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PERSPECTIVE

Understanding Nutritional Epidemiology and Its Role in Policy1,2

Ambika Satija,3,4 Edward Yu,3 Walter C Willett,3–5 and Frank B Hu3–5* 3Department of Nutrition and 4Department of Epidemiology, Harvard School of Public Health, Boston, MA; and 5Channing Division of Network Medicine, Brigham and Women’s Hospital, Boston, MA

ABSTRACT

Nutritional epidemiology has recently been criticized on several fronts, including the inability to measure diet accurately, and for its reliance

on observational studies to address etiologic questions. In addition, several recent meta-analyses with serious methodologic flaws have arrived

at erroneous or misleading conclusions, reigniting controversy over formerly settled debates. All of this has raised questions regarding the

ability of nutritional epidemiologic studies to inform policy. These criticisms, to a large degree, stem from a misunderstanding of the

methodologic issues of the field and the inappropriate use of the drug trial paradigm in nutrition research. The exposure of interest in

nutritional epidemiology is human diet, which is a complex system of interacting components that cumulatively affect health. Consequently,

nutritional epidemiology constantly faces a unique set of challenges and continually develops specific methodologies to address these.

Misunderstanding these issues can lead to the nonconstructive and sometimes naive criticisms we see today. This article aims to clarify common

misunderstandings of nutritional epidemiology, address challenges to the field, and discuss the utility of nutritional science in guiding policy

by focusing on 5 broad questions commonly asked of the field. Adv Nutr 2015;6:5–18.

Keywords: dietary assessment, food policy, meta-analysis, nutritional epidemiology, randomized controlled trials, prospective cohort studies

Introduction Epidemiology has long had its share of skeptics, with Taubes’ 1995 article being the most well-known (1). However, more recent commentaries have attacked nutritional epidemiol- ogy on several fronts. Ioannidis (2) criticizes the observa- tional nature of epidemiologic studies and small trials, stating that “definitive solutions won’t come from another million observational papers or small randomized trials.” He refers to an article by Archer et al. (3), which calls into question the validity of data from the NHANES and suggests that “the ability to estimate population trends in caloric intake and generate empirically supported public policy rel- evant to diet-health relations from US nutritional sur- veillance is extremely limited.” Furthermore, questionably designed and executed meta-analyses have disseminated conflicting messages about nutrition and health, such as the conclusion that being overweight lowers the risk of all- cause mortality (4) and that replacing saturated fat with polyunsaturated fats has no substantial impact on cardiovas- cular risk (5). Such conclusions are not only confusing but

also dangerous because they can be perceived as misleading messages, or can lead to the communication of misleading messages to the public by popular media and the consequent adoption of unhealthy practices by the population at large. For instance, after the publication of the latter meta-analysis, New York Times columnist Mark Bittman told his readers that they “can go back to eating butter” (6).

Many authors have suggested that large randomized con- trolled trials (RCTs)6 are the only solution to circumventing the problems in observational research. In reality, RCTs are far from being the panacea in the study of diet and chronic disease, and the results of such trials can be misleading. A key reason is that the exposure of interest in nutritional epidemiology—dietary intake—is complex, with interac- tions and synergies across different dietary components, which can be difficult to study with use of a linear drug trial approach. A complex behavioral exposure such as diet also makes other aspects important in pharmacologic RCTs, such as high compliance and blinding, difficult and infea- sible in most dietary intervention trials. Consequently,

1 Supported by NIH grants HL60712, DK58845, P30 DK46200, and U54CA155626.

2 Author disclosures: A Satija, E Yu, WC Willett, and FB Hu, no conflicts of interest.

* To whom correspondence should be addressed. E-mail: nhbfh@channing.harvard.edu.

6 Abbreviations used: CVD, cardiovascular disease; DLW, doubly labeled water; IHD, ischemic

heart disease; NTD, neural tube defect; RCT, randomized controlled trial; SSB,

sugar-sweetened beverage; TFA, trans FA; WHI, Women’s Health Initiative.

ã2015 American Society for Nutrition. Adv. Nutr. 6: 5–18, 2015; doi:10.3945/an.114.007492. 5

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nutritional epidemiology has design and analysis issues unique to the field, and understanding the details of nutri- tional epidemiologic studies requires a deep knowledge of nutritional science and its methodologic background.

The purpose of this article is to clarify common misun- derstandings of nutritional epidemiology, address the chal- lenges to the field, and discuss the utility of nutritional science in guiding policy. In particular, we address 5 broad questions that have been commonly raised about nutritional epidemiologic studies.

Can We Reliably Measure Dietary Intakes in Individuals and Populations? Measuring diet in free-living populations is challenging be- cause individual diets are complex exposures with innumer- able and sometimes poorly characterized components that are consumed in varying amounts and combinations by dif- ferent individuals. Dietary variables are rarely dichotomous; often, but not always, the entire population is “exposed” to some degree. Diet is also a time-varying exposure, with in- dividual dietary habits and food composition changing over time. It is not surprising, then, that most dietary assess- ment methods have a component of error, which could be random day-to-day, diurnal, and seasonal variation in an in- dividual’s diet over time, or because of systematic mecha- nisms, such as omission of foods when collecting data. Nonetheless, several techniques have been developed to as- certain dietary intake from free-living populations, and these methods have shown good validity with use of multi- ple criteria. Although each assessment method comes with its own set of limitations, strengths unique to each method make it appropriate for use in specific applications (7–10).

Multiple-week diet records, which require participants to record everything they eat or drink over the course of several weeks, are regarded as the gold standard for ascertaining di- etary information because, unlike other methods, they do not rely on memory. The high participant burden and cost of keeping diet records has limited their use in large-scale epidemiologic studies; however, their ability to accurately ascertain detailed dietary information makes them useful in validation studies of other diet assessment methods, and in monitoring compliance in trials. Another limitation of diet records is that the process of recording can change an individual’s diet, rendering the data atypical of usual in- take, although estimated intakes from diet records have been found to correlate reasonably well with those from multiple 24-h recalls (11). Repeated 24-h recalls involve a respondent reporting all foods consumed in the previous 24 h or calen- dar day to a trained interviewer in person or over the phone. Although reliance on the participant’s memory leaves room for measurement error, a skilled interviewer can produce highly detailed and useful nutritional data comparable to a diet record (11, 12). This method has been widely employed in dietary intervention trials. It is also used in national sur- veys to monitor trends in nutritional intake.

A potential source of error common to these methods is in the estimation of nutrients with use of food composition

tables. The nutrient content of a food varies with season, lo- cation of production, growing conditions, storage, process- ing, and cooking techniques, and many of these factors are unaccounted for in food composition tables. The degree to which this is problematic differs from nutrient to nutrient. Although for some nutrients, such as dietary FAs, it is rea- sonable to assume that these variations do not substantially affect calculated intakes, for others, such as selenium, the variation can result in calculated intakes that are substan- tially different from true intakes (7). In general, however, this source of error does not substantially compromise the ability to rank individuals with respect to nutrient intake so as to evaluate associations with health outcomes (7, 13). Nevertheless, estimating nutrient composition from food intake data is a challenge, especially given the changing food landscape, and it is crucial that we continue to improve the accuracy of food composition databases.

When participants provide biological specimens, re- searchers can additionally measure intake by assaying bio- markers. Examples of biomarkers include doubly labeled water (DLW) (for total energy intake), urinary nitrogen (for protein intake), 24-h urinary sodium and potassium, blood lipid profiles, serum and plasma folate, and selenium and other trace minerals in toenails. Biomarkers allow for objective measurement of intake without any bias because of self-reporting. The limitations of biomarkers, however, have prevented their wider use. In particular, many foods and nutrients lack sensitive or specific biomarkers, their assessment always includes error from multiple sources, they may not be indicators of individual long-term intake, and obtaining and testing for biomarkers is expensive and burdensome. Thus, use of biomarkers to investigate nutrient- disease relations has been mostly confined to nested case- control studies and small trials. Biomarkers are also useful in assessing the validity of less-expensive, self-reported as- sessments of diet, such as FFQs.

An FFQ consists of a structured food list and a frequency response section on which the participant indicates his/her usual frequency of intake of each food over a certain period of time in the past, usually 1 y. This is the most common choice for measuring intake in large observational studies owing to its ease of use, low participant burden, and ability to capture usual long-term dietary intake. These features make possible repeated assessments over time, which is im- portant to capture longer term variation in diets. Table 1 presents a comparative summary of the advantages, disad- vantages, and applications of these dietary assessment methods.

Thus, a collection of diverse diet assessment methods is available; their appropriate application, alone or in combi- nation, allows for a reasonably comprehensive assessment of the diet of free-living populations. Nevertheless, recent critiques of these dietary assessment methods have called into question their utility in examining diet-disease relations and informing policy. A recent example is the article by Ar- cher et al. (3), which criticizes the use of 24-h dietary recall data periodically collected in the NHANES. Archer et al.

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compared reported energy intake as assessed by the 24-h re- calls with expected basal metabolic rate and concluded that recalled energy intake data were implausibly low and recom- mended that NHANES data be eliminated in considering public policy. This finding represents the danger of misun- derstanding methodologic issues and making inferences with use of faulty logic. A recent article by Hébert et al. (13) comprehensively refutes the conclusions drawn from this study. The following section discusses key points from this article while providing an overview of measurement er- ror assessment and correction in nutritional epidemiology.

Nutritional epidemiology has advanced considerably over the last 50 y with respect to understanding types and sources of measurement error in dietary intake data (7, 14). An insufficient appreciation of this can lead to erroneous con- clusions like those of Archer et al. (3). Because of the con- siderable day-to-day variation in dietary intake among

individuals, a single recall, as was used by Archer et al. in their analysis, will tend to capture extremes of dietary intake as opposed to usual current intake, increasing the likelihood that any individual’s single recall will be implausibly high or low. This random variation adds noise to the data, overesti- mating the variance, and flattening the distribution, thereby increasing the numbers of individuals in the extremes of the distribution. Thus, repeated 24-h recalls on nonconsecutive days are recommended to reduce within-person error. More epidemiologic studies that use 24-h recalls to assess diet now obtain multiple replicate measures on each participant, and starting in 2002, a second 24-h recall was introduced in the NHANES to address some of these issues (8).

However, as noted earlier, error in diet assessment need not be completely random. Systematic sources of variation include omission of foods consumed by individuals, errors in estimating portion sizes, and over- or under-reporting

TABLE 1 Comparison of diet assessment methods

Several day/week diet records Multiple 24-h recalls A single 24-h recall Validated FFQ Biomarkers

Advantages Provides accurate, de- tailed, open-ended data on dietary in- take, with no reliance on memory, and di- rect computation of portion sizes.

Provides fairly accurate, detailed, open- ended data on die- tary intake, without reliance on long- term memory.

Provides detailed, open-ended data on dietary intake, with- out reliance on long- term memory.

Provides time-inte- grated data that rep- resents usual long- term intake. Can as- sess past dietary intake.

Provides an objective assessment of intake. Represents bioavail- able dose, which is relevant when it is used in etiologic analyses.

Errors from omission, portion size estima- tion, and recall are least likely.

Has lower respondent burden and is less expensive than diet records, and works well in low-literacy contexts.

Has lower respondent burden and is less expensive than diet records and multiple recalls; works in low- literacy contexts.

The least expensive and most easily adminis- tered diet assess- ment method, with the lowest respon- dent burden.

May be available in ret- rospect (analysis of stored specimens).

Disadvantages Needs literate, moti- vated participants; participant burden is very high when done over several days. Could also alter usual eating habits.

There is scope for short- term recall error, omissions, and errors in portion size estimation.

There is scope for short- term recall error, omissions, and errors in portion size esti- mation. Has high random within-per- son error.

There is scope for long- term recall error. Omissions possible because of fixed- food list. FFQs need to be cul- ture- and population- specific.

Biomarker may not be sensitive to intake, may have low speci- ficity, may not be time-integrated, may not represent usual long-term intake, and is subject to labora- tory errors and other sources of bias.

Expensive and re- source-intensive diet assessment method.

Potential for errors in nutrient estimation from food composi- tion tables.

Has high interviewer burden and is more expensive than a single recall and FFQs.

Potential for errors in nutrient estimation from food composi- tion tables.

Has high interviewer burden and is more expensive than FFQs.

Potential for errors in nutrient estimation from food composi- tion tables.

Semi-quantitative. Potential for errors in nutrient estimation from food composi- tion tables.

Expensive and more in- vasive. Biomarkers are not available for many nutrients.

Applications Validation of other diet assessment methods.

Validation of other diet assessment methods.

National surveillance of mean population intake.

Association analyses in large epidemiologic studies.

Validation of other diet assessment methods.

Monitoring compliance in dietary interven- tion trials.

Monitoring compliance in dietary interven- tion trials. Assessment of trends in dietary intake (current NHANES).

Assessment of trends in dietary intake (earlier NHANES).

Assessing past dietary intake.

Association analyses in epidemiologic stud- ies and monitoring compliance in inter- vention trials

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because of social approval (respond in certain ways to get so- cial praise) or social desirability (respond in certain ways avoid social criticism) (15–17). All of these could have led to the under-reporting of energy intake observed by Archer et al. The underestimation of energy intake from self- reported data has long been known to nutrition researchers, and many strides in methodology have been made to reduce this source of measurement error (7, 18–22). Under-reporting because of omission or portion size estimation errors is un- likely to be differential with respect to determinants of the outcome of interest. In addition, there have been improve- ments in 24-h recall methodology that reduce these sources of error, such as the USDA 5-pass method (8), which is structured to minimize omission of foods and to help partic- ipants report accurate portion sizes by using visual aids. This 5-pass method, which was introduced into the NHANES starting in 2002, was found to agree reasonably well with ac- tual intake assessed by direct observation (r = 0.57, P < 0.05) (23), as well as with energy intake as assessed by the DLW technique (r = 0.32 for males; r = 0.25 for females), which is considered the gold standard for energy intake assessment (provided body compartment masses such as fat mass and water mass are stable over time because DLW is a measure of energy expenditure), although the DLW technique has er- rors of its own (8). Another solution is to use an isocaloric statistical model in analysis, i.e., adjust for total energy in- take. In analytic epidemiology we are generally less inter- ested in the association of absolute energy/macronutrient intake with health outcomes, and more with how dietary composition relates to risk of disease because this is what is most modifiable by individuals or populations. Hence, ad- justing for energy intake is standard practice in nutritional epidemiology. Adjusting for energy intake also diminishes extraneous sources of variation in dietary intake, and to some extent also reduces systematic sources of under- and over-reporting (7, 21, 22). Issues related to measurement error are not isolated to dietary assessment methods, but extend to assessment of most behavioral exposures and bio- markers, including physical activity (24, 25), with which Ar- cher and colleagues, having worked considerably in the area of physical activity epidemiology, are familiar (26, 27).

Hence, although there is no perfect method, there is am- ple evidence that dietary measurements in national surveys have reasonably good reliability and validity. The conclusion of Archer et al. that dietary data with use of these methods cannot support public policy is misleading. National survey data such as the NHANES represent a small fraction of the totality of evidence on the basis of which national guidelines and public policy are made. A main purpose of using na- tional survey data is to assess average population intakes and trends. For example, we recently examined trends in di- etary quality from 1999 to 2010 in the US adult population among a nationally representative sample of 29,124 adults aged 20–85 y with use of the NHANES data (28). We found that better dietary quality, measured by the Alternate Healthy Eating Index, was associated with higher socioeco- nomic status, and the gap between the rich and the poor

widened with time. These data underscore the importance of developing nutritional policies to improve diet quality and reduce health disparities.

Because of its low cost and low participant burden, self- administered computer-processed FFQs are the only option in most large cohort studies to assess usual dietary intakes. FFQs usually have lower random within-person variation than other dietary assessment methods because they are de- signed to assess average usual intake over the past year. For this reason, they are better equipped to assess long-term di- etary intake, the exposure of etiologic interest for most dis- eases (7). Because of their reliance on memory, FFQs may suffer from greater measurement error relative to recalls and records if these methods are used for many days to re- flect longer-term intakes (for certain nutrients, just a few days of diet records or recalls might be enough, provided the days are spread out over the entire reference period of the FFQ). Nevertheless, FFQs have been shown to have ac- ceptable validity when compared to reference measures (29, 30), with typical correlation coefficients for individual nutrients or foods ranging from 0.4 to 0.7 (7). Adjustment for total energy intake, along with use of repeated FFQs in long-term prospective cohort studies, further improves these validity coefficients. Although extended dietary rec- ords are the most popular reference method, when bio- markers are available, triangulation methods can be used to obtain improved estimates of correlations of FFQ intake with true intake (31). These validity coefficients can be used to correct for measurement error in epidemiologic analyses, and the application of these measurement error correction methods is increasingly being extended to more complicated analyses (18–20). These techniques have al- lowed for valid inferences to be drawn from large cohort studies with use of FFQ data.

Despite these developments in reducing measurement er- ror in dietary intake data, continued improvements in dietary assessment methodology and measurement error correction are needed to advance the field. Nevertheless, the consider- able progress made over the past few decades, especially the use of repeated measures of diet over time, has enabled nu- tritional epidemiologists to reliably collect and use dietary in- formation in both individuals and populations.

What Is the Role of Nutritional Epidemiology in Inferring Causality? One of the main criticisms leveled against nutritional epide- miology is that it relies predominantly on observational data, which is deemed to be inferior to experimental data in determining causality. Figure 1 illustrates the typical hier- archy of evidence from various study designs. While ran- domized trials with hard endpoints occupy the highest position in this hierarchy, they are usually not the most ap- propriate or feasible study design to answer nutritional epi- demiologic questions regarding long-term effects of specific foods or nutrients (unless they can be packaged in a pill).

In the absence of evidence from large RCTs on hard endpoints, nutritional epidemiologists typically rely on

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prospective cohort studies, the strongest observational study design in terms of minimizing bias and inferring causality. Being prospective in nature, they are less affected by several biases, such as reverse causation, recall bias, and selection bias, which commonly plague retrospective or cross- sectional study designs. Reverse causation describes the sit- uation in which the outcome affects the exposure, rather than the other way around. This is a common concern with cross-sectional studies and retrospective case-control studies because they assess exposure and outcome at the same time. Prospective cohort studies can minimize the pos- sibility of reverse causation by apparent disease because par- ticipants are followed forward in time, and these studies can examine the extent of reverse causation from subclinical dis- ease by lagged analyses. They are superior to retrospective case-control studies because the issues of selection bias (con- trols not being representative of the underlying population that gave rise to cases) and recall bias (knowledge of disease status affecting recall of diet) can be largely minimized be- cause prospective cohort studies begin with a disease-free population at baseline that is followed up to ascertain inci- dent cases that develop over time. This is evident from the fact that spurious links between total energy intake and co- lon cancer (32), and fats and breast cancer (33), which were reported in case-control studies, have not been replicated in large prospective cohort studies.

A major challenge when working with any kind of obser- vational data is confounding. A confounder is a variable that is associated with both the exposure and outcome but is not caused by either, and when unaccounted for, introduces bias into the exposure-disease relation. The main reason why randomized trials are considered superior in inferring cau- sality is that randomly assigning participants to treatment groups nullifies all sources of measured and unmeasured confounding, provided the sample size is large enough. To account for this type of bias in an observational study design such as a prospective cohort study, researchers must rely on their content knowledge to identify and adjust for all rele- vant confounders. Once data have been collected on these

variables, the investigator can statistically adjust for con- founders in a regression model or restrict the data to a specific subgroup to minimize residual confounding. A well-conducted cohort study can simulate a randomized trial when the most relevant confounders are accounted for (34). Sensitivity analysis further strengthens results by delineating the magnitude of unmeasured confounding needed to com- pletely neutralize an effect. Moreover, a prospective design al- lows for up-to-date tracking of confounders and diminishes the threat of residual confounding because updated informa- tion may reduce measurement error in assessment of con- founders, and additional information on confounders can be collected when needed.

Although there are several ways in which confounding can be accounted for in prospective cohort studies, the crit- ical assumption of “no unmeasured or residual confound- ing” that is needed to infer causality cannot be empirically verified in observational epidemiology (34). For this reason, prospective cohort studies are often seen as providing sta- tistical associations but not causations. This can be a dangerous premise to blindly adhere to, especially when ran- domized trials of hard endpoints are not feasible and policy decisions have to be made based on existing evidence. In this scenario, the Hill criteria, published in 1965 by Sir Austin Bradford Hill, are useful in inferring causality from observa- tional data and making timely policy decisions that could avert preventable morbidity and mortality in the population (35). In his classic paper, Hill outlined a checklist of several key conditions for establishing causality: strength, consis- tency, temporality, biological gradient (dose-response), plausibility, coherence, and experimental evidence. These criteria have been satisfied in several exposure-disease rela- tions such as sugar-sweetened beverages (SSBs) and diabetes (36), whole grains and cardiovascular disease (CVD) (37), and trans fats and CVD (38), which has resulted in timely public health action to reduce the burden of these diseases in the United States.

Given the complex nature of the human diet, another way of inferring causality is to consider different types of ex- posure (i.e., dietary patterns, foods, nutrients, and bio- markers) simultaneously (39, 40). For example, adherence to the Mediterranean-style diet has been known to confer a cardioprotective effect in observational studies and RCTs (41). Staples of the Mediterranean-style diet such as fish, nuts, olive oil, fruits, and vegetables have been individually linked to lower risk of heart disease (42–44). Reviews of ma- jor nutrients abundant in these foods, such as unsaturated fats and polyphenols, have confirmed this finding as well (45, 46), as have studies of related biomarkers (47, 48). Such a convergence among studies provides convincing sup- port for adoption of the Mediterranean-style diet in preven- tion of CVD.

In the study of nutrition and health, prospective cohort studies aren’t the only sources of data used when considering causality. Evidence from animal studies, mechanistic studies in humans, prospective cohort studies of hard endpoints, and randomized trials of intermediate outcomes are taken

FIGURE 1 Hierarchy of study designs in nutritional epidemiology. RCT, randomized controlled trial.

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together to arrive at a consensus. The inference of causal- ity is strengthened when these different types of studies provide consistent evidence. For example, a meta-analysis of randomized trials of trans fat intake has shown harm- ful effects of higher intake on intermediate endpoints, such as increased LDL cholesterol and reduced HDL cho- lesterol (49). Based on observational studies, there is a significant and robust association between higher intake of trans fat and increased risk of ischemic heart disease (IHD) (49). Taken together, these studies forge a strong case for the harmful effects of trans fat consumption on heart disease. The most important aspect of this approach is that it discourages viewing individual studies and mea- sures of association in isolation and encourages interpret- ing them in context of the larger evidence base.

Well-conducted prospective cohort studies thus can be used to infer causality with a high degree of certainty when randomized trials of hard endpoints are impractical. Researchers can minimize bias from confounding and other sources of bias by relying on high-quality study design, care- ful statistical analysis and interpretation, and replications of the findings across different populations. The Hill criteria are a useful tool for establishing causality in the absence of large RCTs on hard endpoints, and corroborating data from multiple study types and populations can enhance the weight of evidence.

Is the Drug Trial Paradigm Relevant in Investigating Diet and Disease Relationships? Some researchers consider RCTs as the be-all and end-all of causal inference (2). This sentiment may be appropriate in the pharmaceutical industry, but the drug trial paradigm cannot be readily translated for use in the nutritional sci- ences. Table 2 summarizes the differences between observa- tional prospective cohort studies and RCTs, and Table 3 outlines the differences between RCTs in pharmaceutical and nutritional research. Unlike classic drug trials, RCTs of dietary interventions typically cannot be blinded, leading to the possibility that the effect of the intervention is due to knowledge of treatment assignment as opposed to the di- etary component of the intervention. Dropout rates also tend to be higher in RCTs of nutritional interventions

relative to those in drug trials, especially if the intervention is implemented for long periods or is very demanding or both. Dietary interventions to promote weight loss routinely have dropout rates of 30–40% even after just 1 y of follow- up (50, 51). Such dropout, when substantial, will reduce an- alytical power in the presence of random loss to follow-up. However, it can also introduce systematic bias in the effect estimate, usually in unpredictable directions, if the dropout is differential with respect to treatment and outcome (52). Another problem faced to a greater extent in nutritional RCTs relative to drug trials is noncompliance, i.e., insuffi- cient adherence by participants to their assigned interven- tion. Such noncompliance may become severe in trials of longer duration. For example, over 8 y of follow-up in the Women’s Health Initiative (WHI), the most expensive hu- man study ever conducted, most of the participants ran- domly assigned to the low-fat group were unable to achieve their fat reduction target of 20% (53). Moreover, during the trial, there were no differences between the low-fat and control groups in plasma concentrations of HDL cholesterol and triglycerides, which are known to change on low-fat diets (53). The WHI, hence, failed to test its original hypothesis, and its null findings were largely uninformative with respect to the causal effect of a low-fat dietary intervention. A similar fate afflicted the earlier Mul- tiple Risk Factor Intervention Trial, in which reduction of serum cholesterol by dietary means failed to produce a sub- stantial contrast between intervention and control groups and thus no significant difference in CVD was seen (54). Randomized trials of nutritional interventions, although free from confounding and selection bias at baseline, can suffer from similar biases postbaseline that we often observe in observational studies, especially when they are of long du- ration, complicating their interpretation and diminishing their utility above prospective cohort studies. An additional issue with trials that last for extended periods of time is that they risk becoming obsolete. During the early 1990s, the WHI was set up to test the prevailing theory that reduced fat intake would decrease breast cancer and CVD risk. How- ever, during the course of the trial, clinical and epidemio- logic evidence that had accumulated to support greater importance of types of fat over total fat substantially

TABLE 2 Prospective cohort studies vs. RCTs of foods and nutrients1

Design criterion Prospective cohort study RCT

Study characteristics Size Variable, usually fairly large Usually small Follow-up time Years and decades Weeks, months, a couple of years

Dietary exposure Naturally occurring distributions Specific predefined intervention and control Endpoint Mortality, incident disease, intermediate outcomes Disease prognosis and management, intermediate outcomes Sources of bias Confounding Residual and/or unmeasured confounding possible No confounding if groups are balanced Selection bias Possible because of differential dropout Possible because of differential dropout Measurement error Possible because of error in diet assessment methods Possible because of incomplete compliance

Generalizability Potential for high generalizability Usually fairly limited Feasibility Usually more feasible Feasibility limited by costs and ethical constraints 1 RCT, randomized controlled trial.

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weakened the original rationale, especially with respect to CVD (55).

The choice of a control group can also be more compli- cated in nutritional intervention trials relative to drug trials because the latter are usually placebo-controlled, which is rarely a possibility in the former because of ethical consider- ations. Thus, the intervention and control groups are differ- entiated in terms of the dose of a nutrient (“high” vs. “low”), and the definition of these doses is also usually determined by ethical constraints. For instance, it may not be ethically feasible to give a very low dose to, or introduce deficiency in, the control group. One way of circumventing this is to conduct a trial in a naturally deficient population by provid- ing supplementation to the intervention group. Even in this instance, it is not ethically feasible to provide the control group with just a placebo, and a minimum level of supple- mentation in the control group is usually necessary. This could result in too narrow a contrast in nutrient intake be- tween the control and intervention groups, undermining the trial’s ability to identify a true effect of the nutrient.

Another factor further complicating the choice of a con- trol group is that nutrients and foods are not consumed in isolation, and decreasing the intake of one nutrient/food usually entails increasing the intake of another nutrient/ food to make up the reduction in calories in isocaloric trials (e.g., a reduction in dietary fat is often accompanied by a compensatory increase in carbohydrate intake or vice versa). Thus, the choice of comparison group can influence the ef- fect observed of a dietary intervention, further complicating the interpretation of dietary intervention trials.

The utility of the drug trial paradigm in nutritional epi- demiology is further diminished by the fact that the human diet is a complex system, not amenable to the reductionist approach of isolating individual nutrients or compounds (56). Although drugs usually target a single system/pathway in the pathology of disease, nutrients are usually pan-systemic, influencing multiple systems and affecting disease risk through multiple pathways. Unlike drugs, which are de- signed to have large and targeted effects on individual path- ways that play out in relatively short periods of time, individual nutrients usually have modest effects that interact with and aggregate across multiple nutrients and systems over long periods of time to cumulatively affect disease risk. In drug trials, other drugs with known interactions are excluded or controlled for in some manner; in nutri- tional intervention trials, synergies and antagonisms with other nutrients and drugs are usually not given adequate

consideration. High-dose vitamin and antioxidant trials mimic drug trials that examine the effect of isolated com- pounds, but these findings have been largely negative (57), which could be explained in part by the inappropriate use of the linear drug trial paradigm, which fails to take into ac- count the complex, interconnected nature of the dietary “ex- posome” (58).

Well-conducted RCTs and observational studies that an- swer similar questions tend to find consistent results (59). However, when RCTs contradict the findings of observa- tional studies, there is a tendency for the academic commu- nity to believe that RCTs conclusively refute the hypotheses generated by such observational studies. Although this is a possibility, an equally, and sometimes more likely, possibility is that the RCTand observational studies are answering very different questions. For example, an observational study might answer the question “are some persons in a popula- tion at increased risk because of low intake of nutrient X?,” whereas an RCT might answer the question “does add- ing more nutrient X to the whole population reduce risk?” In this example, the latter would not necessarily refute the former. In fields like nutritional and chronic disease epide- miology, RCTs typically cannot answer the questions that observational cohorts do answer. RCTs tend to have several exclusion criteria, and with diseases like CVD as the out- come, tend to be carried out in high-risk populations. Ob- servational studies tend to be more inclusive and hence more representative of the general population. Additionally, although observational studies can evaluate any exposure contrast that is observed, RCTs usually examine a narrow ex- posure distribution that is feasible within ethical and practi- cal constraints.

Owing to these limitations, most randomized trials are small (<200 subjects) and test for intermediate endpoints. One exception is Prevención con Dieta Mediterránea (60). In this landmark trial, the investigators tested for primary CVD events in 7447 men and women. After a median fol- low-up of 4.8 y, a Mediterranean diet was superior to a low-fat diet in reducing CVD incidence. It should be noted that the Prevención con Dieta Mediterránea was built on prior observational evidence from both ecologic and pro- spective cohort data that supported the benefits of the Med- iterranean diet. Furthermore, the investigators provided free foods to its participants to ensure high compliance, a crea- tive but often infeasible strategy in large nutritional inter- vention trials. Thus, it is important to remember that although large, well-designed RCTs are desirable when

TABLE 3 RCTs of nutrients or foods vs. drugs1

Design criterion RCTs of nutrients or foods RCTs of drugs

Exposure Complex, interacting network of foods/nutrients Individual, isolated chemical compounds Choice of control Variable, dependent on prior studies, feasibility, and ethicality Placebo Endpoint Disease prognosis and management, intermediate outcomes Clinical events, adverse events Dropout rate Moderate to high depending on length and type of intervention Low to moderate Blinding Not possible with foods and dietary patterns Easy Compliance Often decreases substantially over long period of follow-up High to moderate over follow-up 1 RCT, randomized controlled trial.

Understanding nutritional epidemiology 11

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feasible, the field of nutritional epidemiology cannot solely depend on them, especially when testing individual compo- nents of a dietary pattern. A large dietary intervention study, carried out with use of considerable funds, and over many years, tends to address only one question and only one expo- sure contrast within that question. Hence, the question that it answers needs to be carefully thought through because not examining the most etiologically relevant range of the expo- sure distribution will lead to potentially misleading results. Arriving at the right question to pose with use of an RCT needs valid observational data. The two, thus, go hand-in- hand, with their strengths and limitations complementing each other.

For these reasons, the drug trial paradigm is usually not appropriate for investigating diet and disease relations and, when attempted, can lead to misleading results. Instead, a holistic research approach is likely to be more informative (61). A reductionist view that one compound brings about one physiologic effect ignores the intricacies of physiologic interactions. Foods cannot be treated as drugs, and a broader biological perspective will be necessary to effectively address nutritional questions in the future. Finally, nutritional epi- demiology is not the only field where RCTs can be mislead- ing. Although few would now question the benefits of smoking cessation, RCTs examining this issue have found no effect on mortality, probably because of recidivism and insufficient follow-up time (62). This is sobering consider- ing that smoking is one of the most powerful risk factors known, and diet and other behaviorally related risk factors such as physical activity tend to have more subtle effects on disease outcomes.

Can We Trust the Findings from Meta-Analyses and Systematic Reviews of Nutritional Epidemiologic Studies? Systematic reviews and meta-analyses have been instrumen- tal in advancing the field and informing policy. Because meta-analyses and systematic reviews synthesize aggregate data, they are regarded by some to be the most authoritative form of available evidence (63, 64). Although they can be ex- tremely useful in summarizing relevant literature, they are not immune to limitations. Publication bias, the tendency for null findings to remain unpublished, is a common diffi- culty in such analyses, although Egger’s test (65) and trim- and-fill techniques (66) can be used to detect and correct for bias. Substantial between-study heterogeneity (e.g., dif- ferent exposures, outcomes, study populations, etc.) pre- sents another major obstacle to pooling and interpreting effect estimates, although the presence of statistical hetero- geneity does not necessarily invalidate the pooled results. Several methods have been devised to deal with this prob- lem. First, if heterogeneity (e.g., varying methods for out- come ascertainment across studies) is so severe such that a statistical synthesis of effect estimates is meaningless, then a systematic review and qualitative description of study re- sults is more appropriate. Second, one may choose to subset studies by specific characteristics (e.g., cohorts consisting

only of women and only of men) to explore sources of het- erogeneity. Third, one can use a random-effects model rather than a fixed-effects model, which assumes that re- ported effect estimates do not converge on the same value (67). However, this solution introduces another complica- tion. Random-effects models tend to give more weight to and thus exaggerate the importance of smaller studies, lead- ing to potentially distorted pooled-effect estimates and wider CIs. Lastly, a meta-analysis is only as good as the stud- ies it pools together. If the methodologic quality of included studies is low, the meta-analysis can result in a misleading pooled effect estimate. Thus, it is important to give adequate consideration to the quality of included studies and either exclude lower-quality studies from the analysis or report pooled effects separately for higher-quality studies, and dis- cuss the impact of study quality on the pooled results.

One must exercise care when interpreting a systematic re- view or meta-analysis in nutritional epidemiology. The number of systematic reviews and meta-analyses has ex- ploded in recent years. A search on PubMed for “systematic review” and “meta-analysis” retrieves 4374 hits published from 2000 to 2004, 11,597 hits from 2005 to 2009, and 21,420 hits from 2010 to 2014. The rush to fill in gaps in the literature has also led to sloppy reviews that would ben- efit from a more thorough evaluation. Furthermore, because a review does not require original data, anyone could poten- tially write one; unlike the conduct of original studies, for which the qualifications of the investigators and the research plan are carefully vetted in the funding process. Too often, articles appear to have been pushed to publication by authors who do not fully appreciate the complexity of the subject. Lack of content knowledge and insufficient under- standing of underlying biological mechanisms can lead to incomplete literature searches, flawed analytic methods, and misleading conclusions.

Some of the methodologic problems were evident in a re- cent meta-analysis of BMI and mortality, which concluded that being overweight lowers the risk of all-cause mortality than being normal weight (4). However, this finding is at least partly explained by reverse causation because individ- uals with existing or even preclinical chronic diseases such as cancer and neurodegenerative diseases often experience weight loss long before death (68, 69). Excluding sick indi- viduals (70) or deaths from the first several years of follow- up (71) yields reasonably unbiased estimates that confirm a BMI range of 22–24.9 kg/m2 as having the lowest rates of all- cause mortality. The BMI-mortality analyses were also se- verely distorted by smoking, which is strongly associated with death but lower body weight (72), and restriction of analysis to never-smokers shifts the point of lowest mortality to the normal weight range (73).

Another example is a recent meta-analysis that concluded that types of fat including saturated or polyunsaturated fats have no substantial impact on heart disease, a conclusion stemming in part from an inadequate understanding of nu- tritional epidemiologic methods (5). It has been long known in clinical nutrition and nutritional epidemiology that, when

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examining the effects of macronutrients in an isocaloric manner, one must be cognizant of which other macronutri- ent is replacing the one in question. In the example of satu- rated fat, assuming diets are isocaloric, a diet high in saturated fats must be replacing another nutrient to main- tain the same energy intake. At the population level, most of an individual’s energy is derived from carbohydrates (74, 75), which implies that those who consume high amounts of saturated fats are most likely replacing carbohy- drates. Substituting carbohydrates for saturated fats, how- ever, does not substantially alter the risk of heart disease (76). Refined carbohydrates, in particular, may be more harmful than saturated fats in terms of metabolic effects (77). However, substituting polyunsaturated fats for satu- rated fats substantially decreases the incidence of heart dis- ease (76). The conclusion, therefore, should not be that saturated fat has no impact on heart disease, but that satu- rated fat is not substantially better or worse than carbohy- drates at reducing heart disease.

Thus, although systematic reviews and meta-analyses are useful tools for summarizing a large body of evidence, it is important to recognize their limitations, give adequate con- sideration to sources of heterogeneity or bias, and consider their conclusions in the context of other relevant literature.

What Is the Role of Nutritional Epidemiologic Studies in Developing Policies? In quality rating the strength of evidence, national organiza- tions such as the American Diabetes Association, AHA, American College of Cardiology, US Preventive Services Task Force, and FDA have used well-defined grading systems to assign the weight of evidence to particular study types (78–81). Properly conducted RCTs with disease endpoints occupy the top tier of evidence in most scales, and prospec- tive cohort studies reside one level below RCTs. In the ab- sence of large RCTs with disease endpoints, evidence from prospective cohort studies in conjunction with smaller RCTs with intermediate endpoints is often considered in substantiating nutritional claims or establishing policies. For instance, the USDA/US Department of Health and Hu- man Services Dietary Guideline Advisory Committee has used evidence from prospective cohort studies extensively, in addition to evidence from RCTs, to evaluate the relations between specific dietary factors and chronic disease risk (82), which forms one of the foundations for making dietary recommendations for the US population. Three examples of epidemiologic data affecting policy change are discussed below.

Folate was first identified as an important nutrient in pre- venting neural tube defects (NTDs), such as anencephaly and spina bifida, based on observational data from the United Kingdom in the 1970s (83). Subsequent case-control studies in the 1980s suggested that women who supple- mented with folate before pregnancy had a reduced risk of giving birth to infants with NTDs than those who did not (84–87). Only 1 prospective cohort study was conducted at this time, and the results also supported a strong

protective effect of periconceptual folate supplementation (88). Observational studies examining blood folate concen- trations (89) and randomized trials of folate supplementa- tion (90, 91) confirmed this association. Calls began for government action with commentators proposing several strategies including the promotion of increased fruit and vegetable consumption, recommendation of supplementa- tion to reproductive-aged women, and fortification (92– 95). In 1996, the FDA authorized the enrichment of grain products with folate at the rate of 0.14 mg per 100-g flour, with mandatory compliance by 1998. Fortification had a dramatic effect, leading to a 19% reduction in incident NTDs in just 5 y (96).

Numerous reports have linked SSBs, which include soda, sports drinks, and sweetened juices, with obesity (97, 98), type 2 diabetes (99), and heart disease (100). In addition, 2 large and rigorously conducted RCTs provided convincing evidence that decreasing consumption of SSBs substantially reduces excess weight gain and obesity in children and ado- lescents (101, 102). Calls have been made for policies to re- duce consumption of SSBs. In the United States, one popular proposal has been an excise tax on SSBs. Brownell and colleagues (103) estimate that an increase of 1 cent per ounce would lead to a minimum intake reduction of 10%. Such a tax would not only discourage unhealthy diet, it would also generate revenue and offset health care costs incurred by chronic diseases associated with refined sugar intake (104). In 2013 Mexico approved a 1 peso per liter tax on SSBs (105), and sales volumes for SSBs fell by 5% in early 2014 (106). That same year, Mayor Michael Bloom- berg led efforts to instate a size limit of 16 oz. on soft drinks sold in New York City. The proposal was passed by the city but was later struck down by the state supreme court (107). Other cities such as San Francisco have proposed excise taxes on SSBs, but opposition from soda and sugar lobbyists re- mains stiff. Nevertheless, certain developments, such as the removal of SSBs from most schools in the United States (108) and a ban on their sale in all public buildings in Bos- ton (109), reflect major steps in reducing consumption of SSBs.

A highly successful example of nutritional epidemiology affecting policy is that of trans FAs (TFAs). TFAs were first developed to stabilize vegetable fat at room temperature and quickly became popular in food manufacturing pro- cesses in the early 20th century. Ancel Keys speculated that TFAs were associated with heart disease in the 1950s (110, 111), but it wasn’t until the 1990s that experimental evi- dence suggested that TFAs both increase LDL cholesterol and decrease HDL cholesterol (112). Subsequent epidemio- logic evidence from the Nurses’ Health Study corroborated this link (113). As more evidence mounted, scientists called for a reduction of TFAs in foods (114), and in 2003, the FDA approved a proposal for manufacturers to list TFAs in the nutrition facts label of foods (115). In 2006 a meta-analysis of observational studies estimated that replacing 2% of en- ergy from carbohydrates with the same amount of energy from TFAs would result in a 29% (95% CI: 11%, 49%)

Understanding nutritional epidemiology 13

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increase in IHD risk (116). A follow-up review combined both observational and experimental findings and provided convincing evidence of a causal link between TFAs and IHD (38). New York City and other city and state governments have banned use of trans fats in restaurants and schools (117). It is now estimated that ~72% of trans fats have been removed from the US food supply (118), and as ex- pected, blood lipids have improved in both children and adults (119). In a recent analysis within New York State, rates of IHD declined faster in municipalities that banned trans fat than in those that did not, and it is estimated that this prevented between 518 and 1037 deaths from IHD per year in New York State (120). It is estimated that a nationwide trans fat ban, by removing the remaining par- tially hydrogenated fats, would prevent between 6480 and 12,960 deaths from IHD annually in the United States (120). In 2013 the FDA took preliminary steps to phase out TFAs altogether by deeming them as not generally rec- ognized as safe (121).

These 3 examples recount changes in public policies in the face of mounting evidence from multiple lines of re- search, and well-conducted observational studies have played a major role in shaping the policies. However, re- search is a slow and evolving process, and consensus is hard to achieve within a short timeframe. For substances that have shown potential harmful effects, even in the ab- sence of conclusive evidence, public health experts have sometimes appealed to the precautionary principle to ad- dress the concern. The principle states that when only lim- ited evidence is available, a substance is presumed to be harmful and the burden of proof falls upon the scientific community or the industry to demonstrate that the sub- stance is safe. Observational data are especially important in this regard because they often present the first reports of negative health outcomes associated with certain dietary or other environmental exposures. They are also usually

the first to show lack of hypothesized harm, e.g., in the cases of total fat in the diet and v-6 FA intake, and thus can play a key role in resolving ongoing controversies (45, 122).

Conclusions Nutritional epidemiology is far from being a perfect science, but with a thorough understanding of the discipline, valuable insights on diet and health outcomes can be obtained from free-living populations. Use of repeated measures and vali- dated FFQs is critical for the assessment of long-term dietary intake. Although measurement error is a key problem, careful study design and meticulously developed dietary assessment tools coupled with specific biomarkers and informed statisti- cal analysis can reduce its impact. Well-conducted RCTs can eliminate confounding and selection bias at baseline and are hence considered the highest level of evidence to infer causal- ity; however, the linear drug trial paradigm cannot be directly translated into nutritional research, in which change in one dietary component is typically accompanied by compensatory change in another component, and good compliance is often difficult to achieve in long-term studies. Thus, prospective co- hort studies, which are considered the strongest observational study design when well designed, are an irreplaceable compo- nent of nutritional research. Evidence from several types of studies, in particular prospective cohort studies of hard clin- ical endpoints and intervention trials of intermediate out- comes, in totality can be used to infer causality and inform policy. Summarizing this evidence in systematic reviews and meta-analyses can be especially helpful in understanding a vast evidence base and informing policy. However, meta- analyses and systematic reviews should be conducted with caution and interpreted in light of the broader context of the field.

Although the future of nutritional epidemiology is bright, with large ongoing international cohorts around the world [e.g., EPIC (123) and UK Biobank (124)] collecting detailed

FIGURE 2 A future direction in nutritional epidemiologic research: a systems epidemiology approach to the discovery of interactions between the exposome (all nongenetic elements to which we are exposed) and the quantifiable elements of the human physiome [Reproduced with permission from Franks et al. (130)].

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data on diet and lifestyle, which will help advance nutritional epidemiologic methods and contribute to the understanding of diet and disease relations, it also faces many challenges. The scientific community must consider several emerging is- sues. First, diets are evolving, and researchers will have to adapt to the changing food, societal, and cultural landscapes by developing new approaches to assessing dietary changes in large and diverse populations. There is an increasing need to adopt the socioecologic model to address the widening food quality gap between the rich and the poor and to reduce health disparities that are associated with obesity and poor diet quality (125, 126). Second, the globalization of the food systems and chronic diseases signifies the need for greater focus on low and middle income countries, where nutrition and epidemiologic transitions are occurring at an unprecedented pace, in parallel with rapid economic devel- opment and urbanization. Third, the environmental impact of food consumption and production should be considered when formulating dietary guidelines and agricultural poli- cies. Fourth, there is a need to incorporate a life course ap- proach into nutritional epidemiology (127), studying the effects of nutrition over the entire lifecycle, from gestation to adult life, which would go beyond the prevailing practice of initiating studies in midlife and carrying out randomized trials for extremely short durations.

Lastly, nutritional epidemiology can benefit considerably from the incorporation of recent developments in “omics” technology, which although having its own challenges, holds promise for advancing the field (128–130). “Omics” tech- nology refers to a collection of high-throughput methods for assessing a large number of genomic, epigenomic, tran- scriptomic, proteomic, and metabolomic traits from biolog- ical specimens. The integration of such technology into traditional nutritional epidemiology, or adopting a “systems epidemiology” approach (see Figure 2), can strengthen study designs and provide additional insights on mechanis- tic pathways, which the traditional epidemiologic approach is often unable to do. All of these areas require an interdis- ciplinary approach in which nutritional epidemiologic stud- ies will continue to play an indispensable role.

Acknowledgments All authors read and approved the final manuscript.

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