Peer review of: CYCLIN-B1/2 and -D1 act in opposition to coordinate cortical progenitor self-renewal and (2020)

Reviewers' comments: 
 
Reviewer #1 (Remarks to the Author): 
 
Review Hagey et al. 
 
The paper by Hagey et al performs single cell RNA-seq to characterize the cell populations using 
cluster analysis. Bulk RNA-seq was used to determine how cell cycle phases might be involved in the 
regulation of cell fate in the developing brain. The transcriptional signatures in RGCs and IPCs appear 
to represent genes of distinct cell cycle phases, where RGCs express high levels of G2/M phase cell 
cycle proteins, while IPCs express G1 cyclins like D1. The authors then manipulate the expression of 
cyclins using in utero electroporation and find that manipulation of the expression of cell cycle proteins 
impact the fate of embryonic neural precursor cells. 
 
Overall, this is a very nice study that addresses a very interesting question. The results are very novel, 
and the ss-RNA-seq is a great approach to characterize the transcriptome in the developing brain. I 
have some further suggestions to strengthen the paper: 
 
1. The ssRNA-seq figures showing the trajectories of differentiation on the tSNE plots are very nice. 
The total number of cells used for ssRNA-seq seems rather low, 549. This is very surprising 
considering the embryo has a relatively large number of NPCs. A larger number of cells would 
strengthen the analyses, as some of the clusters contain relatively very few cells. 
 
2. The section ‘Uncommitted cortical progenitors display multipotent differentiation potential in vitro’, 
is less exciting and does not add much to the story, thus I would recommed shortening this section up. 
 
3. The in utero electroporation is an ideal approach by which to manipulate the embryonic brains, and 
the results obtained are clear and convincing, except the section examining division angle. To properly 
assess mode of division, ie symmetric vs asymmetric, a marker should be included that is 
asymmetrically segregated to more definitively demonstrate changes in the mode of division. 
Otherwise, this section should be removed, as it is not conclusive. 
 
4. The authors should elaborate a bit more as to the mechanism by which CyclinB1 
regulates notch signaling. What is the mechanism by which notch signaling is regulated by Cyclin B1. 
 
 
 
 
 
Reviewer #2 (Remarks to the Author): 
 
Hagey et al. investigated the transcription signatures of multipotent and lineage-committed progenitor 
cells. They identified multiple markers of the two neural progenitor populations including key factors 
involving cell cycle regulation. They further showed that B- and D-type cyclins control the timing of 
neurogenesis by promoting neural stem cell maintenance or differentiation, respectively. A detailed 
investigation identified that NOTCH signaling mediates the effects of B-type cyclins. 
 
General comments: 
Overall, I find the paper potentially important and interesting. Cell cycle has long been thought to be 
critical for the balance between neural stem cell maintenance and differentiation. This manuscript 
shows the novel involvement of B-type cyclin in regulating cortical neural progenitor cells. More 

importantly, the authors showed that the effects of cyclins are independent of cell-cycle phase 
dynamics, which is intriguing and unexpected. Cellular and histological investigations are relatively 
thorough and comprehensive. However, the single-cell analysis has not been done properly. 
 
Specific comments: 
1. For the tSNE figures in Figure 1 and Supplementary Figure 1, the way the authors perform 
dimension reduction, data visualization, and cell filtering is bizarre. Generally, for a high-quality 
single-cell RNA seq analysis, radial glia, IPCs, interneurons, excitatory neurons, and microglia should 
be readily identified and separated by an unbiased dimensional reduction using the most variable 
genes. The fact that the authors fail to separate these cell types using this way suggests either low-
quality data or a too small sample size. The authors end up using a defined set of genes to perform 
dimension reduction which makes the figures biased towards the hypothesis. 
 
2. The lineage analysis in Figure 2 is also strange. First of all, a tSNE plot is not most ideal to visualize 
lineages. Have the authors tried UMAP? UMAP is supposed to perform better in terms of consistent and 
meaningful organization of cells and to better visualize lineages. Also, instead of visually identify the 
differentiation trajectories on the tSNE plot, the authors should do this in a more sophisticated way 
using Monocle DDRTree, Slingshot, or RNA velocity. 
 
3. Also in Figure 2, when the authors define early and late differentiation trajectory, they based that 
on the expression of deep-layer and upper-layer genes. There are two problems with this. First, as 
mentioned in my second point, the authors should not assume a lineage relationship simply based on 
the proximity of clusters on a tSNE plot. For instance, it could be that cluster 2’ gives rise to both 
clusters 3 and 3’. Second, the expression of the layer markers should be analyzed in each cluster 
separately, not in the whole “trajectory”. Otherwise, the higher expression of these markers in more 
mature neurons will dominate the results and lead to wrong conclusions for the progenitor cells. 
 
4. The authors describe the use of a directed approach in order to examine the lineage relationship 
between cells. To do so, they use Prom1+ as a sole marker to FACS-sort committed and uncommitted 
progenitor populations from different cortical developmental timepoints for downstream bulk RNA-seq. 
Why was Prom1 chosen for this analysis? Why were different timepoints used to sample Prom1 
negative and positive populations (E11.5 and 15.5 for Prom1+ and E12.5 and 16.5 for Prom1-)? 
Dissecting the intricate trajectory relationships of progenitor cells based on bulk-RNA sequencing of 
cells sorted by a single marker (at two timepoints) seems highly biased. The authors should explain 
the rationale for this approach. 
 
5. The authors hypothesize that the uncommitted E11.5 cells represent multipotent RGCs with the 
potential to generate both deep and upper-layer neuronal lineages. To test this, they chose cell-
surface proteins enriched in upper-layer gene sets for FACS-sorting. It seems that these genes are 
also highly expressed in E11.5 newly committed upper-layer neurogenesis clusters (Fig. 2a, b; Fig. 
3d). How can the authors be sure that FACS sorting is not selecting E.11.5 cells that are already 
committed rather than uncommitted E.11.5 cells as stated? These experiments show the propensity of 
E.11.5 cells to generate upper layer neuron identity at the expense of deep layer identity in vitro, but 
have not shown the reciprocal experiment (generation of deep layer identity at the expense of deep-
layer). Thus, there is a possibility that the in vitro conditions favor the generation of upper-layer 
identity regardless of cell potential. 
 
6. In Figure 4, are SOX2 levels of HMMR+, GPC6+, and EDNRB+ cells higher than SLCA5+ and 
EFNA5+ cells? If SLCA5+ and EFNA5+ cells are IPCs committed to deep-layer neurons, have the 
authors checked if they are TBR2+? 
 

7. Also in Figure 4, the authors should be clear about the terms they are using to describe cell 
populations. In the present manuscript, they are very vague and confusing. For example, on page 11, 
lines 2-3, the authors write “…both multipotent and committed progenitors (respectively referred to as 
RGCs and IPCs from this point on)…”. Are committed progenitor cells all IPCs? How about older radial 
glia cells that only contribute to upper-layer neurogenesis? The authors should be very clear about the 
lineage (deep-layer) and the developmental time point (E11.5) of the committed progenitors they are 
referring to. They should also extend this clarification to the following paragraphs. 
 
8. From Figure 4 back to Figure 1, if the E11.5 deep layer committed progenitor cells are indeed IPCs, 
why are they not EOMES/TBR2 positive in Figure 1? Does it infer the low quality of the single-cell RNA 
seq data? 
 
Minor points: 
9. In figure 6c, 6e and Supp. Fig7 c,e,f. for some images it seems that SATB2 or POU3F2 are 
expressed from the VZ all the way through to the upper cortical layer. At E18.5 they should be 
restricted to the CP region. Is this an antibody specificity issue or are regions of cortex mislabeled? 
 
10. There are several citation oversights. The function of cyclin D in promoting neurogenesis has been 
reported before by the Anderson lab 1. The ability of NOTCH intracellular domain to keep progenitors 
as proliferating radial glia cells has also been reported previously 2. These findings should be properly 
cited. 
 
References: 
 
1. Lukaszewicza, A. I. & Anderson, D. J. Cyclin D1 promotes neurogenesis in the developing spinal 
cord in a cell cycle-independent manner. Proc. Natl. Acad. Sci. U. S. A. 108, 11632–11637 (2011). 
2. Mizutani, K. I. & Saito, T. Progenitors resume generating neurons after temporary inhibition of 
neurogenesis by Notch activation in the mammalian cerebral cortex. Development 132, 1295–1304 
(2005). 
 
 
 
 
Reviewer #3 (Remarks to the Author): 
 
In this study, Hagey and collaborators use single-cell RNA sequencing to investigate the mechanisms 
linking the cell-cycle machinery to cell-fate commitment. 
They find that RGCs are enriched in G2/M-phase genes, such as CYCLIN-B1, while IPCs highly express 
G1/S-phase genes, such as CYCLIN-D1. They also find cell-surface markers capable of isolating RGCs 
and IPCs. Finally, they demonstrate that CYCLIN-B1/2 cooperate with CDK1 to maintain RGCs in an 
uncommitted state by activating the NOTCH pathway, in contrast to CYCLIN-D1 which promotes 
differentiation. They conclude that cell-cycle phase-specific regulatory components act in opposition to 
coordinate the self renewal and lineage commitment of RGCs by controlling core stem cell regulatory 
pathways. 
While these core findings are interesting (the findings of Fig. 4 are particularly nice) and represent a 
considerable amount of work, the manuscript is laid out in an unnecessarily convoluted manner and 
the figures and analyses are very poorly laid out / presented / performed. The authors should go back 
to their manuscript and carefully weigh which elements they think are most important to convey their 
message. Figures should be re-designed in depth. 
 
Concerns: 

1. Page 6 Line 6: “To achieve this, we performed bulk RNA sequencing on PROM1+ progenitors from 
E11.5 and E15.5 cortices and differentiating PROM1- cells from E12.5 and E16.5 cortices.” Why did the 
authors do these experiments at different ages? They could have taken PROM1+ and PROM1- cells 
form the same cortices at E11.5 and E15.5 for instance. 
 
2. Page 6 Line 12: “As visualized in the tSNE-derived nearest neighbour map, this analysis effectively 
separated cells according to their age and expression of the progenitor marker Prom1, the 
intermediate progenitor marker Eomes and the neuronal marker Dcx (Fig. 1c, d).” Why was bulk RNA-
seq used to identify these markers? There are already known markers. 
 
3. The method used to define the maturation stage value is unclear. The authors should provide a 
clearer and more comprehensive explanation. “Maturation stage assignment”. The authors should 
provide references or list the genes used. 
“PC1 and PC2 were then rotated such that the number of detected genes correlated directly with PC1”: 
What does it mean? What is PC1 (=time?)? This should be carefully justified. 
 
4. “Furthermore, E9.5 cells displayed significantly greater gene expression correlations to the E11.5 
cells from the Infomap clusters lacking maturation stage pairs than to E11.5 progenitors newly 
committed deep- or upper-layer neurogenesis (Fig. 2a, b; Fig. 3d).” What is the relevance of this 
statement? 
5. Regarding Fig. 3, description of the bioinformatic analysis is very convoluted. Why was WGCNA 
used, what are the gene set 1 and 2? The authors should refer to a Sup Table here. In f, where do 
Cdca2 and Orc1 emerge from? 
6. Slc1a5+, Efna5+, Sox2low cells are IPs. Given the tSNE in Fig. Sup. 4e, f, how many of the 
collected cells co-express Slc1a5 and Efna5 in the scRNAseq? Given the tSNE in Fig.1 representing 
Eomes expression (a classical IP marker) it seems that most of these cells do not express Slc1a5 and 
Efna5; how do the authors explain this? What is the number of cells that co-express these markers? 
7. Regarding Fig. 5 and the gene set enrichment analysis, it is hard to understand how the authors 
found the GO. Are they at the top of the list? It might be nice to have a ranked list of GO. In 5c, the 
displays are just impossible to understand for non-specialists. The authors should re-think this and 
other panels. 
8. Page 11 Line 20: “To proceed, RGCs and IPCs sorted from E11.5 cortices were labelled with 
propidium iodide (PI) and their cell cycle phase enrichments were determined using FACS.” The 
authors should explain in the text how PI works (that the intensity of the fluorescence detected by the 
FACS will determine the cell cycle phase). Related to Fig 8b. Why show Neurog2 and Tubb3? There is 
no reference of this result in the text (see Page 15). 
9. Related to Fig.9c. IPCs communicate with RGCs through NOTCH signaling. Which data show this? 
Other concerns (in order of appearance in the text) 
 
1. Page 3 Line 7: “and finally cortical glia, 1.”: please remove “,”. 
2. In the introduction, a coma is missing between references in the text. 
3. Page 14 Line 12: “(Fig. 7d, )”. e is missing. 
4. In Fig. 8c and Sup Fig. 10, it would be nice to show the images for GFP control. 
5. Discussion Page 19: “Heterochronic transplantation…”, “Thus, these results are consistent with a 
model by which a population of multipotent RGCs becomes progressively fate restricted with time.” 
The authors should present and discuss the recent findings of Oberst et al, 2019 in this context. Also 
Telley et al, 2019, Pilaz et al, 2016, Pilaz et al 2009 are important contributions which are missing.