Peer review of: Non-cooperative 4E-BP2 folding with exchange between eIF4E-binding and binding-incompatible (2020)

Reviewers' comments: 
Reviewer #1 (Remarks to the Author): 

Dawson et al have performed a thorough structural analysis of the effect of phosphorylation of 
eIF4E-binding proteins (4E-BPs) on their interaction with eIF4E. In particular, they demonstrate that 
the binding affinity of 4E-BPs for eIF4E is modulated by the stabilization of a 4E-BP beta-fold domain, 
which sequesters the eIF4Ebinding site, by hierarchical phosphorylation at five sites. The folding is 
non-cooperative, resulting in a tuneable equilibrium between the folded state and a non-folded, 
alpha-helical state. By fully characterizing the effects of each of the five phosphosites, the authors 
could reject a previously proposed model of phospho-inhibition of 4E-BP:eIF4E binding. They further 
demonstrate by bioinformatics methods that two hairpin structures in the beta fold are 
representative of similar structures found in other proteins and can be directly transplanted into 
them to provide phospho-inducible control of protein stability. 

Overall I find the work to be important for settling an unresolved question, and I believe the overall 
conclusions to be sound. It also provides an interesting model case of functional impact of 
hierarchical phosphorylation, notably in an intrinsically disordered protein, which is of general 
interest in protein signaling and regulation. The identification of a transplantable, phospho-
regulatory motif for protein stabilization and degradation would also be interesting for synthetic 
biology. The text overall is clear and easy to understand, despite protein structural analysis being 
outside the scope of my expertise. 


However, I have a few concerns, particularly about the bioinformatics methods used in attempting 
to broaden the scope to other proteins. I will not assess the protein structure analyses aside from a 
couple minor comments. 

1. The description of the bioinformatics methods is frustratingly vague and confusingly worded 

Unfortunately, the methods as written are such that I am not 100% sure that I know what the 
authors did and I would not know how to replicate it. This makes it difficult to assess the methods' 
appropriateness. The rest of the supplementary methods employ clear mathematical formulae and 
occasional textual examples or reasoning, and thus are easy to follow. I think the bioinformatics 
methods should be rewritten in the same manner. 
Unfortunately, as far as I can tell, the code for this analysis is not available alongside the other code, 
which would have helped in interpreting the written methods.  

For example: 

"To control for redundant structures in our dataset we then normalized motif observations by 
calculating the frequency of observation for every unique 11 residue window found in the PDB...This 
results in 8793 unique 11 residue motifs found in hairpin configuration, each scored by the number 
of hairpin observations divided by the total number of matching motif observations in the PDB." 

What does this mean? Is the normalization in the first sentence distinct from the operation 
described in the second sentence or are these one in the same? Am I correct in interpreting 
"frequency of observation for every unique 11 residue window" to mean "position-specific (i-3 to 
i+7) amino acid frequencies for all 11-residue windows from the entire proteome"? What precisely 
constitutes a "hairpin observation" and a "matching motif observation"? Because it is not clear what 
operation is actually being carried out, I do not know how it is proposed to normalize the results in 
order to control for redundant structures. 

 

In the following sentence, "...we took the sum of frequency values...", does "frequency values" refer 
to the ratio calculated in the previous paragraph? 

 

"The hairpin score for a given xxxTPxGxxx or xxxSPxGxxx sequence is then defined as...": according to 
Figure 8A, the authors also observed some aspartic acid, asparagine, cysteine and methionine 
residues in the +3 position. Do these sequences not have hairpin scores then? 

 

In any case, after some deciphering, I gather that the authors are calculating an empirical position-
specific frequency value for each amino acid in hairpin structures. However, I am then completely 
flummoxed by the statement that the scores are defined "by averaging the frequency values of the 
amino acids at each x position over motifs that match either TPxG or SPxG". I can think of too many 
interpretations. Is it simply the mean hairpin-residue frequency for each residue observed in a given 
sequence, not counting positions i, i+1 and i+3? If so, that could be made much clearer through 
simple mathematical notation. 

 

One particular comment is that the word "motif" appears to have multiple meanings across the 
three short paragraphs. I suggest reserving it for one precise case and finding different words for the 
other cases. For example, for "motifs found in Phosphosite database", I think the authors are 
referring to what might more commonly be referred to as "sequence windows" (a single sequence is 
not a motif). Would that not be more accurately worded as "by scoring the sequence windows found 
in the PhosphoSitePlus database that match the xxxTPxGxxx and xxxSPxGxxx motifs, for both the 
human and mouse proteomes"? 

 

2. Common methods already exist for such bioinformatics scoring 

If the above interpretation of the hairpin score (mean frequency value) is correct, I do not think it 
has a solid statistical foundation: each frequency value is drawn from a different distribution 
depending on the position and there is no reason to believe that the results should be normally 
distributed. Plus, some positions are more well-resolved (i.e. more extreme frequency values) than 
others, resulting in a sort of position-based weighting effect. It would make more sense to treat the 
frequencies as empirical probabilities and to formulate the score in terms of probability/likelihood of 
observing a given sequence in a hairpin structure. 

Well-established methods already exist to score a given sequence against a motif in this way. Such 
position-specific scoring matrices (PSSMs, aka position weight matrices or PWMs) have been around 
for decades and have been particularly common since the introduction of PSI-BLAST. 

In this manner, the authors' score should be reformulated either as the product of the position-
specific probabilities of observing each residue in a sequence or (more commonly) as the sum of 
their log-likelihoods (measured against some background/expected probabilities). There are 
countless suitable references, but consider, e.g. Altschul et al. 1997. Nucleic Acids Res. 25(17): 3389-
3402 for an overview or Yaffe et al. 2001. Nature Biotech. 19: 348-353 for an application of the 
method to phosphosite prediction. 

 

Sequence-weighting methods also exist to reduce the influence of redundant sequences when 
calculating empirical residue frequencies. See, e.g., Henikoff & Henikoff. 1994. J. Mol. Biol. 243: 574–
578, which is used in PSI-BLAST and is easy to implement. 


Finally, the information contained in Figure 8A would more commonly be represented as a sequence 
logo (Schneider & Stephens. 1990. Nuc. Acids Res. 18 (20): 6097-6100), which is easily constructed 
via, e.g. WebLogo (Crooks et al. 2004. Genome Res. 14(6):1188-90) or ggseqlogo (Wagih. 2017. 
33(22):3645-7). This would be more informative and quicker to interpret than a frequency heatmap. 

 Using such existing, well-supported methods would be preferable to what appear to be ad hoc 
methods. Otherwise the authors should explain more clearly the reasoning behind their approach 
and why the established, common methods are unsuitable. 

 

3. The hairpin score performance should be cross-validated 

 The authors should assess how well the hairpin scoring method identifies known hairpin structures 
before applying it to new sequences. Otherwise, we cannot know how many false positives to expect 
to find in their results. That, in turn, would provide a way of assessing what a reasonable score 
threshold would be. This could be achieved through a ROC (Receiver Operating Characteristic; false 
positive rate vs true positive rate) analysis and a precision-recall analysis. It should be done under a 
suitable cross-validation regime, e.g. k-fold cross validation, against some negative cases (such as 11-
residue sequence windows matching the [T/S]PxG motif that are known not to be a part of a hairpin 
structure). 

 

4. Minor concerns 

- The authors refer to the "Phosphosite database" (in Results, Supplemental Methods and Figure 8 
legend), which should more accurately be called the "PhosphoSitePlus database". Also, in the 
supplemental methods, the citation for the database is missing. 

 

- I think Figure 6 could be made a lot easier to read and interpret if the "A-M" variant labels along 
the x-axis could be replaced with the protein diagrams from Supp. Figure 6A. 

 

- The Figure 6 legend should note what the uncertainty bars represent. 

 

- Why are different species sets used to illustrate sequence conservation across the different 4E-BPs 
in Supp. Figure 1A? I would expect the same species to be used for each comparison, unless a given 
isoform is not present in some species' genome. 

 

- The authors state that "We find ... phospho-serine is also capable of forming a hairpin, both in the 
independent SPGGT motif introduced in the C-IDR as well as in a ... double mutant". Given this 
statement, the mutational accessibility of serine from threonine, and the alignments in Supp Figure 
1A, I was left wondering why the threoninies at 37/46 are so conserved and serines are not also 

observed in those positions. The answer is buried in the Supplemental Figure 7 legend, where they 
state that the Gly peaks are "not as down-field shifted" in the double mutant as in the WT, 
"suggesting that the latter is more stable". I think that it is important to make this point about 
stability in the main text. 

 

- The heatmap in Figure 8A uses a diverging color scheme centered on 0.5. A linear scheme (e.g. 0.0 
= dark to 1.0 = light) would be more natural unless 0.5 carries a special meaning. 

 

- For Figures 8C & D, the size of the bootstrap sample (i.e. how many proteins sampled per decile per 
iteration) should be reported. 

 


Reviewer #2 (Remarks to the Author): 

 

The authors present an impressive set of biophysical data from an array of different techniques to 
convincingly illustrate a graded regulatory mechanism by which hierarchical phosphorylation 
modulates domain folding stability and conformational ensemble in the 4E-BP2:eIF4E system. This 
works is a nice continuation from their earlier work, and clearly showcases how phosphorylation in 
the C-terminal intrinsically disordered region (IDR) in 4E-BP2 fine-tunes the accessibility of a 
canonical eIF4E-binding motif, therefore affecting the binding affinity of eIF4E. To systematically 
study the effect of phosphorylation, the authors create a number of phosphorylation constructs and 
use a phosphatase control to rule out a remote possibility that the changes in chemical shifts are due 
to Ala mutations. Remarkedly, the authors further show that the same hairpin turn (pTPGGT) can be 
transplanted into other proteins as a phosphorylation-regulation unit, demonstrating the 
generalizability of their finding. Overall, this manuscript is well written, and the finding is important 
and significant. Therefore, in my opinion, this manuscript is suitable for Nature Communication. I 
would like the authors to consider the following minor points to further polish their work: 

1. The authors use several denaturation conditions to study the non-cooperative stability of 
phosphorylated 4E-BP2 by NMR. I notice that a pH titration has been done for the non-
phosphorylated 4E-BP2 in their previous paper (ref 17). However, to enable a direct comparison, I 
suggest the authors perform at least one identical denaturation experiment to the non-
phosphorylated 4E-BP2 by NMR. Alternatively, they can measure DSC for the non-phosphorylated 
4E-BP2, which could match to Figure 7C for FAF1. 

2. The authors calculate the Rosetta minimization energies for the 4E-BP2:eIF4E structures with and 
without phosphorylation, and conclude that the electrostatic differences cannot explain the binding 
behavior. Due to the inherent dynamic nature of the binding process, this conclusion solely based on 
computation is not quite convincing. I suggest the authors corroborate this by measuring the Kd of 
4E-BP2:eIF4E interaction as a function of salt concentration. 

3. The authors should clarify how the error was calculated for experimental observables throughout 
the manuscript. For example, the errors in the apparent pKa, Kd, R_H, and FRET <E> efficiency. Are 
they based on the bootstrap errors calculated for the bioinformatic estimates in Figure 8 or 
experimental errors? 

4. Maybe it is helpful to label both the N and C ends as well as G39 and G48 in the structure in Figure 
2 for a better readability. 

5. The authors should define the “apparent pKa” plotted in Figure 2A for residues that are not two-
state folders (i.e., residues fitted with more than one pKa). 

6. The spectra in Figure 7A and D are too small to see clearly. 

7. In order to derive Eq. S12, the orientation factor Kappa is assumed to average out during smFRET 
and necessary control experiments will be needed to justify it. Since Eq. S12 was not used in any 
figures, I suggest removing Eq. S12. 

 
Reviewer #3 (Remarks to the Author): 

Dawson et al describe studies of non-cooperative folding of different phosphorylation isoforms of 
eIF4E binding protein (4E-BP). They find that phosphorylation induces partial folding of 4E-BPs that 
hinders 4E-BPs binding to eIF4E. Although the authors use an impressive array of assays, from my 
point of view, current manuscript adds little to the authors’ previous publication (Bah, A. et al. 
Nature 2015) and is more suitable for publication in more specialized journal than Nat Comm. 


In addition, the manuscript is written in cumbersome and intricate way. It contains multiple 
examples of convoluted sentences that are hard to follow (e.g. P. 11 “This indicates that the average 
distance between residue 32 in the folded domain region and residue 91 in the C-IDR increases upon 
two-phospho-induced folding and again upon stabilization of folding, consistent with helical 
conformations sampled in non-phospho 4E-BP2 bringing dyes at residues 32 and 91 into close 
average proximities, and increasing phosphorylation shifting the conformational equilibrium towards 
more extended, β-strand-like conformations that pull the dyes farther apart”). 

Some interpretations of experimental data are also convoluted and seem questionable. For example, 
shifts in FRET toward lower values observed in the presence of GdmCl are interpreted as evidence of 
protein unfolding while shifts in FRET toward lower values observed in the absence of denaturants 
are interpreted as evidence of folding. If 4E-BP folding and unfolding produce similar changes in 
distribution of FRET values doesn’t it make this FRET assay uninformative and uninterpretable?