Editorial: constructive disagreement

“Although I remain highly sceptical about this approach, I want to see this work published” (Reviewer 1)

There is a common conception that peer review is a trial to be endured, where faceless reviewers seek to arbitrarily shoot down manuscripts protected by a screen of anonymity, or where pedants complain about comma placement or that the manuscript isn’t written exactly how they would have written it. At Supramolecular Chemistry, we are fortunate to be able to draw on a pool of active supramolecular chemists who, in my experience, tend to give constructive and high-quality reviews. A recent paper in the journal from the Eggers group is an interesting example of this [1]. The paper concerns a model for fitting host–guest binding data and was published even though both referees were sceptical about the validity of the model used. In this Editorial, I provide a brief overview of this particular peer review process, with the full set of reviewer comments and the authors’ responses to these provided as an Appendix.

In 2013, Castellano and Eggers reported that the free energy of binding of Ca²⁺ to EDTA obtained using isothermal calorimetry (ITC) measurements varied significantly depending on concentration, in apparent contradiction of classical thermodynamics [2]. They described their results using an equation that included an experimentally accessible term for the change in solvation energy that occurs on guest binding. In so doing, they suggest that energy changes between host-bound water molecules and ‘bulk’ water are not accounted for in activities used in classical thermodynamic calculations, and so incorporate the term ΔG_H2O to describe the energetic contribution of the solvent. This approach has subsequently been used by the groups of Eggers [3] and Piguet [4–6] to study metal complexation, but its validity has been questioned by others [7].

In their recent paper, Eggers and co-workers used this approach to study the binding of guest molecules to three macrocycles, β-cyclodextrin (β-CD), cucurbit[7]uril (CB7) and p-sulfonatocalix[4]arene (SC4) by isothermal calorimetry (ITC) [1]. They found that guest binding to CB7 and SC4 displayed a reasonably strong concentration dependence, while no such dependence was observed for binding to β-CD. The authors then discuss the significance of their results, and their implications for how we should understand the hydrophobic effect.

The manuscript was first submitted in February and reviewed by two referees, who both gave detailed and high-quality reviews. Reviewer 1 broadly supported publication but wanted the raw data made available and noted: ‘Let me just also put it out here that, although I remain highly sceptical about this approach, I want to see this work published because this is a very important debate for the community to have and what the authors are proposing here … is not in my opinion out of the question.’

Reviewer 2 suggested ‘reject and resubmit’ based on scepticism about the model used and additionally queried how some of the binding studies had been conducted. They were confident that the ITC experiments had been conducted with ‘technical proficiency and supported by a proper error analysis’ but felt that ‘the variation of the obtained K_a value at different concentrations – a trend observed by both us and others – can be interpreted without the necessity for additional terms in the Gibbs equation for these specific systems.’

While coming to different conclusions in their reports, both reviewers agreed that the manuscript contained interesting and insightful science, although both were unsure about the model used. The lead author was contacted with a request for major revisions and informed that a revised manuscript would be sent out for review, with the original reviewers used again if they were available. The authors subsequently submitted a significantly revised manuscript, which addressed Reviewer 2ʹs concerns about how some studies had been conducted, and included additional discussion of the interpretation of the ΔG_H2O term. This was sent back to the same two reviewers.

Reviewer 1 was again sceptical of the model, but supportive of publication and requested some minor changes. Reviewer 2 also requested some minor changes but was now supportive of publication, stating ‘The authors have made a commendable effort in meticulously addressing the extensive concerns initially highlighted by the reviewers. Although I maintain my stance that the experimental data is not yet robust enough to definitively confirm or reject the proposed model, I find myself aligning with Reviewer 1ʹs viewpoint. This study indeed puts forth an intriguing theory that warrants exposure to the wider chemical community for their critical evaluation. I personally found Reviewer 1ʹs feedback to be insightful, and the authors’ response to the comments, thoughtful. It could be beneficial to include these exchanges alongside the manuscript for added context and transparency. Despite these additional suggestions, I am in support of publishing the manuscript in Supramolecular Chemistry, given the potential impact of the proposed model and the discussion it will incite within the field.’

Based on these comments, a request for minor revisions was made. These were made rapidly and the manuscript accepted without further review.

So, is the use of an explicit solvation term valid? Personally, I don’t feel qualified to comment on this. However, I agree with both reviewers that it’s a discussion worth having. Hopefully, the reviewers’ comments and the authors’ response to them included as an Appendix at the end of this Editorial add further context and nuance to this discussion. More generally, I think this is one of the beauties of the journal: it’s a venue for supramolecular chemists by supramolecular chemists. Hopefully, it’s a place where these kinds of debates can play out in the future.

Acknowledgments

NGW thanks the two anonymous reviewers for their detailed and insightful comments and the authors for their constructive engagement with these comments.

Appendix

The authors and both anonymous reviewers have consented to this material being published.

Very minor edits to spelling or type-setting have been made for clarity. In one case, a confidential figure from an upcoming publication from the Eggers group has been removed.

First round of review and author responses

REVIEWER 1

Reviewer 1: The Eggers group reports here on their study into the solvation term/solvation effects on a number of exemplary host-guest systems in water.

This paper follows from their work (Castellano & Eggers, J. Phys. Chem. B, 2013, 117, 8180; Eggers et al. J. Phys. Chem. B, 2020, 124, 6585) that controversially as the authors acknowledge also here ‘is the system truly non-ideal, or is it the governing equation that is non-ideal.’

Comment 1: Putting it perhaps differently if I may, ‘maybe we have been wrong about how important activities and non-linear solvation effects, etc, are in aqueous systems – it can all be explained with a relatively simple and insightful additional term for solvation as per equation 3 in this paper.’ Or is this misunderstanding what the authors are trying to do?

Authors: We have kept our originally worded question in the introduction. We want it to be clear to the reader that we do not believe the phenomenon responsible for the value of ΔG_H2O has any connection to changing reactant activities as a function of concentration; we view the solvation term as the outcome of a linked equilibrium that is not accounted for by the classical equation (because there is no term that captures the change in chemical potential of the water molecules released to the bulk phase). One reason for our strong belief that the reactant coefficients are constant is the fact that an interaction between two reactant molecules in a millimolar solution should be a rare event when compared to the number of reactant–water interactions. For example, at our highest reactant concentration of 10 mM, the ratio of water molecules to reactant is ~55 M/0.010 M or 5500:1. It seems unlikely that reactant–reactant (self) interactions will lead to altered activity coefficients under the conditions employed in this study.

On a side note, we do believe that one can intentionally alter the reactant activities by adding a secondary solute at a high molar concentration (and we plan to share our results for such conditions in a future manuscript).

Reviewer 1: Before going further – let me just also put it out here that, although I remain highly sceptical about this approach, I want to see this work published because this is a very important debate for the community to have and what the authors are proposing here (and in Castellano & Eggers, J. Phys. Chem. B, 2013, 117, 8180 and Eggers et al. J. Phys. Chem. B, 2020, 124, 6585) is not in my opinion out of the question. More importantly, even as an ‘empirical’ model, the way this approach tries to quantify solvation effects would be quite useful to compare various supramolecular systems irrespective of whether we agree with the authors on the deeper meaning of the ΔG_H2O values obtained. This paper is a case in point as the ΔG_H2O varies significantly and heads towards zero for the β-CD systems which is quite interesting.

Authors: We thank Reviewer 1 for their open mindedness. Scepticism is always a good thing in science. In fact, it was our scepticism in how physical chemists explain the effects of secondary solutes on binding and conformational equilibria (especially protein folding) that motivated us to pursue this research direction in the first place! Related to the ‘deeper meaning of ΔG_H2O,’ and prior to receiving these reviews, we appended the Supporting Information file with a 1-page note on the interpretation of ΔG_H2O that discusses how ΔG_H2O represents ALL linked reaction equilibria that are not accounted for by the term -RTlnK. This realisation occurred after thinking more deeply about the results of Claude Piguet who has applied our equation to his (more complicated) binding experiments with lanthanides in organic solvents. His calculated solvation term, ΔG_S, almost certainly reflects other linked equilibria in addition to the release of solvent (but we will save that discussion for another day, another manuscript).

Reviewer 1: However, before the paper can be published there are a few comments (apart from Comment 1) that I think the authors need to address. Some relate to clarifications. But many also relate to lack of data. In this day and age, for such an important study, the authors should really provide much more details on their calculations and when possible provide access to raw data files. This will allow others to check some of the assumptions that underpin this important work. And it is good practice according to F.A.I.R. data and other common Open Science standards.

Authors: Agreed. See below.

Reviewer 1, Comment 2: Please include all key calculations and data files by depositing them on Github, Figshare or a similar free-to-access server and include the reference to this in the SI. This includes: i) Provide all raw ITC files so others can analyse them including the control runs (so others can see what effect a background subtraction would have if done instead of a constant background). ii) If possible, also the ‘output files’ from the MicroCal program used. iii) Provide all the MatLab files used, especially the code. iv) Details on the WolframAlpha files, codes. Especially the details on the real root found in the two site systems.

Authors: We are working now with our university librarian to post the requested files in the corresponding author’s ScholarWorks page, alongside a link to the published article (if accepted). As this is a highly time-consuming activity, we plan to limit the ITC files to one sample run for each host-guest pairing at each concentration; the raw data file, control file, and MicroCal-generated results will be shared (60 files total). The MatLab codes and details will also be available.

Because the ScholarWorks page is under construction, we have added the following Data Availability statement after the Disclosure Statement in the revised manuscript: ‘Data files that support the findings of this study are available from the corresponding author, DKE, upon reasonable request.’ If the ScholarWorks link is ready when the proofs are shared with the corresponding author, he will insert the URL at that time.

Reviewer 1, Comment 3: Page 6 – eq 3. [AB]_eq is the equilibrium concentration of the host-guest complex at any point of the titration, which will vary as the titration ‘progresses’. So how is Figure 1 then generated? I don’t understand what the x-axis is meant to be unless the values from the second column in Table S1 are used (0.087, etc., instead of 0.1) but what is the rationale behind them?

Authors: We do, in fact, use the concentration that corresponds to the limiting reactant at the 1:1 ratio point in the titration. We now (attempt to) explain our reasoning in a new Discussion section with a new figure that employs a modelling approach to show how K changes during the progress of a titration experiment for different values of ΔG_H2O (Fig. 4a). We also kept the corresponding ITC simulation graph of enthalpy versus molar ratio (Fig. 4b, shared as Fig. 2b in the original manuscript). A key point is that the value of K is nearly constant beyond the 1:1 titration point because the concentration of bound complex is nearly constant beyond this point (approaching 100% of the limiting reactant). Thus, at least 50% of the titration curve (and 50% of the MicroCal analysis fit) depends on the value of K associated with the limiting reactant near saturation (which is nearly equal to the concentration of complex). The ‘true concentration’ that matches exactly with the calorimeter’s software-derived value of K may be slightly smaller than the concentration at the 1:1 point, but it cannot be larger. Thus, the concentration we employ should be viewed as being on the conservative side. If the ‘true concentration’ is smaller, then the Δx value between any two points on our characteristic plot will be slightly smaller, and the corresponding slope will be larger. That is, if one chooses a lower value for the corresponding concentration of complex, then the value of ΔG_H2O will be larger than the numbers we report, and the conclusions remain unchanged. (Much of this paragraph has been inserted into the Discussion section of the revised manuscript.)

Reviewer 1, Comment 4: Page 9 of PDF: ‘This approach to removing the background enthalpy of injection was found to be more reliable than subtracting a once-measured control run for each guest concentration at each temperature.’ What is the justification here? See also Comment 2.

Authors: A constant may be used when control runs suggest the background enthalpy of injection is small in magnitude and nearly constant over the course of a titration. However, because it appears that this work may be scrutinised further by sharing the raw data files, the few titration results that previously involved subtraction of a constant have been re-analysed by subtracting an appropriate control run. The Methods section has been updated to reflect this change. In nearly all cases, the small background enthalpy alters the value of K by only a digit in the third significant figure.

Reviewer 1, Comment 5: Page 10 PDF: ‘For example, if the experiment started with 1.00 mM of host molecule A in the cell, the corresponding concentration of complex at equilibrium was found to be 0.87 mM, as dependent on the number of injections of guest molecule B needed to reach the 1:1 titration point’.

This might be related to Comment 3 but either way, this does not make sense. The concentration of the complex depends BOTH on the amount of the molecule A and B and hence in this particular example it can only be 0.87 mM at one particular point of the titration curve (depending on K of course). Maybe there is something about the wording of this that makes it confusing for the reader.

Authors: To reiterate, the concentration of complex is nearly equal to the total concentration of the limiting reactant, and the limiting reactant for the last half of the titration is the component that was loaded into the calorimeter cell at the beginning of the experiment. The value of K is almost constant for the last half of the titration because the concentration of complex is (nearly) constant for the last half.

Reviewer 1, Comment 6: Figure 3 data – several concerns: Why are the N values not the same and why are they close to 0.5 than 1? And the ΔH a ‘round’ number like −3000 and −6700 which suggests they are fixed in the fitting program? This model is highly questionable given that ‘N’ has been allowed to roam free while ΔH has been fixed (why?). Once again having also access to all the raw and calculation files would also help.

Authors: We fixed the ΔH values because we thought it was logical that the enthalpy of binding should NOT vary as a function of reactant concentration. And, for the two-site analysis approach, the sum of the two N-values should equal unity if the reactants are forming a 1:1 binary complex that happens to form with two different affinities (due to two unique binding sites or due to two different conformations upon binding the same site). Nonetheless, due to the confusion, a comment from Reviewer #2, and our own doubts regarding this analysis, the CB7:TEA results have been removed completely.

Reviewer 1, Comment 7: Table S1 – why is the ΔH not shown like in Table S2?

Authors: The K and ΔH_ITC values are now tabulated for all of the featured binding systems including the β-CD results, as found in Tables S1-S3.

Reviewer 1, Comment 8: Figures S1-S3 – why is the data from these not also collected in more useful data tables similar to Table S1 and S2?

Authors: Fig. S1 is the binding of ⁺H-Phe-NH₂ which has a positive charge and binds too tightly to obtain an accurate K value from the fit. We did not perform multiple ITC trials at multiple concentrations; therefore, no table is necessary. We have retained Fig. S1 with the revised manuscript.

Fig. S2 of the original submission shared an ITC trial at the lowest and highest concentration for the two guest molecules with β-CD. We now share the complete datasets in Table S3, and we also feature the results as (new) Figure 3 in the main article. The (original) Fig. S2 has been deleted from the revised manuscript.

Fig. S3 of the original submission shared ITC trials at higher buffer concentrations to demonstrate how the potassium ion reduced the observed value of K for the SC4:TMA model system. Because we have now repeated the SC4:TMA and SC4:putrescine experiments at a constant concentration of K⁺, this supplementary figure has been deleted.

Reviewer 1, Comment 9: Page 22 PDF: ‘but there is no penalty (or benefit) for removing water from a nonpolar surface.’ But what about entropy? And ‘ordered’ water on hydrophobic surfaces?

Authors: Great question. If the entropy change of water upon release from a hydrophobic surface is favourable, then the enthalpy change upon release must be unfavourable and nearly equal in magnitude (if our ΔG_H2O values are close to correct). One can rationalise that this might be true if one recognises that, in order for waters of hydrophobic hydration to be more ‘ordered’ than the bulk, they must be making stronger (more perfectly aligned) H-bonds with neighbouring water molecules compared to water molecules in the bulk solution (which implies a more negative enthalpy at the hydrophobic surface). From this perspective, the old literature that references ‘ice-like’ structure next to apolar surfaces may be a good analogy, although it is understood that the molecules at the surface are in a dynamic equilibrium with all water molecules in the solution. In any case, we believe an unfavourable enthalpy change for the subset of water molecules released from a hydrophobic surface is highly plausible.

Reviewer 1, Comment 10: Conclusions – I will admit, I am just still sceptical. One reason I think allowing access to the data for others is that (with difficulty) it would possible to fit these data with explicit activity constants to see then if the ΔG_H2O term in Eq 3 becomes unnecessary or at least changes drastically. And reading J. Phys. Chem. B, 2013, 117, 8180 it seems that one key assumption here is that the activity of water itself can be ignored/cancels out? Is that really so?

Authors: This appears to be a misunderstanding. In the Castellano & Eggers paper (J. Phys. Chem. B, 2013, 117, 8180), our derivation section mentions that the standard-state chemical potential term (μ° or gg¯°) cancels out because it is a reference point constant that appears on both sides of the reaction. However, the actual change in chemical potential of water (G¯bulk−G¯surface) is the energetic contribution that defines ΔG_H2O, reflecting the release of water molecules from the reactant surface upon binding.

Reviewer 1, Comment 11: Conclusions – But perhaps my biggest concern is that the binding models used here (and in papers 1 and 2) do not assume that there could be any ‘specific’ competing equilibria between i) the host and water molecule(s) – n.b. here I mean some water molecules more tightly bound to the host than the others, and more importantly ii) other ions or molecules (including impurities) in the buffer with the host. For instance, phosphate anions or potassium cations if PBS used. I think that i) or ii) or some combination of these two could sometimes at least explain the observed concentration dependence in K.

Authors: Yes! You are referring to other linked reaction equilibria, in addition to the solvent contribution, and we totally agree. This idea is now expressed in our new ‘Note on the interpretation of ΔG_H2O,’ found in the Supporting Information file. We still believe that the water contribution dominates the value of ΔG_H2O for all of our model systems. As you probably know, there has been much debate in the literature about the fact that ΔH_ITC does not always agree with ΔH obtained from the van’t Hoff approach that utilises K values (and associated ΔG values obtained from -RTlnK), measured as a function of temperature. We attribute the enthalpy issue to linked equilibria, as well; ΔH_ITC will always reflect the sum of enthalpies from all linked reaction equilibria.

REVIEWER 2

Reviewer 2: The authors delve into the thermodynamics of model host-guest binding reactions, employing isothermal titration calorimetry to determine binding affinity as a function of reactant concentration. Contrary to classical thermodynamics, the authors claim that the equilibrium binding quotient, K, is not a constant for all pairings when evaluated over a concentration range exceeding 1.0 mM. This observation supposably aligns with a proposed equation for binding equilibria that incorporates an explicit term for the change in hydration-free energy upon the formation of the binary complex.

The authors subsequently apply this equation to the experimentally observed concentration dependence of K, enabling the derivation of the energetic contribution of the solvent, ΔG_H2O. They contend that ΔG_H2O is significantly higher and unfavourable for two guest molecules binding to CB7 and SC4, while it is approximately zero for the interaction of two hydrophobic guest molecules with β-CD. These findings lead to a controversial discussion on the driving forces behind the hydrophobic effect.

While I remain open to the concept that improved methods are necessary to accurately depict the solution thermodynamics of binding, I am not persuaded by the theoretical justifications and experimental data offered in this study. Here are my reasons:

- In line with Occam’s razor, additional terms should only be incorporated into simple and well-established physical equations if the experimental data absolutely necessitate it. I do not see such compelling evidence here. In fact, the dataset is quite limited, and for this dataset, the authors frequently put forth defensive arguments to justify certain trends that do not strictly align with their expectations.

- From a mathematical perspective, it is expected that any data can achieve a better fit if additional terms are added into the fitting equations, such as ΔG_H2O. However, a better fit does not necessarily imply the significance of the parameter, unless evidence from a substantially larger dataset provides irrefutable proof.

Authors: Please note that we do not use ΔG_H2O as a fitting parameter for any single titration curve; ΔG_H2O is obtained from the ‘global’ result, after measuring K at multiple concentrations. Of historical significance, it should be noted that we did not collect the concentration-dependent data first, then develop a new equation to match the data. On the contrary, the derivation of the governing equation occurred first (in 2011) and prompted the Eggers lab to investigate the concentration dependence of model binding systems. Prior to that year, the Eggers group had never performed the same ITC binding experiment at two different concentrations! Furthermore, B. M. Castellano, the student who collected all of the data for the 2013 paper with EDTA/Ca²⁺, was not informed of the governing equation at the beginning of the project – it was impossible for the student to have any bias towards the experimental results.

We believe that the current manuscript is an important step in providing ‘a substantially larger dataset’ that will gain more attention from the scientific community. After all, there is no such thing as ‘irrefutable proof’ in science – the best one can do is to continue seeking data in support of a hypothesis. By selecting three commercially available host molecules for this study, other research groups should be able to test our governing equation with any of the numerous guest molecules known to form stable inclusion complexes with CB7, SC4, and β-CD.

Reviewer 2: While I believe that the ITC experiments were executed with technical proficiency and supported by a proper error analysis, I question the selection of the model host-guest system. I will present some counterarguments explaining how the variation of the obtained K_a value at different concentrations – a trend observed by both us and others – can be interpreted without the necessity for additional terms in the Gibbs equation for these specific systems:

- As the authors note, activity coefficients have traditionally been employed to model non-ideal behaviour. For example, it is well known that charged species exhibit varying degrees of ion pairing at different concentrations. In this study, the authors utilise CB7 and SC4, both of which are renowned for being efficient metal cation binders. In fact, the affinity of CB7 for metal cations surpasses that of crown ethers and several other ionophores. SC4 is a highly charged species, and cation pairing strongly influences the binding strength (as evidenced in the work of W. M. Nau et al.). The authors contend that the activity coefficients would not vary with changing concentrations. However, I question this: if the buffer concentration remains constant (at 2 mM) while the host concentration increases, wouldn’t one expect the host-metal-cation equilibrium concentration to also change as a function of the concentration? This would, in turn, affect the host-guest equilibrium. On the other hand, cyclodextrins bind cations less effectively (and also not the buffer anions used in this study), which could provide a straightforward explanation for the absence of a concentration effect on the β-CD-guest binding trends observed by the authors.

Authors: This comment made us realise immediately that our SC4 data may be misleading, because the stock solution of SC4 required four equivalents of KOH to neutralise the sulfonate groups. Thus, a 3 mM stock solution of SC4 contains 12 mM K⁺ from neutralisation plus another 3 mM K⁺ from the 2 mM phosphate buffer (assuming equal amounts of monobasic and dibasic phosphate). Thus, we have repeated the SC4 experiments with TMA and putrescine by supplementing the dilution buffer with KCl in order to maintain a constant concentration of potassium for all tested reactant concentrations. For SC4, all solutions contain 15 mM K⁺ overall (from the stock SC4, buffer, and KCl supplement). The new results for TMA and putrescine at 25°C are now combined into one new figure, Fig. 2. As expected, binding affinity decreased at the lower reactant concentrations, leading to a lower value of ΔG_H2O for both TMA and putrescine, but the overall conclusions are unchanged.

For CB7 as host, slightly less than one equivalent of KOH was required to neutralise acidic salts in the solid reagent. Thus, we also repeated all of the CB7:AcPheNH₂ experiments by maintaining all solutions in phosphate buffer with 10 mM K⁺ overall. Again, the magnitude of ΔG_H2O was decreased for this pairing, but the conclusion is unchanged – a concentration-dependent change in the equilibrium is still detected.

In the interest of time, we did not repeat the SC4/TMA experiments at three more temperatures, so this revision does not contain a van’t Hoff analysis based on the temperature dependence. We greatly thank Reviewer 2 for pointing out our experimental flaw. We knew the SC4 and CB7 binding equilibria were sensitive to the cation concentration, but we failed to consider how much potassium was added to the stock solutions before diluting to the desired concentration for ITC trials. For SC4, the new values of ΔG_H2O seem more in line with our previous two studies for binding models that involve charged species of opposite sign.

Reviewer 2: It’s plausible that the guests and hosts in this study form self-aggregated structures at higher concentrations, and the disassembly of these structures upon host-guest binding could significantly impact the binding energy and equilibrium constants. If the authors wish to substantiate their hypothesis, they need to meticulously select their binding partners and rule out any aggregation effects at various concentrations.

Authors: We agree that aggregation (or oligomerization) of bound complexes or unbound host molecules would greatly affect our results, and, in fact, we reported an example of aggregation in the Supporting Info of our previous paper with a cryptophane host (Eggers et al., J. Phys. Chem. B, 2020, 124, 6585). In this previous case, aggregation was detected as an abnormal titration curve for which the enthalpy peaks got larger in the first half of the titration as more and more complex was formed (which is not possible for normal 1:1 binding events). The calorimeter was measuring the heat of binding plus the heat of aggregation when performing the titration at higher concentrations. With this in mind, we paid careful attention to the shape of the binding curves and the resulting values of ΔH_ITC at each concentration employed in the current study. We have found that the molar enthalpy value, ΔH_ITC, is a sensitive reporter of any binding abnormalities. If ΔH_ITC is relatively constant over the entire concentration range tested, then we believe the results are valid and not influenced by aggregation or oligomerization phenomena.

Reviewer 2: I find the proposition of two binding modes for the tetraalkylammonium guests somewhat questionable. Invoking such a complex system seems counterproductive when attempting to validate a new theory.

Authors: We agree that the CB7:TEA result distracts from the main message of this study. Please see our response to Reviewer 1, Comment 6. The CB7:TEA graphs have been removed.

Reviewer 2: Lastly, I’d like to point out that the typical statistical physics definition of a K_a value is already a simplification that may not always be justified. The basic equation (which also involves an activity term for the solvent) offers the potential to model the influence of water molecules, especially if their standard chemical potential varies under different experimental conditions. This might be conceivable if a significant fraction of water molecules is involved in a solvent shell and is not considered ‘bulk solvent’. For instance, water ice, liquid water, and water vapour each have different standard chemical potentials. So why wouldn’t solvent-shell waters around solutes?

Authors: We are delighted that Reviewer 2 sees no problem with the general concept that water molecules at a surface may have a different chemical potential than the time-averaged value of a bulk water molecule; this is the key concept that the Gilson group refuses to acknowledge in their argument using statistical thermodynamics (Kantonen et al., Biochim. Biophys. Acta, 2018, 1862, 692–704). We concede that the activity coefficients of the reactants may be viewed as including their solvation shells, but a balanced reaction must also capture the chemical potential of the water molecules released to the bulk. Gilson is misleading the reader when he states ‘no water is added or consumed in the course of the reaction’ because a subset of water is added to the bulk phase, and the derivation in the Kantonen paper does not include a chemical potential for the water molecules that join the bulk phase. (Much of this paragraph has been inserted into the Discussion section of the revised manuscript.)

Although statistical approaches may include an activity term for the solvent in their simulations, we have never seen a term that captures the change in thermodynamic activity between a solvation shell and the bulk. In our minds, this is a fallacy of physical chemistry that our governing equation aims to correct. All solutes present a boundary condition for which the water must respond, and, depending on the chemistry of the boundary, the response will be a change in the thermodynamic activity (i.e. Gibbs free energy) of water, relative to water in the absence of the boundary.

Reviewer 2: However, my primary issue with this study is the choice of model systems and the lack of compelling evidence that other interpretations can be dismissed when explaining the observed concentration dependence on the K_a values. In conclusion, while I appreciate the authors’ efforts to explore new ways of describing solution thermodynamics, I am not convinced that their approach is the most appropriate or effective. The choice of model systems, the lack of strong evidence dismissing other explanations, and the potential overcomplication of the fitting equations all raise concerns. I believe more comprehensive data and a more critical examination of potential variables and influences are needed before this new model can be accepted as a significant contribution to our understanding of binding thermodynamics.

Authors: We feel compelled to ask Reviewer 2, what would constitute a better model? Because water is the solvent for all biology, nearly all biomolecules contain one or more polar groups to maintain solubility. If only non-polar–non-polar interactions lead to a constant K value and align with the equation from classical solution thermodynamics, then classical thermodynamics is of questionable value to a biochemist. We are hopeful that our governing equation may one day expand the use of thermodynamics in biology and make the terms ‘ideal solution’ and ‘nonideal solution’ obsolete in the field of aqueous solution chemistry.

Second round of review and author responses

REVIEWER 1

Reviewer 1: The authors have done a fairly good job at respond to my questions and comments. As mentioned earlier (and Reviewer 2 seems to be noting as well) – while I am not still convinced about the data analysis approach here it would be in the interest of science to see this work published – if a debate eventuated from this publication, then it will almost certainly be a good thing as others will then either cement in the approach that the authors are using or alternative superior methods to analyse the raw data here will be found. I do therefore have only two requests at this time from the authors: 1. I am glad to see that the authors are planning to upload their data. I appreciate it could be a bit time-consuming. However, I think it is not only absolutely crucial that this is done but if the data are not already ready online that at least the key MatLab and excel summary files are included (uploaded to the journal as a zip file perhaps) with the paper before it is published. The remaining ITC files should then, if not already there, be uploaded on an open access data server.

Authors: The ITC data files and MatLab modelling directions are now ready to share. The files will appear in the corresponding author’s ScholarWorks page, adjacent to a link to the published article. We are just waiting for the final manuscript acceptance notification, DOI number, and a link to the online publication. We plan to make this publication open access.

The Data Availability statement has been updated to the following:

‘Sample ITC data files and modelling details related to Figure 4 are available on the SJSU ScholarWorks page of the corresponding author at https://works.bepress.com/daryl_eggers/.’

Reviewer 1: Both Reviewer 2 and I have significant doubts about the validity of ignoring calculations of activity – if not of the water itself, then at least of the cations/anions involved. I am ok with letting the paper through without the authors doing such calculations. However, I think it is important that the authors explicitly mention in both the intro and conclusions that they do not use any activity coefficient and that they point out very clearly to the reader that this is unusual but that they are doing so precisely because they are using a new method. What I am suggesting here is that the authors try to prevent a naïve reader reading this and walking away thinking they never have to worry about activity coefficient even if they didn’t bother with using the data analysis method here but a more conventional method. I think there is a real risk that this could happen unless the authors are a bit more explicit about the fact that they are not using activity coefficients but that not everyone necessarily will agree with their approach and in any case, ignoring activity coefficients can, in the authors view, only be done if the authors own analysis approach is used.

Authors: We believe that the mentions of activity coefficients in describing Equation 2 of the Introduction and Equation 5 of the Discussion are adequate for readers to understand that we are not ignoring this parameter. Our approach assumes that the activity coefficients are constants for the dilute solution conditions and low reactant concentrations employed in this work, and we include a short justification of this assumption in the second paragraph that follows Equation 5.

Perhaps, our group’s philosophy on activity coefficients will become clearer to all following publication of our next paper that focuses on the effect of secondary solutes in binding equilibria; some of the same model pairings tested in the current work have been re-examined in the presence of common osmolytes. Below we share a (confidential) figure from this follow-up manuscript that demonstrates how the new data will be analysed.

*Figure removed*

Typically, both the y-intercept (ΔG°) and the slope (ΔG_H2O) change in the presence of a secondary solute, as predicted in the text of our manuscript following Equation 5. Look for the new study to be published in late 2023 or early 2024; much of the new manuscript was completed while waiting for the current paper to finish the review process!

Reviewer 2: The authors have made a commendable effort in meticulously addressing the extensive concerns initially highlighted by the reviewers. Although I maintain my stance that the experimental data is not yet robust enough to definitively confirm or reject the proposed model, I find myself aligning with Reviewer 1ʹs viewpoint. This study indeed puts forth an intriguing theory that warrants exposure to the wider chemical community for their critical evaluation. With that said, I believe the abstract could adopt a more balanced tone, underscoring that this is a tentative model seeking further validation. The preliminary experiments conducted by the authors resonate with this model, but this should be presented in a manner that encourages the community to rigorously examine the model, as opposed to giving an impression that this is a settled issue.

Authors: Because the abstract is limited to 150 words, we found it difficult to insert a new statement regarding the need for further experiments in the future. In fact, we have deleted a few phrases in the abstract of this revision to comply with the word count. As an alternative, we now end the Conclusion section with the following paragraph (which may be more impactful):

‘This work suggests a fundamental change in the application of solution thermodynamics to reaction equilibria. The scientific community is encouraged to examine other binding models as a function of concentration to explore further the utility and validity of the experimental approach employed here.’

As a side note to Reviewer 2, your reference to our work above as ‘tentative’ and ‘preliminary’ brought a smile to our face. Because this is our third publication on the topic, and because we have been working towards the results in this manuscript for 12 years, ‘preliminary’ does not seem an appropriate word to us!

Reviewer 2: I personally found Reviewer 1ʹs feedback to be insightful, and the authors’ response to the comments, thoughtful. It could be beneficial to include these exchanges alongside the manuscript for added context and transparency.

Authors: We also feel the initial manuscript critiques and responses are insightful and demonstrate how the scientific review process should unfold. We considered publishing the reviews alongside our ITC data in ScholarWorks, but upon further reflection, this doesn’t seem wise. Many of the initial reviewer comments pertain to data and figures that are no longer part of the final manuscript, so it might be confusing to the reader. Note that we are leaving the original reviews/responses and all three cover letters in the Author Portal as a historical record for the editors of Supramolecular Chemistry. Perhaps, now or in the future, the managing editor and/or chief editor will feel compelled to write an editorial related to this publication. If that should happen, we give the editors permission to use our manuscript-related files as a resource for their editorial.

Reviewer 2: Despite these additional suggestions, I am in support of publishing the manuscript in Supramolecular Chemistry, given the potential impact of the proposed model and the discussion it will incite within the field.

Authors: Thank you!