Considerations for pharmacoepidemiological studies of drug-cancer associations

Abstract

In this review, we provide general considerations for the planning and conduct of pharmacoepidemiological studies of associations between drug use and cancer development. We address data sources, study design, assessment of drug exposure, ascertainment of cancer outcomes, confounder adjustment, and future perspectives.

Aspects of data sources include assessment of complete history of drug use and data on dose and duration of drug use, allowing estimates of cumulative exposure. Outcome data from formal cancer registries are preferable, but cancer data from other sources, e.g., patient or pathology registries, medical records, or claims are also suitable. The two principal designs for observational studies evaluating drug-cancer associations are the cohort and case-control designs. A key challenge in studies of drug-cancer associations is the exposure assessment due to the typically long period of cancer development. We present methods to examine early and late effects of drug use on cancer development and discuss the need for employing ‘lag-time’ in order to avoid reverse causation. We emphasize that a new user study design should always be considered. We also underline the need for ‘dose-response’ analyses, as drug-cancer associations are likely to be dose-dependent. Generally, studies of drug-cancer associations should explore risk of site-specific cancer, rather than cancer overall. Additional differentiation may also be crucial for organ-specific cancer with various distinct histological subtypes (e.g., lung or ovary cancer). We also highlight the influence of confounding factors and discuss various methods to address confounding, while emphasizing that the choices of methods depend on the design and specific objectives of the individual study. In some studies, use of active comparator(s) may be preferable.

Pharmacoepidemiological studies of drug-cancer associations are expected to evolve considerably in the coming years, due to the increasing availability of long-term data on drug exposures and cancer outcomes, the increasing conduct of multinational studies, allowing studies of rare cancers and subtypes of cancer, and methodological improvements specifically addressing cancer and other long-term outcomes.

Introduction

Use of prescription and over-the-counter drugs represents exogenous exposures that may result in either increase or reduction of cancer risk. Clear associations have been established for a number of drugs, e.g., the preventive effect of aspirin use against colorectal cancer [1,2] or the increased risk of renal cancer with use of phenacetin [3,4]. Further, new hypotheses often arise, such as the recent concerns about carcinogenic effects of lithium [5–7] and pioglitazone [8–12]. A significant challenge in the elucidation of drug effects on cancer development is that the effects typically first become manifest several years after drug initiation. The long period of cancer development and the relatively low incidence of most individual cancer types impede the ability of traditional pharmacovigilance systems, notably spontaneous reporting of adverse effects, to identify drug-cancer associations. Consequently, analyses based on large-scale health care data sets are essential to provide solid data on potential drug effects on cancer incidence.

The public health importance of identifying carcinogenic effects of drugs is apparent, as even small carcinogenic effects of widely used drugs will result in many additional cancer cases. Only about a dozen drugs have been established as ‘definitely carcinogenic to humans’ (Group 1) by the International Agency for Research on Cancer (IARC) [13,14]. However, about 50 drugs are currently classified as ‘possible or probably carcinogenic’ (Group 2A/2B), and additional studies are necessary to confirm or disprove these suspicions [15]. Importantly, and often ignored, pharmacoepidemiological studies may also substantiate lack of carcinogenicity for specific drugs. This has considerable value by reassuring prescribers and patients of the safety of drugs, and thus promote their appropriate use, which may be compromised by preliminary reports of carcinogenicity a variety of sources, including case series, adverse events reporting systems, or animal experiments. Finally, identification of potential beneficial effects of drug use on cancer risk or prognosis may provide important evidence that can be pursued further in experimental and intervention studies, as well as provide clues to development of new agents for medical cancer prevention and treatment.

In the present review, we provide general considerations on the conduct of pharmacoepidemiological studies of drug-cancer associations. Importantly, while we are aiming to describe aspects that should be considered when planning such studies, our suggestions should be viewed as guidance rather than as mandatory requirements. Specifically, we address choices of (i) data sources and (ii) study design, (iii) assessment of drug exposure, (iv) ascertainment of cancer outcomes, (v) confounder adjustment, and (vi) future perspectives.

Considerations regarding data sources

In pharmacoepidemiological studies, the exposure is usually not occurring as a single episode, but prolonged and variable over time, during one or more exposure periods, and thus needs to be handled in a time-dependent manner. Therefore, the most detailed drug use history should be sought – such as claims data on dispensed prescriptions or population-based prescription data from drug registries. Apart from dates of prescription or dispensing, data on dose or duration are also necessary to estimate cumulative exposure. In designing studies to evaluate effects of a particular treatment on cancer incidence, it should be considered that individual cancer types have various induction and latent periods [16,17]. The relevant exposure periods for different drugs thus vary in relation to the time from initiation to manifest malignancy of specific cancers (induction period) or from initiation to diagnosis (latent period). While these induction and latent periods are usually unknown, long-term data on drug exposure and long follow-up allow us to make different assumptions about the relevant exposure periods.

Another challenge in assessment of drug-cancer associations is the low incidence of many cancer types, thus requiring very large sample sizes. One way to overcome this challenge is to perform multi-site, multi-database, or multinational studies. However, such initiatives involve several practical challenges, including legal issues and the lack of established common data models.

Minimum requirement for outcome assessment is to have individual level data on cancer incidence. Although data from population-based cancer registries is preferred, information from other sources such as diagnostic or treatment records may be sufficient. It is also important to obtain data on reasons of loss-to-follow-up – including migration or insurance gaps. Information on death and cause of death are helpful to deal with competing risks. It is also essential to have information on potentially important confounding factors. Some factors such as sex and age are necessary in all studies, while other factors depend on the specific study objectives and design.

As an example of registries useful for studies on drug-cancer associations, the Nordic countries (i.e., Denmark, Finland, Norway, Iceland and Sweden) have nationwide registries containing continuously updated, complete, individual-level data on, e.g., prescription drugs [18,19] and incident cancers [20]. Demographic (including socioeconomic) data and hospital diagnoses are also available and can be used for confounder adjustment. The unique personal identification number, assigned to all residents in each Nordic country at birth or immigration, allows for individual-level linkage of registries and databases continuously over time. Key prescription data include the Anatomical Therapeutic Chemical (ATC) classification [21], formulation, package size and number, number of defined daily doses (DDD) per package, and date of purchase. Further, in all Nordic countries, reporting of all incident cancer cases to cancer registries is mandatory by health care providers. The cancer data include the primary site of the cancer, time of diagnosis, diagnosis code according to the International Classification of Diseases (ICD), currently version 10 (ICD-10), and histology and stage of the malignancy.

In the US, the introduction of drug coverage for older adults, Medicare Part D, in 2006 has facilitated use of the Medicare fee-for-service data for pharmacoepidemiological studies on cancer incidence [22,23]. The Medicare data cover inpatient (Part A) and outpatient (Part B) diagnoses and procedures, as well as prescription data at the pharmacy level (Part D). The advantages of the US Medicare data include population-based and nationwide coverage, size (over 20 million older adults with fee-for-service data within Parts A, B, and D coverage), age range (generally high morbidity, drug use, and cancer incidence), low turnaround (the great majority stay in these plans until death), and the linkage to US death data. Limitations include the lack of information before age 65, issues related to changing co-payments during the calendar year (the “doughnut hole”), and time to release (~18 months). Medicare data can be linked to other data sources (e.g., the National Death Index, cancer registries) but at considerable investment (both time and money).

Considerations for the choice of study design

The two principal observational designs relevant for studying drug-cancer associations are the cohort design and the case-control design. In the cohort design, drug users are compared with non-users or users of comparator drug(s) and followed over time with respect to the outcome of interest. In the case-control design, persons with the outcome of interest, i.e., cancer, are compared with persons without cancer with respect to their history of drug use. The cohort and case-control designs are observational, i.e., the researchers do not interfere with the drug use of study participants but only retrieve data on the drugs they acquire on their own initiative, the outcome(s) of interest, and potential confounding factors.

Cohort vs case-control design

Although the case-control and cohort designs at first glance appear to be exact opposites, the underlying concepts of the two designs are similar, and the case-control study is best understood as an efficient sampling of the experience underlying a cohort study [24]. Specifically, the controls can be viewed as a sample of the exposure distribution in the source population that has not (yet) experienced the outcome of interest. In a well-designed case-control study, the estimated odds ratio provide unbiased estimates of the incidence rate ratio that would have emerged from a cohort study in the same source population [25]. If the case-control study is carefully nested within the source population, incidence rates, incidence rate differences, and attributable proportions can also be estimated. The cohort and case-control designs are equally vulnerable to the influence of unknown or imprecisely measured confounding. While we aim to highlight the differences in the applicability of the two designs below, we believe both designs have merit in studies of drug-cancer associations.

There are circumstances where a cohort approach would be most efficient. One such scenario is if the exposure is rare and the cancer outcome is not rare among users (e.g., risk of skin cancer among immunocompromised patients [26]). Also, if outcomes other than cancer are of interest in the same study, establishing a dataset structured for cohort analyses will be more efficient. Further, the cohort study is generally easier to communicate to non-epidemiological professionals and laymen readers than the case-control study. This not only stems from the seemingly more straight-forward “prospective” way of assessing exposure and outcomes, but also from the cohort study’s ability to display baseline characteristics that can even be balanced by use of propensity score methods [27]. A similar description of characteristics among study subjects in a case-control study (i.e., cases vs. controls) will, as it should, show a higher prevalence of established risk factors among the cases, which may be erroneously perceived as a problematic imbalance in the study [28]. Lastly, the cohort design more readily facilitates the implementation of a new-user design (see below) and the use of active comparators, which can be of great value in handling of confounding within some therapeutic areas.

In some situations, it would be more convenient to choose a case-control rather than a cohort approach. First, cancer is usually a rare outcome. All things equal, this renders a case-control study markedly more efficient in terms of required size of the analytic dataset and computations than a cohort study. It should be emphasized, though, that when using already collected data (e.g., claims data), this gain in efficiency is purely computational, not statistical, and given current computing power often moot, even in very large databases. Second, a cumulative dose-response association is important for establishing plausibility of a causal effect. In a cohort design, this would imply that an exposed person should have his/her exposure level re-classified each time he/she crosses the boundary of an exposure level, which may be computationally demanding, if not difficult. In the case-control design, the exposure level of cases and controls could be computed once, i.e., on their index date, albeit under the assumption of no time-varying confounding. Lastly, the establishment of one dataset that enables investigation of various drug exposures in relation to one (or more) cancer types is more easily performed using a case-control approach, which is valuable in settings where extraction of raw data is taxing in terms of time and expenditure.

New user vs prevalent user designs

When assessing drug effects, including on cancer outcomes, drug initiation is the most principled starting point [29,30]. Studying prevalent rather than new (incident) users of drugs potentially violates several principles of causal inference, including the absence of an underlying hypothetical intervention. As such, using a ‘new user’ design, i.e., restricting the study population to new users of the drug under study, should be considered [30]. The new user design also reduces misclassification of drug use due to left truncation of the time period used for exposure ascertainment in prevalent users. Such misclassification is of particular importance when a carcinogenic effect of limited exposure needs to be assessed. Conversely, when only distant or very long-term drug use is anticipated to influence cancer risk, restriction to new users may hinder a meaningful evaluation [7].

Although the new user design is most readily implemented in cohort studies, it may also be applied in case-control studies, by nesting these within a new user cohorts [31]. Overall, the potential value of employing a new user study design, either as the main analysis or as a sensitivity analysis, should always be considered when conducting drug-cancer association studies [32].

Other study designs

The advantage of clinical trials over observational studies is that randomisation effectively addresses confounding, as covariate balance between drug initiators and non-initiators is guaranteed at baseline. Importantly, this balance extends to covariates that are unmeasured or unknown at the time of the study. The downsides of randomized clinical trials are the prohibitive resource requirements, potential ethical and logistic challenges, and with respect to cancer outcomes, the typically relatively small number of outcomes. For obvious ethical reasons, no randomised clinical trials have been launched with the purpose of demonstrating a carcinogenic effect of a drug. There are, however, some examples of trials aimed at establishing cancer preventive drug effects, e.g., of 5α-reductase inhibitors [33,34], aspirin [35,36] and selective COX2 inhibitors [37–39]. In addition, secondary analyses are increasingly being conducted of clinical trials with primary intervention outcomes other than cancer, e.g., cardiovascular trials of aspirin use [40–43]. Since the original study material were based on randomisation, these secondary analyses preserve some benefits of a clinical trial. Randomisation only removes baseline confounding, however, and treatment changes during follow-up should generally not be ignored when assessing cancer outcomes [44–46].

Several observational self-controlled designs have emerged since the 1990s. These designs share the common feature of comparing the occurrence of outcomes between exposed and unexposed follow-up within the same individual [47]. Thereby, confounders that are stable over time are eliminated by design. However, since they all focus on acute and transient effects of drugs, they have little if any relevance for studying drug-cancer associations.

Finally, ecological, or macro, designs should be mentioned. Here, the unit of analysis is a population rather than an individual. An ecological design would for example compare the use of a drug and a specific cancer incidence rate in one country with another country (or region). Although often surprisingly persuasive for lay readers, epidemiologists generally consider ecological designs as weak. It requires a high population attributable proportion for an ecological design to be effective, i.e., a substantial proportion of the cancer occurrence in the population should be attributable to use of the specific drug. To our knowledge, there are only few good examples of this approach within drug-cancer epidemiology [48–50].

Considerations regarding assessment of drug exposure

For most suspected drug-cancer associations, the relevant exposure window during carcinogenesis is unknown. If the drug exposure influences carcinogenesis (early stage), then the risk period would only start long after initial drug exposure. If the drug has influence on later stages in cancer development, the risk period would start earlier. The period between the first occurrence of a cluster of cancer cells to a stage detectable by screening measures or clinical symptoms is typically long; for some cancer types up to 20–30 years [16]. Hence, it is almost inconceivable that manifest clinical cancer can be an immediate effect of drug exposure due to the long period of development for most cancer types. There are a few examples of relatively rapid cancer development induced by exposure to drug use, e.g., the association between use of systemic immunosuppressants and increased risk of non-Hodgkin’s lymphoma and skin cancer in organ transplant recipients [51–53]. An example of very long cancer development – about twenty years – is the association between use of diethylstilbestrol and adenocarcinoma of the vagina and cervix [54,55].

Variability in latency of carcinogenic drug effects is often described in terms of the drug being either a cancer “initiator” or “promotor”. Conceptually, a cancer initiator is one that is a contributory cause of the first clone of malignant cells, whereas a promotor does not possess this property, but acts a contributory factor in accelerating cancer growth of an already existing neoplastic lesion [17,56]. As such, cancer initiators are thought as having a longer latency than promotors. However, in most drug-cancer studies, the mechanisms underlying a potential carcinogenic, or anti-neoplastic, effect are unknown, at least in terms of what stage of carcinogenesis is affected. Consequently, a conceptual framework of potential promotors and initiators typically provides little guidance when designing a specific study. Nevertheless, as drugs may influence later stages of carcinogenesis, studies monitoring drug-cancer associations relatively shortly after initiation of drug therapy also hold scientific value.

Lag-time

The typically long period of cancer development and latency of any carcinogenic or anti-neoplastic drug effects supports implementation of a ‘lag-time period’. In practical terms, this means that cancer outcomes diagnosed shortly after drug initiation should not be regarded as occurring during ‘exposed time’, as these outcomes cannot meaningfully be ascribed to the drug exposure. Correspondingly, a certain period after drug discontinuation should be considered as time at risk. Since the lag period after drug initiation covers both induction and latency of the specific cancer, and the lag period after drug discontinuation primarily covers the latent period (plus any potential carry-over effect), a longer lag period after initiation than after discontinuation should be considered.

A second reason for lagging drug effects is the possibility of protopathic bias (reverse causation). Consider a middle-aged man who consults his general practitioner (GP) because of obstructive urinary symptoms. Initially, the GP would be likely to interpret the underlying condition as benign prostate hyperplasia and prescribe a drug relieving the obstructive urologic symptoms. However, additional diagnostic work-up may reveal a prostate cancer as the underlying condition. Since the use of symptomatic drugs preceded the cancer diagnosis, an apparent association between these drugs and prostate cancer would emerge. In most cases, however, such reverse causation has a time-frame of less than six months [57].

The typically long induction and latent periods, the possibility of reverse causation, and the likely higher probability to detect prevalent pre-clinical cancer due to medicalization around treatment initiation are the main reasons for employing a lag-time in drug-cancer analyses. Reverse causation justifies a lag-time in the order of minimum a few months [57]. The optimal time-frame for addressing the long induction and latent periods is unknown and depends on the specific drug-cancer association being studied. However, for most drug-cancer associations, it is likely considerably longer than the period necessary to address reverse causation. Acknowledging the uncertainty surrounding the mechanisms of single drug-cancer associations, and thus the optimal (biologically relevant) lag-time, studies should generally evaluate various lag-periods in sensitivity analyses [58].

Dose-response association

Most known drug-cancer associations are dependent on cumulative amount, i.e., stronger associations with higher dosages and longer-term use. This may be expressed either by cumulative duration of drug use, by cumulative quantity of the drug, or by the prescribed daily dose (coupled to duration of use). The choice is often driven by the available data, but mechanistic considerations are also relevant. If it is believed that the dose intensity, i.e. the daily dose, is less important, it would be most appropriate to perform analyses according to the cumulative duration. If the dose intensity does matter, then the cumulative quantity or if feasible a direct measure of intensity over time would be more appropriate. Regardless of the measure used, dose-response or duration of use analyses should always be carried out.

When interpreting dose-response analyses, special attention should be paid to trivial, low-level exposure. If very low exposure shows an association with cancer, there is a chance that the association is explained by confounding [59,60]. While a dose-response pattern is generally considered supportive of causality, caution is advised as some confounders may act in a graded fashion. As an example, progressively heavier use of bronchodilators will likely correlate to smoking history and thereby show a confounded but dose-dependent association with lung cancer risk. Lastly, another good reason for analyzing cumulative dose-response effects is that associations that are explained by reverse causation often have an inverse cumulative dose/duration-response association and thereby can be distinguished from causal effects.

Defining treatment episodes

Constructing treatment episodes for study subjects from prescription registries may be challenging. If prescription data do not include information on the prescribed dose and duration of a specific treatment, treatment episodes need to be estimated on the basis of purchasing dates and quantities of drug prescribed. In the attempt to construct treatment episodes, investigators encounter temporal gaps and overlaps among prescriptions, and different methods accounting for various prescription patterns may lead to different estimates of drug effects [61,62]. As there is typically long latency between the relevant drug exposure and cancer diagnosis, such considerations of the precise period of drug intake may be less important in cancer pharmacoepidemiology than in studies of acute or semi-acute outcomes. Nevertheless, varying prescription patterns without specific knowledge of dose or duration of treatment introduces an additional source of uncertainty regarding exposure ascertainment, and researchers are, for this and the aforementioned reasons, encouraged to apply different exposure measures in individual studies.

Considerations regarding cancer outcome ascertainment

Important objectives of cancer classification and registration are to assemble and compare cancer incidence data across populations and countries, and to provide valid cancer diagnoses for specific research purposes in analytical studies. During the last two decades, official cancer registration and establishment of cancer registries have increased steadily worldwide, substantially facilitating epidemiological and other cancer research [63]. Valuable sources of international cancer incidence data include the United States’ SEER-program [64]; the NORDCAN program covering Scandinavian countries [20]; and the GLOBOCAN program estimating cancer incidence and mortality data on a global scale [65].

Traditionally, the most important diagnostic and clinical modalities used to establish cancer diagnoses are reports from pathology departments (providing histological diagnoses), hospital records, and death certificates, although the proportion of cancer cases identified solely by death certification is low today in most countries [63]. Together, clinical and histological diagnoses provide a high level of precision in the diagnosis. However, access to records from radiotherapeutic and oncology departments, medical records, imaging measures, and hematology laboratories can also provide important information, e.g., for diagnosis of brain and other tumors of the central nervous system and for haematological malignancies. In general, completeness and validity of cancer registration increases with the number of modalities used to ascertain the diagnoses; and significant omissions may raise concerns that case finding is incomplete. Use of multiple sources of cancer ascertainment demands efficient registration procedures to ensure that all records pertaining to the same case are combined into a single registration [66].

In the absence of data from cancer registries, claims based algorithms can be developed to identify cancer incidence. These algorithms usually cover a combination of diagnostic codes, procedures, and take relative timing of these into account. They need to be validated against a gold standard (usually cancer registry data), ideally in a similar population to the one studied. Examples include the commonly used algorithms published by Setoguchi et al. [67] that showed high specificity of a definition using two specific cancer codes within 2 months for a variety of cancers. These algorithms are relatively crude, however, and more work is needed to refine and extend them to specific populations.

Using ‘cancer overall’ as outcome should be discouraged, as this essentially goes against our understanding of cancer as a heterogeneous disease [56]. It is inconceivable that a pharmaceutical agent should act as a universal carcinogen, and not even strong carcinogens, such as tobacco smoking and radiation, are universally carcinogenic [13]. An analysis of cancer overall is essentially driven by the effect of the drug on the cancers with the highest incidence. Currently, cancer diagnoses are most often classified according to organ site, using ICD diagnostic codes. However, in continuation of aspects of specificity, it is unlikely that a given drug would induce all types of cancers, even within the same organ. Thus, if feasible, differentiation according to histological subtypes should be employed in studies of drug-cancer associations. Consider immunosuppressants that are known to induce skin cancer; currently there is only firm evidence that the association pertains to non-melanoma skin cancer, not melanomas [14]. In some organs, e.g. the prostate or colorectum, one histological type (adenocarcinoma) comprises most cancer cases, and as such restriction to adenocarcinomas makes little difference, although it should still be carried out, if feasible. However, at many cancer sites, e.g. esophagus, lung, breast, ovary, testis, and kidney, differentiation into distinct histologic subtypes are important, as an analysis lumping together all histological cancer types would be driven by the effect of the drug on the most prevalent subtype.

Increasing knowledge of the epidemiology, histopathology, and today also molecular profiles of cancer diseases will facilitate even more detailed classifications categorizing subtypes of cancer both within and across organ sites. Identification of more “refined” cancer subtypes may thereby, in the years to come, increase the specificity of risk associations and predictions. While beyond the scope of the present review, readers interested in the application of molecular biology in cancer classification are referred to reviews specifically addressing this issue [68–70].

Considerations regarding confounder adjustment

Adjustment for confounding in drug-cancer association studies should generally follow the same principles as in any other pharmacoepidemiological study. As one noticeable exception, the assessment of confounder variables should take into account the induction/latency period of cancer outcomes, as discussed above. If, for example, no lag-time is considered in the assessment of baseline or time-varying covariates, early symptoms of a cancer or other effects of the increased medical attention preceding a cancer diagnosis may inadvertently be included in the adjustment model. This is especially important in case-control studies, where confounders are often defined on the index date. Further, it is important to emphasize that while many databases used for drug-cancer studies lack information on important and well-established cancer risk factors, e.g., family history, many of these will have no apparent effect on the prescribing of the majority of drugs, and thus will confer no confounding effect in drug-cancer association studies.

Active comparator

Important unmeasured covariates, like for example body mass index (BMI), can sometimes be balanced by study design rather than by statistical control. Take as an example a study on the effects of insulin glargine on cancer outcomes (including colorectal cancer, for which BMI is a risk factor). In this study, BMI would be an obvious confounder if we compared patients initiating insulin glargine with non-initiators, because a high BMI is one of the main reasons to initiate insulin therapy in patients with type 2 diabetes. However, by using an active comparator, human NPH insulin, the confounding potential of BMI is mitigated because BMI does not affect the choice of insulin after the indication for adding insulin has been made [71]. This highlights the value of the active comparator new user cohort study design to reduce the potential for unmeasured confounding. Subtle differences in the indication of comparator drugs might still exist and would need to be controlled for by standard analytic techniques. It is important to point out that with an active comparator the scientific question is changed from absolute effects (e.g., safety) to effects relative to a clinical alternative. The above example of a study with active comparator does not answer the question whether adding insulin in patients with type 2 diabetes increases the risk for colorectal cancer, but the question whether the effect of insulin glargine on colorectal cancer is different from the effect of NPH insulin. As such, if the active comparator has the same potential to cause cancer, e.g., through a shared pharmacological action, a carcinogenic effect might be missed. Lastly, the idea of an active comparator should not be pursued at all costs, but only if a suitable active comparator can be identified, i.e., a drug with comparable indications. If the drug under study is first-line treatment in mild disease, using an active comparator that is only used as second-line treatment or for more severe disease might introduce more bias than it removes.

Time-varying confounding

While confounding at drug initiation can often be limited by study design (and remaining confounding removed during analysis), the time-varying confounding affecting drug persistence and changes in treatment over time is related to (lack of) effectiveness and side effects. Unfortunately, many registries that contain necessary data on drug prescribing do not contain much information (if any) on (immediate) effectiveness and (subtle) side effects. For example, many databases do not include measures of glucose control or other markers of diabetes severity that may affect persistence on antidiabetic drugs and risk for some cancers [72]. Confounding from disease severity can bias a study in either direction. On one hand, more severe disease may be associated with longer duration or higher intensity of treatment. Conversely, severe disease may also be associated with switching and thus shorter duration of first-line treatments [73]. If good data on the drivers of adherence/persistence are available in a database, methods that allow for control for time-varying confounders affected by prior treatment should be used to reduce bias [74].

Future perspectives

The study of drug-cancer associations is in many respects still in its infancy, and the field will likely evolve considerably over the coming years. Three drivers of this evolution deserve to be highlighted. First, the accumulation of long-term data on drug use and cancer incidence is of particular value in studies of cancer etiology, keeping in mind the potentially long induction periods of cancer development. For example, the Swedish Prescribed Drug Registry, covering the entire population of Sweden (approximately 10 million inhabitants), was established in 2005 [75] and in the US, drug coverage (part D) for the Medicare population was introduced in 2006. These databases have thus only recently achieved an age where they begin to contribute meaningfully to the field of drug-cancer studies. Second, as the pharmacoepidemiological community accumulates experience in conducting multinational studies, the door is open for the study of rare types of cancers (or drug exposures). Lastly, methodological work, specifically addressing studies of long-term outcomes, is both needed and ongoing. For example, further research on the implementation of advanced methods, such as marginal structural models or structural nested failure time models, is needed to properly adjust for time-varying factors [76,77]. These three drivers, coupled with other emerging opportunities, such as incorporation of genetic data, clearly indicate that we will be able to perform more comprehensive drug-cancer association studies in the future, to secure the safe use of drugs in the population and potentially identify new therapeutic avenues for cancer prevention and treatment.

Text Box.

The author’s top 10 ‘suggested reading’ relevant to pharmacoepidemiological studies of drug-cancer associations (in non-prioritized order)

#	Authors	Title	Topic	Citation
01	Walker	For drug-induced carcinogenesis, the observations are the hypothesis. Invited editorial for the Mini-Symposium on Cancer Pharmacoepidemiology	Basic concepts	Ann Epidemiol 2016; 26(11):749–750
02	Pinheiro et al.	Challenges in evaluating cancer as a clinical outcome in postapproval studies of drug safety	Basic concepts	Ann Epidemiol 2016; 26(11):735–740
03	Friis et al.	European Code against Cancer 4th edition: Medical exposures, including hormone therapy, and cancer	Basic concepts	Cancer Epidemiol 2015; 29 Suppl 1:S107–19
04	Rivera et al.	Connections between pharmacoepidemiology and cancer biology: designing biologically relevant studies of cancer outcomes	Exposure ascertainment	Ann Epidemiol 2016; 26(11):741–745
05	Pottegård & Hallas	New use of prescription drugs prior to a cancer diagnosis	Reverse causation	Pharmacoepidemiol Drug Saf 2017;26(2):223–227
06	Umar et al.	Future directions in cancer prevention	Cancer biology	Nat Rev Cancer 2012; 12 (12): 835–848
07	Rothman	Induction and latent periods	Induction/latency	Am J Epidemiol 1981; 114(2):253–9
08	Pottegård et al.	Identification of associations between prescribed medications and cancer: a nationwide screening study	Hypothesis generation	EBioMedicine 2016;7:73–9
09	Lund et al.	The active comparator, new user study design in pharmacoepidemiology: historical foundations and contemporary application	The active comparator, new user design	Curr Epidemiol Rep 2015; 2(4):221–228
10	Stürmer et al.	Adjustments for unmeasured confounders in pharmacoepidemiological database studies using external information	Advanced confounder adjustment	Med Care 2007; 45(10 Supl 2):S158–98