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Transformation is in the air…future directions in epidemiology

June 24, 2013

Clock with "Time For Change" textAs the NHLBI moves to advance the state of epidemiology of heart, lung, blood, and sleep diseases and disorders, several new steps were announced at the recent National Heart, Lung, and Blood Advisory Council (NHLBAC) meeting. These initiatives include the establishment of a working group to be led by Dr. Veronique Roger that will include members of both the NHLBAC and the Board of External Experts.

As we address the challenges brought by big data and small budgets, the NHLBI is convening this working group to propose recommendations to the NHLBI director on future directions with existing cohort studies, longer-term epidemiology strategy, and practical clinical trials. The working group will consider the “LEVI’S” concepts – L for large and leveraged; E for external and embedded; V for valuable for informing scientific thought, medical practice, or public policy; I for inexpensive, integrated, and able to preserve/enhance existing investments; and S for scientifically sound.

To provide sufficient time for the working group to address the future direction of cohort studies while preserving the value of existing investments, the NHLBI plans a limited renewal of two cohort studies (the Framingham Heart Study and the Multi-Ethnic Study of Atherosclerosis) to begin at the end of their current project periods in 2015. The working group and the NHLBI aim to strengthen epidemiology by developing a dynamic, state-of-the art program that is achievable and affordable.

We strongly encourage your comments and suggestions, and hope you will consider sharing with us your thoughts on the future directions of epidemiology.

Posted by Michael Lauer, M.D., Director of the NHLBI’s Division of Cardiovascular Sciences.

June 2013 National Heart, Lung, and Blood Advisory Council presentation

6 Comments leave one →
  1. June 25, 2013 9:14 am

    Very exciting, and I look forward to seeing how NIH/NHLBI and epidemiology thrive in this new environment. Very glad that Framingham is being maintained, as well as the Multi-ethnic study of atherosclerosis

  2. Chandra Jackson permalink
    June 26, 2013 8:53 pm

    This is truly exciting! Can we make sure the working group includes some racial/ethnic diversity and/or individuals at least interested in disparities research as it is frustrating/limiting to conceptualize research questions that could make major contributions and potentially illuminate mechanisms that we are *all* undoubtedly interested in only to find that the available studies do not ask the most ideal/relevant questions nor did they have a sufficiently robust sample of racial/ethnic minorities. This country is becoming increasingly diverse, and every concerned citizen should be interested in addressing health disparities to protect our future. I am excited about the future of epidemiology!

  3. Lewis H. Kuller, MD, DrPH permalink
    August 13, 2013 9:25 am

    This is in response to the statement on the transformation in the epidemiology program and request for comments based on the presentation of June 19, 2013 to the NHLBI by Dr. Michael Lauer.

    The mission of the NHLBI is to provide “…global leadership for a research, training, and education program to promote the prevention and treatment of heart, lung, and blood diseases and enhance the health of all individuals so that they can live a longer and more fulfilling lives.” ( The epidemiology program should be based on this NHLBI Mission Statement.

    The rationale for changing the direction of the epidemiology program seems to be based on 3 factors:

    1) The decreasing availability of funding for research at NHLBI;

    2) Very large sample size genetic studies (GWAS) that have supported lack of importance of population sampling, i.e. selection biases, and lesser importance of measures of agent, lifestyles and environment; and

    3) Important advances in understanding the epidemiology and prevention and improved treatment of cardiovascular disease (CVD), which has resulted over time in a remarkable decline in coronary heart disease (CHD) and CVD morbidity and mortality in the United States and other countries and question the need for further longitudinal studies to find “new” risk factors.

    There are 5 important observations:

    1) The age of onset of incident CHD and stroke is getting older. This is especially true among women where first heart attacks may now be occurring in ages 70+;

    2) Very large variations in CHD incidence and mortality exist, both in relation to geography, within states and even within large cities and counties, and by education, SES and ethnic variables in spite of the substantial reduction in the incidence and mortality due to CHD. The continued failure to reduce these disparities is unacceptable;

    3) The incidence and mortality in the United States from CHD has declined. Rates in the United States are still far higher than in many industrialized countries. For example, the incidence and mortality from CHD is 1/3-1/4 in Japan or in France, age-adjusted, especially excluding the oldest age groups, than it is in the United States. This difference in incidence and mortality remains unexplained and is not primarily genetic, i.e. migrant studies, or due to differences in traditional risk factors only. Identification of such factor(s) that account for these differences would have the greatest single impact on CHD morbidity and mortality in the United States;

    4) The incubation period, i.e. the development to clinical CHD, evolves over a long period of time probably beginning in childhood Risk factors early in life are the primary determinants of the subsequent development of clinical CVD. Furthermore, this long incubation period is clinically silent but can now be identified through a variety of technologies that measure extent of atherosclerosis, inflammation and subclinical myocardial injury; and

    5) Identification of individual as opposed to population risk and specific individualized prevention and treatment strategies, i.e. personalized medicine is more difficult than population or group risk classification by traditional epidemiology.

    CHD and stroke are preventable diseases at the population level. They are examples of common source epidemics primarily due to dietary factors. The continued high morbidity and mortality and cost of CVD are primarily to the failure to implement what we know of successful preventative strategies. If the population level of apolipoprotein-B (ApoB) or low density lipoprotein cholesterol (LDL-C) or LDL particles was reduced to 70 mg% or <1000 particles, if the smoking rate was <10% in adults and if systolic blood pressure (SBP) was reduced to <110 or 120 mmHg throughout life and if individuals remained “fit”, the population risk of CHD and stroke would be much lower. This obviously will not happen without very dramatic changes in lifestyles or much wider use of drug therapies.

    A major goal of the NHLBI should be to test strategies, especially in young and middle aged individuals to increase both the number of individuals at very low risk. A good example is the era prior to and after vaccine for poliomyelitis. We must be very careful not to spend resources to develop better “respirators” in an era when we had very effective poliomyelitis vaccine, i.e. the Salk vaccine. We learned during those days that although there were still many people who needed better care for their polio, the big winner was the development of better vaccines and broad utilization of such vaccines across the world to eliminate almost all poliomyelitis.

    CVD today is in a similar situation. Understanding better ways to prevent the underlying atherosclerotic disease progression and acute precipitants of clinical disease, i.e. thrombosis and plaque changes, inflammation, etc., must be the highest priority for the epidemiology program at the NHLBI and not tinkering with numerous ways of trying to slightly modify case fatality and end stage disease. These areas obviously remain important especially for people who already have clinical CVD and advance atherosclerosis but they cannot be the primary purview of a successful epidemiology and prevention program.

    Over the many years in which I have been involved in CV research, almost 50 years, the successful evolution of the epidemiology and prevention program has depended on careful review of the state-of-the-art over time that have resulted in successful initiatives including both longitudinal epidemiological studies and clinical trials to better enhance the understanding of etiology and prevention of CVD. The key was to generate new hypotheses built on previous research and then develop study designs to answer critical questions.

    Numerous epidemiological studies have clearly documented the key risk factors for atherosclerosis and CVD. Epidemiology studies, especially longitudinal studies beginning with the Framingham studies, as well as the basic sciences and animal research have been remarkably successful over the past 50-60 years in establishing unequivocally that: 1) atherosclerosis is the primary determinant of heart attacks, myocardial infarction, angina or sudden CHD deaths; 2) elevated levels of ApoB lipoproteins are the primary determinants of atherosclerosis; and 3) that cigarette smoking, elevated BP, diabetes and several other risk factors, i.e. exercise, are important in determining progression of atherosclerosis and also in the conversion of atherosclerosis to clinical endpoints, i.e. heart attacks, etc.

    Epidemiological and experimental studies have clearly demonstrated that the dietary intake of specific chain-length saturated fats, polyunsaturated fats are the key determinants of the elevation of ApoB levels at both the population level and, to a lesser degree, at the individual level. Furthermore, there are extremely important genetic and other lifestyle factors that affect the response to the specific diet in relationship to the development of atherosclerosis. There is a need to reestablish good nutrition experimental studies in humans that link genetic, i.e. host susceptibility, biochemical measures, metabolomics, proteomics, etc. and measurement of atherosclerosis, thrombosis and clotting. The traditional large diet observational studies are very unlikely to add much new data. New technologies applied to nutrition studies, i.e. energy metabolism, should be a mainstay of future NHLBI epidemiology program, especially in unique populations with different CHD,CVD incidence.

    Many large epidemiological and clinical studies have successfully developed technologies now to measure the extent of atherosclerosis and to study the associations of the extent of atherosclerotic disease and clinical outcomes, such as MI, sudden CHD death or myocardial pathology. These studies began in the 1960s with the development of coronary angiography (see papers by Kuller, Humphries, Conti, Freisinger, etc), the use of fluoroscopy to measure calcification in the arteries and ultimately the measurement of coronary artery calcium (CAC) first by electron beam computed tomography (EBCT) and more recently by fast CT and magnetic resonance imaging (MRI). All of these approaches have been extremely valuable in documenting the extent of atherosclerosis at the individual and population level and provides the unique opportunity of enhancing individualized measurement of risk. At the same time, basic pathology studies established unequivocally that there were extensive variations in the extent of coronary atherosclerosis consistent with epidemiological studies which documented marked variations in CHD incidence and mortality and, most important, that these variations were directly related primarily to dietary and the other risk factors mentioned and that both within- and among-populations the extent of atherosclerosis was strongly related to the levels of these biological risk factors, especially ApoB lipoproteins, BP, smoking, diabetes, etc. Similarly, migrant studies clearly document that these differences were not due to genetics or host susceptibility. The migrants quickly adopted the rates of disease and pathology of the host country.

    Our studies in the 1970s supported by the NHLBI of sudden and unexpected deaths in the community and documented that even young and middle aged individuals who died suddenly and unexpectedly from the first heart attack without any history of CVD or minimal symptomatology still had extensive coronary atherosclerosis, evidence of thrombosis, rupture and hemorrhages in plaques and, most important, evidence of prior healed MI and evidence of left ventricular hypertrophy, especially among blacks. Similarly, pathology studies done by investigators in Washington, DC have shown that healed thrombi and plaque hemorrhages were very frequent on postmortem examination even among individuals who did not die suddenly from CHD, suggesting that severe atherosclerosis evolves over time with a long incubation period, that there is damage to the myocardium and evidence of LVH and that there is recurrent thrombosis and hemorrhages in the plaques that over time can lead to heart attacks and sudden deaths. Studies of epidemiology and pathology of sudden cardiac deaths in younger and middle aged individuals can provide a cost effective method of monitoring trends, genetics and risk factors, i.e. PDAY study, sudden death consortium studies in 1970!

    Further epidemiological studies over the years have convincingly showed that measures of myocardial ischemia and damage are strong predictors of clinical CHD beginning with studies of nonspecific or ischemic changes on resting electrocardiograms to a variety of different types of exercise stress tests, including maximum oxygen consumption, even asymptomatic individuals and, more recently, to measures of high sensitivity troponin (hs-TNT), aminoterminal pro-brain natriuretic peptide (NT-proBNP) and better measures of electrocardiographic abnormalities, echocardiograms, MRI of the heart, etc., identification of arrhythmias, all of which are measuring myocardial damage, effects on the electrical system of the heart leading ultimately to clinical diseases, including heart failure, atrial fibrillation, angina pectoris, MI, etc.

    Studies of atherosclerotic disease have further documented that inflammation plays a critical role in the evolution of the atherosclerotic disease and the instability of the plaques leading to hemorrhage, rupture, erosion of the plaques, etc. The hope that measures of inflammation and plaque characteristics and risk of thrombosis would lead to better individualized and short term prediction of the risk of MI or sudden death has not been successful and remains an extremely important area for epidemiological research. However, such research must be done in the context of the extent of atherosclerotic disease and by very careful measurements in vivo of inflammation, plaque clotting and thrombosis. It is likely that clinical trials with specific drug therapies may ultimately be the key to successfully understanding the interrelationship of inflammation, thrombosis and clotting an acute precipitation of CV events.

    Careful consideration should be given in future epidemiological studies to focus on novel ways of understanding the interrelationship of atherosclerosis, inflammation, clotting, thrombosis and potential therapeutic approaches not in secondary but in primary prevention. The one successful effort done many years ago by Tom Meade with low dose anticoagulation therapy in the prevention of heart attacks may need now to be replicated with the new drug therapies available as well as perhaps expansion of efforts to evaluate anti-inflammatory drugs in reduction in the risk of CHD as well as the natural experiments of high risks of CHD among individuals with various inflammatory disorders, including HIV, rheumatoid arthritis, lupus, psoriasis and inflammation associated with aging. Furthermore, the effects of infectious diseases on both innate and adaptive immunity and CVD, especially in high risk populations, needs to be further evaluated.

    It is surprising that after many years of research, we still cannot predict at what particular moment or within a reasonably short period of time an individual is going to have a heart attack or a stroke. None of our current techniques, in spite of many years of research, have been able to identify this precipitant of an acute event. Much epidemiological research has shown that air pollution, especially fine particulate air pollution, measures of infection, such as pneumonia and influenza, psychosocial stressors, unusual physical activity, time of day, such as morning, day of the week, such as Mondays, seem to have some role in the precipitation of heart attack but the effects are so small at the individual level as to be of little value. Their primary value is at the population level by modifying air pollution, etc. There are excellent models for further evaluating infectious agents, such as the risk of CHD, CVD after pneumonia, influenza, etc. and their relationship to increased risk of thrombosis, clotting and heart attacks, further studies of psychosocial stressors, etc. and clearly there are unique genetic attributes which increase the risk of an event given the same extent of atherosclerosis and environmental risk factors.
    It is extraordinarily unlikely that continuing to measure large numbers of cytokines, CRP, IL6, white blood cell count etc, all of which are related to CHD, is going to enhance the study of inflammation, clotting, thrombosis and precipitation of heart attack or the role of inflammation and the progression of atherosclerosis. Rather, new studies using “deep phenotyping” are the approach, not very large nondescript studies.

    Similarly, epidemiological studies have clearly documented that stroke in the United States at least is a combination of arteriosclerotic and atherosclerotic disease with the primary risk factor being elevated BP. Much of the confusion in clinical epidemiology and clinical trials has been the failure to recognize the differences between atherosclerosis and arteriosclerosis. Elevated BP primarily drives small vessel arteriosclerotic disease in the brain, i.e. stroke, white matter abnormalities and dementia, and in the kidney, i.e. renal failure. New technologies have greatly expanded our understanding of the determinants of elevated BP control and peripheral pressure, vascular stiffness and blood flow characteristics.

    Recent research has also suggested that there are very important unique populations at “high risk” for CVD. First, and perhaps highest priority, should be further studies of the relationship of CV risk factors to pregnancy outcome and the effects of pregnancy on CV risk factors, especially important interrelationships between hypertension, obesity, lipid abnormalities, prematurity, preeclampsia, and risk factors during pregnancy may substantially increase the risk of subsequent CVD in women as well as risks in the offspring. Prevention of elevated CVD risk factors may have a major impact on reducing prematurity, low birth weight, preeclampsia, etc. There are a variety of natural experiments, i.e. unique diseases which cause substantial increases or epidemics of CVD, including HIV and autoimmune diseases. These diseases have well-documented abnormalities of innate and adaptive immunity and specific drug therapies that may lead to testable hypotheses related to inflammation and CHD.

    Third, CVD and aging must be a key priority. The older age of patients with CVD will require a major change to our approaches to prevention as well as treatment of CVD. Older patients with CVD also have very high risk of heart failure, atrial fibrillation, increased risk of stroke, and especially evolving risk of hemorrhagic stroke which may be related to amyloid angiopathy with and without hypertension. The development of new technologies opens up the potential interaction between CVD and both vascular dementia and Alzheimer’s disease (AD) and whether reduction of CV risk, especially treatment of hypertension and prevention of vascular disease in the brain, can reduce risk of brain vascular diseases and dementia, whether modifying lipoproteins will reduce risk of amyloid deposition in the brain, whether drug therapies for CVD may have adverse effects on the brain or benefits in older individuals. The relationship of atrial fibrillation to subclinical brain vascular disease, i.e. white matter disease, infarcts, may also be an important research focus. The interrelationship between frailty, sarcopenia and CVD and especially with heart failure (HF) may be another important topic. Studies such as SHEP have shown that most HF is preventable. Hypertension and CHD account for most HF, i.e. end stage disease. There may be a unique HF of aging possibly with specific mitochondrial abnormalities seen in peripheral muscle disease (sarcopenia) in older individuals. Unique dietary factors may also impact much of HF in the elderly but clearly prevention of hypertensive disease and myocardial damage secondary to atherosclerosis will have, by far, the biggest impact on most types of HF.

    Exercise, especially walking, may reduce risk of dementia, disease and CVD, especially among the elderly. An interesting hypothesis is that only types of exercise enjoyable to the individual are beneficial. It is unclear whether exercise or social networks and support related to exercise is beneficial or whether exercise without modifying “fitness” will reduce incidence or mortality due to CVD. Adherence to long term exercise programs is poor. Clinical trials that documented independent benefit of exercise on CHD, CVD incidence or dementia are lacking, especially in “healthy” and for primary prevention. The interrelationship between changes immune function with aging and precipitation of CV events through inflammation and thrombosis is now testable because of new technologies.

    Epidemiological advances depend on identifying epidemics in time, place and person, designing appropriate studies to test specific hypotheses and inclusion of new technologies that enhance both measurement of host, age, environment and outcomes. One-size-fits-all shoe box designs cannot drive successful epidemiological studies.

    Epidemiology does not advance by very large nondescript studies without hypotheses. Their potential for contributing to epidemiological research is practically nil. Even though their initial cost may be low, the overall cost will be extremely high because they will provide little useful information. Ancel Keys identified the association of dietary factors with both cholesterol levels studying 57 Japanese coal miners; probably one of the first and most successful GWAS studies that had only a few hundred patients, the study of macular degeneration; studies of sudden cardiac death done by the NHLBI in the 1960s-1970s involved relatively small samples but extremely well-defined populations and very deep phenotyping of sudden cardiac death.

    There is obviously a place for very large studies in evaluation of host susceptibility, i.e. genetics, i.e. epi-genetics, and their interrelationship with environment and in quantifying low rates of disease and possibly in program evaluations. There are problems with attempting to use available administrative data bases. These include the well known Berksonian bias in which two diseases or events appear to be related to each other primarily because one is ascertained in relationship to the other, i.e. patients with CAD are very likely to be carefully tested to see whether they have diabetes and therefore there will be more diabetes among patients with CAD or obese individuals are likely to be tested more carefully for their BP, blood lipid and blood glucose levels, etc., different diagnostic tests are a function of geography, patient preference, etc.

    The key to a successful future epidemiology program at NHLBI is:

    1) to identify the important questions that can be answered by epidemiological studies and clinical trials and the types of populations that will best resolve these questions;

    2) to develop innovative strategies for testing specific hypotheses; and

    3) making certain that modern technology, whether it be molecular biology, genetics, deep phenotyping, cellular biology, etc., and population epidemiology studies are carefully linked to provide answers to important questions; and

    4) the goal of the NHLBI is to reduce morbidity and mortality and especially disparities in the population and not just continue to replicate studies or studies which have only a marginal increase in the knowledge base and little effects on prevention or improved treatment of CVD.

    More efficiency in studies will reduce costs. Reduction in costs of technology, laboratory specimens, acquisition and testing, very high-priced personnel, overhead and reporting requirements may have the biggest impact on reducing costs. Better collaboration with Medicare to reduce costs in studies of the elderly and with other insurance providers under age 65 will be important in the future. Collaboration with the FDA to link better evaluations of technology and new drug therapies to NHLBI research may also enhance research studies.

    Much greater collaborations across the NIH institutes and with other federal agencies, CDC, Department of Agriculture, etc. can also greatly improve resources.

    The NIH extramural research program must be both driven and evaluated by the large extramural research community with the primary goal of enhancing the mission statement of the NHLBI. The success of that mission in reducing morbidity and mortality will, in the long run, have the biggest impact on further public and government supporting and funding opportunities.

    CHD and stroke are preventable diseases and the primary aim should be to drive the incidence and mortality rates to levels in countries like France and Japan or in areas of the United States where the rates are 1/3-1/4 of what they are across most of the United States.

  4. Sylvia Wassertheil-S,, permalink
    August 22, 2013 3:53 pm

    One area insufficiently studied is the brain-heart connection, including both the biological mechanisms as well as the psychosocial aspects of that connection. for example we do not completely understand the underlying pathways behind stress and myocardial infarction, or the neurogenic aspects of obesity. Yet the domains of neurology, cardiology and psychiatry seem like separate silos in the epidemiological research community. A suggestion is to embark on collaborative, focuse research spanning these areas. Sylvia Wassertheil-Smoller

  5. NHLBI Moderator permalink*
    August 23, 2013 9:10 am

    We continue to encourage comments on the post: “Transformation is in the air”. Above there are challenging and stimulating comments on new directions. Please add your thoughts.

  6. Mercedes Carnethon permalink
    August 28, 2013 4:32 pm

    The future of epidemiology is best served by expanding in new directions through the use of new technologies, while remaining committed to the research that has yielded a large number of insights into the development of cardiovascular disease in the population. What we have learned from the traditional cohort studies (e.g., CARDIA, ARIC, CHS, JHS, Framingham, MESA) cannot be replicated using existing data frameworks. For example, electronic health records do not include standardized measurements obtained across all people in a population sample, regardless of perceived clinical need. Administrative databases are mostly designed for administration (such as billing) and typically do not provide definite information on the medical diagnoses to which they pertain. Therefore, to continue investigating the multifactorial causes of cardiovascular disease, we must find a way to continue the long term cohort studies. The existing large cohort studies can be augmented with new cohort studies; this is an important step to take to remain current in knowledge generation, but the long history of the existing studies is “information in the bank” which has taken time to accumulate. There is no denying that cohort studies that are formed around patients whose clinical data and health history are available from an electronic health record (EHR) are financially efficient and well-suited to address many of the research questions as described in other posts. However, EHRs cannot be used to answer questions about factors that are not captured within a standard clinical encounter including:

    1. The contribution of health behaviors on disease development
    2. The relationship between subclinical and clinical disease
    3. The myriad economic, social and psychological processes that contribute to health behaviors and disease.
    4. Race and ethnic disparities in health behaviors and cardiovascular disease outcomes

    While each of the large NHLBI-funded cohort studies has answered questions relevant to each of these areas, we cite a handful of examples from the CARDIA study (disclosure: we are both funded CARDIA investigators) that made seminal contributions that would not have been possible without the examinations and participant follow-up that characterizes a “traditional cohort study”.

    1. Diet behaviors are notoriously poorly ascertained in a clinical encounter. CARDIA investigators have published numerous papers on the contribution of diet to risk factor development, including a paper demonstrating that higher intake of dietary fiber are associated with less weight gain over 10 years and a lower probability of developing cardiovascular disease risk factors (Ludwig DS, JAMA 1999; 282: 1539). Think back to your last personal clinical encounter, did your physician spend 30+ minutes asking detailed questions about your diet in order to identify sources of dietary fiber? A structured interview to ascertain health behaviors in a standard fashion is required to provide knowledge about these important issues.
    2. Given what is known from other epidemiologic studies (i.e., MESA) on the association of coronary artery calcification with subsequent coronary heart disease, Cay Loria’s 2007 paper published in JACC (Vol 49: 2013-2020) demonstrating the association of early adulthood cardiovascular disease risk factors with prevalent CAC provides the empirical data linking young adulthood behaviors and clinical profiles with a risk factor for later CHD.
    3. The implications of findings by Wang and colleagues on the contribution of incarceration to the development of hypertension and LV hypertrophy (Arch Intern Med 2009; 169: 687-93) are relevant to large segments of the US population who are transitioning in and out of the penal system. By carrying out this analysis within a cohort study, the authors were able to adjust for a host of relevant confounders and thus isolate the high-risk exposure that incarceration presents. Data from studies such as these can be used by policy-makers in the penal system to support the need for preventive healthcare, proper diets and activity opportunities among inmates.
    4. The NHLBI has demonstrated that the reduction of health disparities is a high priority by establishing and sustaining cohorts characterized by racial/ethnic diversity. CARDIA has leveraged this diversity to test hypotheses about the differential disease experience of blacks and whites. In 2009, Bibbins-Domingo and colleagues published findings on the predictors of incident heart failure in black and white young adults in the New England Journal of Medicine (Vol 160, pages 1179-90). Their findings highlighted a significant racial disparity in a devastating chronic condition, whose prevalence–unlike other cardiovascular diseases, is going up over time.

    In summary, we highlight only a handful of the contributions that the CARDIA study has made in enhancing our understanding the complex and multifactorial contributors to cardiovascular disease incidence and progression. The investment that the NHLBI has made towards supporting CARDIA and other cohort studies is best maximized if these studies continue to collect comprehensive data on health behaviors, social, psychological and economic factors, novel biomarkers and cardiovascular imaging over time. Doing so will not only advance the agenda of the NHLBI, but these longitudinal studies will continue to be a serve as a resource for new and established investigators who wish to answer new questions using the data that are already collected.

    Mercedes Carnethon and David Jacobs

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