Box 2. Specificities of Study Design for Molecular Epidemiology: Nested Case–Control Studies and Case–Cohort Studies

Molecular epidemiology uses the same study designs as the general epidemiology, but some variants are more common. In particular, case–control studies nested in cohorts and case–cohort studies are frequently used to avoid extensive and costly measurements in large cohorts. In nested case–control studies derived from established cohorts, controls are usually matched for age and sex, and also for time variables related to sample collection and disease onset. The method of control selection in these studies is ‘incidence density’ sampling, and an incidence risk ratio is estimated. Controls may develop the disease of interest subsequently to the diagnosis of the case, but they represent the cohort set at risk of developing the disease when each case occurs [24]. The criteria for case inclusion and control matching and selection and their rationale should be reported [1].

In case–cohort studies, unmatched controls come from a sample of the cohort at inception without being matched to cases on time to outcome. The method for control selection in these studies is based only on the population at baseline, without regard to failure times, and a risk ratio is estimated [24],[1].

Both study designs share the important feature that cases and controls come from the same cohort study: recall bias is not of concern if exposure assessment was carried out before disease onset; nonparticipation bias is avoided because rapidly fatal cases have the same probability of inclusion as others; and reverse causation becomes less likely as biological samples were collected before the onset of the clinically documented disease. The nested case–control study tends to be more efficient than the case– cohort study in selecting controls to address confounding. In case–cohort studies, however, the same sample of controls can be compared to different samples of cases (thus different outcomes can be studied). Also, as the sub-cohort is a random sample of the whole cohort, prevalence of exposure can be estimated and external comparisons can be made.

The main concerns regarding nested case–control studies are that controls are not representative of the cohort population and they have few other uses, so the investment in biomarker analyses cannot be leveraged for other research. On the other hand, case–cohort studies rely on the assumption that exposure can be equally well measured in the sub-cohort as in the cases. However, three issues regarding biomarker validity make this assumption questionable: batch effects, the storage effect and freeze–thaw cycles. There are technological and staffing limits to how many samples can be analysed in one go so samples are run in batches or groups. Conditions of the analyses should not vary by batch, but it is clear that for many biomarker measurements this is not true, i.e. there are substantial batch effects (laboratory variation). Also, not all biomarker targets are stable at the usual storage temperature (−80°C), and when samples freeze and thaw, the pH and ionic balance of the liquid phase of the sample can be very different from the natural condition of the sample. Changes in pH and ionic balance can degrade biomarker targets. For these reasons, it may be necessary to include matching by length of storage, batch and freeze–thaw cycles [1].

Box 3. Collection, Handling and Storage of Biological Samples

Several types of human biospecimens can be collected for carrying out molecular epidemiology studies. Blood samples may be stored as a whole or separated into sub-fractions and blood components (red blood cells, serum, plasma, buffy coat and white blood cell sub-fractions). White blood cells contained in the buffy coat are the most widely used source of DNA. Urine can be used as a solution of excreted parent compounds and metabolites to be measured, or as a source of exfoliated cells of the urinary tract. Collection and primary processing are performed accordingly. Other human tissue specimens used in molecular epidemiology studies include body fluids (i.e. cerebrospinal fluids), cell washes (i.e. buccal wash or swabs), epithelial smears, surgical material, nails and hair. Each step in collection, storage, thawing, manipulation and laboratory analysis can introduce errors that may lead to bias and variability. Random error, if evenly distributed in study subgroups, is likely to attenuate or eliminate differences. Systematic errors (e.g. differential clinical conditions, handling or storage of biological samples from cases and non-cases) may generate spurious associations.

Timing of collection often influences the true biomarker level. For example, hormones have hourly, daily or monthly cycles. Prolonged venipuncture can induce release of prolactin or increase white blood cell counts. A very narrow needle causes haemolysis. Several additives can be added to blood, e.g. metaphosphoric acid for vitamin C; anticoagulants such as heparin, EDTA or citrate are needed for plasma collection (i.e. not needed if only serum is collected). There may be disadvantages: heparin binds to many proteins and influences T-cell proliferation; EDTA interferes with cytogenetic analyses. Citrate-stabilized blood affords better quality of RNA and DNA than other anticoagulants. Other additives include protease inhibitors and RNAse inhibitors to avoid degradation of proteins and RNA, respectively.

The goals of proper sample storage are to ensure (i) standardized procedures for all phases; (ii) minimal loss or degrading of material (e.g. because of malfunctioning of freezers); (iii) optimal preservation of material; (iv) blinding, whenever appropriate; (v) easy access to the material when needed; (vi) easy matching of biological material with individual identity; (vii) respect of confidentiality; and (viii) anticipation of emergencies. Stability of the compounds to be measured depends on the type of measurement and temperature of storage: for example, fatty acids should be measured within 2 weeks when samples are stored at 4°C, within a few months when stored at −20°C, up to one year when stored at −80°C. A few studies have been conducted on the stability of different analytes, but the literature is far from being exhaustive.

Box 4. Biomarker Validity and Reliability

To achieve an accurate estimate of the association between a biomarker and a disease, reliable and valid measurements of exposure, covariates (potential confounders and effect modifiers) and outcomes are needed [48]. Validity is defined as the (relative) lack of systematic measurement error when comparing the actual observation with a standard, which is a reference method representing the ‘truth’. While validity entails a ‘standard’, reliability (reproducibility and repeatability) concerns the extent to which any measuring procedure yields the same results in repeated experiments [49].

Validity and reliability are separate entities: a measurement may be perfectly reliable (reproducible in different laboratories and repeatable at different times), but consistently wrong, i.e. far away from the true value; conversely, another one can be unbiased on average, but unreliable if the measurements scatter widely around a true value. Both validity and reliability are important; however, as validity is often not measurable, reliability is sometimes used (incorrectly) as a surrogate.

Timing is also a relevant aspect: inferences about the meaning of biomarker measures are often strictly time specific, as time influences the results in several different ways [49]. For example, while DNA genetic variants are the same for each individual through one's life time, their epigenetic profile may change markedly over time.

Biomarker variability influences associations with the endpoint, thus needs to be assessed and reported upon. A single measure of a biomarker for one individual will be affected by (i) variability within subject (intra-subject); (ii) biological sample variation (i.e. variation depending on the frame of biological sample collection); and (iii) laboratory variation.

Intra-individual variation is sometimes so large that between-individual variation (usually the unit of interest) is hard to detect. A single biological measurement (assume that this is in the absence of laboratory variation) represents the biomarker level/status at a particular time. The biomarker may undergo diurnal, monthly, seasonal or longer variations, e.g. prolactin has a circadian rhythm, oestrogens vary through the menstrual cycle, biomarkers related to recent fruit and vegetable intakes may have seasonal variations. Other biomarkers are more stable, i.e. have less intra-individual variation, and thus, a single measure/sample is usually sufficient (such as mercury in hair, SNPs – single nucleotide polymorphisms). Variation in exposure to other compounds may have influence on the marker level. Intra-individual variability can be measured only if repeated samples from the same individual are collected [50]. Depending on the research question, a measure of a recent, short-term or instantaneous level may be desired (e.g. current CD4 count in a HIV patient), or an average level over a specified time interval (e.g. usual vitamin D level).

Biological sampling variation is related to the circumstances of biological sample collection. For example, hyperproliferation of colonic cells is extremely variable at different segments of the colon mucosa. Therefore, not only the intra-subject variation over time is important, because of the varying exposure to agents that induce cell proliferation, but also the measurements are strongly influenced by how and where the mucosa is sampled from.

Laboratory measurements can have many sources of error, in particular two general classes of laboratory errors: those that occur between analytical batches and those that occur within the batches. Handling, processing and storing of specimens may contribute to errors. Laboratory procedures need to be in place to minimize such variation and avoid biases. Quality control procedures such as the inclusion of laboratory quality control samples and blinded split samples are used to assess the extent of these errors. There should be no identifiers that relate the sample to any other characteristics of the individual from whom it came and in particular of their disease status or any other factor.

The errors of biomarker measurement may have different impact depending on their error distribution. If the epidemiological study has been conducted blindly, i.e. the laboratory analyses have been carried out with no knowledge of the exposed/unexposed or diseased/healthy status of the subjects, the measurement error is expected to be evenly distributed across strata of exposure or disease. However, this is true only if the error is equally distributed across the scale of the exposure. This kind of misclassification leads to underestimation of the risk ratio because of a ‘blurring’ of the relationship between exposure and disease. Both underestimation and overestimation of the association of interest may occur when misclassification is not evenly distributed across the study variables [51]. Individuals with extreme biomarker levels may be excluded, or sensitivity analyses are carried out with and without them to check whether they overly influence the general findings.

The most important single measure of biomarker reliability is the intra-class correlation coefficient (ICC). This is a quantitative measurement of the between-person variance divided by the total (between plus within-subject) variance [52]. It describes how strongly measurements taken in the same subject resemble each other in comparison with the inter-individual variance.

Box 5. Ethical Considerations

Legal issues related to the use of stored human biological material are contained in a European guideline issued by the Council of Europe (http://www.coe.int). In the United States, a useful website is http://nih.gov/sigs/bioethics. When incorporating biospecimen-derived measurements, the following requirements should be met: follow respectful protocols in eliciting information; avoid harm to participants; secure proper informed consent, manage anonymization of interlinking databases; establish confidentiality and security safeguards; develop proper responses to requests for personal data by various parties; devise sound data access, ownership and intellectual property policies; be clear about whether and how individuals will be informed of findings that might be medically helpful for them; and arrange supervision by research ethics and privacy protection bodies [53].

Clearly, each of these requirements would need extensive comments. In particular, how ‘broad’ should the consent be? On the one hand, a broad consent (e.g. ‘the biological samples will be used for the identification of gene variants that may predispose to chronic diseases’) implies a greater freedom of the researcher, who is not obliged to collect further consent forms each time a new gene is investigated. On the other hand, such a generic informed consent form explains very little to the recruitees.

The concept of informed consent was initially formulated in the Declaration of Helsinki in 1964, with the latest revision in 2000 (http://www.wma.net). Recent developments in molecular epidemiology tend to overcome the conflict between ‘broad’ and ‘narrow’ consent forms, introducing the idea of a ‘two-level consent’, i.e. a relatively broad procedure at first, followed by a more specific and detailed approach when studies on single genes/biomarkers are conducted.

For example, there is a broad agreement that low-penetrant variants that are common in the general population and are associated with a slight increase in the risk (interacting with environmental exposures) should not be subject to strict rules as far as ethical implications are concerned. In fact, knowledge of presence or absence of a single allele involved in metabolic pathways neither allows the carrier to modify her/his risk profile substantially nor allows the researcher to identify other members of the family, which would violate confidentiality. The case of highly penetrant gene variants is different: e.g., the identification of the carrier of a rare mutation allows the researchers to identify other family members possibly affected, with potential detrimental effects (e.g. on insurance policies).

The same reasoning applies to biomarkers. The majority of biomarkers used in observational epidemiological research are of little utility to the subjects participating in the research, when taken alone. This is particularly true for the biomarkers of exposure, but also some biomarkers of early biological change/effect may not be meaningful when extrapolated from the research context; for example, DNA adduct level is difficult to interpret at a personal level. Researchers should have a clear view of the practical implications of testing for the study subjects, and in particular what to do in each of these situations: when no effective treatment is possible; when treatment is available with close balance of favourable/unfavourable effects; and effective treatment is available with scarce unfavourable effects. Similar considerations apply to biomarkers, which can be weakly or strongly associated with diseases and less or more associated with family history.

Anonymization of information is another difficult issue. First, there is a problem of definitions: ‘identifiable’ is a sample with name or social security number on it; ‘coded’ is a sample with a code that allows relatively easy identification of the person; ‘encrypted’ is a sample with a code that does not allow easy identification of the person, but this is possible with extra effort; finally, ‘anonymous’ is a sample for which there is no possibility of linking to a person. Clearly, a really anonymous collection of samples is of very little use for epidemiological research, which is based on follow-up and linkage of laboratory data and health-related data.