SYNOPSIS: The purpose of this grant application is to generate “custom tailored cardiomyocytes as a solution to modify and repair injured myocardium”. The author proposes four specific aims. Specific aim one is “to test the hypothesis that human embryonic stem cells (hESCs) or hESC-CMs can be driven into rhythmically-firing pacemaker with a customized firing frequency.” This aim targets cells for possible application for rhythm generation disorders. The goal here is to obtain customized human pacemakers that are engineered to fire at different rates. Specific aim two will “test the hypothesis that the embryonic (and arrhythmogenic) electrical phenotypes of hESC-derived cardiac muscle CMs can be maturated for safer transplantation.” When cardiomyocytes are derived they maintain the electrical properties of embryonic type. In order for these cells to become suitable for transplantation into adults, maturation of their rhythm is required. Specific aim 3 will “test the hypothesis that proteins key to cardiac differentiation and maturation can be identified by comparing the proteomes of hESCs, their cardiac progenitors, fetal and adult human cardiomyocytes.” Aim four is to test the function and efficacy of hESC-CMs as donor cells. In this aim, the author proposes to test the simple but important question of whether donor CMs can functionally integrate with and modify the excitability. The proof of principal will be established in guinea pigs and swine, respectively.
IMPACT AND SIGNIFICANCE: The proposal has scientific significance related to the development of hESCs as models to study the formation of human conduction system cells. The clinical significance is not as compelling, given that conventional pacemakers work quite well and the only potential niche for a biological pacemaker might relate to infants with congenital heart block, a relatively rare entity. However, there is insufficient preliminary data to support this potential therapeutic direction at the present time.
The applicant proposes to improve on existing methods for preparing hESC-derived cardiomyocytes. The logic is three-fold: limitations of "stochastic" differentiation, the electrophysiological immaturity of conventional hESC-derived cardiomyocytes, and the proposed utility of biological pacemakers. Modifying the cells' rate of electrical firing in defined ways is quite interesting, in terms of understanding more concretely how cardiac automaticity is established, but the clinical need for biological pacemakers is not at all convincing, by comparison to other priorities in the field. Several of the needs appear to be exaggerated, alternative approaches are minimized, and potential hazards including integration events and tumorigenicity are disregarded.
QUALITY OF THE RESEARCH PLAN: This proposal is poorly written and full of unnecessary jargon. The same proposal could have been conveyed in a much simpler, cleaner fashion. Aspects of the design are appropriate, but the underlying assumption that expression of modified HCN pacemaker channels in ESCs will somehow lead to the increased formation of ES-derived cardiomyocytes is unclear. HCN channels are actually expressed throughout the early embryonic heart in most cardiomyocytes, and later become restricted to pacemaker and other conduction system cells during subsequent steps of heart maturation. Another potential problem is that there is extreme heterogeneity of the cardiomyocytes that are derived from differentiating ESCs, that include atrial, ventricular, and conduction system cells. Expression of these modified HCN channels are likely to have differential effects on each of these cell types and it may be difficult to unequivocally identify the original cardiac cell type which is being interrogated, resulting in a large scatter of data from expression of a single construct.
Aims 1 and 2: Cell "maturation" on the basis of forcibly expressed exogenous channels alone does not adequately take into account many potential kinds of cell heterogeneity, within the cardiomyocyte lineage. Why not pursue more thoroughly and systematically the strategy of positive and negative selection using the promoters for chamber-specific proteins plus selectable markers? For instance, does MLC2v-RFP as a single criterion optimally identify mature ventricular myocytes derived from hESCs? Would a longer fragment or human bacterial artifical chromosome give better results? Would dual or triple selection give better results? The entire selection strategy is disappointingly superficial and even naive. Alternatively, since any genetic manipulation of the hESCs, whether for selectable markers or for expressed channels, introduces a further safety hazard beyond that of the hESCs alone, why not consider a chemical genomics approach altogether (screen for compounds that elicit the desired properties)?
Aim 3: The applicant proposes to find proteins "key to cardiac differentiation and maturation" by a proteomic screen of differentiating hESCs and fetal or adult heart cardiomyocytes. A screen alone, without functional validation, is a poor choice for a project of 4 years' overall duration. Insufficient indication is given about how positive hits would be prioritized, for later functional testing, or the exact form such testing would involve, if forced overexpression was uninformative.
Aim 4: The described experiments fall short of testing the "functional efficacy" of the engineered cells in disease, except in the narrow context of sick sinus syndrome. An infarction model is not yet in hand, and the relevant experiments are described in cursory fashion. Contractile function would only be ascertained if the cells "do not cause electrical disturbances," and there is no fallback plan at all if the cells are not persistently silent in vivo.
STRENGTHS: The investigator has extensive experience in cardiac biology in general, and electrophysiology of cardiac channels in particular. The applicant has hands-on experience with WiCell and HES2 hESCs, experienced collaborators for many aspects of the work, and excellent publications. The proposal has some interesting aspects, and the goal of understanding hESC-derived cardiomyocytes as a system to study conduction system cells has potential value.
WEAKNESSES: There are many weaknesses in this proposal, but perhaps the most important one is the complete lack of appreciation for where the field currently stands. For example, the author states that it is relatively straightforward to derive cardiomyocytes from hESCs. The applicant cites up to 90% from HES4. This is simply not correct. We are far away from even the basic understanding of how you derive cardiomyocytes from hESCs to start with, before we need to worry about changing their rhythm. The answer to questions such as how many transition states it takes for an hESC to become a cardiomyocyte are neither addressed nor appreciated. Do the cells need to undergo first a change to dorsal mesodermal fate in cardiac lineages? It is not clear how the specific cardiac cell types will be isolated.
Additional weaknesses include the emphasis on biological pacemakers (a clinical need of uncertain value), the excessively narrow focus on electrical maturation, the superficial use of genetic selection, the failure to explore alternative approaches that might bypass the need for genetic vectors, and the failure to test systematically for tumorigenicity.
Furthermore, specific aim 3 proposes a comparative proteomic approach among: hESCs, the cardiac progenitors, fetal and adult human cardiomyocytes. The author may not realize what this means if this is to be done with the appropriate statistical controls. Are cardiac progenitors derived from hESCs a homogeneous population? If they are not, what would that proteomic analysis mean? Given that, unlike mice, hESCs are not inbred; how would one deal with genetic variability at this level of resolution?
The PI is a bright, young, aggressive individual, but the proposal is not well thought out and presented with an amazing amount of unnecessary jargon. The clinical need is not competitive (designing biologic pacemakers over electronic pacemakers). Even if the rationale were strong, the scientific aspects are naïve. The applicant is taking a lot for granted technically. Collectively, the aim is to get cardiomyocytes but it is not easy to get a homogeneous population of these. The study is not comprehensive for the field, and the clinical significance is virtually nill. The PI is well-trained, but his knowledge of hESCs is not strong.