stock 
concentration determination, or in batch-to-batch variation. It doesn't control for grabbing the 
wrong tube. It seems that the authors are drawing quantitative conclusions from measurements 
that were performed once, controlling only for things like instrument drift. 

Also related to the experimental binding curves, this statement (new in this version) is not 
sufficiently specific, and it is not clear if what was done in curve fitting is justified: 
"In cases where the highest analyte concentration is only around the KD, we use the Rmax value 
for a saturating binding isotherm shown on the same plot, as a global Rmax, to fit the binding 
isotherms for weaker interactions and calculate a KD." By “on the same plot” do the authors mean 
that, e.g., for Figure 3C the saturated value for wild-type Dpr10 was used for all Dpr10 mutants? 
Is there evidence this is valid? Was the same thing done to compare curves with different mutant 
proteins on the surface (e.g. Supp. Figure 1)? This requires an assumption of similar loading from 
experiment to experiment because the same surface isn’t being re-used. This requires better 
justification. 

Given the way that the Kd values were generated (no real replicates), the errors are certainly 
much larger than what is reported. A few values could be grossly wrong. There is a serious risk to 
this subfield that these values will be accepted as “real” and propagated in the literature. 

There are two possible routes forward: 

(1) Much preferred: Perform replicate experiments (ideally at least 3 total replicates from different 
days/pipetting series) and report measurement errors that allow an assessment of what 
comparisons are justified 
(2) If replicates can’t be performed for some reason: Because the overall conclusions of the paper 
do not depend critically on any single measurement, and there are trends in the data that suggest 
that many of the authors’ predictions/residue assignment are valid, the authors could make it very 
clear that they are basing their conclusions on approximate/estimated Kd values from single 
measurements that have not been reproduced. In this case, a clear caveat should appear in the 
main text, and all tables/figure legends should refer to the values as “estimated Kd values” and 
use some symbol like Kd* or Kd_est. There is a concern that the appropriate caveats associated 
with these values will be lost in future work, if they are cited, but at least an attentive reader who 
checks the original source will be alerted to the uncertainty. 

In general, there is now greater clarity with respect to what was done in the computational work, 
but there are still some places where the wording is insufficiently precise. I recommend another 
round of careful editing (also to fix typos). 

Two examples that were added in this version are: 

(1) the description of the 3 cases for the evolution filter on p. 29 and following is not sufficiently 
precise that one could write code to reproduce the values (it is ambiguous what "we summed the 
instances where amino acids at a position of subfamily “i” (aai) were different in biophysical 
property from aaj" means. Though the general gist of the approach is clear, it would be better to 

give an equation, since one cannot understand from what is written what set of "instances" was 
summed over. This doesn’t affect the main conclusions. 

(2) this sentence was very difficult to parse: 
To justify this, we calculated the pairwise sequence identities within Insecta orthologs for each DIP 
and Dpr, and the intra-subgroup pairwise sequence identity for each DIP and Dpr Insecta subgroup 
(~78%) using multiple sequence alignments of interfacial residues." How are "the pairwise 
sequence identities within Insecta orthologs for each DIP and Dpr" (no value given) different from 
"the intra-subgroup pairwise sequence identity for each DIP and Dpr Insecta subgroup (~78%)." 
This doesn’t affect the conclusions but is confusing. 

Reviewer #3 (Remarks to the Author): 

I appreciate the author's effort in addressing the comments from all reviewers. I feel the 
manuscript addresses these concerns. In particular, I will address a few points that I made and 
how I feel the authors appropriately modified the manuscript: 

1) It is more clear to me that the biggest innovation of the article is the use of homology models in 
computationally determining protein interaction specificity. I appreciate the difficulty in producing 
accurate homology models and then testing these for specificity determinants. The only questions 
that remains for me is whether FoldX calculations for interactions from homology models are 
worse than for FoldX calculations for actual structures. Answering this would address whether 
homology models are sufficient for determining protein interaction specificity. 

2) I appreciate the inclusion of Supplementary Table 3, which expands the analysis of specificity to 
include those that were previously studied. 

3) I now appreciate that the DIP/Dpr interactions are less specific than Dscams or protocadherins 
and look forward to the groups future work on understanding how the level of specificity affects 
phenotype. I think inclusion of a deeper comparison to specificity of Dscams and clustered 
protocadherins could help put this work in better context for the reader. The authors mention 
(lines 467-472) that specificity is spread across multiple domains in these families, which results in 
greater specificity. This result is addressed specifically in several publications that are not cited. 

4) On the issue of the number of negative constraints needed, I appreciate the inclusion of 
Supplementary Table 4, which describes the negative constraints they found. I also now 
understand that no two sets of negative constraints are the same between any two non-cognate 
pairs. 

Finally, here is a minor change to the corrections: 

Line 52 (and others): Drosophila melanogaster ('m' should not be capitalized)