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Dr. Lu raises a number of relevant technical concerns in his comments above, to which I would add two points that further problematize the presented data in light of the clustering/non-linear integration debate. First – these animals are anesthetized, which has been shown to affect a variety of conductances (Ih in particular) as well as inhibit GABAergic transmission, both of which are of course critical for processing in the cortical microcircuit. Within this paradigm, the investigators are presumably forced to use these 1-second presentations of visual stimulus in order to resolve their Ca2+-signals, which may be totally irrelevant in an awake animal with “intact” corticothalamic activity. Second – in order to isolate dendritic “hotspots”, the authors inject hyperpolarizing current through the soma to prevent axonal AP generation, which is going to significantly alter the balance of membrane conductances, limiting the initiation of any dendritic non-linearities.

Given these issues, as well as those raised previously in the comments, its hard to evaluate the claims in the paper (and the accompanying article by Ferster and Priebe) regarding clustering and non-linear integration. Instead, I think the most parsimonious interpretation comes from what is shown more conclusively in terms of “functional anatomy” – there are representations of different orientations along individual branches in L2 pyramids rather than a restricted whole-branch tuning schema. How the different tuning orientations interact along individual branches and with other branches at the axon in awake behaving animals remains to be seen.

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Obviously the reviews of this paper was so ‘wowed’ by the fancy virus technique that they didn’t bother to wonder if the results are actually sound. This is too bad, since clearly, if this technique is carefully and properly characterized, even if imperfect (labeling only ~10% of presynaptic neurons), it would be a very powerful tool. But sadly, this paper is far from a quantitative or convincing use of this technique, leaving me wondering…. wtf?!

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That said, I’d think that to claim that they’d “validated” this technique, they would have to show physiological (or other) proof of connectivity. Even one demonstration patched pair would be good. It’s not there. It’s a surprise, too, because in the earlier paper they show a couple of example paired recordings and then specifically say that it will be easier to validate the technique physiologically once it can be limited to single cells. So I’m baffled that the reviewers didn’t ask for this. Maybe there’s some reason it wasn’t feasible in this study?

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The link to Alzforum.org used as support in regard to other groups finding that PrP is mediating A-beta-induced synaptic effects is a comment from Walsh et al in regard to a paper (Balducci et al, 2010) that has conflicting behavioral results with Lauren et al. More curious is the lack of reference to these “consistent data” in a Nature News article about PrP and A-beta (http://www.nature.com/news/2010/100824/full/4661031a.html)

However, a very interesting proposition was made at the end of this reply: PrP may not be THE receptor for A-beta, but may help concentrate A-beta at the surface of neurons, thus increasing it’s functional activity via the true receptor for A-beta. PrP is primarily an intracellular protein, though some studies suggest that PrP can exist extracellularly in normal/healthy conditions. This adds a level of complication to the story on the possible existence of a receptor for extracellular prion protein bound to A-beta, or a complex mechanism on how extracellular A-beta can pass through the plasma membrane to bind with intracellular PrP.

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The picture of different sized spleens is visually impressive, but tissue weight needs to be normalized to animal body weight to have meaning.

Intravenous inoculation is a concern, given that the normal route of infection is oral.

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I would have liked to see the affects of NO on growth of the wildtype vs. aox mutant, rather than just oxygen consumption as a measure of respiration. Apparently these experiments were performed, but were “data not shown”. The authors also did not test their aox mutant in a colonization assay of the squid, although perhaps these are experiments in progress.

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Until such questions about the underlying user populations are satisfied it is really difficult to conclude that there is anything clearly associated with the THC/cannabidiol ratio.

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It will be nicer for the authors to illustrate more about the pathogenic or virulence connection of those perturbation being investigated in the paper, such as, SDS, EDTA and albomycin, in addition to recapitulate the function of TAT system in E.coli, because, the substrates between E.coli and Salmonella for TAT system may or may not be the same, though the genes share high conservation.

The paper showed clearly different Salmonella infection consequence between day 4 postchallenge for chickens at age of 4 days and day 1 postchallenge for chickens at age of 7 days, notably, the chickens were all about at age of 8 days. Probably, this is some thing that should be kept in mind when doing Chicken experiments, ie, it seems some kind of fundamental difference between chickens at the age of 4 days and 7 days in term to the susceptibility of Salmonella.

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In this paper, the authors address the question of generalization of dynamics learning across changes in amplitude. They report that subjects generalize from larger to smaller amplitudes but not vice-versa. They hypothesize that this asymmetry arises because increasing amplitude forced the subjects to use higher velocity than experienced during the training, and they could therefore not use what they had learned at lower velocities. They also performed a couple of control experiments to reconcile their data with the data from Goodbody and Wolpert who addressed the same issue ten years ago.
Unfortunately, the conclusions of the paper are based on a flawed statistical argument (comment #1) and most of the analyses are poor (wrong parameter, no normalization for speed differences, …. see comments #2). Therefore, the data might tell something else than what the authors concluded.

Major comments:

1. The statistics are often erroneously interpreted and there is a lack of direct comparison between the groups. One logic that the authors used but is incorrect is the following: if A and B are similar in experiment 1 (A1 and B1) but are different in experiment 2 (A2 and B2), then the outcome of the two experiments is different. This conclusion is obviously not correct. If A1 and A2 are equal to 0 and if B1 is N(1,0.8) and B2 is N(1.4,0.8), then A1 and B1 are not statistically different (p=0.11) whereas A2 and B2 are (p=0.04). Obviously B1 and B2 are not different. This type of argument is used many times throughout the result section.
For instance, the authors used this kind of comparison to assess the difference in generalization between their groups. In Fig. 2.C, actual and expected forces are different whereas they are not in Fig. 4.C. The authors therefore concluded that the patterns of generalization were different in the two experiments. More importantly, the authors used this logic to reconcile their data with the conclusion from Goodbody and Wolpert (Fig.6). However, superposing Fig. 2.C and 7.C clearly shows that the response in the two experiments are similar.
In sum, there is a clear lack of between-group comparisons, which does not allow the reader to assess the actual difference in generalization patterns. Such a difference might be assessed by using functional ANOVA to compare the actual force profiles from Fig. 2.C, 5.C and 6.C (given that expected force profiles are comparable). Finally, to avoid this statistical flaw, the authors should summarize their data by one parameter normalized for speed (see comment #2) and should directly compare their different conditions.
2. In panels E of Fig. 2, 4, 5 and 6, the authors used the difference in total force production as their dependent measure. However, this measure depends on the level of expected force, hence on the speed of the movements, which are different for the two different movement amplitudes. For instance, let’s consider that EF1(t) and EF2(t) are the expected force profiles from panel 2.B and 2.C (15 and 30cm movement amplitudes, respectively) and that the corresponding actual forces are hypothesized to be equal to 0.8*EF1(t) and 0.8*EF2(t). In this case, the total force production (integral of 0.8*EF1(t) and of 0.8*EF2(t), respectively) will differ because EF1 and EF2 are different (given the difference in movement amplitudes). This reasoning shows that the dependent measure chosen by the authors is not comparable across different movement speeds whereas comparing force profiles across different movement amplitudes is the actual goal of the paper.
Therefore, the authors normalize their dependent measure for the level of expected force and at best they use one of the two typical measures that are used to assess the level of adaptation in force-field paradigms, i.e. the percent perturbation or the regression coefficient measures (Scheidt et al. 2000 JNeurophy, Wang and Smith, 2008 JNeurosci). If the authors decided to keep a normalized version of their measures, they should explain the reasons for not using one of the standardized measures.
In addition, people usually found that lateral force production during channel trials was not equal to the expected force, especially after 150 trials (e.g. Scheidt et al. 2000, Wagner and Smith 2008) but quickly reached 80% of the expected force. Therefore, testing whether actual and expected forces are similar does not seem to be adequate.
3. The authors claimed that when there is an increase in movement amplitude, subjects only generalized when the hand velocity was within the range of velocities experienced during training (p.431, right column, second paragraph). I’m still looking for one statistical analysis supporting this claim…
4. In this study, increasing the amplitude led to a corresponding increase in velocity, which, the authors hypothesized, impaired the ability to generalize. If this hypothesis is correct, increasing the amplitude of the movements without increasing their velocity should lead to full generalization (OK given Goodbody and Wolpert). On the other hand, increasing the velocity without changing the amplitude should lead to absence of generalization (opposite to Goodbody and Wolpert). To confirm their theory, the authors should run those two additional experiments.
5. The title of the paper is misleading as the authors studied generalization across different amplitudes AND across different velocities at the same time.
6. The authors should clearly define what they call complete generalization or absence of generalization. It seems to me that the authors did not consider any possibility between those two. However, it has clearly been shown that directional generalization is not on or off but that there is partial generalization for neighboring directions. Fig. 8 from this paper also suggests that there is some generalization going on when the amplitude of the movements are increased.

Conclusion

In sum, given all the flaws above, this paper is really inconclusive with respect to whether there is full or partial generalization across different movement amplitudes and speeds.

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Other than this, and the general lack of detail in some of the figure legends and methods (an all too common problem these days), I think this is a pretty interesting and convincing paper. It’s very interesting to me that there appears to be a migration defect with DISC1 knockdown at later stages, i.e. E15, but not earlier, E13-E14, both here and in the earlier paper, Mao et al., 2009. Compare for example Figure 4A, where if anything DISC1 RNAi at E13 leads to an INCREASE in cells in the cortical plate 3 days later, with Figure 5E, where DISC1 RNAi at E15 completely lacks cells in the CP 4 days later. In contrast, Dixdc1 RNAi impedes radial migration at both early and later time-points. One possible explanation that the authors don’t explicitly consider is that Dixdc1 has two discrete functions related to migration, one of which is potentially completely independent of DISC1. This is suggested by their data in Figure 7B showing that overexpression of Dixdc1 fragment 1 (the N-terminal part with the CH domain) has an equally deleterious effect on radial migration as does fragment 2, which is the DISC1/Ndel1-binding fragment, and which they show inhibits endogenous Dixdc1-DISC1/Ndel1 interaction (Supp Fig 7). Although this is very interesting, it casts doubt on the model that a Dixdc1-DISC1 interaction is at all involved in regulating migration; rather the data seem to be consistent with each protein being involved independently in radial migration. (In that light, also interesting to note that the phospho-mutant Dixdc1 Ser250Ala did not show impaired binding to DISC1.)

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I ask those questions, ’cause it makes me wonder about the generalization of the results they’re discussing. Is the apparent lack of “clustering” species specific, and does it result from the specific physiology of orientation tuning in the mouse?

And, for “curious” there’s no clear answer to what “computation occurs at L2/3 of primary visual cortex.” generally, and almost nothing in the mouse, to my awareness. Someone correct me if I’m wrong.

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The paper itself seems nicely done but I don’t know much about the assay they use. They use FRET-based detection of vesicle fusion, but the fusion event is between two vesicles, rather than a vesicle and the plasma membrane. This may be a critical difference since membrane curvature can have significant effects in fusion events. Does anyone know if this kind of assay is commonly used and accepted in the membrane fusion field?

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One thing I’m wondering about is the synapse-specificity of this type of plasticity. As in, I don’t think there is any. This is similar to another form of plasticity in vestibular neurons referenced often in this paper (Nelson2003). So is there a reason while all the synapses in a cell should potentiate, other that homeostatic regulation?

Nice observation about the switching from VC only in the baseline period to CC and VC after the induction. As you say, seems a little strange that they don’t follow the same protocol for both. I would assume that the plasticity doesn’t occur if they don’t leave the cell in CC after the induction.

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Of course activating a bunch of inhibitory neurons would end up activating some excitatory neurons by rebound spiking or whatever, but it’d still be interesting to see.

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Your experiences with electroporation are illuminating. To some extent, I always expected that there would be the variability that you describe. What is surprising is the way that statistics are done for these experiments. They are counting each cell as an individual “n” and doing their tests on that. Going back and looking at their figures now, that is very obvious, given the tight error bars. I thought they would average the cells and calculate each slice as an “n.” Statistically there’s a huge difference. Doing each cell as an “n” will give a lot of false positives, as you rightly point out. Still it seems incredibly reckless to publish these data unless they were sure of what they were seeing.

About the EM, I think you just have to trust the authors, somewhat. It’s true that the methods used for the RGCs and SNPs were different, although I think at least one RGC was labeled with only DAB. It’s also true that photoconversion can be variable. However I don’t think it’s worth it to look at one panel in a figure and try to decide if they did their EM right. As a side note, it would be good if they specified that the EM was done blind (they do say that the cell counting in Gal 2006 was done blind).

Regarding the Shen 2006 paper, you could say the same thing applies as for the Noctor 2006 which is that something required for the appearance of SNPs is missing in culture. However going back and reading the Gal paper again, they actually do some slice culture experiments where they see SNPs. So they are pretty much in direct conflict with the Noctor papers. Of course, it’s entirely possible that the different results are due to differences in the culturing protocol between labs, since even small differences can have huge effects, especially in the composition of the culturing media. Still the fact that one group sees these SNPs and another does not under similar conditions is alarming.

I’m in complete agreement about doing some in vivo transfection, or infection, or whatever. Anything other than electroporation. Do you think they’ve tried other methods and didn’t see SNPs or are they just so enamored of this method that they don’t think anything else is worth it?

Also how would you explain their experiments showing that the reporter constructs driven by Talpha1 and GLAST seem to identify two morphologically different populations? Do you think they are just labeling two subpopulations of radial glia progenitors? One thing that’s troubling to me is the possibility that the reporter itself is affecting cell morphology. They are adding exogenous Tubulin-alpha1 promoters that are competing with the endogenous promoter. Presumably this decreases the expression of, um, tubulin, a cytoskeletal element that might be required for the radial glia. Still that can’t be the whole story since they see SNPs with straight EGFP reporters.

Thanks again for the discussion.

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Regarding electroporations: I’ve noticed a large degree of variability between different electroporations even with the same construct. If one electroporation is just a little bit more medial or lateral than another, this can result in a very different “migration pattern.” This is dangerous because you can quantify 2000 cells in a slice and then test for significance against 2000 cells in another slice. With this many cells you are very likely to get statistical significance, but this significance would average out if you quantified more slices. Even within the same electroporation results can vary depending upon whether one looks at the center or edge of the electroporation. I’ve been heart broken many times with results that were significant after 3 slices (thousands of cells counted), but went away after repeated testing.

Regarding EM: Perhaps my opinion of the rest of the figures is increasing my skepticism of these images. However, I find it suspicious that the SNP they reconstructed was only done with DAB, while the radial glial progenitor they show was first labeled with DiI and then DAB. Also when I look at figure 5Bi (Gal et al. 2006) there appears to be a radial glial fiber coming out of the top of the SNP. If you are more familiar with looking at EM images, maybe you could ease my paranoia a bit. Any ideas on what that is on top of the cell?

Regarding Noctor’s slice culture: Perhaps there is a shift in cell fate in slice culture, but I’m skeptical that progenitors accounting for 50% of the population (figure 4 Gal et al. 2006) disappear completely. The Shen et al. 2006 article from Sally Temple’s Lab would seem to indicate otherwise as dissociated cortical neurons in vitro appear to generate the same types of neurons in the same order as in vivo. Maybe these SNP’s don’t transfect as well? That would explain the discrepancy between the two groups.

I would find their fluorescent images more convincing if they did use in vivo transfection instead of electroporation. It would be much easier to distinguish single cells in the VZ.

Thanks again for the input.

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Regarding your skepticism about SNPs, I would make a couple of points. First, you refer to Noctor 2008 and point out that they never see a neuron without radial glia. These time-lapse imaging studies are impressive but are done in slice culture, a decidedly artificial situation. Perhaps SNPs are not generated in slice culture, not a very difficult thing to imagine. Second you are not convinced of the resolution in the images presented in Gal 2006. But they did serial section EM reconstruction of a cell without radial glia. How can you get better resolution than that?

-Slightly less pessimistic anon.

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I like the experiments not only because they find the molecular actors that transduce the elements of the induction protocol, but also because the actors’ roles are a bit surprising. Even if you’ve gotten used to the “cerebellum is backwards” routine (i.e. plasticity rules for firing neurons opposite from those in quiescent cells in cortex, hippocampus), the discovery that calcineurin can serve as a potentiating factor is still a bit startling. Even more surprising is the finding that, at least under these conditions, calcineurin and CaMKII, traditionally in opposition to each other in the hippocampus/cortical plasticity paradigms, are working in concert here. It’s a nifty finding.

One follow-up I’d be interested to see concerns the onset of potentiation. In most of the protocols explored, the EPSC amplitude ramps up slowly after the protocol, reaching a plateau 20-25 min afterwards. But in a few experiments here (active calcineurin plus long hyperpol, Fig 1D; active CaMKII with stim in VC, Fig. 3D), the EPSC amplitude reaches maximum right away. Why might that be? Are a few cells showing a sort of PTP that then averages out with other more “normal” cells to give the results, or are these protocols unusually fast at driving AMPA-R insertion (or whatever)?

The only thing about this paper that weirded me out a bit is that, if I understand the Methods correctly, the authors test EPSC amplitude while holding the neuron in continuous voltage clamp prior to protocol onset; and then test EPSCs after protocol onset by maintaining the neuron in current clamp and switching rapidly back to VC for tests. Is this necessary? It would be good if they either justified the rationale for different pre/post testing parameters, or if they repeated at least a few experiments with the same conditions pre/post. This is particularly important given their finding that postsynaptic spontaneous spiking (or membrane potential) influences plasticity induction (e.g. Figs. 5, 6). Or maybe I’m just misreading the methods?

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Figure 1. – The choice of time points baffles me. Going by Takahashi & Caviness 1995 numbers on cycle times in the telencephalon, the time to label cells in m-phase along the ventricular zone should be 3-6 hours prior to the time of the elecroporation not from 2 hours prior to 6 hours after (s-phase ~ 4 hours; G2+M = 2 hours).

The authors intended to address this time discrepancy in a supplemental figure showing that not all cells are electroporated in m-phase. I like the idea of using BrdU labeled plasmid to determine where the plasmid is going immediately after electroporation(Supplemental fig). However, these pictures are horrible, of low magnification and do not indicate where the cell bodies of the electroportated cells are. Radial glial fibers extend throughout the cortical wall. Just because BrdU labeling is found in the upper vz does not mean that cells were electroporated there. For all we know the cell bodies of those cell could all be along the ventricle. It may be that electroporations can reach deeper into the vz than thought, but this paper does not provide adequate evidence of that.

Furthermore, regarding Fig 1, these pictures are too low of a magnification to convincingly show coexpression of anything. For some reason this group feels no need to display all of the channels in black in white and then showing the colored composite. This makes data extremely difficult to interpret.

Figure 2. I’m puzzled the CAG-RFP isn’t on the same graph with the other two traces. The only effect this serves is to prevent comparing the Talpha1 and GLAST promoters to the control. Shouldn’t the GLAST and Talpha1 traces average to look like the CAG-RFP? They don’t. It’s not even close.
Quantifying electroporated slices is dangerous. Three slices is enough to get you a star or statistical “significance” but quite often this statistical significance will go away after quantifying multiple slices from multiple electroporations.

Figure 3. After looking at hundreds of electroporated slices I’m very confident in saying there is no meaningful difference between these images aside from density of labeling. Again with an n of 3-4 slices you can convince yourself of anything.

Figure 4. I want to see these in the same slice. There is too much variability in timing these litters. A mating at the beginning of the pairing vs the end can easily switch from predominantly layer 2/3 to 4 fate. For this figure only 2 slices were quantified. Nice!

Figure 5. Not only are we not allowed to see the grey-scales for each channel, the imaging settings between these images is vastly different. Forget the gfp+ cells. Look at the slice, which should be identical between X and X’. These images are not comparable.

Figure 6. There is no evidence for non-symetric divisions in the svz. It’s 2 progenitors or 2 neurons. Also if I am to believe figure 2 then what neural progenitors would still be BrdU labeled in Talpha1 30hrs post electroporation if they produce post mitotic neurons?

On snp’s in general: Stephen Noctor and Arnold Kriegstein have done beautiful work time-lapsing hundreds of individual neurons (not bulk electroporations) and have yet to see one without a radial glia. In a many of their movies the radial glia narrows as the cytoplasm bulges and pulls down towards the soma, but a thin radial glia remains(see Noctor 2008). I don’t believe the quality of the images taken in this and the 2006 paper would resolve it, especially when they put arrows right over where the fiber would be (see 2006 paper). SNP’s might exist but this and the 2006 paper have provided no reason for me to believe in them. I would certainly welcome someone else’s opinion on this.

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In Fig3 they show hotspots mapped onto the dendritic tree of one cell. All the hotspots are within about 60uM of the soma, which was the imaging area. Are there hotspots in the distal dendrites?

I wonder about the distribution of hotspots with the same orientation selectivity. OK I believe them when they say they are not clustered but with the examples they give, they make it seem like they are evenly spread throughout the dendritic tree, that is spatially distributed, perhaps non-randomly. One would expect if they were placed randomly, some would wind up next to each other by chance. Seems like they could test that if their data set is large enough.

-Yurut

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However, I am not convinced of one of the authors main conclusions: that there is no clustering of inputs. Sure they show that hotspots with the same orientation tuning are distributed. But what exactly is a “hotspot”? Elevated Ca as measured by a OGB-1, a high affinity Ca sensor. That does not mean that a hotspot = a single synapse. Ca-imaging does not have single synapse specificity. So how do we know that a single hotspot does not correspond to a cluster of multiple adjacent synapses with the same orientation tuning? We don’t. The authors provide some weak evidence that the Ca signal they see is similar to what can be produced from a single synapse, but this very important possibility is not directly tested.

So a very interesting paper but I do not feel they provide convincing evidence that there is no clustering of synaptic inputs with similar orientation tuning.

What do you think?

-Yurut

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