Peer review of: A spike-timing-dependent plasticity rule for dendritic spines (2018)

Reviewers' Comments: 
 
Reviewer #1: 
Remarks to the Author: 
In the present article, Tazerart and colleagues provide insights into the synaptic mechanisms 
underlying spike-timing dependent plasticity (STDP) in pyramidal neurons. They developed protocols 
to induce STDP using combination of postsynaptic spikes (bAP) and 2-photon glutamate uncaging at 
single or multiple synapses. This way they can control the spatial and temporal pattern of pre- versus 
postsynaptic pairing and discovered some of the rules governing structural and functional aspects of 
LTP and LTD using deterministic, well-controlled patterns of synaptic activation. This is a significant 
question that has never been explored using such precise and advanced approaches and the results 
are clear cut. The authors show that pre-post sequences of synaptic activation (mimicking a synapse-
specific form of Hebbian plasticity) induce LTP, actin-dependent shortening of spine neck and 
increased eEPSP amplitude whereas post-pre pairing induced LTD without affecting spine neck length. 
Finally, the authors provide evidence that tLTP (but not tLTD) induced by cooperative stimulation of 2 
spines (within ~5microns) triggers a change in both spine head and dendritic Ca2+ accumulation that 
is ~ linearily proportional (following a threshold of ~10 repetitions) to the number of repetitions of 
synaptic pairing. 
I only have a few comments to be addressed: 
 
1- In experiments involved for Figure 6-8, how many spines/dendritic branches were tested? I realize 
that these experiments are complex but I wonder how generalizable these results are since it is very 
likely that a substantial degree of variability exist between branches and even individual spines in their 
expression of this form of synaptic plasticity since (1) work from several groups including Kristen 
Harris (serial EM) and also Thomas Oertner’s group (using functional imaging; PMID: 19706463) have 
shown that ~20-30% of spines in hippocampal or cortical pyramidal neurons (exact fraction seems 
cell-type specific and depends on plasticity history) contains endoplasmic reticulum extensions 
invading the spine neck and head that plays a role in regulating Ca2+ dynamics and structural forms 
of plasticity and (2) that the life history of a neuron especially with regard to synaptic potentiation 
influences the expression of structural and functional forms of synaptic plasticity in spines (PMID: 
30311904). The authors should at least cite and discuss their own results in light of these papers or 
increase their n numbers and determine if all neurons/dendritic segments/spines are equal in their 
ability to express the type of STDP they report. 
2- Regarding the PEP1-TGL and LatA experiments, since most of the results are ‘negative’ the authors 
should consider how effective these treatments were using extracellular application in slices. For 
example for LatA, have the authors tried to determine if there is any effect on F-actin distribution in 
these neurons? The absence of effect on spine neck plasticity might simply be due that this 
manipulation is not very effective at removing polymerized F-actin. In neurons, synaptically localized 
F-actin is very stable and simply preventing new polymerization is inefficient at depolymerizing F-actin 
bc of low turnover. The authors should have a way to show that their negative result is not due to 
inefficient treatment. 
 
 
 
Reviewer #2: 
Remarks to the Author: 
The paper by Tazerart et al. examines the properties of spike timing-dependent plasticity in basal 
dendrites of layer 5 pyramidal neurons. To address this question, the authors combine two-photon 
glutamate uncaging, two-photon imaging, and electrophysiology. The main findings are: 
- For single spine activation, synaptic plasticity follows a bidirectional Hebbian induction rule in which 
pre-post pairing induces LTP, whereas post-pre pairing generates LTD. 

- For clustered activation of two spines, the bidirectional induction rule is converted into a 
unidirectional induction rule in which LTP is enhanced, whereas LTD is diminished. 
- Ca2+ imaging experiments suggest that this change in STDP induction rule is related to a buildup of 
Ca2+ concentration in spines and parent dendrites. 
- LTP is dependent on actin and AMPAR insertion, and associated with changes in spine neck length. 
 
Based on these results, the authors conclude that synaptic cooperativity extends the temporal window 
for the induction of LTP. Although the manuscript contains useful data entry presents a significant 
amount of work, I have two major problems with the manuscript. First, I am not entirely convinced 
about novelty, because several previous studies examined cooperativity at the synaptic level. Second, 
the paper has several flaws and major problems that need to be addressed before publication in any 
journal. 
 
Major points: 
1. The authors examine synaptic plasticity rules using glutamate uncaging. However, the rules of 
plasticity induction may not be the same for Ca2+ uncaging and synaptically released glutamate. The 
authors should either corroborate their results with synaptic stimulation experiments, or alternatively 
make very clear in title, abstract, and main text that the results hold, and only hold, for uncaging 
responses. 
 
2. Experiments were performed in young mice and at room temperature. At the very least, a major 
effort is to be undertaken to validate the results in older mice and at physiological temperature. 
 
3. A major difference between the present work and previous studies is that plasticity is not 
associated with spine head volume changes. The discussion of possible reasons is not convincing. If 
the authors think that different divalent concentrations are responsible for these differences, they 
should experimentally test this possibility. 
 
4. The present paper also stands in stark contrast to several previous papers that have studied STDP 
at the synaptic level and found reliable spike-timing dependent LTD. These include Markram et al., 
1997, Science; Normann et al., 2000, J Neuroscience; Sjöström et al., 2001; 2003, Neuron, etc. In all 
these papers, it is likely that multiple closely spaced synapses were activated. At the very least, these 
differences need to be better discussed. 
 
5. Previous work (e.g. Froemke et al., 2005, Nature; Sjöström and Häusser, 2006, Neuron; Letzkus et 
al., 2006, J Neuroscience) demonstrated that the rules of STDP induction are dependent on 
somatodendritic distance. However, the possible influence of this factor is largely ignored in the 
present paper. The dependence of cooperativity rules on somatodendritic distance should be analyzed. 
 
6. The mechanisms of t-LTP and t-LTD induction should be better worked out. This seems particularly 
important for t-LTD. Previous work revealed that t-LTD is NMDAR-dependent, mGluR-dependent, or 
CB1 receptor dependent. It would be nice to know in which category the t-LTD reported in the present 
paper falls. A strength of the uncaging experiment is that presynaptic effects are lacking, which 
simplifies the interpretations. Unfortunately, the authors miss this unique opportunity. 
 
7. The mechanisms underlying the cooperativity should be more thoroughly explored. The authors 
apparently think that passive propagation of local depolarizations along the dendritic cable is 
important, but the “length constant” of cooperativity only partially fits to the length constant of 
dendritic cable. Previous work showed that active conductances in the dendrites play a role in 
cooperativity (Sjöström and Häusser, 2006). The role of active mechanisms should be better 
addressed. 

 
8. I assume the Ca2+ transients are mediated by NMDARs, but this should be tested directly. 
 
9. The quantification of LTP and LTD is unusual. The authors measure either the maximal change or 
the average over the entire period after induction. A standard way is to measure the average 20 - 30 
min after induction, to better incorporate the long-lasting nature of the potentiation in the definition. I 
also find statistical testing on maximal values (i.e. outliers) dubious. 
 
10. Finally, the paper is not very well written. The manuscript is far too long in relation to the novel 
information it contains. The results section often provides repetitive descriptions, and the legends are 
almost exact repeats of each other. Redundancies should be removed. The figures also require 
improvement. Additional EPSP original traces (single traces and averages) should be included in the 
panels. Likewise, more high-resolution images documenting the changes in spine neck length (and the 
absence of spine head size changes) should be included to convince the reader. 
 
Minor points: 
Page 2: The abstract should mention that recordings were made in neocortical layer 5 pyramidal 
neurons. Furthermore, the terms t-LTP and t-LTD need to be introduced. 
 
Line 63: How simultaneous is “nearly simultaneous”? 
 
Line 75: “uEPSP” should be introduced as “uncaging EPSP”. 
 
Line 101: “similar results were observed” – more precise statements are needed. 
 
Line 139: “inputs that are uncorrelated” - the statement is not strictly correct, because a post-pre 
activity sequence implies a correlation. 
 
Line 149: “amount of voltage” – clumsy, replace. 
 
Line 153: “demonstration of cooperativity … has yet to be obtained” – I don’t think the authors can 
say this (Sjöström et al., 2001). 
 
Line 170: “significant increases … occurs” should read “significant increases … occur”. 
 
Line 240: “These results suggest that the control of AMPA receptor content in spines could contribute 
significantly …” – this seems to be a well established fact in the scientific literature. The authors are 
reinventing the wheel. 
 
Line 345: Why is P < 0.05 given sometimes, whereas the precise P values are given elsewhere? 
Precise P values should be given throughout. 
 
Line 442: These apologetic statements should be replaced by more experiments and additional data. 
With an n = 6, there is no way to tell whether there is a difference or not. 
 
Line 458: “building upon previous observations” should probably read “extending previous 
observations”. 
 
Line 496: The authors should more carefully distinguish between the “length constant” of the synaptic 
cooperativity and the length constant of the dendritic cable. 
 

Line 498: “can extends” should read “can extend”. 
 
Line 517: The paper by Markram et al., 1997, Science, should be cited here. 
 
Line 517: “controversy” – do the authors mean “discrepancy”? 
 
Line 624: What was the series resistance in these recordings? This factor is equally or perhaps more 
relevant than the presence of spines or spine necks. 
 
Line 651: Why is the time course of the uEPSPs not temperature dependent, given that all underlying 
processes (transmitter release, channel kinetics) are temperature dependent? 
 
Line 658: A 10-ms pulse cannot be called brief. How much of the observed effects is generated by the 
pulse itself, rather than the action potential evoked by the pulse? 
 
Line 691: How exactly was threshold determined? What was the derivative criterion? 
 
Line 697: “the membrane potential” – which? Resting or baseline? 
 
Line 702: “not significantly different … 10% variation” – this vague statements should be supported by 
test of statistical significance. 
 
Line 706: “using Wavemetrics” – the authors mix up program and provider. 
 
Line 713: What is meant by “majority”? 
 
Line 729: “we set the length ….” – this seems completely arbitrary. 
 
Line 740: “a least squares technique” – this is a minimization criterion, not a technique. 
 
Line 777: The authors use t tests for statistical analysis. If they want to maintain this, they have to at 
least test for normality. Alternatively, and better, they should use nonparametric tests throughout. 
 
Line 777: It should be stated whether numbers are expressed as mean +- SEM and whether 
membrane potentials are corrected by junction potentials. 
 
References are often incomplete and need to be checked. 
 
Line 1140: “extracted value” should be “estimated value”. 
 
Line 1284: “our model indicate” should read “our model indicates”. 
 
Figure 4: Wouldn’t it be better to include latrunculin-A in the pipette? 
 
Figure 6: What are the units of delta F? If these are arbitrary units, this should be mentioned. Is delta 
G / R given in %? 
 
Figure 9: The labels > 5 µm and > 40 µm define overlapping ranges. Unequivocal labeling should be 
provided. 
 
 

Supplementary material: 
Figure S1: Panels should be labeled ABCD. 
 
Line 24: “Actual values” should probably read “absolute values”. 
 
Why was Dunnet’s test used for multiple comparisons in some cases, but Tukey’s test used in other 
cases?