Progressive overfilling of readily releasable pool underlies short-term facilitation at recurrent excitatory synapses in layer 2/3 of the rat prefrontal cortex

Reviewer #3 (Public review):

The central issue for evaluating the overfilling hypothesis is the identity of the mechanism that causes the very potent (>80% when inter pulse is 20 ms), but very quickly reverting (< 50 ms) paired pulse depression (Fig 1G, I). To summarize: the logic for overfilling at local cortical L2/3 synapses depends critically on the premise that probability of release (pv) for docked and fully primed vesicles is already close to 100%. If so, the reasoning goes, the only way to account for the potent short-term enhancement seen when stimulation is extended beyond 2 pulses would be by concluding that the readily releasable pool overfills. However, the conclusion that pv is close to 100% depends on the premise that the quickly reverting depression is caused by exocytosis dependent depletion of release sites, and the evidence for this is not strong in my opinion. Caution is especially reasonable given that similarly quickly reverting depression at Schaffer collateral synapses, which are morphologically similar, was previously shown to NOT depend on exocytosis (Dobrunz and Stevens 1997). Note that the authors of the 1997 study speculated that Ca2+-channel inactivation might be the cause, but did not rule out a wide variety of other types of mechanisms that have been discovered since, including the transient vesicle undocking/re-docking (and subsequent re-priming) reported by Kusick et al (2020), which seems to have the correct timing.

In an earlier round of review, I suggested raising extracellular Ca2+, to see if this would increase synaptic strength. This is a strong test of the authors' model because there is essentially no room for an increase in synaptic strength. The authors have now done experiments along these lines, but the result is not clear cut. On one hand, the new results suggest an increase in synaptic strength that is not compatible with the authors' model; technically the increase does not reach statistical significance, but, likely, this is only because the data set is small and the variation between experiments is large. Moreover, a more granular analysis of the individual experiments seems to raise more serious problems, even supporting the depletion-independent counter hypothesis to some extent. On the other hand, the increase in synaptic strength that is seen in the newly added experiments does seem to be less at local L2/3 cortical synapses compared to other types of synapses, measured by other groups, which goes in the general direction of supporting the critical premise that pv is unusually high at L2/3 cortical synapses. Overall, I am left wishing that the new data set were larger, and that reversal experiments had been included as explained in the specific points below.

Specific Points:

(1) One of the standard methods for distinguishing between depletion-dependent and depletion-independent depression mechanisms is by analyzing failures during paired pulses of minimal stimulation. The current study includes experiments along these lines showing that pv would have to be extremely close to 1 when Ca2+ is 1.25 mM to preserve the authors' model (Section "High double failure rate ..."). Lower values for pv are not compatible with their model because the k1 parameter already had to be pushed a bit beyond boundaries established by other types of experiments. The authors now report a mean increase in synaptic strength of 23% after raising Ca to 2.5 mM. The mean increase is not quite statistically significant, but this is likely because of the small sample size. I extracted a 95% confidence interval of [-4%, +60%] from their numbers, with a 92% probability that the mean value of the increase in the full population is > 5%. I used the 5% value as the greatest increase that the model could bear because 5% implies pv < 0.9 using the equation from Dodge and Rahamimoff referenced in the rebuttal. My conclusion from this is that the mean result, rather than supporting the model, actually undermines it to some extent. It would have likely taken 1 or 2 more experiments to get above the 95% confidence threshold for statistical significance, but this is ultimately an arbitrary cut off.

(2) The variation between experiments seems to be even more problematic, at least as currently reported. The plot in Figure 3-figure supplement 3 (left) suggests that the variation reflects true variation between synapses, not measurement error. And yet, synaptic strength increased almost 2-fold in 2 of the 8 experiments, which back extrapolates to pv < 0.2. If all of the depression is caused by depletion as assumed, these individuals would exhibit paired pulse facilitation, not depression. And yet, from what I can tell, the individuals depressed, possibly as much as the synapses with low sensitivity to Ca2+, arguing against the critical premise that depression equals depletion, and even arguing - to some extent - for the counter hypothesis that a component of the depression is caused by a mechanism that is independent of depletion. I would strongly recommend adding an additional plot that documents the relationship between the amount of increase in synaptic strength after increasing extracellular Ca2+ and the paired pulse ratio as this seems central.

(3) Decrease in PPR. The authors recognize that the decrease in the paired-pulse ratio after increasing Ca2+ seems problematic for the overfilling hypothesis by stating: "Although a reduction in PPR is often interpreted as an increase in pv, under conditions where pv is already high, it more likely reflects a slight increase in pocc or in the number of TS vesicles, consistent with the previous estimates (Lin et al., 2025)." I looked quickly, but did not immediately find an explanation in Lin et al 2025 involving an increase in pocc or number of TS vesicles, much less a reason to prefer this over the standard explanation that reduced PPR indicates an increase in pv. The authors should explain why the most straightforward interpretation is not the correct one in this particular case to avoid the appearance of cherry picking explanations to fit the hypothesis.

(4) The authors concede in the rebuttal that mean pv must be < 0.7, but I couldn't find any mention of this within the manuscript itself, nor any explanation for how the new estimate could be compatible with the value of > 0.99 in the section about failures.

(5) Although not the main point, comparisons to synapses in other brain regions reported in other studies might not be accurate without directly matching experiments. As it is, 2 of 8 synapses got weaker instead of stronger, hinting at possible rundown, but this cannot be assessed because reversibility was not evaluated. In addition, comparing axons with and without channel rhodopsins might be problematic because the channel rhodopsins might widen action potentials.

(6) Perhaps authors could double check with Schotten et al about whether PDBu does/does not decrease the latency between osmotic shock and transmitter release. This might be an interesting discrepancy, but my understanding is that Schotten et al didn't acquire information about latency because of how the experiments were designed.

(7) The authors state: "These data are difficult to reconcile with a model in which facilitation is mediated by Ca2+-dependent increases in pv." However, I believe that discarding the premise that depression is always caused by depletion would open up wide range of viable possibilities.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Shin et al. conduct extensive electrophysiological and behavioral experiments to study the mechanisms of short-term synaptic plasticity at excitatory synapses in layer 2/3 of the rat medial prefrontal cortex. The authors interestingly find that short-term facilitation is driven by progressive overfilling of the readily releasable pool, and that this process is mediated by phospholipase C/diacylglycerol signaling and synaptotagmin-7 (Syt7). Specifically, knockdown of Syt7 not only abolishes the refilling rate of vesicles with high fusion probability, but it also impairs the acquisition of trace fear memory.

Overall, the authors offer novel insight to the field of synaptic plasticity through well-designed experiments that incorporate a range of techniques.

Comments on revisions:

The authors have adequately addressed my earlier comments and questions.

Reviewer #2 (Public review):

All the comments from Reviewer #2 are the same as her/his comments to our original manuscript. Therefore, we have already responded to all the following comments in the first revision. Here we described our additional responses to the same comments.

Summary:

Shin et al aim to identify in a very extensive piece of work a mechanism that contributes to dynamic regulation of synaptic output in the rat cortex at the second time scale. This mechanism is related to a new powerful model and is well versed to test if the pool of SV ready for fusion is dynamically scaled to adjust supply demand aspects. The methods applied are state-of-the-art and both address quantitative aspects with high signal to noise. In addition, the authors examine both excitatory output onto glutamatergic and GABAergic neurons, which provides important information on how general the observed signals are in neural networks. The results are compellingly clear and show that pool regulation may be predominantly responsible. Their results suggests that a regulation of release probability, the alternative contender for regulation, is unlikely to be involved in the observed short term plasticity behavior (but see below). Besides providing a clear analysis of the underlying physiology, they test two molecular contenders for the observed mechanism by showing that loss of Synaptotagmin7 function and the role of the Ca dependent phospholipase activity seems critical for the short term plasticity behavior. The authors go on to test the in vivo role of the mechanism by modulating Syt7 function and examining working memory tasks as well as overall changes in network activity using immediate early gene activity. Finally, they model their data, providing strong support for their interpretation of TS pool occupancy regulation.

Strengths:

This is a very thorough study, addressing the research question from many different angles and the experimental execution is superb. The impact of the work is high, as it applies recent models of short term plasticity behavior to in vivo circuits further providing insights how synapses provide dynamic control to enable working memory related behavior through non-permanent changes in synaptic output.

Weaknesses:

While this work is carefully examined and the results are presented and discussed in a detailed manner, the reviewer is still not fully convinced that regulation of release probability is not a putative contributor to the observed behavior. No additional work is needed, but in the moment, I am not convinced that changes in release probability are not in play. One solution may be to extend the discussion of changes in rules probability as an alternative.

As the Reviewer #3 suggested, we examined the dependence of EPSC amplitude on extracellular [Ca²⁺] ([Ca²⁺]_o) in order to test our assertion that vesicular release probability (p_v) is already saturated in resting conditions at L2/3 recurrent synapses. A three-fold increase is expected according to Dodge and Rahamimoff (1967), if resting p_v has enough room to increase, when [Ca²⁺]_o is elevated from 1.3 to 2.5 mM. We found an increase in the baseline EPSC amplitude only by 23%, and this change was not statistically significant, supporting our assertion.

Fig 3. I am confused about the interpretation of the Mean Variance analysis outcome. Since the data points follow the curve during induction of short term plasticity, doesn't these suggests that release probability and not the pool size increases?

We separated the conventional release probability into a multiplication of p_v and p_occ, in which p_v = probability of TS vesicles and p_occ = occupancy of release sites by TS vesicles. In this regard, the abscissa of V-M plot represents the conventional release probability. Because p_v is close to unity, we interpreted a change along the abscissa as a change of p_occ.

Related, to measure the absolute release probability and failure rate using the optogenetic stimulation technique is not trivial as the experimental paradigm bias the experiment to a given output strength, and therefore a change in release probability cannot be excluded.

We agree to this concern. Because EPSC data were obtained by optogenetic stimulation, it cannot be ruled out a possibility that optogenetic stimulation biased the release probability. Although we found that STP obtained by dual patch experiment was not different from that by optogenetic stimulation, it needs to confirm our conclusion using dual patch or other methods.

Fig. 4B interprets the phorbol ester stimulation to be the result of pool overfilling, however, phorbol ester stimulation has also been shown to increase release probability without changing the size of the readily releasable pool. The high frequency of stimulation may occlude an increased paired pulse depression in presence of OAG, that others have interpreted in mammalian synapses as an increase in release probability.

Provided that pv of TS vesicles is very high, the OAG-induced increase in EPSC1 and low STF and PTA are consistent with higher baseline p_occ in PDBu conditions, while the number of docking sites is limited. It should be noted that previous PDBu-induced invariance of the RRP size is based on measuring the RRP size using hypertonic solution (Basu et al., 2007). Given that this sucrose method releases not only TS but also LS vesicles, the sucrose-based RRP size may not be affected by PDBu or OAG at L2/3 synapses too. Therefore, PDBu or OAG-induced increase in p_occ (proportion of TS vesicles over LS+TS vesicles) would result in an increase in release probability without a change in the RRP size.

The literature on Syt7 function is still quite controversial. An observation in the literature that loss of Syt7 function in the fly synapse leads to an increase of release probability. Thus the observed changes in short term plasticity characteristics in the Syt7 KD experiments may contain a release probability component. Can the authors really exclude this possibility? Figure 5 shows for the Syt7 KD group a very prominent depression of the EPSC/IPSC with the second stimulus, particularly for the short interpulse intervals, usually a strong sign of increased release probability, as lack of pool refilling can unlikely explain the strong drop in synaptic output.

Comments on revisions:

I am satisfied with the reply of the authors and I do not have any further points of concern.

Reviewer #3 (Public review):

The results are consistent with the main claim that facilitation is caused by overfilling a readily releasable pool, but alternative interpretations continue to seem more likely, especially when the current results are taken together with previous studies. Key doubts could be resolved with a single straightforward experiment (see below).

The central issue is the interpretation of paired pulse depression that occurs when the interval between action potentials is 25 ms, but not when 50. To summarize: a similar phenomenon was observed at Schaffer collateral synapses (Dobrunz and Stevens, 1997), but was interpreted as evidence for a decrease in pv. Ca2+-channel inactivation was proposed as the mechanism, but this was not proven. The key point for evaluating the current study is that Dobrunz and Stevens specifically ruled out the kind of decrease in pocc that is the keystone premise of the current study because the depression occurred independently of whether or not the first action potential elicited exocytosis. Of course, the mechanism might be different at layer 2/3 cortical synapses. But, it seems reasonable to hope that the older hypothesis would be ruled out for the cortical synapses before concluding that the new hypothesis must be correct.

The old and new hypotheses could be distinguished from each other cleanly with a straightforward experiment. Most/maybe all central synapses strengthen a great amount when extracellular Ca2+ is increased from 1.3 to 2 mM, even when intracellular Ca2+ is buffered with EGTA. According to the authors' model, this is only possible when pv is low, and so could not occur at synapses between layer 2/3 neurons. Because of this, confirmation that increasing extracellular Ca2+ does not change synaptic strength would support the hypothesis that baseline pv is high, as the authors claim, and the support would be impressive because large changes have been seen at every other type of synapse where this has been studied (to my knowledge at least). In contrast, the Ca2+ imaging experiment that has been added to the new version of the manuscript does not address the central issue because a wide range of mechanisms could, in principle, decrease release without involving prior exocytosis or altering bulk Ca2+ signals, including: a small decrease in nano-domain Ca2+, which wouldn't be detected because nano-domains contribute a minuscule amount to the bulk signal during Ca2+-imaging; or even very fast activity-dependent undocking of synaptic vesicles, which was reported in the same Kusick et al, 2020 study that is central to the LS/TS terminology adopted by the authors.

Additional points:

(1) A new section in the Discussion (lines 458-475) suggests that previous techniques employed to show that augmentation and facilitation are caused by increases in pv did not have the resolution to distinguish between pv and pocc, but this is misleading. The confusion might be because the terminology has changed, but this is all the more reason to clarify this section. The previous evidence for increases in pv - and against increases in pocc - is as follows: The residual Ca2+ that drives augmentation decreases the latency between the onset of hypertonic solution and onset of the postsynaptic response by about 150 ms, which is large compared to the rise time of the response. The decrease indicates that the residual Ca2+ drives a decrease in the energy barrier that must be overcome before readily releasable vesicles can undergo exocytosis, which is precisely the type of mechanism that would enhance pv. In contrast, an increase in pocc could change the rise time, but not the latency. There is a small change in the rise time, but this could be caused by changes in either pv or pocc, and one of the studies (Garcia-Perez and Wesseling, 2008) showed that augmentation occluded facilitation, even at times when pocc was reduced by a factor of 3, which would seem to argue against parallel increases in both pv and pocc.

We greatly appreciate for pointing out our mis-understanding. We acknowledge that the post-tetanic acceleration of the latency in the hypertonicity-induced vesicle release may reflect a decrease in the activation energy barrier (ΔEa) for vesicle fusion resulting in an increase in fusion probability of TS vesicles (Stevens and Wesseling, 1999; Garcia-Perez and Wesseling, 2008). We agree that such latency changes are not easily explained by increases in p_occ alone. Indeed, Taschenberger et al (2016) concluded that PTP is similar to the PDBu-induced increase in baseline EPSCs. Subsequently, Lin et al (2025) estimated PDBu-induced changes of TS vesicle pool size and p_fusion of TS vesicles (these correspond to p_occ and p_v in this study, respectively), and found that PDBu increases majorly the former (2 folds) and minorly the latter (1.3 folds). Although it has not been directly tested, it is possible that PTP increases p_v. Accordingly, we corrected the first statement of the paragraph, and mentioned the possibility for a post-tetanic increase in p_v of TS vesicles.

It should be noted, however, it is still puzzling what is represented by the acceleration of the latency in the hypertonicity-induced vesicle release. Schotten et al (2015) simulated how vesicle release rate is affected by reducing ΔEa for vesicle fusion. They found that a reduction of ΔEa resulted in increases in the peak amplitude and shorter time-to-peak of vesicle fusion, but did not accelerate the latency. Therefore, it remains to be clarified whether shorter latency can be regarded as lower activation barrier. Moreover, the sucrose-induced release rate is comparable with the vesicle recruitment rate (1-2/s; Neher, Neuron, 2008). This slowness of sucrose-induced vesicle release rate makes it difficult to distinguish the vesicle fusion rate from their priming rate.

(2) Similar evidence from hypertonic stimulation indicates that Phorbol esters increase pv, but I am not aware of evidence ruling out a parallel increase in pocc.

As noted above, none of known mechanisms can clearly explain the PDBu-induced shorter latency to hypertonicity-induced vesicle fusion (Schotten et al, 2015). Even if shorter latency reflects higher p_v, it does not rule out a concurrent change in p_occ. Supporting this notion, Lin et al. (2025) showed in the framework of the two state vesicle fusion model that PDBu application leads to a substantial increase in the number of TS vesicles (vesicles having high fusion propensity), with a moderate change in fusion probability (p_fusion). In light of previous observation that high tonicity (500 or 1000 mOsm) did not alter the RRP size (Basu et al., 2007), the results of Lin et al. (2025) can be interpreted as an increase of ‘p_occ’ in terms of the present study.

Reference:

Schotten et al. (2015). Additive effects on the energy barrier for synaptic vesicle fusion cause supralinear effects on the vesicle fusion rate. eLife 4:e05531.

Lin, K.-H., Ranjan, M., Lipstein, N., Brose, N., Neher, E., & Taschenberger, H. (2025). Number and relative abundance of synaptic vesicles in functionally distinct priming states determine synaptic strength and short-term plasticity. J. Physiology.

Comments on revisions:

There are at least two straightforward ways to address the main concern.

The first would be experiments analogous to those in Dobrunz and Stevens that show that - unlike at Schaffer collateral synapses - paired pulse depression at L2/3 synapses requires neurotransmitter release. I proposed this in the first round, but realized since that a simpler and more powerful strategy would be to test directly that pv is/is-not near 1.0 in 1.2 mM Ca2+ simply by increasing to 2 mM Ca2+ (and showing that synaptic strength does-not/does change). This would be powerful because the increase in Ca2+ greatly increases synaptic strength at Schaffer collaterals by about 2.5-fold. Concerns about a confounding elevation in the basal intracellular Ca2+ concentration could be easily neutralized by pre-treating with EGTA-AM, which the authors have already done for other experiments.

We thank to Reviewer #3 for suggesting an experiment for testing our assertion that the vesicular release probability (p_v) is very high at layer 2/3 recurrent excitatory synapses. As the Reviewer recommended, we assessed EPSC changes induced by an increase in extracellular calcium concentration ([Ca²⁺]_o). The results are added as Figure 3—figure supplement 3 to the revised manuscript.

Dodge and Rahamimoff (1967) discovered a fourth-power relationship between end-plate potential (EPP) and [Ca²⁺]_o at a neuromuscular junction. More specifically they found

EPP amplitude µ ([Ca²⁺]_o / (1 + [Ca²⁺]_o /1.1 mM + [Ma²⁺]_o /2.97 mM))⁴.

This equation nicely predicts the effects of high external calcium on EPSC amplitudes observed at the calyx synapses: a 2.6-fold increase of EPSC by changing [Ca²⁺]_o from 1.25 to 2 mM (Thanawala and Regehr, 2013; predicted as 2.57); a 2.36-fold increase by changing [Ca²⁺] from 1.5 to 2 mM (Lin and Taschenberger, 2025; predicted as 2.16). In the framework of two-step priming model, Lin et al. (2015) estimated a 1.9-fold increase (from 0.22 to 0.42) in p_v of TS vesicles and a 1.23-fold increase in the number of TS vesicles. It is clear that the increase in p_v would be possible only if p_v is not saturated, while the increase in the number of TS vesicles is still possible regardless of baseline p_v of TS vesicles.

The Dodge and Rahamimoff’s equation predicts a 3.24-fold increase in baseline EPSC amplitude by elevating [Ca Ca²⁺]_o from 1.3 mM to 2.5 mM at L2/3 synapses. Contrary to this prediction, our recordings revealed a 1.23 fold increase in baseline EPSC amplitude, and this change was not statistically significant.

Given the steep dependence of vesicle release on [Ca²⁺]_o, this minimal increase strongly suggests that p_v at L2/3 recurrent synapses is already near maximal at rest, limiting the dynamic range for further enhancement through increased calcium influx. Accordingly, we observed a small but statistically significant decrease in the paired-pulse ratio (PPR) at higher [Ca²⁺]_o. Although this reduction in PPR might be indicative of increased p_v, it is more consistent with a slight increase in p_occ rather than a substantive increase in p_v under the context of very high p_v. Accordingly, Lin et al. (2025) recently estimated an increase in the TS vesicle subpool size as 1.23-fold by elevating [Ca²⁺]_o under the framework of the two-step vesicle priming mode. Taken together, these findings suggest that an increase in the number of TS vesicles or p_occ may contribute to both an increase in baseline EPSC amplitudes and a decrease in PPR.

Overall, our central claim that baseline p_v is near maximal at L2/3 recurrent synapses is supported by 1) high baseline PPR; 2) insensitivity to EGTA-AM; 3) high double failure rate; 4) insensitivity to elevating [Ca²⁺]_o. These data are difficult to reconcile with a model in which facilitation is mediated by Ca²⁺-dependent increases in p_v. Instead, our results support a mechanism in which facilitation arises from changes in release site occupancy.

References

Dodge, F.A., & Rahamimoff, R. (1967). Co-operative action of calcium ions in transmitter release at the neuromuscular junction. J Physiol, 193(2), 419–432.

Thanawala, M.S., & Regehr, W.G. (2013). Presynaptic calcium influx controls neurotransmitter release in part by regulating the effective size of the readily releasable pool. J Neurosci, 33(11), 4625–4633.

Lin, K.-H., Ranjan, M., Lipstein, N., Brose, N., Neher, E., & Taschenberger, H. (2025). Number and relative abundance of synaptic vesicles in functionally distinct priming states determine synaptic strength and short-term plasticity. J. Physiology.

Neher E, Sakaba T (2008) Multiple Roles of Calcium Ions in the Regulation of Neurotransmitter Release. Neuron 59:861-872.