"...something akin to hitting the cells over the head with a sledgehammer of a pH 5.7 (physiological pH is more typically thought of as around 7.4), they report the blood cells of 1-week old mice turned on expression of an Oct-GFP reporter as they floated around in clusters in the media."
"...the team provided pretty good evidence that the STAP cells arose from the differentiated blood cells themselves rather than potentially from rare pre-existing primitive stem cells in the cell populations."
"...After a relatively quick read, no particular red flags jump out at me from the STAP cell paper. It just seems too good and too simple of a method to be true, but the data would suggest so far at least that this team is onto something really important."
But key open questions remain before anyone can really say just how important this is.
1. Will it be reproducible by other labs? 2. Will it work in human cells? 3. Will it work in adult cells? 4. What are the molecular mechanisms? 5. Do these cells possess significant rates of mutations or epi-mutations, the latter being abnormalities in the epigenome? 6. Are these cells tumorigenic (besides forming teratoma)?
In particular, if the answer to one or more of the first 3 questions is no, then the impact could be significantly muted.
H. Obokota et al.report ( a new method of) "conversion of somatic cells into pluripotency ". Although these papers describe interesting observations, the authors should know that it is not necessary to convert somatic cells into pluripotency. Indeed we have reported in 2012: C.R. Biologies 335 454-462 (DOI: 10.1016/j.crvi.2012.05.005) that "Adult hematopoietic progenitors are multipotent in chimeric mice" as a subpopulation of normal, untreated, CD34+bone marrow cells from normal adult mice can give rise to tissues and organs derived from the 3 embryonic layers.
I think you are missing the point of the paper entirely. Its message is that you CAN do it, and with what appears to be relative ease. I won't even begin to open the discussion of mutli-potent HSC. I think Wagers and Irv Weissman et al have addressed this ad infinitum. Bottom line is no one can conclusively show HSCs contribute to all three germ layers, hence the very obscure publications and calls for retractions of some of these articles.
I believe that our demonstration of pluripotent (capable of giving rise to healthy animals) cells in normal adults is of tremendous theoretical interest . Of course we know the literature and there are quite a few explanations to account for the lack of reproducibility of some of the reported data in the literature. One of them may be that "our" bone marrow CD34 positive cells, which we find multi(pluri)potent, grow IN SUSPENSION and that most (if not all) procedures discard those cells! And of course they never give rise to any kind of tumors
A "minor " point: do the endodermal cells (Extended Data Fig 3d) express villin?
The "ultimate" proof that "STAP" cells generate embryos would be the presence of the Y chromosome in organs generated after injection of male cells into blastulas.That would eliminate cell fusion etc.... Also it is surprising that the authors do not show tissue (organ)sections. In addition what does "brain" mean? Brain is not a "simple" organ and by the way contains 10 percent cells derived from the hemopoietic system i.e. microglia.
Perhaps I don't know enough, but I am struggling to understand the results presented in figure 1i and how they can come about - any clarification would be great, because internet searches have failed to resolve this.
Both the fibroblast and the ES line shown in that gel have an unrecombined TCRB band, and the lymphocyte sample is representative of a population with multiple recombined variants but no unrecombined one, as expected. However, both OCt4-GFP+ samples, which are derived from CD45+ lymphocytes as per the text, have bands of both recombined and unrecombined lenghts - are there known cellular mechanisms that will undo this VDJ recombination, somehow?
you are correct regarding that TCRB band. it should not be there according to their model. If ~20% of the cells become oct4-gfp+ and the starting cells are all rearranged at the TCR, then how do they end up with that big fat band indicative of no somatic recombination?
What is sorely lacking from this study is the use of lineage tracing. ie they should have done something like a cd4-cre to lineage trace then show they traced cells become oct4-gfp positive. just sorting by cd45 alone doesn't convince me 100% that those are lymphocytes. similarly they use cells derived from organs could be anything. for instance, the "muscle": to me muscle is multinucleated myotubes (not satellite cells). did the myotubes dedifferentiate, turn on oct4-egfp and then undergo cytokinesis?
This will either be one of the greatest reprogramming papers or "cold fusion". Funny thing is most of the comments in the interviews were far more positive than I am. Yamanaka not so much, nor Jaenisch fwiw. but I disagree with Jaenisch: I don't think they did the right experiments regarding the lineage/FACS sorting/cell purity etc. They do convince me of the fact they made the mice however.
plan on seeing a correction soon because in the cell counting their scale is 10E60!!! I find this kind of stupid error to be inexcusable frankly, either on the part of the reviewers, nature and the authors. Read the friggin proofs already! just sloppy
Regarding the 10E60 scale: How do you know it's a "stupid error"? Did you actually try to understand the experiment, or did you just make a snap judgement?
Yes, 10E60 is a big number. Obviously they did not grow that many cells. Maybe you should consider the possibility that the authors and reviewers actually understand the experiment and you don't. And maybe firing off critiques without stopping to think is what's really "sloppy" and "inexcusable".
As you point out 1E60 cells were not grown. So how would you interpret "Cell number" in the axis label? The text and methods don't seem to bother with such detail (this is Nature).
My guess is that the culture went through loads of passages (and cell divisions) and the axis shows how many cells could have resulted if all cells had behaved as those kept. Each point represents a passage and maybe a 10-fold increase in the number of cells. 10x every 2 days for 120 days would give 1E60?
There are not that many cells in the human body, not even close! Please tell me how I misinterpreted that data. How do you interpret it? Again please tell me how I should understand it. Now I stand by my statement that putting that large of number in a graph of cell counting-that is what they are doing-cell counting-is silly. not terribly difficult to understand: they probably squirted them in some sort of cell counter or a cytometer, maybe they even used a hemocytometer.
here is the figure legend: Robust growth of STAP stem cells in maintenance culture. Similar results were obtained with eight independent lines. In contrast, parental STAP cells decreased in number quickly. Nature 505, 641??"647 (30 January 2014) doi:10.1038/nature12968.
I guess you didn't understand my comment. Let me try a slightly longer version. Imagine they put 10 cells in a culture flask and let them grow for 2 days, at the end of which they have divided several times so that there are about 100. Then the culture is passaged and one flask containing 10 cells is kept. The cycle starts again.
If this sequence continues, one could say that every two days the number of cells tends to increase 10-fold under those culture conditions. Now lets do the thought experiment of keeping all the cells instead of just a few at each passage. A 10-fold increase every 2 days for 120 days means that the number would have increased 10-fold 60 times: 10x10x10x10... (60 times), which is 1E60.
I think that's where the number of 1E60 comes from. It's the predicted number of cells that would have been produced if all had been kept. The main assumption in this calculation is that the cells kept at each passage were representative (particularly in terms of growth and division) of the rest population, which is not an unreasonable assumption.
An equivalent representation would have been to plot "fold increase/day" against time or number of passages. A flat line would be expected.
i understand that is what they are doing. as i said, its a bizarre and yes silly way of presenting the data. why not just do population doublings over the course of 120 days? i have never come across somebody plotting "predicted cell numbers". As I mentioned since the paper is of such high profile, why not pay attention to details. naturally its not a major point of the work so I shouldn't have addressed this point.
This representation is actually quite common in some fields. For example, see Maus et al, Nat Biotech 2002, where expansion of T lymphocytes is plotted cumulatively as it is here. This representation gives an estimate of how many cells could potentially be grown, and then transferred to a patient, and as such is therapeutically relevant. One could imagine not discarding the cells after each passage, but growing them on separate plates for further storage. As you also point, the other advantage is that it give a curve of growth over time: doubling time is not a constant, growth may slow down after a while, and this can be visualized easily on the graph.
I guess CD45+ cells here are not all T cells. They probably include B cells, NK, monocytes etc, all of which are in germline configuration. Since the CD45+ fraction also contains T cells, there is a mix of germline and rearranged configurations...
Correct me if I am wrong, but since they produced cloned mice derived from single clones of STAP stem cells, previously derived from T-cells (cd45), the cloned mice should present only one kind of TCRB recombination, not a mixture, right? A simple PCR on TCRB of the cloned mice should show that?
In my view the main concern is that is all done with a gfp-oct4 reporter transgenic line. if for whatever reason that reporter became responsive to pH you will have Oct4 expression , and this may be the event leading ti reprograming rather than the indicator of an ongoing reprograming state? What about an independent gfp-oct4 reporter line.? what about a non tarnsgenic liene? are these cells also reprogarmed? In any case I think this is a fascinating paper both in its simplicity and econmic implicances on regenerative therapy. You cannot patent HCl tretments!
Figure 1i lane 3... At higher magnification the background of that lane 3 is darker than the rest of the gel. Also vertical straight change background on each side.
I agree that lane 3 was clearly spliced in. It is difficult to imagine how one can splicing in a lane in the middle of a blot by accident.
It is disconcerting that the only blot that the authors choose to display in the article itself has an undeclared splice. This most certainly should not happen in 2014, especially in a field that has seen too many high-profile instances of misconduct and/or sloppiness.
If the linked image is indeed Figure 1i, it does certainly look as if lane 3 was spliced in. I am under the impression that the correct procedure where two or more images are shown side by side is to leave a small gap. The authors do not appear to have followed the correct publication procedure here. A response from the authors would be welcome.
Are you getting the original from a pdf of the article? If so the pdf compression itslef may have introduced segmentation compression based on vertical line segmentation that the authors had nothing to do with. Unless you are looking at a raw electronic image or video you are always looking at a machine altered image i colr and transpositional replication to save data size.
Well it could also be an enhancement of the contrast for a single line with photoshop which was not enough visible. I did it once for the PhD of my girlfriend...
I don't believe that this is a compression artefact; the pixelation would be visible.
That somebody altered the contrast of a lane is less unlikely, but some of the lane (near the bottom) is no different to its surroundings, arguing at least against a simple adjustment.
In Fig 5d, antibody staining for OCT4 and NANOG - signal is cytoplasmic and should be NUCLEAR!! As it is the case for KLF4 and Esrrbeta, in the same figure. This result does not "compromise" any of the main claims of the paper, but reveals careless experiments, missed also by reviewers… signs of times.
I think Fig 5d looks at clusters of cells (as would indicate the scale bar), so it's not possible to really discriminate nucleus vs cytoplasm at this magnification. DAPI is probably used to visualize individual cells, and seems to mostly overlay with red staining, as one would expect...
please compare "correct" nuclear staining of KLF4 and ESRRB with that of Nanog or Oct4. Same magnification, same clusters of cells. Oct4 and Nanog staining is almost exclusively cytoplasmic!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!
As a naive viewer, I agree with Unreg that it is rather difficult to discern anything in the image. But maybe the nuclear/cytosolic localisation of the staining is obvious to experienced viewers. Could tell us what in the image points to the localisation?
What I can see: i) more punctate, discrete antibody staining in Klf4 and Esrr-beta ii) in the Esrr-beta overlay, the DAPI-stained nuclei seem to contain red dots (indicating strong overlap)
By the way, the sizes of the nuclei stained by DAPI seem rather different across the bottom row. Is that expected if they are all shown at the same scale?
If you zoom in you can see nuclear overlap from the pinkish red/blue in all of them. As is common, each have red in some cell overlaps, showing they are not overlapped and there is some cytoplasmic detection (including Essrbeta, which makes me confused about your comment). This should be expected as they are not always in the nucleus at each point in time in every cell. It is comparable to the following staining in iPSCs such as here: http://www.nature.com/mt/journal/v21/n1/images/mt2012245f1.gif
Knoepfler keeps on blogging, although there's maybe not that much substance at this stage (he mentions not having read the sister paper yet). Readers may find an interview with Vacanti of interest
Vacanti has made revolutionary claims in the past that have not been easy for most labs to reproduce. These have concerned "spore-like" cells (or VSELs - Very Small Embryonic Like stem-cells), which were claimed to be virtually indestructable. In the interview linked above, Vacanti makes the claim that STAP cells are probably VSELs. Anybody wishing to comment on that work could make a start here:
I think crowd-sourcing replication attempts is a great idea. I could easily imagine that even if nobody could reproduce the work that not much of that effort would appear in public. There might be some whispering at conferences etc, but quite possibly nothing in print.
In general, failure to reproduce is too often explained away as poor skills of the "reproducer", when in fact it should be treated as a serious issue by authors and journal.
I'm doing a new poll 2nd week into the STAP situation (you can vote again in this one) to judge the dynamic ranging opinions on the STAP paper and methods. http://www.ipscell.com/2014/02/do-you-believe-in-stap-stem-cells-new-poll-week-two/ Please voice your opinion via this poll. I'm curious if people are becoming more convinced or less or staying about the same as this story evolves. Paul
STAP stem cell crowdsourcing flowing along nicely! http://wp.me/P1xWpk-4pP 3 reported attempts, all didn't work. Still early days, but nice to see people into openscience like this. Paul
Agreed that the more detail that is available, the more useful these reports will be. The response from the authors (and implicitly from the journal) if these reports continue to build up will be that the attempts were "not done properly" in some way.
They conclude that their data indicate that strong stress reprograms mature lymphocytes into multipotent stem cells. As discussed on this site I also think their data are still not very solid for this conclusion.
It seems to me that the data might instead demonstrate stem cells residing in mouse tissue such as "Muse cells" (Proc. Natl. Acad. Sci. USA. 108(24):9875-9880 2011) and they are the only survivors of the treatment. Usage of T cell clones, instead of crude T cells, would be helpful to exclude this possibility.
interesting, but haven't labs made iPS cells from clonal cells ie derived from a single cell? I don't know for sure this would argue against the MUSE cell idea, at least with regard to fibroblasts either way this underscores the real need for the authors to have done rigorous lineage tracing as opposed to FACS on a single antigen
Agreed - some of this is a little unclear. The apparent gel splice has already been commented. I'm guessing that the commenter is also suspicious about the odd-looking pixels in the images with fluorescent cells, but I'm not convinced that those couldn't be compression artefacts. Maybe I'm missing something.
The blogger who reported the "unclear" issues with the images linked above has left an apology (in Japanese) to the authors stating that these are indeed likely to be compression artifacts and he regrets not taking more care discussing such a high profile paper: http://blogos.com/article/80340/
"Regarding the previous entry that talked about a portion of the image that was suggested to be unnatural, we have received numerous inputs from the readers that it may be an artifact that emerged during the compression of the jpeg image. Therefore, we have now eliminated the said image and the accompanying part of the blog. We apologize to the readers and everyone involved for any inconvenience caused.
Also, because the said blog entry has created unforeseen amounts of attention, there is a risk that the contents of this passage could be reported by the mass media who misinterprets and sensationalizes the content, and because some of the comments left on my blog were verging on threats, the said blog article will be temporarily held from publication. It is one of our duties as researchers to discuss published work from various angles, however, it seems that our deeds can be easily misinterpreted by those outside of science.
As I have talked about it on multiple occasions in this blog, I am greatly amazed by the STAP research by Dr. Obokata and her colleagues and look forward to seeing its future progress. That is why we dared to talk about the feature of the image that was suggested to be unnatural. We thought it would be unfair to just talk about how amazing the study is without raising the issues of possible caveats. We'd like to stress that it was never aimed to personally dishonor the researchers involved."
update: 2014.2.15
It appears that Riken has launched its own investigations on the part of the image suggested to be unnatural.
(link to the news on how Riken started the investigation)
We will wait to hear the results of this investigation. We've seen other people suggest that our blog was key that led to this investigation, but that is not true. Our blog article went online on Feb 14 while Riken had already contacted the outside consultants as of Feb 13. It is presumable that it was the following English website that triggered the investigation.
(link to PubPeer)
Also, the following site shares the results from some of the attempts to independently test the STAP protocol. It seems that it has yet to be completely reproduced, however, there are some results that seem slightly positive.
There's something I find slightly odd about Extended Data Fig. 2g. Most of the rightmost (4th) lane seems to be darker than the immediately adjacent background. The issue is just discernible with the naked eye, but I've adjusted levels and contrast to highlight it in this image:
Intuitively, I would have expected any signal simply to add to the background and therefore to increase the overall intensity. There are other variations in background of similar magnitude across the image (darker towards the bottom left), but the change at the edge of the 4th lane is rather sharp and well aligned with the lane.
Is a scale bar in Fig. 2a correct? In my view, size of DAPI-positive nuclei is completely different among panells in Fig. 2a. However, they used only one scale bar for them. What do you think about this?
Could you explain what is the point of these polls? They seem a little silly. You're just wondering how people are "feeling" about the papers? I can't see how this aims to help the scientific process. PubPeer aims to be a serious website...they should be embarrassed for linking to such drivel.
I think unreg is going in a bit hard here. Yes, there's not much science in a poll, but I looked at the results anyway (stem cell people don't know what's happening either...). As long as the hospitality is not abused, I don't mind the odd link of this sort appearing on pubpeer from time to time. The other posts and particularly the crowd-sourcing on the site [Knoepfler's] are certainly fair game.
Thank you. It was disturbing seeing many interjections/links to this blog. From comments on pubpeer suggesting it was legitimate I found the blog had about 20 links to STAP posts which feature sensationalist titles (tabloid like), and content devoid of substance. Some of these then appear on Pubpeer. E.g., "Paul Knoepfler goes skeptic" (Peer 2). And it is based on things such as: "a mature cell *easily* becoming totipotent" cannot be true because if stress created stem cells than we would have teratomas after injuries or spontaneously [asterisks mine].
The STAP process described is considered a natural, easy stress? On what basis do we say that if there is a latent STAP process occurring naturally it would be accompanied with mechanisms prone to teratocarcinoma? The authors raised the question themselves (to have it used against them, it appears). Furthermore, the experiments did not say that full pluripotency or teratomas would or should arise from natural stress in vivo; they show stress far beyond normal contexts inducing strong Oct4 expression allowing eventual in vitro formation of PSCs after specific conditioned culture, but fail to find anything beyond mild Oct4 induction in their reflux esphagitis model. Wild extrapolations to discredit peers degrades scientific discussion.
It will be nice to see replications in other labs but this seems to have been a case of images being mixed up when assembling the paper. Surely these results will be reproduced soon?
====================== On February 18th, in response to the inquiry regarding a suggestion that two placenta images looked identical, Dr.Teruhiko Wakayama, a professor at Yamanashi University and a co-author on the STAP article led by the unit leader Obokata, has responded to Asahi News paper and explained, “It is a simple mistake in which 2 different images of the same mouse taken from different angles were used when one of them was supposed to be removed”.
Prof. Wakayama used STAP cells to produce the mice and imaged them. He took multiple images of the same embryo from different angles. As a result, Obokata misunderstood the identity of those images and used them redundantly. Being overextended with making figures while performing revision experiments all by herself may have been a cause for such misunderstanding, explains Prof.Wakayama.
He adds, “After multiple revisions, the final manuscript does not refer to the two images, but she forgot to remove them”.
Waseda University to begin its own investigations
On February 18th, Waseda University from which Obokata has obtained her PhD has also launched its own investigations. Her dissertation refers to the paper she published in 2011 while studying at Harvard University, and some blogs have raised skepticism that there may have been another duplication of some of the images in this publication.
The figures in question describe the presence of certain genes, however, there were several places in which what appear to be identical images were labeled with different gene names. Prof. Charles Vacanti has explained to the journal, Nature, that it appears to be a simple mistake without any ill intent and has requested to removes these images from the article last week. Spokesperson at Waseda University states, “Even if the said images were removed from the article, we consider that this will have no impact on the validity of her doctorate”.
If you increase the brightness in Fig. 3B you will see that the control image on left is all red without any green and the acid-treated panel on the right is all green with no red. Different filters cubes used on the scope for control vs. experimental = bad news.
Just take a screenshot of the whole figure, open in Photoshop, and adjust the brightness way up. At some point you'll see that the control panel is all red, no green.
I'm not sure that this concern is valid. The control (bottom left of Fig. 3B) seems to have slightly more red and green background than is found around the labeled cells (bottom right), but both colors are there in both panels as far as I can see.
I completely agree, I spotted this a few days ago. I was surprised at just how black the control image was, then I looked a little closer and was very surprised. You can even see without altering anything there is one red spot in the control, just left of the middle and about 10% of the height up from the bottom. If you boost the levels of the image there is no green in the control image. I would expect some background noise to appear green. I have no good explanation for this, but maybe one of the authors, or co-authors, might clarify why this could be the case.
Corresponding mean number of B cells (Fig. 5a) and that of neutrophils (Fig. 5b) are unnaturally similar to each other, while S.Ds are different between the corresponding values.
It is almost impossible that two independent data with different cell types and conditions extremely looks alike.
I have a feeling that there may be hints of what could be vertical splice marks around the second lane of Extended Data 2g, which would fit with this. Very faint, though. Maybe somebody who is good at the image processing can produce a worthwhile image or rule out this concern.
They are similar but not the same, and to my knowledge that is not too strange. Suspicion is good to have, but we should not make uncertain accusations.
Regarding similarity, most of the bands in lane 3 are brighter than 2, but the faint band in the upper-middle is not proportionally more bright, and the shape of this faint band also differs. The background darkness is equal, supporting they are not splices with altered contrast/brightness. The bottom bands have a distinct appearance. Try copying lane 2 and adjusting the brightness and making the size dimensions roughly the same--there is a different shape, particularly distinct at the bottom of the band and the brightness around edges. The bands also differ in their relative size. When expanding lane 2 so that the bottom band had the same width as lane 3's bottom band, other bands between lanes do not match in their width. More simply you can probably see the width variation in the original image does not match. Lastly, if 3 was cut from 2, the top band in 3 does not match up. Honestly, I am a bit surprised at the suspicion over some images that are potentially similar when we cannot be certain. It is 2014, I personally doubt many people would be so careless as to fake in this manner. It is easy to catch in this day and age, I feel you would have to be quite foolish to attempt it.
Regarding similarity of TCR rearrangement in PCR of DBeta2 PCR, I am not knowledgeable in this area, however, a similar result can be seen in this image http://www.cell.com/cell-reports/image/S2211-1247%2812%2900384-1?imageId=figs1&imageType=large (Keller 2012, Cell). Although more distinct variation is possible IMHO there do not appear to be grounds to say the lanes are too similar.
I believe people nowadays are wrongly finding more falsifications often. In the context of this experiment, it would not need to be made by image falsification. It's like a criminal leaving behind fingerprints. Someone wanting to falsify could, sadly, do a better job that is impossible to catch, which is also true over some of the concerns about fluorescent images. Unless one has the original lab notebooks it is pretty hard to verify these accusations, and I do not think it is fair to make them without certainty. I believe verification rests in the hands of those attempting to follow and reproduce these findings.
Extended Figure 2a Endogenous Oct4 staining does not match with Oct4-GFP expression. It is acceptable that Oct4 staining increases from day2 to day7, but a complementary pattern is quite odd. A fundamental question is: Does Oct4-GFP faithfully reflect expression of endo?
I don't think their Oct4-GFP is a fusion protein to represent proper localization, instead simply it appears to be a reporter. The original plasmid is GOF18-EGFP. I believe EGFP was replacing LacZ as a separately coded protein in the vector construction. Under the control of the Oct4 regulatory elements it will presumably signal throughout the cell, while the Oct4 staining will detect normal Oct4 separately.
Positions of GFP-positive cells and Oct4-immunopositive cells do not match in day7 culture. This can be seen clearly if you separate green and red channels from the original color panel.
I am pretty sure they are not supposed to match. The GOF18-EGFP construct is described as a EGFP reporter driven by Oct4 promoter/enhancer (a 18 kb Oct4 genomic fragment). I.e., EGFP is expressed as a separate protein driven by Oct4 activity, thus the GFP and Oct4 antibody should not match. A similar type is found here: http://www.ncbi.nlm.nih.gov/pmc/articles/PMC3572702/figure/F0002/
This can explain intracellular difference in distribution (nuclear versus cytoplasmic), but can not explain difference between cells. Concern is that cells with high endo-Oct4 show little GFP signal.
I cannot see the cell with high endogenous Oct4 and no reporter (red but no green). I guess you mean the middle cells which have low intensity, because I actually do not see any cell shown there without Oct4-GFP. Theoretically the reporter and actual gene should be proportional, but these things are noisy by nature, so the lack of proportionality in one or two cells is realistic.
At day2, Oct4-GFP positive cells should be only a small fraction of total cell population. Therefore the signal in green channel at day2 is likely to be background fluorescence. At day7, cells should proliferate in culture and more Oct4-GFP cells should be detected. I can see two cells with higher intensity in green channel at the lower border of the image at day 7 , but these two cells are negative for endogenous Oct4. In general, intensities of Oct4-GFP and endogenous Oct4 at day 7 are not correlated at all, but rather complementary. These data suggest that Oct4-GFP signal is not a reliable marker of endogenous Oct4 gene expression.
It should be noted that the Oct4-GFP line used in this paper has been widely used in investigations of reprogramming and tracking developmental Oct4 processes, so perhaps that is the quickest assurance of its reliability.
The GFP in day 2 is very unlikely to be background fluorescence. They say the Oct4-GFP are a substantial part of the population remaining viable, but in either case the investigators are only looking at GFP positive cells intentionally for that image, which had the purpose to phenotype STAP cells.
The two GFP+ cells without any Oct4 endogenous expression fits with reprogramming processes having inefficiency, particularly in early stages; I think this should be expected. It is likely in some cells the chromatin is not permissive, to a greater than average degree. We do not know how the stress or acid treatment induces Oct4 activity in detail.
It is likely that in a larger sample we would see more correlation, because of the superior performance of the stronger GFP cells in teratoma formation and expression of pluripotency markers mentioned. Perhaps a reason for a somewhat complimentary pattern is
A final thought, I think the GFP intensity may have been limited in day 7 through the image acquisition/laser power, out of preference for limiting bright green (in their other figures, there is more of a increase in GFP intensity by day 7).
Two regions in Extended Data Fig. 2g seem to display very little noise. This can be seen in this processed version, in which a 'sharpen' operation slightly increases the noise and equalises the background, followed by a shadowing operation. The absence of noise gives a flat grey appearance.
What does that mean? If you are making an accusation about the image could you please clearly state the problem and reasoning? For my image program I get the same image as you using "emboss" not "sharpen".
For one thing, some of these areas would not cover an entire gel length (I assume you are saying something was edited out). Could this be an artifact of compression? Isn't low noise expected where the gel is mostly dark in lane 3, for a relatively low quality DNA gel which was likely compressed? There is no imperative for researchers to use high quality DNA gel images, and believe this can be found normally. I tested your "emboss" method of noise measurement on random google images of DNA gels and found they are common in background (zero noise outside of bands: https://encrypted-tbn1.gstatic.com/images?q=tbn:ANd9GcQPlBbfEw0_Usk5hdWfEfBVtnFumbVXnv8aeeek6pEB7SKf9N3t )
Secondly, the part in lane 2 where you indicate little noise is fairly natural, in the original image in that region, with faint smear edges continuously forming a normal gel appearance. I.e., a faint blur which fits in with the rest of the gel which has noise according to your image.
Lastly, looking at the spots in lanes 2 and 3 highlighted as having little noise, it appears that there is nothing that would be in their benefit to falsify in those areas. A band or absence of band in the area of low-noise would not alter the conclusion.
"What does that mean? If you are making an accusation about the image could you please clearly state the problem and reasoning?"
The post was deliberately limited to a statement of fact. In the context of the surroundings, the "flat' zones struck me as slightly unexpected. Thus, the background between lanes, where noise should be minimal and the processed image should have the highest probability of being flat, is nowhere flat in this image.
Smoothing away unwanted features _could_ give rise to such flat image regions, but maybe they can also arise by chance, as you suggest. I have no strong opinion about possible "benefits' of smoothing away features in these regions, although simple embellishment to remove imperfections is always a possibility. I note that the smooth region in lane 3 corresponds to a distinctive spot in lane 2 and other have suggested above that the two lanes are quite similar.
ED Fig. 2g has at least one other issue - the signal-lower-than-background in lane 4 that I mentioned earlier in the thread.
The sentence for "Karyotype analysis" in methods section of this article is exactly similar to "Chromosome preparation" methods in other researchers' article, "In Vitro Cell Dev Biol Anim. 2005 Sep-Oct;41(8-9):278-83.". Nevertheless, authors of the Nature article did not cite this source.
The former is for STAP cells-derived teratoma, and the latter is for bone marrow sphere-derived teratoma. However, immunohistochemistry images in Nature's Fig.2e and D.thesis's Fig.14 are similar to each other.
does it mean that the figures published in the doctoral thesis should not be published in a journal again? just curious to know. This paper has already reached 100 comments and there is still going on.
Moreover, the Image of STAP cells-derived mesoderm (alpha-smooth muscle actin) in Fig.2d of this Nature article is similar to that of bone marrow-derived mesoderm in Fig.11 of the Obokata's doctoral dissertation published in 2011.
I think the point here is that they are supposedly the results from different experiments. I am however not sure if they really are different experiments without the context. Can the original poster elaborate a bit more? They do look the same for sure.
As far as I know, Nature also prohibits any reuse of figures that have been already published. Whether an author's dissertation counts as a prior publication is a different question (someone can probably chime in).
> I am however not sure if they really are different experiments without the context.
Sorry. I confirmed that they should indeed be from different experiments, since the one in this article is splenic T cells-derived, and the one in the dissertation is bone marrow-derived. It's not just a reuse of a figure.
"I am however not sure if they really are different experiments without the context. "
This is the key point. If the thesis is about the same work, which is not totally impossible from 2011, it might all be OK (I can't imagine that "publishing" one's thesis would preclude using that data in a paper). The figure legends of the thesis figures are in English, so maybe the thesis is too. Could somebody link to it or better yet give the context allowing other readers to see whether the experiments are the same or not?
my understanding of pubpeer is that comment on a particular published papers is sent to the corresponding author of that paper. Did the corresponding author(s) of this particular Nature paper respond to the comments posted here? It is hard to notice any of these 104 comments are from the corresponding authors? Please enlighten me.
The left figures (Nature 2014) are shots of STAP cells-derived mesoderm, and the right figures (Obokata Doctral Thesis 2011) are the bone marrow-derived mesoderm. Two are claimed to come from two separate experiments on two separate things done some three years apart.
It is quite difficult to verify that the right figures are actually from her thesis because it is not available online. The PubPeer rule says that the comments should be based on "publicly verifiable information". Is it possible to show some proof that the figures are truly from her thesis?
The ensuing investigation revealed that Obokata plagiarized doctoral thesis. 33 pages of Obokata’s doctoral dissertation introductory chapter, it was almost all copy and paste.
Thanks for the tineye research. Just a couple questions to make sure of the misdemeanors:
1. Are you sure the directionality of the plagiarism? That O took the photos from those sites, versus the reverse. (Just a check--I have seen this sort of thing.)
2. Does O represent the work as her own experimental work? Agreeably, any copying of an unattributed photo is wrong. But I'm just interested if the photos are descriptive (e.g. in an intro section). Versus being represented as her experimental results. The latter is worse.
The report is not yet available in English at Riken.
There are apparently two clear examples of image manipulation that are tantamount to falsification. In the news coverage it is not stated which, though they appear to be gels.
It is not clear if the papers will be retracted. Obokata objects to the findings.
If the Riken report is available in Japanese if would be of interest to have an English translation posted. Or even a summary of the key points.
The video image of STAP cell generation displayed in RIKEN homepage suggests to me that two GFP+ cells are dead because of the following reasons. 1. These cells form bubbles inflating and disappearing for an instant just before green fluoresence generation (about 11 seconds after the start of the vido). 2. These cells do not show any movements at all after the fluoresence fomation. 3. The sizes of these cells are very small like apoptotic cells.
If I see Videos 1 and 2 supplemented in this paper without any assumptions, I will believe that these video images display phagocytosis of green particles by macrophages. Macrophages reside in spleen and express CD45. Because macrophages are known to ingest dead cells, it can be supposed that several dead cells generating green fluorescence can be phagocytosed by a macrophage and thereby look like cell clustering. Macrophages move very actively in culture even after phagocytosis, and therefore green fluorescent “cell clusters” look like mobile with cell processes.
When I read the paper for the first time one of the things that struck me was the incredible perfect differentiation of pancreas and endoderm in their teratomas. I even thought they were sections of real pancreas and intestine not a teratoma. With all the unethical usage of images in the paper and in Obokata thesis now I think that it's possible that those pictures indeed are sections of pancreas and intestine. I hope that someone in Riken is willing to analise this issue.
Before a press conference on the final report of investigation committee about STAP papers, RIKEN replaced the interim report of the investigation released on 15 Mar with a new version which deleted large parts of gel images on 31 Mar WITHOUT ANY NOTIFICATION, just a day before the press conference.
See pp.9-10: large parts of Gel 1 / Gel 2 images were deleted.
In the press conference on 1 Apr, the committee explained Obokata requested to delete the large parts of Gel 1 / Gel 2 as mentioned above because they were "unpublished data".
But some experts argue that Gel 1 seems to be an original version of a gel image in their application to international patent, Fig. 20.
Madhusudana Girija Sanal | Mar 10 2014 18:33 EST It is a common observation that stressed cells, dying and dead cells start to become fluorescent. So early observation of florescence as a pointer to pluripotency (Oct4-GFP) needs to be substantiated by other experiments. The authors need to provide more evidence (molecular biological and morphological) and details (protocol) regarding STAP during the early hours to days post-stress, because this period seems to be the most critical in reprogramming (compared to characterization of the final product-STAPs). The authors underscore that the production of STAP is not the result of any type of “selection” during culture. However in a subsequent protocol paper (doi:10.1038/protex.2014.008) they see a ‘possibility of negative cell-type-dependent bias’. In the new protocol paper they also didn’t observe any T-Cell receptor rearrangement. So what type of PTPRC (CD45+) cells contributed to STAP? It is also difficult to understand or define the difference between STAP cells and STAP stem cells.
The Science piece about the retraction is quite interesting. The gel splice that was commented early on had been spotted by a referee at Science (who then rejected the MS).
http://www.ipscell.com/2014/01/review-of-obokata-stress-reprogramming-nature-papers/
"...something akin to hitting the cells over the head with a sledgehammer of a pH 5.7 (physiological pH is more typically thought of as around 7.4), they report the blood cells of 1-week old mice turned on expression of an Oct-GFP reporter as they floated around in clusters in the media."
"...the team provided pretty good evidence that the STAP cells arose from the differentiated blood cells themselves rather than potentially from rare pre-existing primitive stem cells in the cell populations."
"...After a relatively quick read, no particular red flags jump out at me from the STAP cell paper. It just seems too good and too simple of a method to be true, but the data would suggest so far at least that this team is onto something really important."
But key open questions remain before anyone can really say just how important this is.
1. Will it be reproducible by other labs?
2. Will it work in human cells?
3. Will it work in adult cells?
4. What are the molecular mechanisms?
5. Do these cells possess significant rates of mutations or epi-mutations, the latter being abnormalities in the epigenome?
6. Are these cells tumorigenic (besides forming teratoma)?
In particular, if the answer to one or more of the first 3 questions is no, then the impact could be significantly muted.
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A "minor " point: do the endodermal cells (Extended Data Fig 3d) express villin?
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