Disordered proteins interact with the chemical environment to tune their protective function during drying

Reviewer #1 (Public Review):

Summary:

The individual roles of both cosolvents and intrinsically disordered proteins (IDPs) in desiccation have been well established, but few studies have tried to elucidate how these two factors may contribute synergistically. The authors quantify the synergy for the model and true IDPs involved with desiccation and find that only the true IDPs have strong desiccation tolerance and synergy with cosolvents. Using these as model systems, they quantify the local (secondary structure vis-a-vi CD spectroscopy) and global dimensions (vis-a-vi the Rg of SAXS experiments) and find no obvious changes with the co-solvents. Instead, they focus on the gelation of one of the IDPs and, using theory and experiments, suggest that the co-solvents may enable desiccation tolerance, an interesting hypothesis to guide future in vivo desiccation studies. A few minor points that remain unclear to this reviewer are noted.

Strengths:

This paper is quite extensive and has significant strengths worth highlighting. Notably, the number and type of methods employed to study IDPs are quite unusual, employing CD spectroscopy, SAXS measurements, and DSC. The use of the TFE is an exciting integration of the physical chemistry of cosolvents into the desiccation field is a nice approach and a clever way of addressing the gap of the lack of conformational changes depending on the cosolvents. Furthermore, I think this is a major point and strength of the paper; the underlying synergy of cosolvents and IDPs may lie in the thermodynamics of the dehydration process.

Figure S6A is very useful. I encourage readers who are confused about the DSC analysis, interpretation, and calculation to refer to it.

Weaknesses:

Overall, the paper is sound and employs strong experimental design and analysis. However, I wish to point out a few minor weaknesses.

Perhaps the largest, in terms of reader comprehension, focuses on the transition between the model peptides and real IDPs in Figures 1 and 2. Notably, little is discussed with respect to the structure of the IDPs and what is known. Notably, I was confused to find out when looking at Table 1 that many of the IDPs are predicted to be largely unordered, which seemed to contrast with some of the CD spectroscopy data. I wonder if the disorder plots are misleading for readers. Can the authors comment more on this confusion? What are these IDPs structurally?

Related to the above thoughts, the alpha fold structures for the LEA proteins are predicted (unconfidently) as being alpha-helical in contrast to the CD data. Does this complicate the TFE studies and eliminate the correlation for the LEA proteins? Additionally, the notation that the LEA and BSA proteins do not correlate is unclear to this reviewer, aren't many of the correlations significant, having both a large R^2 and significant p-value?

The calculation of synergy seems too simplistic or even problematic to me. While I am not familiar with the standards in the desiccation field, I think the approach as presented may be problematic due to the potential for higher initial values of protection to have lower synergies (two 50%s for example, could not yield higher than 100%). Instead, I would think one would need to really think of it as an apparent equilibrium constant between functional and non-functional LDH (Kapp = [Func]/[Not Func] and frac = Kapp/(1+Kapp) or Kapp = frac/(1-frac) ) Then after getting the apparent equilibrium constants for the IDP and cosolvent (KappIDP and KappCS), the expected additive effect would be frac = (KappIDP+KappCS)/(1+KappIDP+KappCS). Consequently, the extent of synergy could be instead calculated as KappBOTH-KappIDP-KappCS. Maybe this reviewer is misunderstanding. It is recommended that the authors clarify why the synergy calculation in the manuscript is reasonable.

Related to the above, the authors should discuss the utility of using molar concentration instead of volume fraction or mass concentration. Notably, when trehalose is used in concentration, the volume fraction of trehalose is much smaller compared to the IDPs used in Figure 2 or some in Figure 1. Would switching to a different weighted unit impact the results of the study, or is it robust to such (potentially) arbitrary units?

Reviewer #2 (Public Review):

Summary:

The paper aims to investigate the synergies between desiccation chaperones and small molecule cosolutes, and describe its mechanistic basis. The paper reports that IDP chaperones have stronger synergies with the cosolutes they coexist with, and in one case suggests that this is related to oligomerization propensity of the IDP.

Strengths:

The study uses a lot of orthogonal methods and the experiments are technically well done. They are addressing a new question that has not really been addressed previously.

Weaknesses:

The conclusions are based on a few examples and only partial correlations. While the data support mechanistic conclusions about the individual proteins studied, it is not clear that the conclusions can be generalized to the extent proposed by the authors due to small effect sizes, small numbers of proteins, and only partial correlations.

The authors pose relevant questions and try to answer them through a systematic series of experiments that are all technically well-conducted. The data points are generally interpreted appropriately in isolation, however, I am a little concerned about a tendency to over-generalize their findings. Many of the experiments give negative or non-conclusive results (not a problem in itself), which means that the overall storyline is often based on single examples. For example, the central conclusion that IDPs interact synergistically with their endogenous co-solute (Figure 2E) is largely driven by one outlier from Arabidopsis. The rest are relatively close to the diagonal, and one could equally well suggest that the cosolutes affect the IDPs equally (which is also the conclusion in 1F). Similarly, the mechanistic explanations tend to be based on single examples. This is somewhat unavoidable as biophysical studies cannot be done on thousands of proteins, but the text should be toned down to reflect the strength of the conclusions.

The central hypothesis revolves around the interplay between cosolutes and IDP chaperones comparing chaperones from species with different complements of cosolutes. In Table 1, it is mentioned that Arabidopsis uses both trehalose and sucrose as a cosolute, yet experiments are only done with either of these cosolutes and Arabidopsis is counted in the sucrose column. While it makes sense to compare them separately from a biophysical point of view, the ability to test the co-evolution of these systems is somewhat diminished by this. At least it should be discussed clearly.

It would be helpful if the authors could spell out the theoretical basis of how they quantify synergy. I understand what they are doing - and maybe there are no better ways to do it - but it seems like an approach with limitations. The authors identify one in that the calculation only works far from 100%, but to me, it seems there would be an equally strict requirement to be significantly above 0%. This would suggest that it is used wrongly in Figure 6H, where there is no effect of betaine (at least as far as the color scheme allows one to distinguish the different bars). In this case, the authors cannot really conclude synergy or not, it could be a straight non-synergistic inhibition by betaine.