《科学》对STAP手稿的专家评审意见曝光

  《科学》对传说中的STAP细胞论文的三名评审专家意见，过去一直被雪藏，今天终于被曝光。专家对这一研究的评价不高，认为非常全面的描述性研究，如果结果确定，可能导致发育生物学大厦的颠覆，其实是不相信这种研究结论。因为没有当时的投稿件，所以没有办法对这些评价进行更深入分析。不过这些资料显然都在某个地方，只是拥有的人不愿意拿出来。

Retraction Watch readers are of course familiarwith the STAP stem cell saga, which was punctuated by tragedy last month whenone of the authors of the two now-retracted papers in Nature committed suicide.

 

In June, Science‘s news section reported:

 

  Sources in the scientific community confirm that early versions of theSTAP work were rejected by Science, Cell, and Nature.

 

Parts of those reviews reviews havesurfaced, notably in a RIKEN report. Science‘s news section reported:

 

  For the Cell submission, there were concerns about methodology and thelack of supporting evidence for the extraordinary claims, says [stem cellscientist Hans] Schöler, who reviewed the paper and, as is standard practice atCell, saw the comments of other reviewers for the journal. At Science,according to the 8 May RIKEN investigative committee’s report, one reviewerspotted the problem with lanes being improperly spliced into gel images. “Thisfigure has been reconstructed,” the RIKEN report quotes from the feedbackprovided by a Science reviewer. The committee writes that the “lane 3”mentioned by the Science reviewer is probably the lane 3 shown in Figure 1i inthe Nature article. The investigative committee report says [co-author Haruko]Obokata told the committee that she did not carefully consider the comments ofthe Science reviewer.

 

The entire reports, however, have not beenmade available. Retraction Watch has obtained the full text of the editor’scover letter and reviews of the rejected Science paper. The reviews are full ofsignificant questions and doubts about the work, as would be expected in arejection. We present them here, to fill in some of the gaps and help readersconsider how the research eventually made it through peer review:

 

21 August 2012

 

Dr. Haruko Obokata

 

Anesthesiology

 

[ROOM NUMBER REDACTED]

 

Brigham and Womens Hospital/Harvard MedicalSchool

 

75 Francis Street

 

Boston MA 02115

 

USA

 

Dear Dr. Obokata:

 

Manuscript number: [REDACTED]

 

Thank you for submitting your manuscript“Stress altered somatic cells capable of forming an embryo” to Science. We havenow received the detailed reviews of your paper. Unfortunately they are notpositive enough to support publication of the paper in Science. Although werecognize that you could likely address many of these specific criticisms in arevised manuscript, the overall nature of the reviews is such that the paperwould not be able to compete for our limited space. We hope that you find thecomments helpful in preparing the manuscript for submission to another journal.

 

We are grateful that you gave Science theopportunity to consider your work.

 

Sincerely,

 

NAME REDACTED, Ph.D.

 

Senior Editor

 

REVIEWS

 

Reviewer 1

 

This paper claims that cells from anysomatic tissue can be reprogrammed to a fully pluripotent state by treatmentfor a few days with weak acid.

 

This is such an extraordinary claim that avery high level of proof is required to sustain it and I do not think thislevel has been reached. I suspect that the results are artifacts derived fromthe following processes: (1) the tendency of cells with GFP reporters to gogreen as they are dying. (2) the ease of cross contamination of cell lines keptin the same lab.

 

I believe that the green transformation isindeed due to stress as reporters are often upregulated in stressed or dyingcells. But the cells that go green may not be the ones in the later greencolonies. I think these are more likely to be ES cells acquired by crosscontamination and selected for growth by the B27-LlF medium. This would explainthe results on marker expression, promoter demethylation, differentiation, andchimera formation. In Fig.2B and the other RT-PCR studies, it is not statedwhether the Y-axis is linear or logarithmic. If it is linear, which seems morelikely, then I am very surprised that all of the pluripotency genes measured inthe ESC control have virtually the same RNA abundance, which exceeds that ofGAPDH.

 

The claim about all the other tissues beingsimilarly reprogrammed by low pH treatment is truly extraordinary. Much moredetail needs to be provided about the nature of the cells and the cultureconditions. Otherwise this is simply not credible, since the principal celltype of several of these tissues is postmitotic.

 

The DNA analysis of the chimeric mice isthe only piece of data that does not fit with the contamination theory. But theDNA fragments in the chimeras don’t look the same as those in the lymphocytes.This assay is not properly explained. If it is just an agarose gel then thesmall bands could be anything. Moreover this figure has been reconstructed. Itis normal practice to insert thin white lines between lanes taken fromdifferent gels (lanes 3 and 6 are spliced in). Also I find the leading edge ofthe GL band suspiciously sharp in #2-#5.

 

Minor points:

 

1. It is by no means clear that newt cellscan revert to “stem cells” (presumably this means pluripotent stem cells).Recent work on newt regeneration has indicated conservation of tissue type inmost cases. The Wolf (1895) reference is out of date.

 

2. p.8 heading: “exposure” not “expose”.

 

3. The sentence on p.12 line 6 up “mixture…. analyzed” is very confusing.

 

4. In the Fig. 4 legend it should be madeclear which experiments are done with 2N and which with 4N hosts.

 

On the positive side, I do agree with theauthors that the many claims of pluripotent stem cells from adult mammalsprobably arise from partial reprogramming due to stress followed by selectionin culture. But I don’t think such cells often match ESC in pluripotentbehavior, especially the ability to form chimeras in 4N hosts.

 

Reviewer 2

 

Obokata et aI. describe a novel method forreprogramming somatic cells to a state that possesses many features ofpluripotent stem cells. By subjecting C045+ hematopoietic cells to low pH,mechanical trituration, and culture in LlF-B27 medium, ESC-like properties canbe induced, including ESG-like levels of Oct4, Sox2, and Nanog mRNA andcritically, the potential for germline transmission and tetraploidcomplementation — two of the most stringent functional assays for there-acquisition of pluripotency. If these data are indeed robust then theobservation is highly significant.

 

Unfortunately, the paper presents only asuperficial description of many critical aspects of the work. A detaileddescription of the methods used to induce and maintain SACs was not provided,and the mechanisms and explanations are either not compelling or poorly defined(Figure 3). Given the novelty of the claims, a thorough characterization of theSACs is warranted. as is some probing of the mechanisms. This would necessitatea more sophisticated genomic analysis of SACs, through microarray or RNA-seq,and genome-wide DNA methylation analysis — analyses that other pluripotent stemcell lines have been routinely subjected to and for which methods for smallercell numbers have been developed.

 

Issues to be addressed:

 

1) From the experiments performed by theauthors, it cannot be ruled out that rare multipotent progenitors are beingselected for and expanded under stress conditions. While this in itself wouldbe extremely interesting, it suggests a very concept [sic] than what is beingclaimed about reprogramming of “mature” adult somatic populations. It isunclear whether cells are harvested from any other stages than young (7-day old)mice. Might the cells in these young mice be errant migratory germ cells orsome other stem cell-like progenitors? CD45+ cells are harvested from thespleens and these are called lymphocytes, but hematopoietic stem cells (HSCs)express CD45, and the spleen contains HSCs at this young age. Thus stressconditions may be acting on HSCs, rather than fully differentiated somaticcells, which would imply a very different main conclusion of this work. Shouldthe authors wish to maintain their conclusion, they should rule out thepotential germ cell or HSC origin of SACs. This could involve perhaps theexamination of genomic imprints, or expression of c-Kit.

 

2) The analysis of TCRb gene rearrangementin fig S6 purporting to show derivation from fully mature T cells with TCRbrearrangement is flawed. If mice are clonally derived, they should have asingle gene rearrangement, not a population of polyclonal rearrangements asappears in at least some of these animals. This analysis should be done usingSouthern Blots to avoid the problems of PCR contamination; see Hochedlinger andJaenisch, Nature 2002.

 

3) The evaluations of stress-mediatedresponse pathways and analysis of mitochondria are purely correlative and haveno demonstrated mechanistic link to the observed reprogramming.

 

4) The ability to permanently maintainthese cell lines is not well-described. The authors claim that “sphericalcolonies grew to approximately 70 um in diameter … and spherical colonies couldbe maintained for another 7 days in that culture condition.” Figure 2C–itappears that the expression of mESC-associated pluripotency genes is decreasingsignificantly over time in bulk SAC populations. If these cells are trulypluripotent. they should not only exhibit the developmental potential of ESCs/iPSCsbut also the ability to indefinitely self•renew. For ESCs/iPSCs, past groupsprovided evidence of telomerase activity to indicate the capture of animmortalized cell line. In the case that the cells cannot self-renewindefinitely, a description of what happens (differentiation, death, etc.), andan explicit statement on unlimited or limited proliferative potential of theSACs should be provided.

 

5) Reprogramming efficiency alter stressexposure should be monitored for each cell population. Presumably many cellsdie after low pH treatment, and the 40% of surviving cells expressing Oct4-GFPafter 7 days represents a selected and subsequently expanded population, butthis is not clear. This would help understand the proportion and give clues tothe nature of the cells undergoing reprogramming. For example, more refinedcell isolation followed by analysis of conversion efficiency could be veryinformative.

 

6) The nature of the B27 medium was notdescribed. Is it serum-free or serum-containing? What is the base medium used?These are critical details because “B27 medium” is not a conventional conditionfor mouse ESC/iPSC propagation. but rather for primitive neural stem cellderivation/propagation. For serum-free culture of mouse ESCs/iPSCs in LlF andB27 supplement, they require N2 supplement and BMP4 or N2 supplement and 3i/2i(Ying et al. Cell. 2003; Ying et al. Cell. 2008). The original work that firstdescribes the use of LlF-B27 medium was not cited (Tropepe et al. Neuron.2001). In that study, they critically observed that LlF-B27 ESC-derived neuralcolonies are competent to colonize both neural and non-neural when exposed toan appropriate environment Given the claim of acquired pluripotency, theauthors need to rule out that they have generated primitive neural stem cellsby genomic characterization of the SACs they generated, and more preciselycapture the nature of the “reprogramming” that is claimed (microarray, DNAmethylation analysis, etc.). A systematic genome-wide characterization of SACswill establish the molecular identity of SACs in relation to other mousepluripotent stem cell lines.

 

7) From the FACS analysis of Oct4expression in day 1 CD45+ cells, it is not clear if there is a small populationof weakly-expressing Oct4-GFP cells. How can the expansion of a pre-existingQct4-GFP expression population be ruled out, rather than de novo expressionfrom mature cells? Because the authors claim a significant increase inefficiency and pace of Oct4 locus reactivation, they should compare theirmethod with the predominantly established method by which hematopoietic cellsare reprogrammed: by defined factor induction. A head-to-head comparison of SACinduction and iPSC generation is needed (a la Figure 1B).

 

8) The authors surveyed changes in the mRNAexpression levels of an array of stress-response genes, but did not assesstheir functional relevance by shRNA knockdown or overexpression during conversion.

 

9) Considering that mouse strains known tobe either recalcitrant (e.g. Bl6) or permissive (e.g. 129) to ESC derivationwere used in this study, was there any correlation between SAC derivation andstrain?

 

10) It is stated that there was no differentiationtendency of SACs derived from any tissues when incorporated into chimeras. Thisdoes not appear to be true as liver-derived SACs exhibit a low contribution,and are skewed to liver differentiation. Similarly, skin-derived SACs appear todemonstrate a tendency to contribute to the skin.

 

11) Embryos generated by tetraploidcomplementation should be taken to term. In figure S5E, the example of theBDF1/GFP embryo presented does not look normal.

 

12) Regarding the existing molecular dataon the identity of the cell lines, the embryonic gene expression qPCRs (Figure2B, S3C) show unusually high values for expression levels relative to GAPDHlevels. Even though the figure has an ESC control, and it may be aprimer-specific phenomenon, mRNA levels of genes such as Nanog and Rex1 aremore like 0.05 or 0.15 of GAPDH levels, whereas the authors observed levels ashigh as 12 -14 times GAPDH.

 

13) The authors did not describe “the lowpH solution (pH5.5)” treatment in detail (Methods). The authors need to providea detailed description of what the composition of the pH solution was, how longthe treatment was, and how the cells were handled.

 

14) The authors did not describe thesubstrate used during conversion. Did they use feeders or gelatin? These are theconventional substrates on which pluripotent stem cells are derived andmaintained.

 

15) Because the authors claimed acombination of pH decrease and mechanical stress caused Oct4 reactivation, theauthors should show data indicating how the two procedures additively orsynergistically promote Oct4-GFP reactivation.

 

16) Figure S1C — the authors quantified thenumber of spherical colonies, but they did not provide a normalization. Thisfigure would additionally be significantly enhanced if the authors showed themorphologies of the spherical colonies they are obtaining in the differentculture conditions

 

17) A more detailed description on thecomposition of the different media tested was not provided (Figure S1C).Additionally, ACTH is not conventionally used for pluripotent stem cellculture. The manuscript would be enhanced if the authors provided anexplanation for the use of ACTH.

 

18) Decreased cellular size is a feature ofpluripotent stem cells, but the authors did not include data or a discussion onthe ESCs/iPSCs cell size in their examination of cell size (Figure 1D).

 

19) Figure 2B — the nuclear localization ofthe Nanog signal in SACs should be very clear, however the staining appears tobe non-specific.

 

20) The authors should refer to the 2007Cell Stem Cell paper from the Jaenisch lab when discussing reports of theexistence of Oct4-expressing pluripotent adult stem cells. Here it was shownthat Oct4 gene ablation in adult tissues did not affect regenerative capacity.

 

21) Figures are often not referred to inorder, making the manuscript slightly difficult to follow at times.

 

Reviewer 3

 

The finding described in this manuscript isvery unusual and unexpected. Under certain circumstances, it appears that anon-physiological non-specific stress can trigger reprogramming of terminallydifferentiated cells, such that the cells enter a pluripotent stem cell-likestate. If these results are repeatable, a paradigm of developmental biologywould be changed. Currently, that paradigm is that terminally differentiatedstates are set and cannot be reset. Although Yamanaka broke this biologicalrule by overexpressing pluripotency-associated factors, that system is highlyartificial. The authors of the present manuscript propose that cells have anintrinsic capacity to reprogram. I found the manuscript to be clearly writtenand concise, although sometimes mildly unorthodox in terms of literature cited.

 

However, the methods and cell protocolsused must be described in far more detail. For example, the section on Oct4should state how many cells were sorted and describe the appearance of thecells. Is it possible that rare populations of cells pre-exist or are alreadyapparent on day 1 (thus, what are the “dots” of Fig. 1?). The authors willargue that, indeed, under certain circumstances, they were able to reprogramterminally differentiated cells, and that this was attributable to TCRrecombination. I think, ideally, that the cells should be experimentally taggedand traced. This would unequivocally clarify the source of the cells and,further, would exclude the possibility that some cells pre-existed in apluripotent state.

 

Critically, it is necessary to determinewhether SAC cells can propagate stably in culture and whether such cells can bepassaged. CD45.2 cells from the spleen are differentiated and, unless activatedby an antigen, are supposed to be in G0. Do these cells re-enter the cellcycle? The cells should be further characterized.

 

Some negative controls are missing. SeeFigs. 2A, S3B, S3C, S5A, and S5B. Unstressed cultured cells should be used asnegative controls.

 

In Figs. 3C and D, it would be interestingto see the ATP and ROS levels in both ES and SAC cells.

 

In Figs. 3C and D, it is apparent that mEScells show rises in ATP and ROS levels, and in mtDNA copy number. These resultsshould be compared to other publications.

 

In Fig. 2, Nanog is not located in thenucleus. Also, do the authors have data on staining of Oct4 in thisexperimental context?

 

Update, 6:30 p.m. Eastern: Here’s PaulKnoepfler’s take on these reviews.

http://blogs.nature.com/news/2014/09/new-details-emerge-on-retracted-stap-papers.html

 

相关专题：小保方事件追踪
转载本文请联系原作者获取授权，同时请注明本文来自孙学军科学网博客。
链接地址：https://blog.sciencenet.cn/blog-41174-827034.html

上一篇：只有研究方案也可发表成论文
下一篇：呼吸氢气对噪声诱导的耳聋具有治疗作用