Tumor-Based Case–Control Studies of Infection and Cancer: Muddling the When and Where of Molecular Epidemiology

Molecular epidemiology has made great strides in uncovering the causes of cancer. We wish to call attention to a type of retrospective case–control study that assesses infections as risk factors for cancer, and utilizes molecular tests on tumor tissue to assign exposure status for the cancer cases (1–6). The advantages and limitations of this “tumor-based case–control study” design and appropriate interpretation of such studies have not been described. In this Commentary, we review limitations in making inferences from tumor-based case–control studies, which arise due to (i) the retrospective timing of exposure assessment and (ii) differential exposure assessment for cases and controls. We illustrate how these limitations can lead to biased estimates of the strength of association between infections and cancer risk.

As an initial step in assessing whether a viral, bacterial, or parasitic infection causes cancer, tumor tissue from cases can be evaluated for markers of that infection that plausibly relate to exposure. For example, if the exposure is a viral infection, patient tumor specimens can be tested for the presence of the viral genome. Preliminary studies of this type, which evaluate solely human tumor tissues, are considered case series.

As a next step, investigators sometimes conduct a tumor-based case–control study. Importantly, the purpose of tumor-based case–control studies, as in other case–control studies, is framed as assessing the association between the infection and cancer. Although the tumor-based case–control study is similar to a case series, in that it uses the tumor tissues from cases to assess their exposure status, as a type of case–control study it always includes control subjects without the cancer of interest.

The use of tumor tissue to assess exposure in cancer cases may seem natural in tumor-based case–control studies. However, because control subjects do not have the cancer of interest, another tissue must be assessed for them. Therefore, tumor-based case–control studies differ from other retrospective case–control studies, which use the same tissues for assessing both cases and controls.

In a tumor-based case–control study, two approaches for selecting tissues for control subjects are readily available (Table 1). Among controls, the tissues evaluated for exposure can include normal tissue from the same body site that gives rise to the cancer (e.g., normal breast tissue for comparison with breast cancer tumors). Another common approach is to use “sentinel” specimens in contact with these body sites, for example, skin swabs to reflect the exposure of the skin, exfoliated cells or cervical lavage specimens to reflect the status of the cervix, or buccal rinse specimens to reflect the status of the oral cavity or oropharynx. Investigators can then utilize highly sensitive and specific techniques to detect infection in these tissues, as well as tumor tissues from cases, assaying for microbial DNA (e.g., using PCR), RNA (in situ hybridization), or proteins (IHC).

The difficulties in tumor-based case–control studies arise from exposure misclassification. These can be understood in comparison with one standard epidemiologic design, the cohort study. In a cohort study, exposure is assessed at subjects' baseline visit (and perhaps additional time points), and subjects are followed subsequently for disease occurrence. Typically, an exposure exerts its causal effect during an “etiologic window” of time. Because cancers develop over a prolonged period, the etiologic window can be years (or even decades) before development of disease. Cohort studies attempt to assess exposure status in this window. Measuring exposure before development of disease in the cases establishes a temporal relationship between exposure and outcome (7). In addition, measuring exposure uniformly, that is, using the same tissue and assay method for future cases and noncases, reduces the likelihood that any exposure misclassification is differential by case–control status.

In a case–control study (the other major type of epidemiologic study), cases with disease are evaluated along with a sample of nondiseased control subjects. A nested case–control study can be viewed as an efficient way to sample subjects from a large cohort study (2), and in such a study, the investigator can assess the subjects' prior exposure status using previously collected biospecimens. In contrast, in a retrospective case–control study, exposures can only be evaluated using information or biospecimens collected at the time of selection. A key consideration is how well this retrospective assessment reflects subjects' earlier exposure status, especially during the etiologic window. In most retrospective case–control studies, the investigator uses similar biological specimens for cases and controls, and applies uniform methods to assess exposure. Thus, retrospective case–control studies suffer from a lack of information on the temporal relationship between exposure and outcome, but in most such studies, uniform exposure assessment helps ensure that exposure misclassification is nondifferential by case–control status.

A tumor-based case–control study, as we describe it, is similar to other retrospective case–control studies in starting with cases who already have the disease and a sample of people without the disease. Similar to other retrospective case–control studies, tumor-based case–control studies lack information on the temporal relationship between exposure and outcome, so they cannot provide an unambiguous measure of exposure during the etiologic window. In addition, the unique issue for tumor-based case–control studies is that the exposure status of case and control subjects is assessed using different tissues, which has the potential to yield a different assessment.

These two issues of tumor-based case–control studies both relate to exposure misclassification—we describe them as “when” and “where” issues:

1. The “when” of exposure assessment: retrospective assessment may not accurately reflect exposure during the etiologic window.

2. The “where” of exposure assessment: use of different tissues for cases and controls may not provide comparable exposure assessment.

Retrospective ascertainment of exposure (“when”) is problematic for all retrospective case–control studies. For example, infection may have first occurred only after the etiologic window, leading to a false-positive assessment (i.e., low specificity) for exposure based on the retrospective assessment at the time of subject selection. Also, some infections may be cleared over time, leading to low sensitivity for retrospective assessment (8).

With respect to the “where” issue, use of various tissues in control subjects can have low sensitivity. For example, within an organ, infections may be focal and microscopic, and a random biopsy can miss the site of infection. Furthermore, even when the infection is present, the amount of microbial material in control tissues may be very small. In contrast, lack of sensitivity typically affects cases less. This situation is likely when viruses are the agents of interest, because if the virus caused the cancer, it is usually reasonable to assume that it will be present in at least one copy per tumor cell. Thus, clonal multiplication of infected tumor cells ensures a reasonable sensitivity for many molecular tests of tumor tissue in cases.

Both the “when” and “where” issues can be present simultaneously in tumor-based case–control studies, because use of different tissues for cases and controls may combine to cause differential assessment of exposure for the earlier etiologic window. For example, among controls, infection may only be detected intermittently in sentinel samples, whereas infection may be persistently detectable in case tissues. This difference leads to lower sensitivity for detecting exposure during the etiologic window for controls than cases, leading to a spuriously positive association. Alternatively, changes in tumors and surrounding tissues as the cancer develops can reduce the ability of infections (especially bacteria) to persist. This “disease effect” decreases sensitivity selectively among cases, potentially leading to spuriously reduced associations relative to the truth.

Substantial evidence links human papillomavirus (HPV) to cervical, anal, penile, vulvar, vaginal, and oropharyngeal cancers (1). The model whereby HPV is posited to cause cancer is through continued expression of viral oncoproteins (1). Some initial data supporting etiologic associations were derived from tumor-based case–control studies in which tumor tissues were assessed for HPV using molecular techniques (e.g., PCR for HPV DNA; refs. 1–4); HPV status of controls without cancer was evaluated using sentinel samples, for example, cells obtained through swabs, rinses, or lavages. Importantly, the etiologic window during which HPV infection first affects progression to cancer is many years before diagnosis (1, 8).

With respect to the “when” of exposure assessment, retrospective assessment of HPV infection is somewhat problematic. This issue may be especially difficult for controls, among whom HPV infection may have been transient. For example, among healthy young women, incident cervical HPV infections are frequently cleared. HPV clearance rates are not well characterized for other sites of infection. These considerations complicate interpretation of results from controls as reflecting their HPV status during the preceding etiologic window. For cases, in contrast, one may argue that evaluation of tumor tissues has high sensitivity for HPV infection during the etiologic window (i.e., if the virus caused the cancer, it must still be detectable in the tumor). However, detection of HPV in the tumor may have low specificity, because the virus may have been acquired later and be present in the tumor coincidentally. Evidence that HPV can be present coincidentally in tumors is provided by the observation that multiple HPV subtypes can sometimes be detected in a tumor, even though only one of the subtypes is causally related (9).

Alternative approaches may help increase the specificity of exposure assessment during the etiologic window in cases. For example, some viruses (including HPV) can integrate into host DNA (1). In such instances, a clonal pattern of viral integration within a tumor (demonstrated through tumor sequencing) supports that viral infection of the tumor cells occurred before the key neoplastic steps that led to clonal tumor growth, i.e., during the etiologic window. However, testing for clonality of viral integration cannot be used for normal tissues in controls, because the control tissues are not themselves clonal.

About the “where” of exposure assessment, it is important to consider that the researcher typically wishes to assess exposure for the entire person, the relevant organ, or the particular tissue at risk of cancer. One may posit that HPV detection is highly specific for concurrent infection for both cases and controls. However, for some sites of interest, sensitivity for detection of HPV infection likely varies between cases and controls based on differences in the evaluated biospecimens.

For oropharyngeal cancer, for example, the assessment of tumor tissue is highly sensitive for detecting HPV in case tumors, and it is probably very sensitive for detecting infection in the entire organ (i.e., the whole oropharynx) as well. However, it is difficult to determine the sensitivity of oral rinses used for assessing HPV exposure among controls. Oral rinses frequently miss HPV infection in oropharyngeal cancer cases (10, 11). If sensitivity of oral rinses is low in cases, it could be even lower in controls, because controls likely have only low-level or localized infection. These considerations point to differential sensitivity in assessment of oropharyngeal infection in cases and controls as a result of relying on different tissue types (e.g., tumor tissues vs. oral rinses). In contrast, the “where” issue would not be as important in assessing controls in a study of cervical cancer, because cytobrushes and cervical lavages have high sensitivity for detecting cervical HPV infection.

Helicobacter pylori, a bacterium, is an established cause of gastric cancer (1). H. pylori infects the stomach lumen adjacent to the epithelial lining, and induces chronic inflammation and gastric atrophy. These changes set the stage for development of gastric cancer. However, as cancer develops, the stomach becomes less supportive of H. pylori infection, leading to loss of the bacterium (i.e., a disease effect; refs. 1, 12–14). Some tumor-based case–control studies of H. pylori and gastric cancer have evaluated tumors from cases and random gastric biopsies from noncancer control subjects (e.g., patients with gastritis), using various staining procedures to identify the bacterium (5, 6).

The challenge for any retrospective case–control study of gastric cancer is the accuracy of its assessment of H. pylori infection status during the etiologic window (“when” issue). For a tumor-based case–control study, use of gastric biopsies for controls plausibly has reasonable sensitivity both for current infection and infection during the earlier etiologic window, because H. pylori often causes diffuse and longstanding gastritis. However, use of tumor tissue for exposure assessment in cases likely would have lower sensitivity because of the disease effect (both a “when” and “where” issue).

Tumor-based case–control studies, which utilize diseased tissue to assess exposure status in cases, have been used to study infections as cancer risk factors. One reason why investigators may consider tumor-based case–control studies attractive is that it is natural to interpret molecular evidence for a microbe in tumor tissue as reflecting infection that predates development of the cancer. It therefore seems straightforward to define exposure for cases in that way, and it then only appears necessary to obtain some comparison tissues from controls. However, we argue that this approach suffers from difficulties in assessing exposure during the etiologic window (the “when” issue) and a lack of comparable tissues for control subjects from which to assess exposure (the “where” issue). We summarize limitations of tumor-based case–control studies in Table 2 in the context of evaluating associations between infections and cancer.

Exposure assessment is a challenge for any epidemiologic study. Some assays for infection (e.g., serum antibody assays for HPV or H. pylori infection) may lack sensitivity or specificity. Therefore, even if the assays are applied uniformly for all subjects, using the same types of biologic sample, they may still produce a biased measure of association. If the misclassification does not differ between cases and noncases, then the bias is typically toward the null. A cohort study can assess exposure at a defined time point before development of cancer, and assessment is uniform for cases and controls. All retrospective case–control studies face challenges from the “when” issues that we describe, even though most typically utilize the same method of exposure assessment in cases and controls. The subset of tumor-based retrospective case–control studies uniquely suffer from the “where” issue, which results in differential exposure misclassification.

Because of this vexing “where” issue, tumor-based case–control studies may be expected to yield measures of association (e.g., ORs) between infection and cancer that are upwardly or downwardly biased away from the true association. For example, for many viral infections, differential exposure assessment yields good sensitivity in case tumors but lower sensitivity in control tissues. The difference in the tissue types will lead to inflated ORs even for high-quality assays. A bias in the opposite direction can occur in tumor-based case–control studies of other infections (e.g., H. pylori), if the infection is lost over time as the tumor develops (12, 15).

Unfortunately, a measure of association, such as an OR, is usually interpreted as providing information on the relative risk for developing cancer in exposed and unexposed people. Given the biases that we describe, we believe it is inappropriate to make quantitative interpretations of ORs from tumor-based case–control studies, such as, “exposure is X-fold more common in cancer cases than controls,” or even more problematically, “exposure is associated with an X-fold increased risk of developing cancer.” Unfortunately, we have seen both interpretations in the published literature. Even when the true association is quite strong, the bias in the estimates derived from tumor-based case–control studies can have important downstream ramifications. For example, clinicians may attempt to use such results for risk stratification, or public health researchers may use them to predict disease burden. Those models will produce unreliable results if the strength of the association is incorrectly estimated.

Meta-analyses are an important source of confusion in equating tumor-based case–control studies with standard case–control studies. Many primary studies comparing case tumors with normal tissues present their findings in terms of the proportion of specimens of each tissue type that exhibits evidence for the infection of interest, and do not present measures of association, such as an OR. However, meta-analyses that summarize the evidence linking an infection to cancer include these studies and derive ORs, thereby converting them into de facto tumor-based case–control studies. The meta-analyses then frequently present summary OR estimates that are interpreted to reflect associations between the exposure and risk of subsequently developing the cancer. Examples of such meta-analyses include evaluations of HPV and bladder, breast, and laryngeal cancers (16–18); Epstein–Barr virus and breast cancer (19); simian virus 40 and mesothelioma, brain tumors, sarcomas, non-Hodgkin lymphoma, and colon cancer (20); and H. pylori and liver cancer (21, 22). Although systematic reviews of published studies are always informative, we suggest that investigators refrain from quantitative summaries, or they should clearly state that differences between groups should not be interpreted as measures of risk.

If tumor-based case–control studies do not reliably provide a measure of association between risk factor and outcome, they can still serve a useful role, especially early in a line of research when little is known. They can provide qualitative laboratory evidence for a possible relationship between the exposure and cancer. For instance, because persistent expression of viral oncogenes is often thought to be required in viral carcinogenesis, frequent detection of infection in case tumors helps support an etiologic role; such evidence is captured under Bradford Hill's criteria for causality as “coherence” (7). The key distinction is that tumor-based studies do not yield reliable quantitative measures of association, which are required under Bradford Hill's criterion of “strength of association” (7). Tumor-based case–control studies can also serve as helpful benchmarks in assessing the reliability of laboratory testing, by demonstrating consistent differences in detection of infection between different tissues (e.g., by ruling out PCR contamination).

As a final point, we note that the tumor-based case–control study design differs from other case–control studies that use tumor tissue only to separate cases into subgroups, not for exposure assessment. A classic example is the division of breast cancer cases according to tumor expression of hormone receptors (23), and the approach has also been used in case–control studies to divide cancer cases into infection-positive and negative subgroups (24). Investigators have then investigated whether the case subgroups exhibit different risk factors, by uniformly assessing all of the cases and controls for another exposure of interest. Because of its uniform exposure assessment, this approach does not suffer from the “where” issue we describe for tumor-based case–control studies.

In summary, standard cohort and case–control study designs provide the strongest framework for measuring associations between infections and cancer. Given the “when” and “where” issues faced by tumor-based case–control studies, their results, particularly measures of association, should be interpreted with caution.

No potential conflicts of interest were disclosed.

Conception and design: E.A. Engels, S. Wacholder, H.A. Katki, A.K. Chaturvedi

Development of methodology: S. Wacholder

Writing, review, and/or revision of the manuscript: E.A. Engels, S. Wacholder, H.A. Katki, A.K. Chaturvedi

This work was supported by the Intramural Research Program of the National Cancer Institute.

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