During an individual’s lifetime, blood-forming cells in the bone marrow called hematopoietic stem cells (HSCs) supply all the red and white blood cells needed to sustain life. These blood stem cells are unique because they can make an identical copy of themselves (self-renew). Disorders of the blood system can be terminal, but such diseases may be cured when patients are treated with a bone marrow transplant. Unfortunately, bone marrow is in short supply due to limited availability of donors, and it is not yet possible to expand HSCs outside of the human body; HSCs that are removed from their native environment, or niche, rapidly lose their ability to self-renew and thus cannot sustain hematopoiesis in a transplant recipient. Furthermore, attempts to make blood stem cells from embryonic stem cells (ESCs) have also proved unsuccessful to date because these “tailored HSCs” are defective in self-renewal as well. These problems suggest that our understanding of the biology of HSCs is not sufficient to foster their maintenance or generation. To address this issue, we propose to study hematopoietic stem cells in the context of mammalian development; the entire complement of a person’s HSCs is made in a very short time window during the first trimester of pregnancy. By increasing our understanding of how HSCs are made and acquire self-renewal in vivo, we hope to develop better methods of generating HSCs in vitro and learn to provide the missing cues to coax them into becoming fully functional, self-renewing hematopoietic stem cells. Specifically, we plan to investigate how the fate decision that delineates blood cells from their embryonic precursor, called specification, is maintained at the molecular level. Second, we are interested in what cell type human HSCs descend from so as to understand what precursor to look for when attempting to differentiate ESCs into blood stem cells. Finally, we plan to apply molecular analyses to the property of self-renewal by looking at cell populations that cover a spectrum with regards to self-renewal: HSCs, cultured HSCs (not self-renewing), HSC precursors (not self-renewing), and ESCs differentiated to non-self-renewing HSCs. These comparisons will help define the molecular regulation of self-renewal, and place ESC-derived progenitors on the spectrum of self-renewal. Through these studies, we hope to better understand blood stem cells as they are made and maintained during human development with the ultimate goal to provide wider access to stem cell-based therapies.
Funding of research to understand hematopoietic stem cell (HSC) biology offers rewards beyond the pursuit of knowledge. HSCs are responsible for providing all of the blood cells in the body, including both red cells that carry oxygen and white cells that mediate immunity. Inherited disorders affecting HSCs and their progeny are responsible for diseases such as sickle cell anemia, Severe Combined Immunity Disorder (SCID), and leukemia; these devastating ailments change the lives of thousands of people in California every year, and currently most are incurable without a bone marrow or cord blood transplant. Due to the limited availability of donors, other alternatives, such as differentiating embryonic stem cells (ESCs) into HSCs, are being explored. One critical fault of ESC-derived progenitors is their inability to “self-renew”, i.e. produce more of themselves, thus eliminating their usefulness for transplantation. However, a deeper understanding of the developmental and molecular processes that create functional HSCs that can self-renew may ultimately make the goal of deriving HSCs from ESCs attainable. Research into the mechanisms of self-renewal may also improve treatments of cancers such as leukemia, as these diseases are a function of over-proliferation of cells caused by uncontrolled self-renewal; targeting genes or proteins involved in abnormal self-renewal programs may provide more specific cancer fighting drugs, and would likely foster collaborations with biotechnology companies. Furthermore, as all stem cells in the body have the ability to self-renew, a clear understanding of self-renewal mechanisms will benefit all stem cell research, and could have a positive effect in a wide range of biomedical specialties.
SYNOPSIS: The first hematopoeitic cells formed during development are transient, non-self renewing myelo-erthyroid progenitors, which are replaced later by definitive, self-renewing hematopoetic stem cells. These two hematopoeitic programs use the same specification mechanism, which is dependent on the b-HLH transcription factor SCL, but differ in the sites at which the progenitor cells arise. The transient progenitors arise in the yolk sac, whereas the definitive hematopoetic stem cells (HSC) arise from the aorta-gonad mesonephros and, at least in mice, from the placenta. The ability of definitive HSC to self-renew is rapidly lost in vitro. The general goals of this proposal are to understand the epigenetic processes that contribute to HSC specification, to better define the cell of origin of the definitive HSC in vivo both in mice and humans, and to characterize the epigenetic changes that distinguish self-renewing definitive HSC from transient HSC and from HSC that have lost the capacity for self-renewal in vitro.
In the first Aim, the applicant will extend her previous studies, which identified by transcriptional profiling a group of genes whose expression is regulated by the transcription factor SCL, to identify direct targets of SCL by ChIP-chip in murine embryonic stem (ES) cells as they differentiate to hematopoietic lineages. Potential changes in the histone and DNA marks in the promoters of these SCL targets will also be determined. She will further study how these modifications are maintained in the absence of SCL, which is only transiently required for HSC specification. Similar analyses will be performed with in vitro differentiated human ES cells.
In Aim 2, the PI will focus more on the developmental origin of definitive HSC in the placenta and the developmental timing of epigenetic changes in hematopoetic genes using mice marked genetically with hematopoeitic lineage tracers. Furthermore, placental HSC will be identified and purified from human placentas by immune staining for endothelial cells that co-express SCL.
In the first part of Aim 3, the PI will use human fetal tissue to identify the earliest definitive, self-renewing HSC. Initial data from the PI shows that by 5 weeks the human fetus has multipotent progenitors that sustain long term T lymphocyte chimerism in transplanted SCID mice. In follow-up studies the PI will identify the earliest mutilineage, serially transplantable HSC from the human fetus. The second part of this Aim addresses questions related to how the self-renewal capacity of definitive HSC is established. Different populations of human and mouse HSC , including HSC that have lost self-renewal after growth in vitro, will be assessed by global gene expression profiling, to determine whether genes involved in self-renewal, senescence, etc. might be differentially expressed. Epigenetic changes will be examined in the same way. The typical expression profiles of self-renewing vs. non-self-renewing HSC will be compared to HSC derived from ES cells to determine the closest in vivo correlate of an ES-derived HSC.
STRENGTHS AND WEAKNESSES OF THE RESEARCH PLAN: This is a lucid, well-written and in part innovative proposal to study the developmental biology and epigenetics of hematopoetic stem cells. The proposal builds on work the PI did as a postdoc in the Orkin lab, studying the developmental origin of definitive HSC in vivo, and on the role of the SCL transcription factor in hematopoetic specification. This is a highly significant project, as this knowledge will impact not only our basic understanding of stem cell biology, but also has a direct impact on clinical work.
The applicant proposes to characterize the histone modifications and DNA methylation patterns of HSC at a variety of developmental states using state-of-the art approaches for cell isolation and epigenome analysis. These studies will undoubtedly produce a lot of information; however, it is unclear how the applicant will prioritize this information or use it to better understand HSC function. Also, the approach that she proposes is not particularly imaginative. Many gene expression profiling studies of HSC have been performed previously, and the generic characterization of histone modifications and DNA methylation marks proposed is highly similar to studies previously performed on ES cells by the applicant's collaborator. Furthermore, some aspects of the HSC epigenome that the applicant proposes to describe have already been uncovered in recent analyses published by the Weissman and Nakauchi groups. However, as these studies focused primarily on adult HSC, the applicant’s analysis of fetal HSC populations, and particularly of placental HSCs is novel, and may yield new targets. The prospective identification of early human HSC proposed in Aim 3 also would be novel and significant, and uses the applicant's unique resources and expertise.
In most respects, the proposed studies make use of technologies with which the applicant has demonstrated expertise. In particular, she is clearly a leading expert on the isolation and analysis of early fetal HSC from various anatomic locations. However, while she has recruited an expert collaborator to help with epigenetic analysis, the proposal does not specifically address how bioinformatic analysis of the data generated will be performed, what stringency filters will be imposed, how candidate genes will be selected and how they will be pursued in order to obtain more mechanistic insights into hematopoietic specification. Such a discussion would have helped in understanding the likely impact of the data to be generated. It further appears premature to propose to do exactly the same experiments in human ES cells without prior evidence that the more experimentally accessible mouse system has yielded useful results.
Under Aim 2, the applicant proposed the biological goal of determining whether HSC emerge directly from placental endothelium during development. These are clever studies that are certain to be informative, if not entirely definitive, since it is not clear that the proposed epigenetic analysis of hematopoietic genes will in fact accomplish this goal. A description of the promoter status of these genes should provide new information about the timing of epigenetic changes that accompany HSC specification in vivo, but could not provide direct evidence for a lineal relationship between putative hemogenic endothelium and fetal HSCs. In addition, it seems such an analysis would be highly dependent on the choice of the genes to be analyzed, and it is not clear which these are, or how they were chosen. Regarding the identification of human placental HSCs, there should be some question about the numbers of such cells that can be isolated and therefore whether the molecular studies are feasible as proposed.
Aim 3 is the most risky, but also the most interesting and innovative. With regard to the identification of serially transplantable HSC from the human fetus, preliminary data would have been helpful to assess the feasibility of this novel approach. Also, it is somewhat uncertain that the pathways which govern self-renewal will be unveiled by the proposed global gene expression profiling and epigenetic analyses, and a clear rationale for the inclusion of all the proposed cell populations is lacking. This would have been especially useful as some of the populations appear to be redundant with previously published gene profiling analyses, and so what will be different about these studies is not clearly highlighted.
The proposal generally lacks appropriate discussion of potential difficulties and alternative approaches. For example, the ability to identify direct targets of SCL in small numbers of sorted cells will depend on whether the anti-SCL antibody performs well in mini-ChIP experiments. Since the relative efficiency of mini-ChIP can vary greatly depending on the antibody and ChIP target, the feasibility of this approach should be demonstrated in small numbers of cells. Alternative approaches if SCL mini-ChIP does not suceed are not discussed. Likewise, obtaining meaningful and accurate molecular analysis of human cells after sorting by intracellular FACS would seem to be a challenging undertaking, and the feasibility of this strategy is not demonstrated. Finally, in order to isolate early fetal HSC from human tissues, the applicant proposes to screen by intrahepatic injection into Rag2/gamma-deficient mice, which has been successful for analysis of cord blood HSC, but it is possible that the very early human cells she proposes to isolate will not engraft as well in this model. Preliminary data and/or alternative approaches should have been discussed to support the feasiblity of this strategy.
In conclusion, this proposal can come across as overambitious as the volume of work and data generated here is tremendous. Perhaps a better, more focused approach might be useful. It is very clear that the PI has the ambition and talent to fulfill all the goals. Because of her strong qualifications, the PI should get the benefit of the doubt that she knows how to prioritize her follow up and deal with unexpected issues lying ahead.
QUALIFICATIONS AND POTENTIAL OF THE PRINCIPAL INVESTIGATOR: Hanna Mikkola received her MD and PhD in 1997 from the University of Helsinki. She did postdoctoral work at Lund University (1998-2000) and Dana Faber Cancer Institute (as a Research Associate, 2000-2005). She was then appointed an Assistant Professor in the MCB department and Institute for Stem Cell Biology at UCLA. Dr. Mikkola is clearly well-qualified to lead these studies. She has trained with experts in stem cell biology (Steffan Karlsson and Stuart Orkin), and already can be considered a leader in the HSC field in her own right. She has made multiple seminal discoveries in her career, including identification of the placenta as a major source of fetal HSC in the mouse and that SCL is required only transiently for HSC development. She has an impressive publication record with numerous papers in top journals throughout her research career, and since starting her laboratory has been quite successful in obtaining funding. She has received an R21, a seed grant from CIRM, a V Scholar award, and an award from ASH. These are in HSC biology, but do not overlap this proposal. The candidate's plan for developing a successful career is well-defined and sensible and she has clearly embraced her role as a teacher and mentor. There is no hesitation affirming that she and her team are perfectly qualified to perform all the specific aims of this grant.
INSTITUTIONAL COMMITMENT TO PRINCIPAL INVESTIGATOR: UCLA has demonstrated a clear committment to advance the career of this young investigator. The institution has provided ample laboratory space in the new Biomedical Sciences Building, where much of the MCB faculty and faculty of the Institute for Stem Cell Biology are located. Dr. Mikkola was supplied with plenty equipment, core facilities, administrative assistance and start up funds to support her research. In addition, Dr. Mikkola's career development is supported by formal mentorship interactions with senior faculty (Dr. Robert Goldberg, Dr. Utpal Banerjee, and Dr. Owen Witte). The scientific environment is stellar, and provides unique and necessary collaborative interactions that support the proposed studies.
UCLA has a long and successful history of promoting the successful development of research faculty. In addition, there clearly is a major investment in stem cell science in particular at UCLA, with the establishment of the Institute for Stem Cell Biology under the direction of Dr. Witte. The UCLA graduate program recruits and trains top-notch students, who will contribute to Dr. Mikkola's research program. She is apparently a popular choice with the graduate students.
DISCUSSION: The PI is clearly an excellent investigator, with an exemplary track record, including seminal papers describing her pioneering discovery that the placenta is a site of hematopoiesis in mouse. This research provides the PI with unique skills in this area. The proposal is very well-written, but it is not imaginative or innovative, e.g. there is no novelty in the proposed epigenetic analysis. A lot of profiling, high throughput analysis, is proposed, and it remains unclear how the PI will analyze the data. Furthermore, a lot of similar profiling has already been performed by others, and their data are available online for data mining. Another concern was that some of the proposed research relies on a lot of technology falling into place, and a lack of preliminary data for technically challenging experiments calls into question the feasibility of some aspects of this study.
Notwithstanding these concerns, the panel expressed great enthusiasm for the possibility that the proposed work may lead to the identification of HSC in the human placenta, which would be of great significance to the stem cell field. Although a risky goal, this PI is clearly positioned, having discovered the presence of HSC in mouse placenta, to achieve this objective. Since there was a concern that this important goal was presented only as a sub-aim in the proposal, the panelists collectively recommended that the PI should place special emphasis on the human placental work.