Peer review of: Pre-clinical study of induced pluripotent stem cell-derived dopaminergic progenitor cells for (2020)

Reviewers' comments: 
 
Reviewer #1 (Remarks to the Author): 
 
This paper comes from one of the groups currently planning or carrying out clinical trials of human 
pluripotent stem cell-derived dopaminergic neurons to treat Parkinson’s Disease, in this case using iPS 
cells. As the authors point out, the requirements of different regulatory agents around the world differ, 
and it is of general interest to know the types and extent of preclinical data that have been obtained 
and required in different regulatory domains. In the present case, the authors described the preclinical 
data that they obtained to support their planned clinical trial in Japan. The report is valuable to those 
interested in understanding and deciding upon the types of data required before trials in man are 
undertaken. However, in the context of point made by the authors about differences between different 
regulatory regimes, it would have been interesting if they had included more in their Discussion about 
their discussions with the Japanese regulatory agency indicating what, if anything, was absolutely 
required, what may have been suggested, and if the authors carried out anything beyond what was 
required. Apart from that the manuscript does need some clarifications and I have the following 
comments: 
1. In the Results the author briefly described the iPS cell line used in the study, mentioning that they 
established a clonal master cell bank – and ‘preserved the iPSCs in hundreds of frozen vials as one lot’. 
Given that this paper is giving details of the preclinical characterisation of the cells they were planning 
to use for their clinical study and, as I understand it, telling the readers about the preclinical data used 
to justify safety and efficacy, then I think they should provide more precision in the details of exactly 
how these particular iPS cells were derived and the ‘clonal master cell bank’ established – how was the 
cloning done? how long were the cells grown before freezing? how were they frozen? How many vials 
are ‘hundreds’? This information could be included in the Supplementary Data. Also, I presume that 
the regulators required data to indicate no retention of any of the reprogramming vectors? Is that the 
case and how was it achieved? 
2. In a similar vein, when the authors say that they modified our protocol to induce DAPs from human 
iPSCs to meet the GMP-grade culture condition, I think they should give details of the modification – 
maybe the best would be to include in the supplementary data the SOP for their production of GMP 
grade DAPs. 
3. I found that some of the Figures, notably Fig 1 b-c and Fig 3a as well as 3c-e and g-o, were too 
small and of too low magnification for me to make out anything useful. These figures should be at 
greater magnification and/or enlarged. 
4. On page 3, under ‘Characterisation of the final product in vitro’ they authors say “We repeated the 
induction of DAPs from each randomly chosen vial of MCB003 25 times”. Does this mean they did this 
from 25 random vials, testing each one once? Or did they induce DAPs 25 times from cells from just 
one vial. 
5. On page 5, the details of the tumorigenicity studies need to be clarified. In particular, the authors 
write “Initially we grafted day-30 spheres ….. into 80 (…) and 50 mice (….) as transplantation and 
control groups. I don’t understand what is the control since it implies both groups were grafted with 
spheres! I can’t read the Figure properly as it is too small but it looks as though the control is actually 
with medium injected rather than cells, but it is not clear in the text. The authors also conclude that 
there is no significant difference between the survival curves of the experiments and control mice – 
but from eye-balling the figure it looks as though the female experimental mice do have a slightly 
reduced survival; I cannot see which is the male experimental line. 
 
 
 
 
Reviewer #2 (Remarks to the Author): 

 
This study by Doi et al. contains all the safety and efficacy data that lead to the approval of their stem 
cell derived therapy for PD in Japan. We think it is extremely important to publish such data and to 
make it available for the scientific community. As such it is a highly valuable contribution to the stem 
cell therapy field. The paper is well structured and very well written, but the format for publication is a 
little different and we find it hard to review the paper as a regular scientific study as the data 
presented here have already been approved by the Japanse authorities. 
 
We have therefore focused our evaluation on the presentation of the data, identifying where data 
could be presented clearer, and suggesting where additional text edits are recommended. 
 
1) Characterization of final product in vitro: 
a. Add here the % of Corin and TRA1-60 positive cells before sorting. 
b. The limit of detection is stated to be 0.1% but this is a bit tricky to define and sensitivity varies 
between methods and instruments. Please refine this statement. 
c. The spike-in assay contains a group of 0.001% spiked in PSCs. How was the dilution made and how 
was it confirmed after mixing? 
 
2) Tumorgenicity, toxicity and biodistribution 
a. DAPs from 6 separate differentiations were tested but it is unclear how many animals from each 
group were analysed. 
b. How was the maximum feasible dose determined? 
c. The teratoma assay is poorly described, please clarify. 
3) Efficacy study 
a. Was the number of TH+/FOXA2 positive cells quantified? 
b. The extent of innervation in Figure 4 is not evident from the images provided. 
 
4) Discussion 
a. It is stated that 92.5% of the cellular component is iPSC-derived DAPs. Is this in vitro at day 30 or 
after transplantation? 
b. It is stated that the rest are GABAergic neurons or midbrain astrocytes but these data are not 
presented in the result section. 
 
5) Methods 
a. The cell differentiation protocol is not sufficiently detailed, It refers to two previous publications by 
the same group but there are slight differences in protocol used in the quoted Kikuchi et al and Doi et 
al. studies. We recommend to include all details of the protocol in this current mansucript. 
 
6) Additional points 
- The ability to reduce TTR-expressing choroid plexus like cells is not suffiently decribed. Also, given 
that these cells only appeared in a less than 50% of the grafts means that a higher number of 
transplants need to be analysed in order to safely conclude athat the presence of this cell type is 
redunced. 
- The statement that the appearance of TTR-expressing choroid plexus like cells may be species 
specific should be nuanced. An equally plausible interpretation for why they do not appear in the 
primate grafts could be that only 3 animals where included in this group.