Additive effects on the energy barrier for synaptic vesicle fusion cause supralinear effects on the vesicle fusion rate
Decision letter

Michael HäusserReviewing Editor; University College London, United Kingdom
eLife posts the editorial decision letter and author response on a selection of the published articles (subject to the approval of the authors). An edited version of the letter sent to the authors after peer review is shown, indicating the substantive concerns or comments; minor concerns are not usually shown. Reviewers have the opportunity to discuss the decision before the letter is sent (see review process). Similarly, the author response typically shows only responses to the major concerns raised by the reviewers.
Thank you for sending your work entitled “Additive effects on the energy barrier for synaptic vesicle fusion cause supralinear effects on the vesicle fusion rate” for consideration at eLife. Your article has been favorably evaluated by Randy Schekman (Senior editor), a Reviewing Editor, and two reviewers, one of whom, Frederic Pincet, has agreed to share his identity.
The Reviewing editor and the reviewers discussed their comments before we reached this decision, and the Reviewing editor has assembled the following comments to help you prepare a revised submission.
In this combined experimental and modelling study, the authors develop a kinetic model in which they describe the RRP release kinetics, and then use this model to show experimentally (using sucroseevoked release at hippocampal autapses in culture) that the fusion rate is supralinearly dependent on the energy barrier to fusion. The consensus of the reviewers is that the idea that there is an additive/multiplicative relationship between energy barrier and the fusion rate is an attractive one, and the agreement between experiment and model is intriguing. However, the reviewers expressed some serious concerns about the manuscript, which are described in detail below. To address these, the authors need to perform additional control experiments, provide more explanation about the details of the model and how the model was derived from the experimental data, and place their results better in the context of the literature.
1) The model is briefly described in the second section of the Results (Minimal vesicle state model). It is basically a chemical reaction between a depot vesicle pool, a readily releasable pool (RRP) and fused vesicles. However, more clarification is required regarding the following points:
A) The authors should explain better which features of the data/traces constrain which parameters in the model, alone or in combination, during the fitting procedure. This is required to better understand the reliability of the fitting procedure, how the parameter values are identified by it, and therefore how the conclusions of the manuscript are actually reached. Additional supplemental figures might be helpful in this regard.
B) How different is this model from several published pool models, including an example cited in the paper (Weis, 1999)? The authors should clarify which parts of the model the authors specifically derive for the case of the RRP are actually novel.
C) How are the various parameters derived from the experimental data? There is a brief description in the supplementary materials, but, for instance, it is not clear whether (and how) k_{1}, k_{1}, D and R were separately obtained from the steady state before fusion and the response during fusion (e.g. provide an example using supplementary information if necessary).
D) It seems that the third, fourth and fifth sections of the Results are meant to validate the model by showing that R (amount of vesicles in the RRP) predicted by the model is consistent with what is obtained experimentally. However, quantitative comparisons with experiments are lacking. The authors have to use experimental values (their own or published ones) to prove their point. This is true for R, but also for the various rates in Equations (6) and (7). Also, why do the parameters change from one table to the next?
E) In the fifth section of the Results (“Modulation energy barrier by genetic and biochemical perturbations”) and corresponding Figure 5, the authors should provide more explanation for how they obtained these curves. How do they define the peak release rate?
F) The authors should provide more discussion about whether the rates and sizes of the various pools derived by their model are reasonable in light of previously estimated values for these parameters.
2) The authors aim to show supralinear dependence of the fusion rate with the activation energy for fusion. The idea that additive effects on energy barrier causes supralinear effects is not new, and is expected for any thermally activated system. This has been known for many decades (see H. A. Kramers, Physica (Amsterdam) 7, 284, 1940 and P. Hänggi, P. Talkner, and M. Borkovec, Rev. Mod. Phys. 62, 251 1990), and recently revisited by Evans and others (e.g. E. Evans and P. M. Williams, in Physics of BioMolecules and Cells, edited by F. Julicher, P. Ormos, F. David, and H. Flyvbjerg SpringerVerlag, Berlin, Germany, 2002, p. 145). So, the primary goal here is to show that, indeed, activation energy is a key element that controls the kinetics of fusion. This raises the following concerns:
A) It appears that Equation 1 is valid only in vacuum where quantum vibrations can be connected with thermal agitation. In the present case, viscosity makes the system overdamped and the prefactor is more of the order of 10^710^10 s^1 (see references above). Currently it is ∼10^13 s^1. Should not all activation energy values be shifted by ∼6kBT?
B) There is a sort of loophole in the current reasoning presented in the manuscript. The authors start from a nonlinear equation (Equation 1), use this equation to deduce activation energy from the fusion rate and claim that the fusion rate varies nonlinearly with the activation energy. The only result that suggests that the supra linearity is real is that presented in Figure 6 where the presence of PDBu increases the fusion rate and this increase can be explained by a constant shift of the activation energy barrier for all hypertonic stimulations. This strongly suggests that the supralinear model is correct in this case. However, this is not true anymore with Complexin for which the shift of the activation energy barrier is dependent on the level of hypertonic stimulation. This difference in behavior should be specifically discussed.
3) In the recordings of sucroseevoked EPSCs, it is unclear how the authors dealt with nonlinearities of the postsynaptic response, such as saturation or desensitization of postsynaptic receptors. Control experiments with kynurenic acid + cyclothiazide would help address this issue.
4) Related to the above point, why do the traces of HS responses become less noisy in the high sucrose concentration limit? This could indeed be due to desensitization or saturation. Or is this simply due to a different number of traces used for averaging? Clearly, this point must be rigorously addressed.
5) Systematic and statistical errors for the estimated rates should be determined. Statistical errors, for example, could be easily obtained by bootstrap analysis.
6) The authors claim several times that the sucrose evoked release is Ca^{2+}independent, but do we really know this? The best solution would be to perform control experiments in the absence of extracellular Ca^{2+}. At the very least, this point should be phrased and discussed more carefully, referring to the relevant literature.
7) The exchange time for the sucrose application should be quantified a bit better. It is unclear how noninstantaneous and nonuniform exchange will affect the conclusions.
8) An interesting implication of the present work is that the nonlinear relation between activation energy and rate may underlie the cooperativity in the Ca^{2+} dependence of release. This is only briefly discussed in the paper. The manuscript would benefit from an expansion of this interesting aspect.
https://doi.org/10.7554/eLife.05531.032Author response
1) The model is briefly described in the second section of the Results (Minimal vesicle state model). It is basically a chemical reaction between a depot vesicle pool, a readily releasable pool (RRP) and fused vesicles. However, more clarification is required regarding the following points:
A) The authors should explain better which features of the data/traces constrain which parameters in the model, alone or in combination, during the fitting procedure. This is required to better understand the reliability of the fitting procedure, how the parameter values are identified by it, and therefore how the conclusions of the manuscript are actually reached. Additional supplemental figures might be helpful in this regard.
We agree that a better explanation is in fact required. We created four supplemental figures and added detailed descriptions in the Materials and methods. In Figure 2–figure supplement 3 we added how each model parameter affects the shape of the hypertonic sucrose (HS)induced response in a specific manner. This is further explained in the subsection headed “Vesicle state model”. In Figure 3–figure supplement 5 and in the subsection “Fitting procedures and statistics”, we explain how our fit method reliably discriminates between the contributions of different model parameters to the HSinduced response. Finally, in Figure 6–figure supplement 1, 2, we display random examples (10 per condition) of synaptic responses induced by 0.3 or 0.5M sucrose in the presence or absence of PDBu to show how well these traces are fitted by our model, which is also mentioned in “Fitting procedures and statistics”.
B) How different is this model from several published pool models, including an example cited in the paper (Weis, 1999)? The authors should clarify which parts of the model the authors specifically derive for the case of the RRP are actually novel.
We added a more elaborate description in the Materials and methods of how our model differentiates from the Weis et al. model (please see the subsection “Vesicle state model”). The unique/novel features of our model are that for the first time synaptic responses to hypertonic sucrose are modelled, and the relation between RRP depletion and release kinetics, and RRP replenishment during HSstimulation. This is now added to the aforementioned subsection. Our model also differs from other pool models in the number of primed pools that is assumed, 1 pool vs 2 (Walter, 2013, Wolfel, 2007) or 3 pools (Voets, 1999), and the trigger for release that is simulated, hypertonic sucrose vs flashCa^{2+} (Walter, 2013, Wolfel, 2007, Voets, 1999).
C) How are the various parameters derived from the experimental data? There is a brief description in the supplementary materials, but, for instance, it is not clear whether (and how) k_{1}, k_{1} , D and R were separately obtained from the steady state before fusion and the response during fusion (e.g. provide an example using supplementary information if necessary).
We agree that the description of how the parameters are derived from experimental data has not been optimal. We have added an explanation in the Materials and methods. As described above (point 1A) and shown in Figure 2–figure supplement 3, different parameters constrain unique features of the HSinduced synaptic responses. We use this the other way around to constrain the model parameters when fitting the experimental traces as explained in the “Fitting procedures and statistics” subsection and shown in Figure 3–figure supplement 5. All parameters are obtained fitting the response during fusion. R at steady state is obtained from the ratio of the fitted parameters k_{1}D/k_{1}. Although there is an option in our software to fit k_{1} and D separately to account for decay of refill phase, for instance during long HSstimulations, we used here the option to fit product k_{1}D as a constant (priming rate). This is more clearly explained in the subsections “Vesicle state model” and “Fitting procedures and statistics”.
D) It seems that the third, fourth and fifth sections of the Results are meant to validate the model by showing that R (amount of vesicles in the RRP) predicted by the model is consistent with what is obtained experimentally. However, quantitative comparisons with experiments are lacking. The authors have to use experimental values (their own or published ones) to prove their point. This is true for R, but also for the various rates in Equations (6) and (7). Also, why do the parameters change from one table to the next?
The reviewers are right. Quantitative comparisons with experiments are lacking and should have been included to validate the model. We have now included comparisons of our fitted parameters with estimated parameter values in previous studies, except for k_{2.max} and the activation energy associated with HSinduced release since we are the first to quantify these with our method. k_{1}D is compared with published priming rates (subsection headed “Assessing RRP size and release rate constants”). RRP is compared with pool sizes from 7 different studies. We have added a derivation for RRP recovery after depletion in the Materials and methods section (Equation 21) to compare the inverse of k_{1} with previously published RRP recovery time constants in autapses. As discussed in the text, all our parameter estimates are in the range of published values. Variation in the parameters between different tables arises from the fact that they are obtained from different experiments, performed at different points in time and in different labs. Hence, this is general variation between experiments.
E) In the fifth section of the Results (“Modulation energy barrier by genetic and biochemical perturbations”) and corresponding Figure 5, the authors should provide more explanation for how they obtained these curves. How do they define the peak release rate?
We agree and have now provided more explanation, both in the main text (in the subsection entitled “Modulation of the activation energy for fusion by genetic and biochemical perturbations”) and in the figure legend of Figure 5. Peak release rate is defined as the release rate at the peak of a HSinduced response. We plotted the reported peak release rates and corresponding depleted RRP fractions for different perturbations in one graph in Figure 5. The predicted curve in Figure 5 is obtained by plotting the peak release rates and depleted RRP fractions obtained from different simulations of HSinduced responses with only the model parameter k_{2max} varied.
F) The authors should provide more discussion about whether the rates and sizes of the various pools derived by their model are reasonable in light of previously estimated values for these parameters.
We agree, see point 1D.
2) The authors aim to show supralinear dependence of the fusion rate with the activation energy for fusion. The idea that additive effects on energy barrier causes supralinear effects is not new, and is expected for any thermally activated system. This has been known for many decades (see H. A. Kramers, Physica (Amsterdam) 7, 284, 1940 and P. Hänggi, P. Talkner, and M. Borkovec, Rev. Mod. Phys. 62, 251 1990), and recently revisited by Evans and others (e.g. E. Evans and P. M. Williams, in Physics of BioMolecules and Cells, edited by F. Julicher, P. Ormos, F. David, and H. Flyvbjerg SpringerVerlag, Berlin, Germany, 2002, p. 145). So, the primary goal here is to show that, indeed, activation energy is a key element that controls the kinetics of fusion. This raises the following concerns:
A) It appears that Equation 1 is valid only in vacuum where quantum vibrations can be connected with thermal agitation. In the present case, viscosity makes the system overdamped and the prefactor is more of the order of 10^710^10 s^1 (see references above). Currently it is ∼10^13 s^1. Should not all activation energy values be shifted by ∼6kBT?
We completely agree with the reviewers. Equation 1 is in fact not the right equation to apply. The assumption of thermally driven dissociation of the activated complex in a quantum oscillator model is not valid for our reaction (which occurs in solution and involves complex molecular rearrangements of proteins and lipids). The consequence is that the previous values of the exponential prefactor were an overestimation, as the reviewers correctly pointed out. To circumvent the necessity of investigating assumptions underlying the derivation of the Eyring equation (which may not be valid in our system), in the revised version, we decided to describe the rate constants based on the empirical Arrhenius equation, which differs from the Eyring equation by containing an empirical prefactor (A). A consequence of this new notation is that we now consider relative changes of the activation energy (E_{a}) for fusion, not absolute values, at least until the Discussion. We have now plotted energy differences with respect to the activation energy for fusion at rest, which also allows us to directly show the estimated consequences of hypertonic solutions. In this way, we can still substantiate all our main claims, but the switch to an empirical equation leads to altered labels on most graphs and Equation 15. We thank the reviewers for pointing out this crucial flaw in our reasoning.
In addition, using the Arrhenius equation makes it clearer that an increase in the reaction rate constant can result either from an increase in the preexponential factor (A), or from a decrease of the energy barrier (E_{a}), or both. In our manuscript we now discuss these possibilities explicitly and provide arguments that the effect of hypertonicity is most likely due to a reduction in the energy barrier (please see the subsections “Sucrose stimulation reflects a decrease in the activation energy for fusion” and “The Arrhenius equation infers the activation energy for synaptic vesicle fusion”). We have also added a sentence emphasizing that changes in the preexponential factor will also contribute to changes in the fusion rate.
B) There is a sort of loophole in the current reasoning presented in the manuscript. The authors start from a nonlinear equation (Equation 1), use this equation to deduce activation energy from the fusion rate and claim that the fusion rate varies nonlinearly with the activation energy. The only result that suggests that the supra linearity is real is that presented in Figure 6 where the presence of PDBu increases the fusion rate and this increase can be explained by a constant shift of the activation energy barrier for all hypertonic stimulations. This strongly suggests that the supralinear model is correct in this case. However, this is not true anymore with Complexin for which the shift of the activation energy barrier is dependent on the level of hypertonic stimulation. This difference in behavior should be specifically discussed.
We acknowledge this flaw in our previous reasoning. We have removed this and now start with stating explicitly that: “direct measurements of the exact contributions of different molecular events inside living nerve terminals to the activation energy for SV fusion are not possible” (please see the Introduction and the subsection entitled “The Arrhenius equation infers the activation energy for synaptic vesicle fusion”). Subsequently, we argue that according to the Arrhenius equation a class of modulations of synaptic release might exist, which will result in supralinear effects on synaptic release rate through an additive effect on the activation energy. The effect of PDBu is indeed in line with this (as noted by the reviewers), whereas the effect of complexin appears to be more complex. As the reviewers suggest, we have discussed this in the revised manuscript (“Supralinear modulation of release kinetics by Phorbol esters and Complexins through additive effects on the activation energy”). Several previous observations in literature provide leads (clamping a secondary Ca^{2+}sensor for spontaneous and asynchronous release, rendering the synapse more sensitive to spontaneous Ca^{2+} fluctuations, changing the cooperativity of exocytosis).
3) In the recordings of sucroseevoked EPSCs, it is unclear how the authors dealt with nonlinearities of the postsynaptic response, such as saturation or desensitization of postsynaptic receptors. Control experiments with kynurenic acid + cyclothiazide would help address this issue.
We agree with the reviewers that the effect of receptor desensitization or saturation on sucroseevoked EPSCs have been underexposed in our manuscript. These issues were extensively studied by Pyott et. al., 2002 using kynurenic acid + cyclothiazide. No effect was found on RRP measurements with 0.5M. We refer now to this paper. In addition, we performed new experiments and tested whether AMPA receptor saturation affected the kinetics of synaptic responses to 0.5 and 0.75M. We confirmed that saturation does not affect measurements with 0.5M. However, for 0.75M the release rate constant was about 30% faster in the presence of KYN (see new Figure 3–figure supplement 3). We conclude that quantifications of model parameters obtained from responses to 0.75M and higher should be interpreted with caution (see the subsection entitled “Assessing RRP size and release rate constants”). However, this does not change any of our main conclusions.
Several studies report that, in addition to blocking AMPA receptor desensitization, CTZ stimulates the presynaptic release machinery (Bellingham, 1999, Diamond, 1995, Ishikawa, 2001). Therefore, we could not use this drug to test a potential effect of receptor desensitization, as suggested by the reviewers. However, when examining noise levels (see point 4 below), we concluded that desensitization was negligible for responses to concentrations up to 0.5M. Since the experiments with PDBu or Complexin were performed with 0.5M and lower, we conclude that these measurements were not affected by receptor saturation or desensitization. This is added to the revised manuscript.
4) Related to the above point, why do the traces of HS responses become less noisy in the high sucrose concentration limit? This could indeed be due to desensitization or saturation. Or is this simply due to a different number of traces used for averaging? Clearly, this point must be rigorously addressed.
All traces are single responses (not averaged), recorded with the same filter settings. We analyzed the noise levels on all traces and found indeed that responses to sucrose concentrations beyond 0.5M tend to have lower noise levels. In view of point 3 above, we interpreted this as an effect of saturation and/or desensitization. This point is now addressed in the text where we state that quantifications of model parameters obtained from responses to 0.75M and higher should be interpreted with caution. We thank the reviewers for pointing this out.
5) Systematic and statistical errors for the estimated rates should be determined. Statistical errors, for example, could be easily obtained by bootstrap analysis.
We have performed experiments with KYN to determine systematic errors due to receptor saturation (see point 3, Figure 3–figure supplement 3). In addition we have performed experiments with glutamate receptor blockers DNQX and AP5 to determine the systematic error due the contribution of nonreceptor currents to HSinduced responses, and found that this effect was negligible (Figure 3–figure supplement 4). Bootstrap analysis was performed for all experiments to determine 95% confidence intervals. Results are now given in the supplementary tables. For the effect of PDBu and complexin on the fusion rate constant, we calculated the 95% confidence intervals for the mean difference in k_{2,max} between the experimental (PDBu or CpxKO) and the control (no PDBu or Cpx WT) group and plotted these as error bars in Figure 6D and 7D. All mean differences were within the calculated 95% confidence intervals.
6) The authors claim several times that the sucrose evoked release is Ca^{2+}independent, but do we really know this? The best solution would be to perform control experiments in the absence of extracellular Ca^{2+}. At the very least, this point should be phrased and discussed more carefully, referring to the relevant literature.
The Ca^{2+}dependency of HSinduced responses has been extensively studied, for instance in Rosenmund and Stevens in Neuron (1996), showing that neither buffering intracellular Ca^{2+} by BAPTA nor blocking Ca^{2+} influx using CdCl_{2} had an effect (Rosenmund, 1996). Several other extensive studies are already available. We discuss this now more carefully in the text with a reference to this paper (in the subsection headed “Minimal vesicle state model for synaptic vesicle release”).
7) The exchange time for the sucrose application should be quantified a bit better. It is unclear how noninstantaneous and nonuniform exchange will affect the conclusions.
To address this point we have performed opentip experiments with 0.5M and 1M sucrose (Figure 2–figure supplement 2). We show that the solution exchange is instantaneous (within 0.4 seconds after switching barrels), compared to the induced postsynaptic currents, which respond with a delay of 1.1 (1M)1.6s (0.25M), and therefore will not affect the conclusions in this paper. This is discussed in the first paragraph of the Materials and methods section.
8) An interesting implication of the present work is that the nonlinear relation between activation energy and rate may underlie the cooperativity in the Ca^{2+} dependence of release. This is only briefly discussed in the paper. The manuscript would benefit from an expansion of this interesting aspect.
We agree with the reviewers that this is an interesting implication of our work. Therefore we expanded the discussion with a derivation of the allosteric model for Ca^{2+} dependence of vesicle release within the framework of the paper. We show that the supralinear relation between the intracellular Ca^{2+} concentration and the fusion rate follows directly from eq. (Bellingham, 1999), when assuming that the Ca^{2+} sensor reduces the activation energy for fusion with a fixed amount ΔE_{Ca} for each Ca^{2+} ion binding. This is illustrated in a new figure (Figure 8).
https://doi.org/10.7554/eLife.05531.033