Unofficial and hypercritical peer review of a paper on p53’s role in hESC regulation

Once I wrote shortly about the following peer review paper which was popped out of my PubMed feeds to draw some attention to it: Han Qin, Tianxin Yu, Tingting Qing, Yanxia Liu, Yang Zhao, Jun Cai, Jian Li, Zhihua Song, Xiuxia Qu, Peng Zhou, Jiong Wu, Mingxiao Ding, Hongkui Deng
Regulation of apoptosis and differentiation by p53 in human embryonic stem cells.
J Biol Chem. 2007 Feb 23;282(8):5842-52


Now I got a very thorough comment on this paper by an author nicknamed “wolf” which systematically goes through the paper and gives a highly critical peer review of it. So I just publish the comments and next ask the authors (the first or the last) of the criticized paper and give them the possibility to defend their experiments and statements. My role here is the role of the blog”publisher”.

Comments re Qin paper p53 and hESC apoptosis by “wolf”:

This paper starts with making a fundamental mistake in not determining the kinetics of UV induced apoptosis and therefore missing the modulation of p53 target genes.
Subsequently they attempt to explain the absence of this by using transient transfections and analysing the cells at timepoints when half of the cells (mainly the undiff cells) are already dead and then interpret the data of the differentiated transfected (more resistant) hESC as if they were undiff hESC. The paper then desperately tries to come up with explanations for their own contradictory results). The data set further lacks controls (lentiviral mock transduced cells, no isotype controls etc), uses the wrong assays (such as PI staining to assess apoptosis, morphological assessment of differentiation by surface area) and lacks insight into the mechanisms controlling apoptosis (no cyt c release, no idea how p53 by itself might trigger mitochondrial apoptosis, etc).


Materials and Methods

Page 2: The authors use mainly one line of late passage hESC (p42-p68) grown in KSOR, which are highly CD30 positive leading to alterations in apoptosis regulation. We use three hESC lines at passages before p12 only.

Page 3: endoderm differentiation occurs in 4 days after Activin addition ? This is very quick with >80 % of hESC expressing sox17 after 100 ng/ml activin ?

Page 3: In immunostaining no antibody controls were used instead of isotype control with identical concentrations. We use isotype controls for all our immunos.

Page 3: Cells appeared healthy after transient transfection ? Even after irradiation ? That is funny since their data suggest that 30-40 % die within 6 hours after irradiation. This is clearly going to affect the reporter assay data since we show that the differentiated hESC die slower than the undifferentiated cells and because these are also the cells that are most easily transfected as compared to the undifferentiated hESC you expect that with increasing UV exposure the undiff cells will have more luciferase activity. Indeed this is what their data show. This can however NOT be interpreted as a preferential acitivation of p53 transcriptional activity in undiff hESC ! If the authors would have bothered to look which cells were actually transfected they would have noticed this.

Page 3
Note that the caspase 9 assay harvests all cells on the plate and then measures caspase 9 activation. How can the authors be certain that this activity is coming from the hESC and not the fibroblasts ? Better to use in situ detection of caspase 3 to show caspase activation or cleaved caspase 3 westerns.

Page 4
How did the authors select p53 shRNA transduced cells since this construct does not have the EGFP marker ? No control for lentiviral transduction effects !!

Page 4 results
The authors expose hESC to UV light for 5 hours ?

Page 4 results
Fig 1A; the annexin V assay shows that without UV 9 % of hESC are necrotic (PI pos) and 8 % are undergoing apoptosis (annexin V pos PI neg). After UV 28 % is necrotic and 38 % apoptotic. In further experiments they only use PI positive cell assay, which does NOT discriminate between apoptosis and necrosis. Despite a claim that p53 siRNA transduced cells show no p53 expression only 50 % of cell death is reduced in these cells. Are these authors claiming that not all UV induced death is controlled by p53 or that the rest is plain necrosis ? This is also not consistent with the apparent total inhibition of cell death by pif-mu.
In fact the annexin V assay is inappropriate for hESC due to the high background caused by the fragility of (in particular undiff) hESC. Better to use TUNEL.

Fig 1B
This figure does NOT show an increase in p53 expression as judged by an immuno with 8 cells. Furthermore there is no evidence that p53 translocates to the mitochondria after UV. In fact it appears that most cells show increased nuclear p53 expression after UV. But the piccies are so bad that one cannot judge this accurately at all. Also the nuclear morphology after UV suggests that these are dead cells already.

Fig 1C
Since there is no gel to show proper amplicons nor a protocol to quantify such bands it is not clear how these experiments were performed. The most likely explanation for the failure to detect upregulation of these classical p53 target genes is however that the undiff hESCs that apoptose very rapidly (4-6 hrs) have already died and detached from the plate so would not have been analysed. If the authors would have performed dose and time dependence expts they would have discovered that they have missed the window of p53 target gene regulation, which occurs around 4-6 hours. Because the diff hESC die much slower the authors can show modulation of these targets in the diff hESC.

Fig 1D
As outlined earlier transient transfection of reporters occurs predominantly in diff hESCs and 6 hours after UV more than half of the (mainly undiff hESC) cells are dead and will not contribute to the luciferase activity. Therefore the data mainly assay the effect of UV on p53 reporter activity in diff cells. It is therefore not surprising that there is no effect of UV on reporter activity in undiff (dead) hESC.
Furthermore the supposed control MG-15 was not shown anywhere, since this would have shown the exact same data as the real reporter.

Fig 1E
The same argument applies here as for mRNA expression. The cells are already dead or detached from the plate at this point in time and scrape harvesting is going to make it even worse. The increase in p21 can be explained since p21 is not expressed in undiff hESC and this proves that the authors are looking at alterations in protein expression in diff hESC only. Furthermore the supplemental fig S1 does NOT show p21 but Bax expression and to our surprise this appears to be expressed in the nucleus (DAPI overlay) what is the explanation for this phenomenon ?

Fig 1G and H and I
The authors again do not entertain the idea that the transfection of the reporter occurs mainly in diff hESC. This explains why the inhibitor works on the reporter in transients. Pif-a does however not affect apoptosis in undiff hESC. This inhibitor is ineffective in human cells and many authors report this.

Page 6 Fig 2
The authors state that p53 can induce apoptosis through a mitochondrial pathway and cite Moll et all and Chipuk. These papers however demonstrate that mitochondrial induced apoptosis by p53 requires PUMA or Bax upregulation in the nucleus, something the authors do not find in their flawed data but choose to overlook when making this misleading statement.
Fig 2 We have looked carefully but the immuno’s do NOT show any evidence of cytoplasmic p53 or any colocalisation with mitochondria before or after UV.

Fig 2B
The authors state that the mitochondria were free of nuclear contamination although there is a clear Histone 3 band in the mito fraction as well as clear cox iV bands in the nuclear fractions. The fact that a dead p53 transcriptional inhibitor has no effect on mitochondrial association of p53 is not surprising is it ?

Fig 2C
Showing activation of caspase 9 in whole lysates from hESC cultures does NOT give any indication that mitochondrially targeted p53 is responsible for this activation.

Fig 2D
There is no indication of the purity of the p53 siRNA transduced .hESC or the level of knockdown of p53 in this figure. Interestingly, in the left bottom corner there is a cell that still strongly expresses p53. What is the explanation for the fact that cells that are not green, and therefore presumably did not have the siRNA construct (if GFP was actually used in this siRNA construct) do not show p53 expression ?

Fig 2F
The authors now switch to PI positive cells as their apoptosis assay (in fact measuring primary and secondary necrosis) and at the same time the rate of apoptosis, which was 67 % after 12 hours (Fig1) now drops to less than 40 % after 12 hours ? What is the explanation ?

Fig 3A
The TUNEL assay shown does NOT co-localise with the DAPI signal, there is no minus TdT control, it does not conform to the accepted morphology of nuclei undergoing apoptosis and the TUNEL signal seems rather to be generated by bleed trhough of the red p53 signal into the FITC channel.

Fig 3B and C
Again the data show that the hESC culture is NOT pure and that there are large numbers of untransduced hESC in the colony. The proper thing to do would have been to determine apoptosis in the GFP pos cells. Again PI staining does not assay apoptosis. Nor is it clear how one accurately counts by hand cells that are evidently growing on top of each other. Why not use a FACS based TUNEL assay on a pure transduced hESC line.

Fig 3E
Here the authors show that only 1 % of colonies remain undifferentiated after dissociating them to single cells and that this is enhanced to 4 % in their transduced line.

Fig 3G
Here the authors use the MTT assay that is reliant on mitochondrial dehydrogenase activity. Unfortunately the induction of mitochondrial mediated apoptosis would preclude the use of this assay. Also the conclusion is wrong that p53 siRNA transduced cells grow more quickly since MTT merely is an indication of cell number and therefore rather reflects the reduction in background apoptosis in these cells. If the authors measure BrdU incorporation they could conclude that.

Fig 3H
The analysis of karyotype at passage 25 is not informative when the authors themselves state that they use the cells up to passage 68, in particular in light of the published data showing that hESC frequently turn abnormal after prolonged passages (>p40).

Fig 4A and B
Measuring differentiation by surface area of subjectively identified differentiating cells is flawed. For example, some cells differentiate into neurons with very little surface area and also hESC can adopt a flat morphology while still expressing Oct4.
In addition the displayed Oct4 staining does not appear to be nuclear and is not quantifiable.

Fig 4C
It is unclear how differentiation was determined in this figure.

Fig 4D
The authors suggest that all hESC differentiate into sox17 positive endoderm and no other cell types in response to activin within 3 days. This truly unique finding,( other groups report maintenance of hESC undifferentiated state by activin), is the first evidence of lineage specific differentiation by a single molecule in record time. There is no explanation why at higher activin concentrations the effect of p53 knockdown all of a sudden disappears.

Fig 4E
The immuno’s do not show the nuclei and one cannot judge how many cells there are or where they start or end. In addition the staining of these markers is not only very bad but also not in accordance with published data. If one wants to demonstrate pluripotency teratomas are the assay of choice.

Fig 4F and I
Here the authors suggest that this constitutes evidence that p53 is required for suppression of Oct4 and nanog. However they previously suggested that the p53 siRNA transduced cells are less differentiated and therefore should have more Oct4 and nanog than the controls. The mRNA data do not show this, in fact there is less oct4 mRNA but more nanog mRNA. The western blots however do show more Oct4 in the p53 siRNA cells but here nanog expression is reduced as compared to the null cells.

Fig 5
We cannot detect a clear increase in mdm2 from the immunos nor a clear reduction of p53 by the immunos. How there is now all of a sudden alterations in p53 downstream target expression after infection with a negative regulator of p53, while the authors previously suggested that there was no p53 regulation of target genes in hESC is unclear. The model is not supported by the authors findings; there is no evidence of absence of mdm2 feedback regulation of p53, there is binding of p53 to multiple promoters in hESC, there is activation of a p53 reporter gene, there is modulation of nanog upon siRNA knockdown of p53 but nevertheless the authors suggest that there is no transactivation of p53 target genes occurring in response to UV. As argued above the majority of the expts that these authjrs base their conclusions on are flawed or misinterpreted. A lot of handwaving needs to happen to offer explanations for their results (ie, repression of genes does happen but activation doesn’t and this is gene dependent etc). There is no evidence of translocation of p53 to the mitochondria nor any explanation how p53 can trigger an apoptotic cascade in the absence of Bax or PUMA upregulation. Lastly there is no evidence that p53 inhibits Oct4 or Nanog transcription in this paper. This therefore negates every arrow in their model.