Decoding Spine Nanostructure in Mental Disorders Reveals a Schizophrenia-Linked Role for Ecrg4

Reviewer #1 (Public review):

Summary:

Kashiwagi et al. undertook a population analysis of dendritic spine nanostructure applied to the objective grouping of 8 mouse models of neuropsychiatric disorders. They report that spine morphology in cultured hippocampal neurons shows a higher similarity among schizophrenia mouse models (compared with autism spectrum disorder (ASD) mouse models), and identify an effect of Ecrg4 (encoding small secretory peptides) on spine dynamics and shape in these models.

Strengths:

The study developed a method for objectively comparing spine properties in primary hippocampal neuron cultures from 8 mouse models of psychiatric disorders at the population level using high-resolution structured illumination microscopy (SIM) imaging. This novel technique identified two distinct groups of mouse models according to the population-level spine properties: those with ASD-related gene mutations and those with schizophrenia-related gene mutations. Functional studies, including gene knockdown and overexpression experiments, identified an effect of Ecrg4 on the spine phenotype of the schizophrenia model mice.

Weaknesses:

The main weakness is that the study is wholly in vitro, using cultured hippocampal neurons. The authors present this as an advantage, however, arguing that spine morphology as measured in a reduced culture system can demonstrate direct effects of gene mutations on neuronal phenotypes in the absence of indirect influences from nonneuronal cells or specific environments.

Another weakness is that CaMKIIαK42R/K42R mutant mice are presented as a schizophrenia model, the authors justifying this by saying that "CaMKII-related signaling pathway disruption has been implicated in the working memory deficits found in schizophrenia patients". Since mutations in CAMK2A cause autosomal dominant intellectual developmental disorder-53 (OMIM 617798) and autosomal recessive intellectual developmental disorder-63 (OMIM 618095), and mice carrying the CAMK2A E183V mutation exhibit ASD-related synaptic and behavioral phenotypes (PMID: 28130356), I think it's stretching credibility to refer to the CaMKIIαK42R/K42R mice as a schizophrenia model.

Although the manuscript is largely well written, there are some instances of ambiguous/unspecific language. This extends to the title (Decoding Spine Nanostructure in Mental Disorders Reveals a Schizophrenia-1 Linked Role for Ecrg4), which gives no indication that the work was in vitro on cultured neurons derived from mouse models.

Reviewer #2 (Public review):

Okabe and colleagues build on a super-resolution-based technique that they have previously developed in cultured hippocampal neurons, improving the pipeline and using it to analyze spine nanostructure differences across 8 different mouse lines with mutations in autism or schizophrenia (Sz) risk genes/pathways. It is a worthy goal to try to use multiple models to examine potential convergent (or not) phenotypes, and the authors have made a good selection of models. They identify some key differences between the autism versus the Sz risk gene models, primarily that dendritic spines are smaller in Sz models and (mostly) larger in autism risk gene models. They then focus on three models (2 Sz - 22q11.2 deletion, Setd1a; 1 ASD - Nlgn3) for time-lapse imaging of spine dynamics, and together with computational modelling provide a mechanistic rationale for the smaller spines in Sz risk models. Bulk RNA sequencing of all 8 model cultures identifies several differentially expressed genes, which they go on to test in cultures, finding that ecgr4 is upregulated in several Sz models and its misexpression recapitulates spine dynamics changes seen in the Sz mutants, while knockdown rescues spine dynamics changes in the Sz mutants. Overall, these have the potential to be very interesting findings and useful for the field. However, I do have a number of major concerns.

(1) The main finding of spine nanostructure changes is done by carrying out a PCA on various structural parameters, creating spine density plots across PC1 and PC2, and then subtracting the WT density plot from the mutant. Then, spines in the areas with obvious differences only are analyzed, from which they derive the finding that, for example, spine sizes are smaller. However, this seems a circular approach. It is like first identifying where there might be a difference in the data, then only analyzing that part of the data. I welcome input from a statistician, but to me, this is at best unconventional and potentially misleading. I assume the overall means are not different (although this should be included), but could they look at the distribution of sizes and see if these are shifted?

(2) Despite extracting 64 parameters describing spine structure, only 5 of these seemed to be used for the PCA. It should be possible to use all parameters and show the same results. More information on PC1 and PC2 would be helpful, given that the rest of the paper is based on these - what features are they related to? These specific features could then be analyzed in the full dataset, without doing the cherry picking above. It would also be helpful to demonstrate whether PC1 and 2 differ across groups - for example, the authors could break their WT data into 2 subsets and repeat the analysis.

(3) Throughout the paper, the 'n' used for statistical analysis is often spine, which is not appropriate. At a minimum, cell should be used, but ideally a nested mixed model, which would take into account factors like cell, culture, and animal, would be preferable. Also, all of these factors should be listed, with sufficient independent cultures.

(4) The authors should confirm that all mutants are also on the C57BL/6J background, and clarify whether control cultures are from littermates (this would be important). Also, are control versus mutant cultures done simultaneously? There can be significant batch effects with cultures.

(5) The spine analysis uses cultures from 18-22 DIV - this is quite a large range. It would be worth checking whether age is a confounder or correlated with any parameters / principal components.

(6) The computational modelling is interesting, but again, I am concerned about some circularity. Parameter optimization was used to identify the best fit model that replicated the spine turnover rates, so it is somewhat circular to say that this matched the observations when one of these is the turnover rate. It is more convincing for spine density and size, but why not go back and test whether parameter differences are actually seen - for example, it would be possible to extract the probability of nascent spine loss, etc. More compelling would be to repeat the experiments and see if the model still fits the data. In the interpretation (line 314-318) it is stated that '... reduced spine maturation rate can account for the three key properties of schizophrenia-related spines...', which is interesting if true, but it has just been stated that the probability of spine destabilization is also higher in mutants (line 303) - the authors should test whether if the latter is set to be the same as controls whether all the findings are replicated.

(7) No validation for overexpression or knockdown is shown, although it is mentioned in the methods - please include. Also, for the knockdown, a scrambled shRNA control would be preferable.

(8) The finding regarding ecgr4 is interesting, but showing that some ecgr4 is expressed at boutons and spines and some in DCVs is not enough evidence to suggest that actively involved in the regulation of synapse formation and maturation (line 356).

(9) The same caveats that apply to the analysis also apply to the ecgr4 rescue. In addition, while for 22q the control shRNA mutant vs WT looks vaguely like Figure 2, setd1a looks completely different. And if rescued, surely shRNA in the mutant should now resemble control in WT, so there shouldn't be big differences, but in fact, there are just as many differences as comparing mutant vs wildtype? Plus, for spine features, they only compare mutant rescue with mutant control, but this is not ideal - something more like a 2-way ANOVA is really needed. Maybe input from a statistician might be useful here?

(10) Although this is a study entirely focused on spine changes in mouse models for Sz, there is no discussion (or citation) of the various studies that have examined this in the literature. For example, for Setd1a, smaller spines or reduced spine densities have been described in various papers (Mukai et al, Neuron 2019; Chen et al, Sci Adv 2022; Nagahama et al, Cell Rep 2020).

(11) There is a conceptual problem with the models if being used to differentiate autism risk from Sz risk genes. It is difficult to find good mouse models for Sz, so the choice of 22q11.2del and Setd1a haploinsufficiency is completely reasonable. However, these are both syndromic. 22qdel syndrome involves multiple issues, including hearing loss, delayed development, and learning disabilities, and is associated with autism (20% have autism, as compared to 25% with Sz). Similarly, Setd1a is also strongly associated with autism as well as Sz (and also involves global developmental delay and intellectual disability). While I think this is still the best we can do, and it is reasonable to say that these models show biased risk for these developmental disorders, it definitely can't be used as an explanation for the higher variability seen in the autism risk models.

(12) I am not convinced that using dissociated cultures is 'more likely to reflect the direct impact of schizophrenia-related gene mutations on synaptic properties' - first, cultures do have non-neuronal cells, although here glial proliferation was arrested at 2 days, glia will be present with the protocol used (or if not, this needs demonstrating). Second, activity levels will affect spine size, and activity patterns are very abnormal in dissociated cultures, so it is very possible that spine changes may not translate into in vivo scenarios. Overall, it is a weakness that the dissociated culture system has been used, which is not to say that it is not useful, and from a technical and practical perspective, there are good justifications.

(13) As a minor comment, the spine time-lapse imaging is a strength of the paper. I wonder about the interpretation of Figure 5. For example, the results in Figure 5G and J look as if they may be more that the spines grow to a smaller size and start from a smaller size, rather than necessarily the rate of growth.

Author response:

Reviewer #1

(1) The main weakness is that the study is wholly in vitro, using cultured hippocampal neurons.

We appreciate this reviewer's concern about the limitation of cultured hippocampal neurons in extracting disease-related spine phenotypes. While we fully recognize this limitation, we consider that this in vitro system has several advantages that contribute to translational research on mental disorders.

First, our culture system has been shown to support the development of spine morphology similar to that of the hippocampal CA1 excitatory synapse in vivo. High-resolution imaging techniques confirmed that the in vitro spine structure was highly preserved compared with in vivo preparations (Kashiwagi et al., Nature Communications, 2019). The present study used the same culture system and SIM imaging. Therefore, the difference we detected in samples derived from disease models is likely to reflect impairment of molecular mechanisms underlying native structural development in vivo.

Second, super-resolution imaging of thousands of spines in tissue preparations under precisely controlled conditions cannot be practically applied using currently available techniques. The advantage of our imaging and analytical pipeline is its reproducibility, which enabled us to compare the spine population data from eight different mouse models without normalization.

Third, a reduced culture system can demonstrate the direct effects of gene mutations on synapse phenotypes, independent of environmental influences. This property is highly advantageous for screening chemical compounds that rescue spine phenotypes. Neuronal firing patterns and receptor functions can also be easily controlled in a culture system. The difference in spine structure between ASD and schizophrenia mouse models is valuable information to establish a drug screening system.

Fourth, establishing an in vitro system for evaluating synapse phenotypes could reduce the need for animal experiments. Researchers should be aware of the 3Rs principles. In the future, combined with differentiation techniques for human iPS cells, our in vitro approach will enable the evaluation of disease-related spine phenotypes without the need for animal experiments. The effort to establish a reliable culture system should not be eliminated.

(2) Another weakness is that CaMKIIαK42R/K42R mutant mice are presented as a schizophrenia model.

We agree with this reviewer that CAMK2A mutations in humans are linked to multiple mental disorders, including developmental disorders, ASD, and schizophrenia. Association of gene mutations with the categories of mental disorders is not straightforward, as the symptoms of these disorders also overlap with each other. For the CaMKIIα K42R/K42R mutant, we considered the following points in its characterization as a model of mental disorder. Analysis of CaMKIIα +/- mice in Dr. Tsuyoshi Miyakawa's lab has provided evidence for the reduced CaMKIIα in schizophrenia-related phenotypes (Yamasaki et al., Mol Brain 2008; Frankland et al., Mol Brain Editorial 2008). It is also known that the CaMKIIα R8H mutation in the kinase domain is linked to schizophrenia (Brown et al., 2021). Both CaMKIIα R8H and CaMKIIα K42R mutations are located in the N-terminal domain and eliminate kinase activity. On the other hand, the representative CaMKIIα E183V mutation identified in ASD patients exhibits unique characteristics, including reduced kinase activity, decreased protein stability and expression levels, and disrupted interactions with ASD-associated proteins such as Shank3 (Stephenson et al., 2017). Importantly, reduced dendritic spines in neurons expressing CaMKIIα E183V is a property opposite to that of the CaMKIIα K42R/K42R mutant, which showed increased spine density (Koeberle et al. 2017).

Different CAMK2A mutations likely cause distinct phenotypes observed in the broad spectrum of mental disorders. In the revised manuscript, we will include a discussion of the relevant literature to categorize this mouse model appropriately.

References related to this discussion.

(1) Yamasaki et al., Mol Brain. 2008 DOI: 10.1186/1756-6606-1-6

(2) Frankland et al. Mol Brain. 2008 DOI: 10.1186/1756-6606-1-5

(3) Stephenson et al., J Neurosci. 2017 DOI: 10.1523/JNEUROSCI.2068-16.2017

(4) Koeberle et al. Sci Rep. 2017 DOI: 10.1038/s41598-017-13728-y

(5) Brown et al., iScience. 2021 DOI: 10.1016/j.isci.2021.103184

Reviewer #2

We recognize the reviewer's comments as important for improving our manuscript. We outline our general approach to addressing major concerns. Detailed responses to each point, along with additional data, will be provided in a formal revised manuscript.

(1) Demonstrating the robustness of statistical analyses

We appreciate this reviewer's concern about our strategies for the quantitative analysis of the large spine population. For the PCA analysis (Point 2), our preliminary results indicated that including all parameters or the selected five parameters did not make a significant difference in the relative placement of spines with specific morphologies in the feature space defined by the principal components. This point will be discussed in the revised manuscript. The potential problem of selecting a particular region within a feature space for spine shape analysis (Point 1) can be addressed by using alternative simulation-based approaches, such as bootstrap or permutation tests. These analyses will be included in the revised manuscript. The use of sample numbers in statistical analyses should align with the analysis's purpose (Point 3). When analyzing the distribution of samples in the feature space, it is necessary to use spine numbers for statistical assessment. We will recheck the statistical methods and apply the appropriate method for each analysis. The spine population data in Figures 2 and 8 cannot be directly compared, as the spine visualization methods differ (Figure 2 with membrane DiI labeling; Figure 8 with cytoplasmic GFP labeling) (Point 9). Spine populations of the same size are inevitably plotted in different feature spaces. This point will be discussed more clearly in the revised manuscript.

(2) Clarification of experimental conditions and data reliability

Per this reviewer's suggestion, we will provide more information on the genetic background of mice and the differences in spine structure from DIV 18-22 (Points 4 and 5). We will also provide additional validation data for the functional analyses using knockdown and overexpression methods, for which we already have preliminary data (Point 7). Concerns about the interpretation of data obtained from in vitro culture (Point 12), raised by this reviewer, are also noted by reviewer #1. As explained in the response to reviewer #1, we intentionally selected an in vitro culture system to analyze multiple samples derived from mouse models of mental disorders for several reasons. Nevertheless, we will revise the discussion and incorporate the points this reviewer raised regarding the disadvantages of in vitro systems.

(3) Validation of biological mechanisms and interpretation

In the computational modeling (Point 6), we started from the data of spine turnover (excluding the data of spine volume increase/decrease), fitted the model with the data, and found that the best-fit model showed three features: fast spine turnover, lower spine density, and smaller size of transient spines in schizophrenia mouse models. As the reviewer noted, information about spine turnover is already present in the input data. However, the other two properties are generated independently of the input data, indicating the value of this model. We plan to add additional confirmatory analyses to this model in the revised manuscript.

In response to Point 8, we will provide supporting data on the functional role of Ecgr4 in synapse regulation. We will also refine our discussion on the ASD and Schizophrenia phenotypes based on the suggested literature (Points 10 and 11). Quantification of the initial growth of spines is technically demanding, as it requires higher imaging frequency and longer time-lapse recordings to capture rare events. It is difficult to conclude which of the two possibilities, slow spine growth or initial size differences, is correct, based on our available data. This point will be discussed in the revised manuscript (Point 13).