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RC1-00112-1: Intracellular signaling mechanism for control of hESC pluripotency

Recommendation: Not recommended for funding 

Public Abstract (provided by applicant)

It has been widely appreciated that human embryonic stem cells and somatic stem cells are expected to be sources of cells to regenerate or rejuvenate damaged tissues, yet the research work on human embryonic stem cells has been hindered by the difficulties in manipulating their self-renewal versus differentiation properties in vitro. This is largely due to lack of understanding of the molecular and cellular basis for maintenance of human embryonic stem cell pluripotency, the ability to duplicate itself and also give rise to other types of cells with specialized functions such as blood cells, neural cells in the brain and skeletal muscle cells. Like many other cell types, the functions of human embryonic stem cells are regulated by extracellular signals. A unique intracellular signal transduction mechanism can interpret various extracellular signals, guiding the cell to adjust its activities for adaptation to the changes in the environment. One important biochemical mechanism for signal transduction is reversible phosphorylation on proteins, in which a phosphate can be added or removed from proteins. This reversible process is facilitated by two groups of enzymes, i.e. kinases that can add a phosphate on a protein and phosphatases that remove a phosphate from a protein. The applicant discovered a phosphatase that operates in the initial step of intracellular signal transduction more than a decade ago. Notably, his group has found that removal of this phosphatase promotes mouse embryonic stem cell self-renewal. More recently, the applicant has also observed that this phosphatase has a similar function in human embryonic stem cells. On this project, the applicant and his colleagues will use their expertise on the phosphatase and stem cells to investigate and illuminate the biological properties of human embryonic stem cells. Based on the database accumulated from other research groups, this laboratory will do experiments and develop a better set of biological markers for identification of human embryonic stem cells. Finally, the applicant and his colleagues will develop new reagents that can be used to amplify the human embryonic stem cells without changing its property in culture for basic research and clinical application.

Statement of Benefit to California (provided by applicant)

This applicant must say at the outset that I am very proud of being an American, in particular a Californian. Californians have the tradition of stimulating an entrepreneurial spirit, thus making the state ahead of others to launch novel and risky ventures, particularly in the biotechnology field, and in the stem cell research. In the 21st century, there is no doubt that the research work on human embryonic stem cells will take the lead in the advancement of biomedicine and biotechnology. Progress in this type of research will benefit people suffering from many different types of diseases such as cancer, neurodegenerative diseases and cardiovascular disorders. On the proposed project, the applicant and his colleagues will take advantage of decade-long research experience in molecular and cell biology, particularly on mouse and human embryonic stem cells. We will carefully investigate the human embryonic stem cell properties, to understand better how these cells can duplicate themselves and also produce other cell types with specialized functions, such as blood cells, neural cells and skeletal muscle cells. This information will be instrumental for future research and application of human embryonic stem cells in and outside of California. Based on experimental results from this and other laboratories, we will be able to develop a better set of biological markers for identification of human embryonic stem cells. Finally and most importantly, we will design and produce new reagents that can be widely used in culturing and amplification of human embryonic stem cells for basic research and clinical application. All this will benefit tremendously Californians and people in this country, and in the world.

Review

SYNOPSIS OF PROPOSAL: This proposal seeks to establish a role of a known protein in human embryonic stem cell (hESC) function. The preliminary data indicate that knockdown of known gene expression using siRNA or pharmaceutical inhibition of known protein activity in hESCs leads to impaired differentiation and enhanced self-renewal. The hypothesis is that by elucidating the action of a known protein, the investigators will be able to sort out the common and distinct signaling events between hESCs and murine ESCs (mESC) in the control of self-renewal versus differentiation for better understanding of the molecular basis of “stemness”. Areas of focus are to determine the impact of known protein deficiency on genetic control of hESC pluripotency; to investigate the effect of known protein deficiency on epigenetic control of hESC identity; to elucidate the link of intracellular signals to genetic/epigenetic control of hESC pluripotency; and to isolate/develop reagents that maintain hESC pluripotency.

IMPACT AND SIGNIFICANCE: This investigator seeks to use a single-gene approach focusing on the known protein and its intracellular signaling partners in mouse and hESC cells, and determine its role in hESC pluripotency. The impact/significance of this study is that it is true, as claimed by the PI, that there is relatively little information on cytoplasmic signaling molecules and signal transduction cascades (which are so well defined in fibroblast and in cancer cells) that talk to the key nuclear regulators such as NANOG, OCT4 and SOX2. Thus, the definition of these cascades and their role in maintaining or instructing pluripotency would be quite useful. However, this moderate enthusiasm is tempered by the fact that it is extremely well established that molecules like the known protein are highly promiscuous and talk to many, many different signal transduction pathways suggesting that their manipulation, either genetically or pharmacologically, may not be useful in deriving or maintaining specific lineages of hESCs.

The known protein is a molecule expressed in many cells of the body and is downstream of many growth factors. An understanding of this pathway and its regulation is of fundamental interest, however the study proposed is focused strictly on this molecule and its potential role in ES cell differentiation. The PI has previously shown that in mESC null for the known gene, differentiation is slowed as is the growth rate. Here extensive studies are proposed based on the hypothesis that the known gene is a key player in maintaining the undifferentiated state, and that this would be most helpful for future large scale use of hESCs. Extensive data gathering with state of the art technology are proposed but unfortunately without much rationale or indication of how the data will be interpreted. While this molecule has a role that is likely to be downstream, the more innovative and interesting potential outcome is the identification of small molecules that may be used transiently to sustain the undifferentiated status of hESC as they are expanded. However, there are several big “ifs” to this outcome, including whether this inhibition could be reversible, and if proliferation could be maintained during this inhibition.

The PI was the first to show an effect of known gene deletion on mouse and now hESC self renewal and differentiation, and now proposes to use this as a hook to undertake an extensive investigation of hESC self renewal. To the extent that the proposed work could lead to an improved understanding of hESC self renewal it may have high level of significance. The major concern is that the entire approach depends on demonstrating that “known protein” is a valid target for promoting ES cell self renewal and preventing differentiation. Unless this is definitively established, one questions the entire basis of the application. This would ideally be demonstrated both in mouse ES cells and hESCs (where restoration of the known gene could restore teratoma forming ability). Unless data of this type exists, there is cause to question whether the extensive studies proposed here are justified.

QUALITY OF THE RESEARCH PLAN: This is a very descriptive study of known protein function in hESCs. It seems to mirror many of the previous studies done by this PI. The key piece of preliminary data seems to be that the known protein in mouse ES cells increases self renewal and suppresses differentiation. This is interpreted by the PI as evidence that known protein functions in a key role in mESC pluripotency. The PI will determine gene expression profiles in wild type and knockout mESC and apparently in hESC as well. These experiments are fraught with difficulties as a huge number of genes are modified by these molecules. The proposal continues with highly descriptive information including: analysis of global CpG methylation and the role of “known protein” function in the genetic or epigenetic control of hESC pluripotency. In fact, for one aim there is no specific experiment described at all other than integrating an expression data and epigenetic data set.

The proposal provides an ambitious array of high technology experiments without clear rationales or interpretations. A team of collaborators has been enlisted to provide expertise for all the high tech experiments. While differences in regulation of differentiation and self renewal between mESCs and hESCs are important for our understanding and future use of these cells, the experiments proposed are mainly in mESCs and seem more to be included for their “state of the art” technology than for clear hypothesis testing. In addition, important published work that may have direct relevance to the success of the proposed project appears to have been overlooked in the design of the research plan. Overall, a considerable body of data will be generated on mESCs and less on hESCs, but the impact of this is not apparent. However, the final goal is aimed at developing small molecule inhibitors for the known protein, which has important potential for the scale up of hESCs. However, this is pretty much highly speculative, and it is questionable whether it is appropriate to pursue at this time.

In summary, the experimental plan is, essentially, a huge amount of descriptive experiments on a molecule, likely to mediate many signals. Whether this is at all specific to hESC function or maintenance is unclear. There was not enough preliminary data to evaluate this and it is simply premature at this time to know whether this is a promising new direction. In addition, the application is not very responsive to the RFA as the laboratory is not doing mature and ongoing studies of hESCs. This may be more appropriate for a SEED grant.

STRENGTHS: The experience of the investigator and the importance of defining potential pharmacological targets for manipulating hESC function are strengths. A talented team of collaborators has been enlisted to provide expertise for all the high tech experiments. The PI has large base of knowledge and reagents and has previously reported that known protein loss results in delayed differentiation and decreased growth rate. The investigator’s track record of productivity is a strength, and s/he is a leading authority in known protein function in ES cells.

A head-to-head comparison of “known protein” in mESCs and hESCs in the same lab is important, but there are some issues that significantly complicate the interpretations. The small molecule screen for inhibitors of the known protein has already identified one potential molecule that is to be tested in hESC to see whether there is a reversible maintenance of a undifferentiated state while scaling up expansion.

The apparent consistency of the proteins effects across both mouse and human ES cells is attractive, and the proposed extensive use of local and national resources and expertise is a strength. Also, the environment is outstanding.

WEAKNESSES: Relevant, important databases available from published literature were not used to generate hypotheses for this proposal. The published work suggests that the known protein is downstream of some but not all the known renewal genes. These data imply a great complexity since the PI reports data that Nanog, Oct4 and Sox2 are changed when the known protein is absent in mESCs.

It is unclear how effective the knockdown of the known gene in hESCs is. There is a suggestion that with nucleofection a 90% efficiency is achieved but no preliminary data on the efficacy of knock down is provided. It is promising that a Lentiviral vector for shRNA is being tested.

Many of the high-tech experiments are proposed but without much detail of rationale or interpretations on how they will be used to address the hypothesis that the known protein is regulating hESC pluripotency.

The lack of experience of the PI in hESC function is a concern, and the preliminary data on the role of the known protein”in mESC function is of marginal quality; the figures in the Preliminary data are of exceptionally poor quality.

One questions the extent to which the apparent similarity in the known protein’s effects in mouse and human ES cells is mechanistically similar since tne known pathway activation is not sufficient for hESC self renewal.

The single-gene approach proposed is a weakness, and combined with the unclear specific relevance of the known protein to mESC/hESC pluripotency maintenance or function, there is cause for concern. It is very likely that activities of the known protein will be highly promiscuous. More focus on validating the known protein as a true “self renewal” target is needed.

DISCUSSION: Reviewers and discussants agreed that the central premise of this proposal was unfounded given the lack of convincing preliminary data to support the idea that the known protein is involved in self-renewal. Recommended were careful knock-down and add-back experiments to establish the role of the known gene, especially in light of its predicted promiscuity.

Also agreed upon was a sense that the proposal was propelled more by an historical interest in a single gene than by hypothesis-driven science.

The discussants felt that the proposal suffered from a lack of three important elements: experimental support for the central idea, clear relevance to hESCs and hypothesis-driven science.

The following Working Group members had a conflict of interest with this application and were therefore recused from participating in review of, discussion of, and voting on the application:

• Feinberg, Andrew
• Lansing, Sherry