In human nutrition, man is the ultimate court in which hypotheses are both generated and tested. Nutritional epidemiology, through its observational studies, demonstrates possible links between diet, physical activity, and disease (Willett, 1998). It is not the only way in which such possible links are gener-ated but it is a critically important one in modern nutrition. Experimental human nutrition takes the hypothesis and through several experiments tries to understand the nature of the link between nutrients and the metabolic basis of the disease. Once there is a reasonable body of evidence that particular nutri-tional conditions are related to the risk of disease, experimental nutritional epidemiology examines how population level intervention actually influences the incidence of disease. In effect, experimental human nutrition and experimental nutrition epidemiology both involve hypothesis testing. However, the former is more often intended to understand mechanisms and generally involves small numbers. The latter, in contrast, uses very large numbers to examine the public health impact of a nutrition intervention that, under the controlled con-ditions of the laboratory, showed promise.
The use of experimental animals for human nutrition research offers many possible solutions to experimen-tal problems. However, the definitive experiments, where possible, should be carried out in humans. Studies involving humans are more difficult to conduct for two major reasons. First, humans vary enormously compared with laboratory animals. They vary genetically and they also vary greatly in their lifestyle, background diet, health, physical activity, literacy, and in many other ways. Second, it is far more difficult to manipulate human diets since we do not eat purified or semi-purified diets.
Experimental diets in human nutrition intervention studies
In the 1950s, an epidemiological study across seven countries presented data to suggest that the main determinant of plasma cholesterol was the balance of saturated, monounsaturated, and polyunsaturated fatty acids (MUFAs and PUFAs). To test this hypoth-esis, a series of studies was carried out on human volunteers using “formula diets.” Dried skimmed milk powder, the test oil, and water were blended to form a test milk with specific fatty acid compositions. The volunteers lived almost exclusively on these formulae. Although this type of study is simple to conduct, it does not represent the true conditions under which normal humans live. At the other end of the spectrum of options for manipulating human diets is that of issuing advice that the subjects verify by way of a food record. It is difficult to prove that subjects actually ate what they say they have eaten. Sometimes, adherence to dietary advice can be ascertained using tissue samples (blood, saliva, hair, fat) and biomarkers. For example, adherence to advice to increase oily fish intake can be monitored using platelet phospholipid fatty acids.
In between these two extremes of formula feeds and dietary advice lies an array of options in which convenience is generally negatively correlated with scientific exactitude. In the case of minerals and vita-mins, it is possible simply to give out pills for the volunteers to take and measure compliance by count-ing unconsumed pills and perhaps using biomarkers. When it comes to macronutrients this is not generally possible. Whereas asking someone to take a mineral supplement should not alter their eating habits, asking someone to consume a liter of milk a day or a bowl of rice bran per day will alter other aspects of the diets of the volunteers. It will not then be possible to attri-bute definitively an event to the intervention (1 l/day of milk or 1 bowl/day of rice bran). The event could have been caused by possible displacement of some other foods by the intervention. The only option in human intervention experiments is to prepare foods for volunteers to eat, which differ only in the test nutrient. If the objective is to examine the effect of MUFAs relative to saturated fatty acids (SFAs) on blood lipids, then fat-containing foods can be pre-pared that are identical except for the source of fat.
The more foods and dishes that can be prepared in this way, the more successful the experiment will be.
The final dilemma is where the test foods will be consumed. A volunteer may share the test foods, which are almost always supplied free of charge, with friends or family. To be sure of consumption, volun-teers may be asked to consume the test meal in some supervised space, usually a metabolic suite. This, however, is a very costly option. Nutritional interven-tion studies with different macronutrient distribution of food content within energy-restricted diets are typical in nutrition research (Abete et al. 2006).
The randomized clinical trial is the most powerful design to demonstrate cause–effect relationships. It is unique in representing a completely experimental approach in humans. The major strength of random-ized trials is that they are able to control most biases and confounding even when confounding factors cannot be measured. The CONSORT statement has established the CONsolidated Standards Of Reporting Trials (http://www.consort-statement.org/). The CONSORT guidelines comprise a checklist and a flow diagram offering a standard way for reporting the research and assessing its quality. The major method-ological issues to be considered and reported in a randomized trial include the following aspects: enrol-ment, allocation, follow-up, and inclusion in analysis of participants, sample size, proceedings for the randomization, blinding of the allocation, blinded assessment of the outcome, comparability of groups regarding major prognostic variables, ascertainment and measurement of end-points, statistical analyses, subgroup analyses, results description, ancillary anal-yses, adverse events, interpretations, generalizability, and overall quality of the reported evidence.
As the researcher designs the options for altering the intake of nutrient under investigation, so too the design of the study requires careful thought. The metabolic effect of the nutrient in question may be influenced by age, gender, and other variables, such as high levels of alcohol intake or physical activity, smoking, health status, prescribed drug use, and family history. On an experiment-by-experiment basis, the researcher must decide which attributes will exclude a volunteer (exclusion criteria).
The volunteers recruited can now be assigned to the various treatments. When the numbers are small, ran-domly assigning subjects to the treatments may lead to imbalances that could confound conclusions. For example, if one has 45 volunteers for three treatments, it could be that the 15 assigned to treatment A include the five heaviest subjects and the five lightest subjects. Another treatment may be predominantly one gender. In such instances, a minimization scheme can be used. Minimization is a technique in which individuals are allocated to treatment groups, ensuring a balance by minimizing the differences between groups in the dis-tribution of important characteristics (age, weight, physical activity). To apply minimization, during the recruitment process the investigators must keep an ongoing analysis of differences between groups in the major variables that may affect the result and allocate new individuals to the group that leads to a more bal-anced distribution of these characteristics. Another option is stratified randomization in which strata are identified and subjects are randomly allocated within each stratum. While stratification and minimization are potentially very useful, it is impractical to stratify individuals for many variables at the same time or to try to minimize every conceivable variable that may affect the result. To a considerable extent, the need to balance groups becomes less important when all sub-jects are rotated through all treatments (crossover designs). For this to happen, the number of experi-mental periods must equal the number of treatments. For any given period, all treatments must be repre-sented. An important factor to consider in this type of design is whether or not a washout period is needed between treatments, and its duration.
Consider the situation above if the study was to examine the effect of fish oil (treatment A) versus olive oil (treatment B) on lymphocyte function. If it is deemed necessary that 20 days are needed to alter the membrane phospholipids of lymphocytes, then it is likely that 30 days will be needed to return to baseline. If it is necessary that each treatment should commence at baseline, then a washout period, where volunteers resume their normal routine, is needed.
A final consideration is the occasion when it is not possible to balance all confounding factors. Take as an example a study to examine the effect of supplemental calcium on bone mineral density in premenopausal women. The treatment group will receive a supple-ment of 1000 mg of calcium as a tablet and the control will receive a placebo tablet. What factors might one wish to balance in such a study? Among the possibili-ties are age, parity, use of oral contraceptives, intake of coffee, smoking, and physical activity. To balance these factors adequately is impossible. However, if they are recorded, then, when the data are being evaluated on a statistical basis, they can be included to ascertain their effect on the measured outcome, bone mineral density. To accomplish this aim, multivariate methods such as multiple regression or logistic regression should be used.
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