Reporting
and Review of Human Genome Epidemiology Studies
Julian Little
Tables | Box | References
Introduction
The recent completion of the first draft of the human genome
sequence (1,2,16)
and advances in technologies for genomic analysis are generating tremendous
opportunities for epidemiologic studies to evaluate the role of genetic
variants in the etiology of human disease (3). The
basis of this evaluation will be identification of the allelic variants
of human genes, description of the frequency of these variants in different
populations, identification of diseases influenced by these variants
and assessment of the magnitude of the associated risk, and identification
of gene-environment and gene-gene interactions. The process of identifying
DNA variation that may be associated with disease is under way through
the cataloguing and mapping of single nucleotide polymorphisms (SNPs)
throughout the genome. The analysis of genotype data on SNPs may aid
in the identification of DNA alterations that result in or contribute
to disease states.
Not surprisingly, the number of published human genome epidemiologic
studies has increased rapidly (4). Therefore, integration
of evidence will become increasingly important as a means of dealing
with potentially unmanageable amounts of information. Heterogeneity
between studies can be assessed, and when this occurs, attempts can
be made to explain it. So far, few gene-disease associations have been
replicated (5-7). This is also true for gene-environment
and gene-gene interaction (8,9). It
is important to determine how far methodologic issues may account for
differences between studies. This requires that the studies are adequately
reported and appraised. Investigation of heterogeneity between studies
can lead to the formulation of new hypotheses.
In this chapter, we consider the reporting and systematic review of
human genome epidemiologic studies. Systematic reviews differ from traditional
reviews in that systematic reviews are supported by evidence that is
integrated in explicitly defined stages (see below). Meta-analyses form
a subset of systematic reviews in which quantitative methods are obtained
to obtain an overall measure of effect across different studies or detect
and explain heterogeneity between studies. Pooled analysis of data on
individual subjects from multiple studies has many features in common
with systematic reviews, but involves obtaining and re-analyzing the
primary data, as distinct from aggregating published information (10)
Critical appraisal and integration of evidence require that the evidence
be adequately reported. Brief checklists or guidelines for reporting
gene-disease associations have been proposed (11,12).
In this chapter, we present a more detailed overview of issues in the
critical appraisal of studies of genotype prevalence, gene-disease associations,
and gene-environment interactions, based in large part on the deliberations
of an expert panel workshop convened by the Centers for Disease Control
and Prevention and the National Institutes of Health in January 2001
(4,13). A checklist intended to guide
investigators in preparation of manuscripts, to guide those who need
to appraise manuscripts and published papers and to be useful to journal
editors and readers is presented in Table 10-1.
It should not be regarded as an exhaustive list of points that have
to be presented in all journal articles. Addressing all of the considerations,
for example in studies of rare conditions in clinical settings, may
not always be feasible.
Reporting and Appraisal of Single Studies
Hypothesis specification
Associations between several genes and a disease can be tested according
to a priori hypotheses based, for example, on a documented biologic
mechanism of these genes in determining the disease. For example, the
associations between a number of gene variants whose products are thought
to influence the metabolism of folate and related nutrients and colorectal
neoplasia have been investigated, because of the roles of folate in
methylation and DNA synthesis (14). It is becoming
usual practice in human genome epidemiology studies to initiate a study
to test hypotheses that are current at that time and to establish a
resource to test additional hypotheses proposed later on the basis of
knowledge external to the resource. These are all a priori hypotheses.
Hypothesis-testing is important to distinguish from hypothesis-generation.
In gene-disease association studies and studies of the prevalence of
allelic variants, it has been suggested that data on genotypes are presented,
because it is the genotype that determines risk (13).
A point to consider in appraising studies is the choice of categories.
In a two-allele system, for example, justification would be sought for
the decision to consider heterozygotes separately, include them in the
reference category with homozygotes for the common variant, or group
them with homozygotes for the rarer variant(s). This is more complex
for multi-allelic systems.
In studies of gene-environment and gene-gene interactions, many hypotheses
of interaction can potentially be tested. The distinction between a
priori hypotheses and hypothesis generation is, again, important. Even
in the simplest case of a dichotomous genotype and dichotomous exposure,
genotype and environment can interact in six ways (15).
Many more can be defined if more categories are introduced. For instance,
Taioli et al. (16) have proposed a model in which
an effect of the genotype is apparent at low environmental exposures
but is not apparent at high exposures. Once multiple categories of dose
are defined for the environmental variable, many different dose-response
models can be tested in the data. Clearly, model specification becomes
more difficult as more environmental factors (and levels of exposure),
and more genes (and alleles), are included.
Design
In appraising studies, it is important to consider design as this affects
the biases that may occur and generalizability (17,18).
Most studies of gene-disease associations and gene-environment and gene-gene
interactions for late-onset diseases have used the case-control design.
Much of the discussion therefore focuses on this design. However, DNA
samples are being collected in a number of ongoing cohort studies. Compared
with case-control studies, cohort studies have a number of advantages,
including the capacity to examine age-at-onset distributions and multiple-disease
outcomes (19-21). The use of case-cohort and nested
case-control analysis of archived samples that are suitable for genotypic
analysis potentially can minimize the disadvantages of the cost of genotyping
an entire cohort. A major advantage of the case-cohort design for studies
in which use of expensive assays is planned is that the same comparison
group can be used for several different disease outcomes. Therefore,
this design is likely to be used increasingly. Because the detection
of gene-environment and gene-gene interaction is particularly challenging,
novel study designs, most notably the case-only design and multistage
designs, have been proposed (17). Concern about the
possible impact of population stratification has stimulated the development
of family-based case-control designs; these are discussed briefly in
the section on population stratification.
Issues that are particularly important in the appraisal of studies
of genotype prevalence, gene-disease associations, and gene-environment
and gene-gene interactions include the analytical validity of genotyping,
selection of subjects, confounding (especially as a result of population
stratification), statistical power, and multiple statistical comparisons.
In addition, exposure assessment is an important issue in the appraisal
of studies of gene-environment interaction. Because many methodologic
issues are common to the three types of study, these are discussed in
parallel.
Assessment of genotypes
The definition of the genotype(s) investigated should be clearly presented.
The validity of grouping genotypes on the basis of putative functional
effects depends on the availability and quality of functional studies
of gene variants, and information on functional effects is likely to
change over time. For multi-allelic systems, genotypes have been grouped
according to functional effects in some investigations. For example,
grouping according to inferred rapidity of acetylation has been done
for the NAT2 polymorphisms (8).
True functional variants are important to distinguish from markers
associated with a disease only because they are in linkage disequilibrium
with a functional variant. Typing several polymorphisms throughout a
candidate gene may be useful in order to construct haplotypes, which
could then be tested for association with the phenotype of interest.
The increasing availability of mapped SNP markers (20-24)
offers the opportunity for such an approach and presents methodologic
challenges (see below).
Other factors affecting the analytical validity of genotyping, including
the types of samples and timing of collection, the method used for genotyping,
and quality control procedures are summarized in Table
10-1. These issues are discussed in Chapter 5 and Little et al.
(13).
Assessment of exposures
Not surprisingly, exposure assessment is important in studies of gene-environment
interaction. Points that need to be considered are the method of exposure
assessment, and its validity and reproducibility. Exposure misclassification
can bias the estimation of an interaction effect, the magnitude of which
depends on the prevalence of the misclassified exposure and on the interaction
model (Chapter 8, 25). If interaction is defined as lack of fit to a
multiplicative model, a test for interaction will be conservative (26).
In theory, case-control studies are more vulnerable to differential
misclassification than are cohort studies (and the related case-cohort
and nested case-control designs). However, provided that the extent
of misclassification of exposure does not vary by genotype, differential
misclassification between cases and controls is not a serious problem
for the detection of departures from a multiplicative gene-environment
joint effect (26).
Selection of subjects
Evaluation of potential selection bias requires consideration of study
design and fieldwork. It is important to distinguish between studies
that aim to detect an association from those that aim to estimate the
magnitude of an association. In the former situation, cases may be “overselected”
from multiplex families to increase the power to detect an association;
presenting the measure of association as an estimate of population association
would be inappropriate. In the latter situation, the principles underlying
study design are essentially the same as for the investigation of the
magnitude of association with environmental risk factors, including
the minimization of the potential for selection bias emphasized in many
epidemiologic textbooks (27-30). In a number of studies
the selection of cases has not been well described (31).
In a review of type1 diabetes and HLA-DQ
polymorphisms, the authors noted that many studies were based on convenience
samples of cases in which persons with type 2 diabetes who used insulin
in their treatment regimen had been included (32).
In several studies of cancer, prevalent cases have been included to
varying extents (33). In these studies, bias would
occur if the genotype affected survival or if genotypes were assayed
by a phenotypic test that was influenced by disease progression or treatment.
A recurrent problem in case-control studies of gene-disease associations
with unrelated controls has been that the controls were not selected
from the same source population as the case-subjects (8,
9, 31, 32). The
potential problem of selecting controls who do not represent the population
from which case-subjects arise is illustrated by the divergence in odds
ratios for the association between colorectal cancer and the GSTT1
null genotype (34), when the different control groups
were analyzed (9). In regard to genotype prevalence,
many early studies were based on convenience samples and not infrequently,
little information was given about how the samples were selected (8,
9, 31, 35).
Population stratification
Concern has been raised about the possible effects of population stratification
on the results of population-based case-control studies (36-41).
Population stratification includes differences between groups in ethnic
origin and can arise because of differences between groups of similar
ethnic origin but between which there has been limited admixture, such
as in isolated populations. For example, a population might comprise
the descendants of waves of immigrants from the same source but differ
generally because of founder effects. The differences may then be apparent
because insufficient time has elapsed for mixture between the groups.
In an exploration of the possible degree of bias from population stratification
in U.S. studies of cancer among non-Hispanic Americans of European descent,
this bias was considered unlikely to be substantial when epidemiologic
principles of study design, conduct, and analysis were rigorously applied
(42). A similar conclusion was reached using data
from case-unrelated control studies of non-Hispanic U.S. whites with
hypertension or type 2 diabetes, and Polish subjects with type 2 diabetes
(43). Variations in the frequency of certain genotypes
in African Americans appear to be much wider than those observed in
persons of European origin and therefore the possibility of stratification
may be higher (44). Evidence was weak for an effect
of population stratification in data from a case-unrelated control study
of hypertension in African Americans, but this was no longer apparent
when the study was restricted to persons with U.S.-born parents and
grandparents (43).
Concern about the possible effects of population stratification has
stimulated development of family-based case-control designs, which essentially
eliminate potential confounding from this source (45,
46). The most commonly used examples of such designs
involve the use of siblings or parents as controls. Sibling controls
are derived from the same gene pool as cases. However, selection bias
could result because a sibling may not be available for every case–bias
would arise if determinants of availability (e.g., sibship size) were
associated with genotype. In addition, compared with a study in which
unrelated controls were used, a study using an equivalent number of
sibling controls has less statistical power because of over-matching
on genotype (47). This loss of power generally does
not occur for case-parental control studies (46),
which have been advocated for the identification of modest gene-disease
associations (48). However, the need to obtain samples
from parents is a practical problem limiting the applicability of the
design for diseases of late onset. Clearly, the study design is appropriate
to consider in assessing the possible impact of population stratification.
Another approach proposed to minimize the potential problem of population
stratification when unrelated controls are used is to measure and adjust
for genetic markers of ethnicity that are not linked to the disease
under investigation (49-52). This would be expected
to control for ethnic variation in disease risk attributable to genetic
factors. However, residual confounding from other sources of ethnic
variation in disease risk would be a potential issue. A single measure
is unlikely to capture the important sources of ethnic variation (53).
In appraising case-unrelated control studies, or cohort studies, points
to consider are the adequacy of matching for ethnicity or adjusting
for it in analysis.
Confounding from other sources
Confounding of a gene-disease association, and of gene-environment and
gene-gene interactions, potentially could result from linkage disequilibrium.
Linkage disequilibrium depends on population history and on the genetic
make-up of the founders of that population (7, 54).
Linkage disequilibrium varies between populations (54)
and may in part account for the variable results of studies of gene-disease
associations (7). In a correctly designed association
study, except for allelic associations that extend for a short genomic
region from the locus under investigation, the comparison of groups
of individuals defined by genotype could be equivalent to a randomized
comparison (26). However, so far data on linkage disequilibrium
for SNPs show that the extent of linkage disequilibrium varies by region
of the genome, and that its variation at all distances is great (54).
Moreover, studies of microsatellite polymorphisms have shown linkage
disequilibrium between a few loci that are separated by many megabases
(>= 1 cM) (55).
In studies of gene-environment interaction, confounding of exposures
is a potential problem. The principles regarding the control of confounding
are the same as those for studying the relation between exposure and
disease. In practice, the use of biomarkers of exposure may need care
in interpretation because the genotype may influence the presence or
level of the biomarker. Rothman (56) noted that an
extraneous risk factor is a confounder only if its effect becomes mixed
with the effect under study. For example, an exposure may cause altered
physiology, which in turn causes disease. A biomarker of the altered
physiology is a risk factor for the disease and is unrelated to exposure
because it results from exposure. It is not confounding because the
effect of the exposure is mediated through the effect of the altered
physiology, and therefore no effects are mixed. However, decisions about
whether a biomarker represents an intermediate factor in aetiology or
is a potential confounder are difficult when uncertainties exist about
the mechanism of effect of exposure. This would also apply to genes.
In case-cohort studies, controls are a random sample of the cohort,
and the effect of age, which is the key time variable, is controlled
for in the analysis only. In more traditional nested case-control designs,
controls are selected to match the cases on a temporal factor, such
as age, and the main comparisons are within the time-matched sets (60).
In appraising case-cohort studies, the method of age adjustment and,
in appraising nested case-control studies, details of the matching on
age or other temporal factors are important to consider.
Statistical issues
In appraising studies, the main statistical issues are study power,
multiple testing and method of analysis.
Power
A small study size is a limitation of many studies testing a priori
hypotheses about gene-disease associations, (e.g., references and 9
and 58). This problem is exacerbated in studies of
gene-environment and gene-gene interactions. To test for departures
from multiplicative effects, it has been noted that study size should
be at least four times larger than needed to detect only the main effects
of the individual factors (59). In studies of modest
gene-environment interactions, the sample size requirement is of the
order of a thousand cases or more. When non-differential misclassification
of exposure is taken into account, many thousands of cases may be needed
(25). The biggest problem facing the field of gene-environment
interaction is that almost no published studies have these sample sizes.
A possible solution is pooled analysis (see below).
Multiple testing
One proposed research strategy is large-scale testing by genomewide
association mapping (48, 60-62).
This strategy is hypothesis-generating rather than hypothesis-based
and thus may require additional safeguards against type 1 error. For
example, Risch and Merikangas (48) suggested specifying
a higher significance level. However, increasing the significance level
will increase the number of subjects required to have adequate statistical
power, although this may not make studies unfeasible (48).
In the analysis of gene-environment interactions, a large number of
potential interactions could be tested for in a typical data set. Current
data sets often already have several dozen genotypes determined, and
many dozen, or even hundreds, of different environmental variables may
be determined for each person in the data set (e.g., a typical food-frequency
questionnaire will measure intake of more than 100 foods and permit
estimation of more than 50 nutrients). Moreover, it is important to
know whether there was an a priori choice of categories or scale used
to quantify the amount of exposure, because this will give insight as
to whether multiple testing is an issue for interpretation. In addition,
the interaction model must be specified (see earlier discussion of the
many models of gene-environment interaction). An approach of assessing
interaction of every genotype with every environmental variable under
every possible interaction model would generate a large number of false-positive
results. Increasing the significance level is unlikely to solve the
multiple comparisons problem in this context. The limited power to detect
even established interactions at the p<0.05
level in most studies (because of modest effects and limited sample
sizes) means that adjusting for multiple comparisons would be equivalent
almost never declaring statistical significance for “true”
interactions. In other words, reducing the nominal p
value would mitigate the false-positive problem by creating a potentially
unacceptably high false-negative rate.
Methods of analysis
Well-established methods exist for describing the prevalence of exposure
and for measuring associations (27, 28).
These can be applied to describing genotype prevalence and assessing
gene-disease associations. In regard to trend-tests for gene-disease
associations, even in the case of a single gene with two alleles, a
decision is needed about whether to treat genotype as a trichotomous
variable in which heterozygotes are categorized separately (i.e., assuming
co-dominance) or to combine them with one of the two groups of homozygotes
(i.e., assuming a dominant or recessive model). A problem in the choice
of such models is the lack of functional information. There can be substantial
loss of statistical power when a test suitable for one mode of inheritance
is used where another mode is the true one (63).
Methodologic issues relating to haplotype analysis are still under
development. In particular, in studies based on unrelated persons, haplotypes
can be estimated only probabilistically on the basis of allele frequencies.
If external estimates of haplotype frequency in the population are applied,
inference may be affected by the quality and availability of the data
on haplotype frequencies in the relevant population. As more SNP loci
are identified, the number of possible haplotypes can become huge, in
turn raising the issues of multiple comparisons and sparse data for
many haplotypes (60, 64). A potential
limitation of the approach of constructing haplotypes is that the effect
of a true functional variant might be diluted when haplotypes rather
than loci are the units of analysis.
The methods of assessing gene-environment and gene-gene interaction
are less established. Three common methods have been used to assess
the statistical significance of gene-environment interactions, when
defined as departures from multiplicative effects. First, an interaction
term is introduced into a logistic model and the Wald p
value for the coefficient of the interaction term reported. In the case
of multiple ordered categories of the environmental variable entered
as an ordered categorical variable, the interaction term tests whether
the linear trend in the environmental variable is significantly different
between the dichotomous categories of genotype. Second, a cross-product
“dummy” term is introduced into the logistic model for each
combination of genotype and environment category (omitting the combination
for the reference category). The p value
for interaction is then given as the difference in the log-likelihood
between this model and the model containing the main effect estimates
for the genotype and environment variables. When both genotype and exposure
are dichotomous, then these two tests are equivalent. However, when
there is more than one category, they test different models. In this
situation, a point to appraise is whether the model of interaction was
specified a priori. A potential problem with the likelihood ratio test
for interaction is that it does not directly test for trend. In situations
in which the data depart from an ordered trend, the likelihood ratio
test may give a significant result because the cross-product terms improve
the fit of the model to the data. Therefore, assessing gene-environment
interaction solely by screening for level of significance of a formal
test for interaction should be avoided.
Third, estimates of environmental effects are compared between genotype
strata. However, the finding of a significant effect in one or more
strata but no significance in at least one other stratum does not constitute
statistical evidence of interaction. Often such a pattern has been observed
when inadequate power exists in one of the strata. Whether a formal
test of statistical interaction has been performed to assess the strength
of the evidence for interaction should be considered.
Analytic methods to test for gene-environment and gene-gene interactions
are still under development. For example, the application of hierarchical
models is being explored (65, 66).
Little work has been done on testing for departures from additive models
of genetic and environmental effects (26, 67).
Systematic Review
The stages involved in systematic review are (1) specification of the
issue for which integrated evidence is needed; (2) identification of
studies; (3) critical appraisal of studies; (4) abstraction of data;
and (5) synthesis.
Specification of the issue
Typically, the need exists to specify the allelic variant, then consider
one or more of questions relating to its frequency (at an early stage
in research), its variation in frequency (as data accumulate), its relations
with specific diseases, and whether it modifies the effect of exposures
that are etiologically important (and vice versa).
Identification of studies
A comprehensive search is one of the key differences between a systematic
review and a traditional review (68). Typically, the
strategy used to identify relevant papers for a systematic review involves
specifying the search terms, the time period of publication, the databases
searched and software used to do this (69). Because
problems may exist with the indexation of papers, hand-searches of the
reference lists of relevant papers identified from the original search
and of key journals are common practices. Thus, for example, in a review
of the association between glutathione S-transferase polymorphisms and
colorectal cancer, Medline and EMBASE were searched using the MeSH heading
"glutathione transferase" and the textwords "GST"
and "glutathione S transferase" for papers published between
1993 and 1998 (9). The CDC Office of Genomics and Disease
Prevention Medical Literature Search was also searched and reference
lists in published articles were hand-searched.
A further issue is the possible inclusion of unpublished sources, including
abstracts, technical reports, and non-English journals (70)
that may not be identified by electronic searches, as a means of minimizing
the potential impact of publication bias (see below). However, this
material should be treated with caution because it may not be peer-reviewed
and may be subject to modification and revision. In addition, information
on study methods may be insufficient to assess study quality.
Several instances have occurred of sequential or multiple publications
of analyses of the same or overlapping datasets. For example, in studies
of CYP1A1 polymorphisms and breast cancer,
substantial overlap between the studies of Ambrosone at al. (71)
and Moysich et al. (72), and between that of Taioli
et al. (73) and Taioli et al. (74),
is likely. An aid to identifying this problem is to organize evidence
tables (see below) first by geographic area and then by study period
within a specified area. If the reports clearly relate to the same or
overlapping datasets, then a consistent method of dealing with this
should be adopted, such as including data only from the largest or most
recent publication. Under these circumstances, details of the methodology
may be described in greater detail in an earlier publication. If so,
the reference to the earlier publication should be given with the reference
to the publication from which the data were abstracted in the evidence
tables.
Critical Appraisal
Issues in the appraisal of single studies have been discussed above.
A number of reports have been published about the rating of the quality
of analytical observational studies. Several relate to case-control
studies (27, 29, 75-79).
Some (75, 76) are part of a series
of articles documenting the deficiencies of epidemiologic research;
they have been challenged on the grounds of technical errors, failure
to distinguish important from unimportant biases, and ignoring the need
to weight the totality of the evidence about a relation (80,81).
Other issues include possible over-emphasis of the potential problems
of case-control studies in comparison with cohort studies (78)
and difficulty in assessing differences between methods applied in the
case and control groups, or between different exposure (prognostic)
groups (79,82).
Several authors have proposed quantitative quality scoring systems
for critical appraisal (82). Other schemes have been
developed for meta-analyses in which an attempt has been made to assess
the importance of study quality in accounting for heterogeneity of results
between studies (83-85). This type of assessment also
has been considered for pooled analysis (86, 87).
Certain features of the assessment schemes are specific to the disease
or the exposure under consideration, and each aspect of the study is
given equal weight. Thus, summation of points might result in worse
quality scores for a study with several minor flaws than for a study
with one major flaw. Although empirical studies on a large number of
primary investigations might suggest an overall relation between a specific
aspect of study design and the reported results, this relation is ecologic
and may not be true for a specific investigation. Therefore, specific
non-causal factors, which might affect the interpretation of a single
investigation, are difficult to isolate. Jüni et al. (88)
observed that the use of scores to identify clinical trials of high
quality is problematic and recommended that relevant methodologic aspects
should be assessed individually and their influence on the magnitude
of the effect of the intervention explored. Similar caution in consideration
of studies of gene-disease associations is likely to be justified. As
in clinical trials, multidimensional domains may be more appropriate
to consider than a single grade in the integration of evidence from
observational studies.
Little or no empirical evaluation exists of the quality scoring of
association studies. However, many users of data on genotype prevalence
and gene-disease associations need a robust means of grading evidence.
This approach has been proposed by the Scottish Intercollegiate Guidelines
Network (89). In this approach, studies of gene-disease
association in which all or most of the criteria specified as appropriate
to a research question are satisfied would be graded as “++.”
Criteria that have not been fulfilled would not affect the grade if
the conclusions of the study were considered very
unlikely to be affected by their omission. Studies in which some
of the criteria have been fulfilled, and criteria that were not fulfilled
considered unlikely to alter the conclusions
would be graded as “+.” Studies in which few or no criteria
were fulfilled and the conclusions of the study considered likely
or very likely to be altered by multiple
omissions in required criteria for an acceptable study, would be graded
as “-.”
Abstraction of Data
Specific forms are often used for this purpose, for example, that used
for the Human Genome Epidemiology Network’s
e-journal reviews (90). The form should be piloted
to ensure a consistent approach to data abstraction. Ideally, this would
be done by two independent reviewers and discrepancies resolved, but
resources may not permit this (91,92).
Typically, such forms include reference details, information about study
eligibility, study methods, and study results.
Synthesis of the Evidence
The first steps include describing the volume of evidence and preparing
evidence tables that summarize the basic characteristics of the studies,
factors relating to study quality, measures of association (with indicators
of precision), and the reference. On this basis, consideration is given
to combining results. The simplest way of combining results is counting
the number of studies showing positive, negative and inverse associations.
However, this approach is very limited as no account is taken of study
quality or of the magnitude of the association. Other approaches take
account of these issues.
Hierarchy of Evidence
In many schemes of qualitative synthesis of evidence, a hierarchy exists
whereby certain study designs are considered inherently superior to
others. In general, analytical epidemiologic designs are stronger than
ecologic designs and studies of case series or reports. Although cohort
studies may be less subject to bias than case-control studies, important
issues exist about quality of follow-up and case-ascertainment. Therefore,
it seems more rigorous to weight the evidence from specific studies
of these types on the basis of a full critical appraisal rather than
solely on the basis of general design.
Quantitative synthesis
There are two types of quantitative synthesis of evidence: (1) meta-analysis
of the results of studies and (2) pooled analysis of data on individual
subjects obtained in several studies. The validity of meta-analysis
of observational studies has been debated (69, 93).
On the one hand, meta-analysis may indicate a “spurious precision”
and either meta-analysis of observational studies should be abandoned
altogether (94) or possible sources of heterogeneity
between studies should be considered (95). On the
other hand, meta-analysis can help clarify whether an association exists
and indicate the quantitative relation between the dependent and independent
variables (96). The indication of the quantitative
relation, although potentially biased, may be valuable in considering
public health effects of interventions based on knowledge of the genetic
factor or its interactions.
Pooled analysis requires data on individual
subjects. This approach offers many advantages over the meta-analysis
of the results of studies, including standardization of definitions
of cases and variables, better control of confounding, and consistent
determination of subgroup effects (10, 86).
For example, this approach has been used successfully to study the effect
of chemokine and chemokine receptor alleles on HIV-1 disease progression
(97) . Nevertheless, pooling approaches require much
greater resources (98). Interestingly, the results
of meta-analyses of the glutathione S-transferase M1 polymorphism and
cancer of the lung (99) and bladder (67)
were similar. Pooled analysis is preferred to meta-analysis of the results
of studies when a high degree of accuracy of the measures of effect
is required. However, stratification by original study may still be
important, to allow for and elucidate causes of heterogeneity among
the data sets being pooled.
Interpretation
The main issues appear to be consideration of possible publication bias
and application of guidelines for causal inference.
Publication
Bias. Publication bias is the selective publication of studies
on the basis of the magnitude and direction of their findings (100).
Research with statistically significant results has long been accepted
to be more likely to be submitted and published than work with null
or non-significant results (101), and this has led
to a preponderance of false-positive results in the literature (102).
Therefore, publication bias is a potentially serious problem for the
integration of evidence on gene-disease associations (6,7),
especially in relation to gene-environment and gene-gene interactions.
In addition to the larger number of potential comparisons implicit in
the concept of multiple interacting variables, authors face the problem
that large tables of gene-environment interaction estimates are very
cumbersome and difficult to assemble in publishable format. This inevitably
increases the potential for publication bias.
In other fields, quantitative and qualitative methods of detecting
publication bias have been used, such as the fail-safe technique where
the number of new studies averaging a null result needed to bring the
overall effect to non-significance is calculated (69,
103). Then a judgment can be made as to whether it
is realistic to assume that such a number of studies have been unpublished
in the field of investigation. If the assumption were realistic, then
the validity of conclusions based on published evidence would be doubtful.
Other quantitative and qualitative methods have been reviewed by Sutton
et al. (92) and by Thornton and Lee (104).
In general, all the methods have limitations. Therefore, it seems appropriate
to account for the possibility that the evidence base may be skewed
toward positive results in drawing conclusions about causal relations.
Another potential method of identifying publication bias is to search
research registers such as CRISP (105) and the Directory
of On-going Studies in Cancer Prevention (106).
Administering research registers on studies of genotype prevalence and
gene-disease associations is challenging because data for each additional
allele genotyped would need to be added to the database. It is even
more difficult for studies of gene-environment and gene-gene interactions,
because of the diversity of joint effects which can be investigated.
Causal inference. Well-established
guidelines exist for causal inference (Box 10.1).
However, in practice, only limited subsets of these tend to be used
(110). For example, in cancer epidemiology, the guidelines
most often applied are consistency, strength, dose-response, and biologic
plausibility.
Consistency: In relation to
consistency of gene-disease associations and gene-environment and gene-gene
interactions, differences between studies in distributions of subjects
by age and sex are sources of heterogeneity. For example, hormonal alterations
can affect ligand binding, enzyme activity, gene expression, and the
metabolic pathways influenced by gene expression. In particular, some
inconsistency between the results of gene-disease association studies
may be secondary to variation among studies in the prevalence of interacting
environmental factors that have not been assessed. Testing a priori
hypotheses about differences in gene-disease associations and genotype
frequencies between studies that may arise from these sources would
be appropriate.
In relation to interactions, heterogeneity may occur if the allele
under study is associated with disease due to linkage disequilibrium
with a gene that is truly causal. Such a “marker” allele
may behave differently in populations with different genetic backgrounds
resulting from differences in the extent of the linkage disequilibrium,
even if the “causal gene” has the same effect in the different
populations. Differences between populations in allele prevalence may
result in differences between studies in the statistical power to detect
both the main effect of the genotype and gene-environment interactions.
Similarly, the prevalence of exposure, or variability of exposure, may
influence whether an interaction exists or is detectable.
Strength: As noted by Rothman
(56), the strength of an association is not a biologically
consistent feature but rather a characteristic that depends on the relative
prevalence of other causes. In studies of the general population, the
associations between disease and biomarkers of susceptibility are not
likely to be strong. In particular, many of the genetic variants so
far identified as influencing susceptibility to common diseases are
associated with a low relative and absolute risk (108).
Therefore, exclusion of non-causal explanations for associations is
crucial. In this situation, an interaction between a gene and exposure
(or another gene) would be expected.
Dose-response: In the context
of gene-disease associations, the value of considering dose-response
relations will depend on information about the functional effect(s)
of the relevant gene. As already noted, in the particular instance of
gene-environment interaction, when multiple categories of dose are defined
for the exposure, then many different dose-response models can be tested
in the data, and tests for interaction can be applied to the trends
across strata. Consequently, false-positive results are likely to be
a problem.
Biologic plausibility: This
is a particularly important issue in the evaluation of gene-disease
associations, gene-gene, and gene-environment interactions. For example,
in investigations of associations with genetic polymorphisms of carcinogen
metabolism and DNA repair, many genotypes have been assessed without
data on their functional significance. Investigations confined solely
to genotypes potentially would lead to numerous false-positive associations.
Consideration of biologic plausibility involves determining (1) whether
a known function of the gene product can be linked to the observed phenotype;
(2) whether the gene is expressed in the tissue of interest; and (3)
temporal relations, including the time window of gene-expression in
relation to age-specific gene-disease relations. Thus, the gene should
be in the disease pathway and/or involved in the mechanism that is responsible
for the development of the disease. If not, then the effect of the gene
may be indirect. In studies of cancer in young persons, maternally mediated
effects of the maternal genotype and parental imprinting also may be
relevant to consider. As an example of the need for careful interpretation,
N-acetyltransferases have been considered to be important in detoxification.
However, NAT has been observed to catalyse O-acetylation (109).
O-acetylation is thought to be an activating step.
Specificity: Although specificity
has been included as a criterion of causation, it may be inappropriate
in relation to the effects of complex exposures that may influence several
outcomes such as tobacco smoking, or genetic variants that may influence
the metabolism of a variety of exposures, such as cytochrome P450 gene
variants. For example, CYP1A1 gene variants
have been investigated in relation to a variety of types of cancer (33),
macular degeneration (110), Parkinson’s disease
(111), endometriosis (112), primary
dysmenorrhea (2) and orofacial clefts (113).
Temporality: Although a correct
time relation is specified in many methodologic texts, it seems to be
seldom used in causal inference (107). In the situation
of gene-disease associations, the disease could influence the result
of a phenotypic assay of the genotype under investigation. This should
not be a problem with PCR methods. If data were available on the time
window of gene-expression, it would be relevant to consider this in
relation to age-specificity of gene-disease relations. As a perhaps
extreme example, if an association existed between a type of cancer
in infants and the CYP1A1 or CYP1A2
genotype of the index child, this probably would be indirect (e.g.,
reflecting an effect of maternal genotype) because the enzymes coded
by these genes are not expressed in the fetal liver (114,
115).
Experimental support: In the
context of gene-disease associations, experimental support is most likely
to be derived from studies of gene expression in knockout or other experimental
animals, from in vitro data on gene function, or from experimental interventions
based on clinical trials of interventions aimed at normalizing the function
or levels of a product regulated by the gene. For example, initially
transgenic mouse models appeared to support a role for certain genes
in the etiology of orofacial clefts (116). It is
now apparent that clefts often occur in knockout and insertion experiments,
and that gene expression at a critical time and in a tissue relevant
to development of the lip and palate should also be taken into account.
An example of in vitro investigation on gene function is an investigation
of the effect of the MTHFR C677T polymorphism
on folic acid deficiency-induced uracil incorporation into human lymphocyte
DNA (117). In regard to trials of interventions aimed
at normalizing a gene product, trials of the drug CPX are under way
(118). CPX acts by binding to the mutant channel
protein, helping it to mature and gain access to the plasma membrane,
and it is thought that repair of the defect in trafficking to the membrane
helps suppress the high level of synthesis and secretion of IL-8 that
is involved in pathogenesis.
Coherence: This criterion
has been defined as being satisfied when an association being consistent
with the state of knowledge of the natural history and biology of the
disease (119). In practice, this criterion has been
little used, perhaps because it has been considered equivalent to biologic
plausibility (107). Elwood (29)
defines an association as being coherent “if it fits the general
features of the distribution of both the exposure and the outcome under
assessment.” He notes that the concept holds only if a high proportion
of the outcome is caused by the exposure, and if the frequency of the
outcome is fairly high in those exposed. An additional constraint on
the use of this criterion arises when information about the distribution
of the relevant exposure and outcome is inadequate. Information about
the distribution of many biomarkers is limited. In the situation of
gene-disease associations, the “exposure” would be the genotype
being investigated.
Conclusion
There has been a tremendous increase in the number of published human
genome epidemiologic studies, and this increase is set to continue.
So far, few gene-disease associations, gene-environment or gene-gene
interactions have been replicated. This may in part be due to methodologic
issues. Methodologic issues that are particularly important include
the assessment of genotypes, selection of subjects, confounding, statistical
power and multiple statistical testing. In the assessment of gene-environment
interaction, assessment of exposure is also an important issue. It is
hoped that the checklist presented in this chapter will be useful to
investigators preparing manuscripts, to those who need to appraise manuscripts
and published papers, and to journal editors and readers. In regard
to the integration of evidence, established principles of systematic
review should be applied. Meta-analysis and pooled analysis can help
address concerns about statistical power and provide a formal means
of investigating possible heterogeneity between studies. Pooled analysis
is labor intensive. It is preferred to meta-analysis when a high degree
of accuracy of the measures of effect is required. In interpreting this
evidence, the potential for publication bias is an important consideration.
To address the problem of publication bias, a register of research is
needed that would include negative findings. In terms of specifying
hypotheses to be tested and interpretation of the biologic plausibility
of study findings, inter-disciplinary collaboration in this fast expanding
field is crucial.
Acknowledgments
Much of this chapter is the result of discussions at an expert panel
workshop convened by the Centers for Disease Control and Prevention
and the National Institutes of Health in January 2001. We thank the
following contributors for comments: Linda Bradley, Molly S Bray, Daniel
Burns, Mindy Clyne, Gwen W. Collman, Janice Dorman, Darrell L. Ellsworth,
James Hanson, Robert A. Hiatt, David J. Hunter, Muin J. Khoury, Joseph
Lau, Thomas R O’Brien, Nathaniel Rothman, Donna Stroup, Emanuela
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