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  • v.16(2); 2019 Feb

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COSMOS-E: Guidance on conducting systematic reviews and meta-analyses of observational studies of etiology

Olaf m. dekkers.

1 Department of Clinical Epidemiology, Leiden University Medical Center, Leiden, the Netherlands

2 Department of Clinical Endocrinology and Metabolism, Leiden University Medical Centre, Leiden, the Netherlands

3 Department of Clinical Epidemiology, Aarhus University Hospital, Aarhus, Denmark

Jan P. Vandenbroucke

4 Faculty of Epidemiology and Population Health, London School of Hygiene and Tropical Medicine, London, United Kingdom

Myriam Cevallos

5 Institute of Social and Preventive Medicine (ISPM), University of Bern, Bern, Switzerland

Andrew G. Renehan

6 Manchester Cancer Research Centre, NIHR Manchester Biomedical Research Centre, Division of Cancer Sciences, School of Medical Sciences, Faculty of Biology, Medicine and Health, University of Manchester, Manchester, United Kingdom

Douglas G. Altman

7 Centre for Statistics in Medicine, Nuffield Department of Orthopaedics, Rheumatology and Musculoskeletal Sciences, University of Oxford, Oxford, United Kingdom

Matthias Egger

8 Centre for Infectious Diseases Epidemiology and Research (CIDER), School of Public Health and Family Medicine, University of Cape Town, Cape Town, South Africa

Associated Data

To our knowledge, no publication providing overarching guidance on the conduct of systematic reviews of observational studies of etiology exists.

Methods and findings

Conducting Systematic Reviews and Meta-Analyses of Observational Studies of Etiology (COSMOS-E) provides guidance on all steps in systematic reviews of observational studies of etiology, from shaping the research question, defining exposure and outcomes, to assessing the risk of bias and statistical analysis. The writing group included researchers experienced in meta-analyses and observational studies of etiology. Standard peer-review was performed. While the structure of systematic reviews of observational studies on etiology may be similar to that for systematic reviews of randomised controlled trials, there are specific tasks within each component that differ. Examples include assessment for confounding, selection bias, and information bias. In systematic reviews of observational studies of etiology, combining studies in meta-analysis may lead to more precise estimates, but such greater precision does not automatically remedy potential bias. Thorough exploration of sources of heterogeneity is key when assessing the validity of estimates and causality.

As many reviews of observational studies on etiology are being performed, this document may provide researchers with guidance on how to conduct and analyse such reviews.


Systematic reviews aim to appraise and synthesise the available evidence addressing a specific research question; a meta-analysis is a statistical summary of the results from relevant studies. A systematic review should generally be the basis of a meta-analysis, whereas a meta-analysis is not a necessary feature of a systematic review if reviewers decide that pooling of effect estimates is not appropriate. Many systematic reviews are based on observational studies. In 2014, of about 8,000 systematic reviews published that year, 36% were on etiology, prognosis, or diagnosis [ 1 ].

Etiological studies examine the association of exposures with diseases or health-related outcomes. Exposures potentially causing diseases are also called risk factors and may take many forms; they can be fixed states (e.g., sex, genetic factors) or vary over time, for example metabolic risk factors (e.g., hypercholesterolemia, insulin resistance, hypertension), lifestyle habits (e.g., smoking, diet), or environmental factors (e.g., air pollution, heat waves). Conceptually, these exposures differ from interventions, which explicitly aim to influence health outcomes and have a clear starting point in time [ 2 ]. Observational studies are important to study exposures that are difficult or impossible to study in randomised controlled trials (RCTs), such as air pollution or smoking. Also, observational studies are important to study causes with long latency time, such as carcinogenic effects of environmental exposures or drugs.

The epidemiological study of risk factors typically relies on comparisons (exposed versus unexposed); such comparisons can be made in cohort studies in which exposed and unexposed people are followed over time [ 3 ]. Other approaches such as self-controlled studies, case-control studies, cross-sectional studies, ecological studies, instrumental variable analyses, and mendelian randomisation also rely on comparisons. Box 1 presents an overview of observational study designs used to study etiology.

Box 1. Observational designs and approaches for studying etiology

Cohort study

Cohort studies follow a study population over time. Researchers can study the occurrence of different outcomes. In etiological research, an exposed and an unexposed group are compared regarding the risk of the outcome. Different levels of exposure and exposures that vary over time can be studied. Instrumental variable methods and self-controlled case series studies are types of cohort studies (see below).

In a large population-based cohort study, the occurrence of infectious complications was compared between patients with and patients without Cushing disease [ 4 ].

Instrumental variable methods/mendelian randomisation

Instrumental variable (IV) analyses use an external factor that determines the exposure of interest but is (ideally) not associated with the outcome other than through its effect on the exposure. In other words, the instrument is not associated with the factors that may confound the association between exposure and outcome. The instrument can be calendar time, geographical area, or treatment preferences [ 5 , 6 ]. Mendelian randomisation studies are examples of IV analyses using genetic factors as instruments.

A Mendelian randomisation study investigated whether more years spent in education increase the risk of myopia or whether myopia leads to more years spent in education [ 7 ].

Self-controlled designs

In self-controlled case series, the occurrence of the outcome is compared between time windows during which individuals are exposed to a risk factor and time windows not exposed. In contrast to standard cohort designs, the comparison is within individuals. The design is used to study transient exposures for which exact timings are available, such as infections, vaccinations, drug treatments, climatic exposures, or disease exacerbations [ 8 ].

A self-controlled study examined the effect of cold spells and heat waves on admissions for coronary heart disease, stroke, or heart failure in Catalonia [ 9 ].

Case-control study

In case-control studies, exposures are compared between people with the outcome of interest (cases) and people without (controls) [ 3 ]. The design is especially efficient for rare outcomes.

A multicentre case-control study examined the association between mobile phone use and primary central nervous system tumours (gliomas and meningiomas) in adults [ 10 ].

Cross-sectional studies

In cross-sectional studies, study participants are assessed at the same point in time to examine the prevalence of exposures, risk factors, or disease. The prevalence of disease is then compared between exposure groups like in a cohort study, or the odds of exposure are compared between groups with and without disease, like in a case-control study [ 3 ]. The temporal relationship between exposure and outcome can often not be determined in cross-sectional studies.

A cross-sectional analysis of the United Kingdom Biobank study examined whether neighbourhood exposure to fast-food outlets and physical activity facilities was associated with adiposity [ 11 ].

Ecological studies

In ecological studies, the association between an exposure and an outcome is studied and compared between populations that differ geographically or in calendar time. Limitations include the ecological fallacy, in which associations observed at the aggregate level do not hold at the individual level and confounding, which is often difficult to control.

An ecological study of male circumcision practices in different regions of sub-Saharan Africa and HIV infection found that HIV prevalence was lower in areas where male circumcision was practiced than in areas where it was not [ 12 ]. The protective effect of male circumcision was later confirmed in randomised trials [ 13 ].

Aim and scope of COSMOS-E

For systematic reviews of randomised trials, guidelines on conduct [ 14 ] and reporting [ 15 ] have been widely adopted. For systematic reviews of observational studies, reporting guidelines were published almost two decades ago [ 16 ], and, to date, there are, to our knowledge, no guidelines on their conduct. Despite similarities in the general structure of the review, the ‘roadmap’ of systematic reviews of observational studies is less standardised [ 17 ], and some design issues are not settled yet [ 18 ]. The aim of Conducting Systematic Reviews and Meta-Analyses of Observational Studies of Etiology (COSMOS-E) is to discuss and give guidance on key issues in systematic reviews of observational studies of etiology for researchers. We address all steps in a review on observational studies, even though some will be similar to reviews of RCTs of medical interventions. COSMOS-E covers the basic principles as well as some more advanced topics but does not address systematic reviews of nonrandomised studies of interventions, or of diagnostic, prognostic, or genetic studies. COSMOS-E is not formally meant to be a guideline; it provides guidance but does not formally prescribe how researchers should perform or report their review. Also, this paper will not settle some ongoing debates and controversies [ 18 ] around the performance of reviews of observational studies on etiology, but rather will give the different viewpoints and possibilities. The writing group included researchers experienced in meta-analyses and observational studies of etiology. No external advise was sought; standard peer-review was performed.

Preparing the systematic review

Building a review team.

At the design stage, the team should cover both content knowledge and methodological expertise. For example, identifying potential confounding variables or assessing exposure measurements requires content knowledge. Similarly, the statistical analysis can often be complex, highlighting the need for statistical expertise. Questions may arise about whether and how different designs (for example, case-control studies and cohort studies) can be combined in meta-analysis or whether a dose-response meta-analysis is feasible. An information specialist will ensure comprehensive and efficient literature searches.

Shaping the research question

A systematic review of observational studies requires a clear research question, which can be broad initially but should be narrowed down subsequently in the interest of clarity and feasibility. In other words, and contrasting with systematic reviews for RCTs, the research question may be iterative. After framing the question, reviewers should scope key papers to get an idea of what evidence is available about the problem, including what type of research has been done. This exploratory step has two aims. It clarifies whether the question has already been addressed in a recent systematic review and indicates whether and how the question needs to be refined and focused so that it can be the subject of feasible systematic review.

Defining population, exposure, contrast, and outcome

In line with the well-known Population, Intervention, Control, and Outcome(s) (PICO) format [ 15 ], for systematic reviews of epidemiological studies, Population, Exposure, Control, and Outcome(s) (PECO) should be defined [ 19 ]. The study population should reflect the target population, i.e., the population to which the results should be applicable [ 20 ]. This can be the general population, as in a meta-analysis of the association of insulin-like growth factor and mortality [ 21 ], or a restricted population, such as in a review of the association between breastfeeding and childhood leukemia [ 22 ]. The study population must be defined such that the exposure–outcome association can be validly studied [ 23 ]. For example, if a radiation exposure is assumed to damage growing tissues, then children are a more appropriate study population than adults (see discussion of ‘study sensitivity’ [ 23 ] later in this article).

Studies on risk factors should ideally include people who are free of the outcome under study at start of follow-up, but this is often unverifiable in population-based studies. Subclinical or early disease might go undetected if such conditions are not ruled out explicitly. In a review on the association between insulin resistance and cardiovascular events, not all population-based studies explicitly excluded participants with cardiovascular disease at baseline. These studies were not excluded but considered at higher risk of bias [ 24 ].

Exposure(s) and outcome(s) should be clearly defined. The definition and measurement of many exposures in observational studies of etiology, such as socioeconomic status, diet, exercise, or environmental chemicals, need careful attention, and the comparability of assessments across studies needs to be assessed. Similarly, many outcomes—such as diseases (e.g., breast cancer, thrombosis, diabetes mellitus) or health-related states (e.g., quality of life, levels of risk factors)—can be defined, classified, or measured in many different ways. Consideration of outcomes thus includes not only ‘what’ is the outcome of interest but also ‘how’ it was determined. Only death is insensitive to method of measurement or ascertainment. The exposure–control comparison also needs attention. In a study of the effect of leisure physical activity, the exposure category (for example, weekly sport for more than 2 hours) might be compared to either less than 2 hours per week or to no sport. Neither of these comparisons is wrong, but they address different questions.

Reviewers may develop precise definitions and criteria for exposure and outcomes, but if no single study used these definitions, the review will not be able to answer the research question. Iteration and pragmatism are required in this situation. In the case of fat mass and cardiovascular risk, a sophisticated exposure measurement—magnetic resonance imaging (MRI)—may have been used only in a few small studies. The reviewers may then decide also to include studies using body mass index or waist:hip ratio, which will ensure the inclusion of more and larger studies. Whether the studies can be combined statistically in a meta-analysis is a different question, which we will address later in this article.

Considering confounding and bias

Confounding is a crucial threat to the validity of observational studies. Confounding occurs when comparison groups differ with respect to their risk of the outcome beyond the exposure(s) of interest due to a common cause of exposure and outcome. When planning the review, researchers should carefully consider which factors might potentially confound the exposure–outcome associations under study. Importantly, confounding is not a yes/no phenomenon but a matter of degree. For example, strong confounding is expected in studies that compare mortality between vegetarians and nonvegetarians because these groups will differ in many other lifestyle characteristics, which will be associated with causes of death. The opposite is true when studying smoking as a cause of lung cancer. There will be little confounding because other strong risk factors for lung cancer are rare, and it is also unlikely that they are strongly associated with smoking. In general, strong confounding is unlikely for adverse effects that were unexpected at the time the study was conducted, for example, the link between asbestos and mesothelioma [ 25 ]. Indeed, substantial confounding may be rare in occupational epidemiology, even by risk factors strongly associated with the outcome of interest [ 26 ].

Other threads to the validity of the effect estimation are measurement (misclassification) bias or selection bias. Misclassification is a crucial bias in environmental and occupational epidemiology, particularly for long-term exposures [ 26 ]. Thinking up front about potential confounding and bias will facilitate the ‘scoping’ of the crucial validity threats for the specific research question and judgments on what types of studies are likely to provide the most unbiased estimate.

The protocol

Every systematic review should be planned in a detailed protocol. The key issues that need to be addressed are listed in Box 2 . It is not always possible to specify fully all review methods beforehand; the writing of the study protocol will often be an iterative process, informed by scoping the literature and piloting procedures. Reviewers should take care not to change the protocol based on study results, but the protocol may be adapted, for example, based on the number and type of available studies. Registering the protocol in the International Prospective Register of Systematic Reviews (PROSPERO) [ 27 ] increases transparency and allows editors, peer reviewers, and others to compare planned methods with the published report and to identify inconsistencies or selective reporting of results. This does not mean that protocol deviations are not possible, but such changes or additions should be made transparent in the reporting phase.

Box 2. Key elements of a protocol for a systematic review of observational studies of etiology

Searching for relevant studies

Searching for eligible studies is a process that includes several steps: (i) selection of electronic databases to be searched (e.g., MEDLINE, EMBASE, specialised databases such as Toxicology Literature Online [Toxline], or databases of regulatory authorities); (ii) developing of search strategies and piloting and refining these in collaboration with an information scientist or librarian [ 28 ]; (iii) consideration of other approaches, such as citation tracking or scrutinising references of key papers; and (iv) deciding whether to search the grey literature (e.g., conference abstracts, theses, preprints). As many relevant studies may be identified in sources other than electronic databases [ 29 , 30 ], searches that extend beyond the standard electronic databases should be considered.

Identification of observational study designs in literature databases is not straightforward, as the indexing of study types can be inaccurate. Several electronic databases should be searched, as no single database has adequate coverage of all the relevant literature [ 31 ]. A bibliographic study concluded that no efficient systematic search strategies exist to identify epidemiologic studies [ 32 ]. Compiling a list of key studies that should be identified is helpful to check the sensitivity of the electronic search strategy. As the number of hits from the search may be very large relative to the number of eligible studies, the challenge is to focus the search as much as possible without compromising sensitivity. Summarized Research in Information Retrieval for Human Technology Assessment (HTA) ( www.sure--info.org ) is a web-based resource that provides guidance on sources to search and on designing search strategies, including search filters to identify observational studies. The incremental value of searching for observational studies in languages other than English has not been evaluated but will depend on the research question. In general, it is prudent to assume that language restrictions could introduce bias. Researchers should search not only for studies on ‘the exposure and outcome’ of interest but have an open mind for studies with negative exposure and outcome controls, ecological and time trend studies of exposure and/or outcome, and papers from basic science.

Study selection

The search produces bibliographic references with information on authors, titles, journals, etc. However, the unit of interest is the study and not the publication—the same study might have been reported more than once [ 33 ], and a single publication can report on multiple studies. First, all identified reports are screened based on title and abstract to remove duplicate publications and articles that are clearly not relevant. This leads to a set of studies for which the full texts are required to determine eligibility and potential overlaps in study populations. Even with clearly defined eligibility criteria, not all decisions will be straightforward. For example, if researchers want to perform a review restricted to children, some studies may have included young adults without providing data for children only. In this case, reviewers may have to decide what proportion of adults is acceptable for a study to be included, or they may attempt to obtain the data on children from the authors.

There is no standard answer to the question of whether study design or methodological quality should guide inclusion of studies [ 18 ]. If, for a specific review, a design characteristic is clearly related to high risk of bias and easy to identify (for example, case-control studies of long-term exposures), then such studies could be excluded upfront. An argument for not restricting reviews in this way is that the assessment of risk of bias will often be subjective to some extent, potentially leading to inappropriate exclusions of studies, and that including all studies may lead to important insights when exploring between-study heterogeneity [ 34 ].

Recording and reporting reasons for exclusions enhances the transparency of the process and informs sensitivity analyses to examine the effect of excluding or including studies. Reviewers should therefore document their decisions throughout the process of study selection and summarise it in a flowchart. Fig 1 gives an example. Dedicated software to support the process of selecting studies may be helpful (see http://systematicreviewtools.com/ ), including tools using machine learning and text mining to partially automate finding eligible studies and extracting data from articles.

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From [ 15 ].

Data extraction

Article screening, data extraction, and assessments of risk of bias should preferably be done independently by two reviewers to reduce errors and to detect any differences in interpretation between extractors [ 35 , 36 ]. Discrepancies can then be discussed and resolved [ 37 ]. Standardised data extraction sheets should be developed for each review, piloted with a few typical studies, refined, and then implemented in generic (for example, EpiData) or preferably dedicated software (for example, Covidence; see http://systematicreviewtools.com ). For all included studies, the following core data should be extracted:

Bibliographic information includes the journal or preprint server, publication year, volume and page numbers, and digital object identifier (doi). The definition of the study design should be based on an assessment of what was done, not on how the study was described in the title or indexed in a database [ 3 ]. Indexing of observational study designs is often inadequate, and authors may themselves confuse designs. In specialty journals, 30%–50% of studies indexed as 'case-control studies' are not in fact case-control studies [ 38 , 39 ]. Characteristics of study participants and outcomes are extracted separately for exposed and unexposed (cohort studies) or cases and controls (case-control studies).

Extracting effect estimates and standard errors

Studies will typically report an effect estimate and a measure of precision (confidence interval) or P value. The effect estimates may be odds ratios, rate ratios, risk ratios, or risk differences for studies with a dichotomous outcome and the difference in means for continuous outcomes. In general, extraction of the standard error or standard deviation may not be straightforward (a standard error may wrongly be described as standard deviation or vice versa), and sometimes, the standard error needs to be calculated indirectly. S1 Box provides practical guidance.

The confounder-adjusted estimates will be of greatest interest for observational studies, but it is useful to additionally extract the unadjusted estimates or raw data. Comparisons of adjusted and crude estimates allow insights into the importance of confounding. Many studies report effect estimates from different models, adjusted for different sets of confounders. In this situation, meta-analyses of maximally adjusted estimates and minimally adjusted or crude estimates may be performed, as was done in a meta-analysis of insulin-like growth factor and cancer risk [ 40 ].

Assessing quality and bias

The assessment of methodological aspects of studies is a crucial component of any systematic review. Observational studies may yield estimates of associations that deviate from true underlying relationships due to confounding or biases. Meta-analyses of observational studies may therefore produce ‘very precise but equally spurious’ results [ 41 ].

The term ‘study quality’ is often used in this context, but it is important to distinguish between quality and risk of bias. The quality of a study will be high if the authors have performed the best possible study. However, a high-quality study may still be at high risk of bias. For example, in a case-control study of lifetime alcohol consumption and endometrial cancer risk, the authors used a state-of-the art population-based design to reduce the risk of selection bias [ 42 ] but had to rely on self-reported alcohol intake over a lifetime. It is likely that some women will have underreported their alcohol intake, introducing social desirability bias [ 43 ].

The concept of ‘study sensitivity’ [ 23 ] refers to the ability of studies to detect a true effect and is more closely related to study quality than bias. If the study is negative, does this really mean that there is evidence for no exposure–outcome association? For example, were the numbers of exposed persons sufficient and the levels and duration of exposure adequate to detect an effect? [ 23 ]. Was follow-up long enough to allow for the development of the cancer of interest? Study sensitivity is particularly relevant in occupational and environmental epidemiology but is also of great concern in pharmacoepidemiology in the context of adverse effects of drugs. Reviewers should consider assessing both the risk of bias and study sensitivity in reviews of observational studies.

Risk of bias in individual studies: Confounding, selection bias, and information bias

Many possible sources of bias exist, and different terms are used to describe them. Bias typically arises either from flawed collection of information or selection of participants into the study so that an association is found that deviates from the true value. Typically, bias is introduced during the design or implementation of a study and cannot be remedied later.

In contrast to bias, confounding produces associations that are real but not causal because some other, unaccounted factor is associated with both exposure and outcome ( Box 3 ). Time-dependent confounding is a special case of confounding ( S2 Box ). Confounding can be adjusted for in the analysis if the relevant confounding variables have been well measured, but some residual confounding may remain after adjustment ( Box 4 ). Confounding is often confused with selection bias. In particular, the situation in which comparison groups differ with respect to an important prognostic variable is often described as selection bias. The term selection bias should, however, be used only for the situation in which participants, their follow-up time, or outcome events are selected into a study or analysis in a way that leads to a biased association between exposure and outcome. Directed acyclic graphs (DAGs) are useful to clarify the structures of confounding and selection bias (see Box 3 ) [ 44 ]. Another important category of bias is information bias, in which systematic differences in the accuracy of exposure or outcome data may lead to differential misclassification of individuals regarding exposures or outcomes. Bias needs to be distinguished from random error, a deviation from a true value caused by chance variation in the data. Finally, it is important to note that confounding and selection bias refer to biases that are internal to the study (‘internal validity’) and not to issues of generalisability or applicability (‘external validity’) [ 20 ]. How should the risk of bias in observational studies best be assessed? A review identified more than 80 tools for assessing risk of bias in nonrandomised studies [ 45 ]. The reviewers concluded that there is no ‘single obvious candidate tool for assessing quality of observational epidemiological studies’. This is not surprising considering the large heterogeneity in study designs, contexts, and research questions in observational research. We believe that the quest for a ‘one size fits all’ approach is misguided; rather, a set of criteria should be developed for each observational systematic review and meta-analysis, guided by the general principles outlined below.

Box 3. The causal structures of confounding and selection bias

A directed acyclic graph (DAG) consists of (measured and unmeasured) variables and arrows. They are useful to depict causal structures: arrows are interpreted as causal effects of one variable on another [ 37 ]. Common causes of exposure and outcome confound the association between exposure and outcome. For example, as shown in the DAG in Fig 2 , the association between yellow fingers and lung cancer is confounded by smoking. The association is spurious, i.e., it is entirely explained by smoking.

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Selection bias occurs if the probability of inclusion into the study depends both on the exposure and the outcome. In a hospital-based case-control study, inclusion into the study naturally depends on being admitted to the hospital; it is conditional on hospitalisation. For example, in a case-control study of alcohol and prostate cancer, the inclusion of controls hospitalised because of injuries suffered in traffic accidents will introduce an association between alcohol consumption and prostate cancer because alcohol is a cause of traffic accidents ( Fig 2 for a graphical display). In general, conditioning on common effects of exposure and outcome means that the probability of inclusion depends on the exposure and outcome, which leads to selection bias. This structure applies to many biases, including nonresponse bias, missing data bias, volunteer bias or health worker bias, or bias due to loss of follow-up in cohort studies [ 44 ]. All of these biases have the causal structure of selection bias.

Box 4. Approaches to deal with confounding in observational studies

Statistical adjustment in the analysis

Statistical adjustment for confounding can be performed using standard regression techniques (for example, Cox or logistic regression). All of these models, including more advanced techniques such as propensity scores [ 46 ] or inverse probability weighting, rely on the assumption of no unmeasured confounding for the validity of the effect estimate. This assumption is often unlikely to hold in practice because some confounding factors may not have been assessed or have not been measured precisely. Residual confounding may therefore persist after adjustment, which should be taken into account when interpreting combined estimates from meta-analysis of observational studies.

Matching is an intuitive approach to control for confounding at the design stage of a study, particularly in case-control research [ 47 ]. The choice of the variables, exact approach to matching, and the statistical analysis are complex and need careful consideration. Bias may be introduced, for example, when matching for variables that are on the causal pathway from exposure to disease [ 3 ]. Matching is particularly relevant in situations in which the distribution of important confounders differs substantially between cases and unmatched controls [ 48 ].

Instrumental variable methods

Instrumental variables may be useful to control for confounding [ 49 ]. An instrument is an external variable that is associated with the exposure of interest but ideally is not associated with the outcome variable other than through its effect on the exposure. In essence, instrumental variables circumvent the problem of unmeasured confounding. For example, mendelian randomisation studies make use of common genetic polymorphisms (for example, the rs1229984 variant in the alcohol dehydrogenase 1B gene) that influence levels of modifiable exposures (alcohol intake [ 50 ]). As with any other instrumental variable analysis, the validity of mendelian randomisation depends critically on the absence of a relationship between the instrument (genes) and the outcome (for example, cardiovascular disease) [ 5 ].

Negative controls

The use of ‘negative controls’ for outcomes or exposures can be helpful to assess the likely presence of unmeasured or residual confounding in observational research [ 51 ]. The rationale is to examine an association that cannot plausibly be produced by the hypothesised causal mechanism but may be generated by the same sources of bias or confounding as the association of interest. For example, it has been hypothesised that smoking increases the risk of depression and suicide because of effects on serotonin and monoamine oxidase levels [ 52 ]. However, in large cohort studies, smoking is also positively associated with the risk of being murdered—the negative, biologically implausible outcome control [ 53 ]. Similarly, in cohort studies, vaccination against influenza not only protected against hospitalisation for pneumonia but also against hospitalisation for injury or trauma [ 46 ], indicating that the beneficial effect on pneumonia may have been overestimated. Negative exposure controls are usefully introduced in questionnaires to gauge possible recall bias in case-control studies. A study of the association between multiple sclerosis (MS) and childhood infections included questions on other childhood events not plausibly associated with MS, such as fractures and tonsillectomy [ 54 ].

General principles

When assessing the risk of bias, seven general principles are relevant, based on theoretical considerations, empirical work, and the experience with assessing risk of bias in RCTs and other studies [ 55 – 57 ].

1. The relevant domains of bias should be defined separately for each review question and for different study designs

Relevant domains of risk of bias that should be considered include (i) bias due to (time-dependent) confounding, (ii) bias in selection of participants into the study (selection bias), (iii) bias in measurement of exposures or outcomes (information bias), (iv) bias due to missing data (selection bias), and (v) bias in selection of studies or reported outcomes (selection bias) [ 56 ]. The risk of bias should be assessed for each domain and, if required, for different outcomes. The focus should be on bias. For example, whether or not a sample size calculation was performed or ethical approval was obtained does not affect the risk of bias.

2. The risk of bias should be assessed qualitatively

For each study and bias domain, the risk of bias should be assessed in qualitative categories, for example, as ‘low risk’, ‘moderate risk’, or ‘high risk’. These categories and the criteria used to define them should be described in the paper. Quantitative assessments by assigning points should be avoided (see also point 6).

3. Signalling questions may be useful

Within each bias domain, simple signalling questions may be useful to facilitate judgments about the risk of bias ( Table 1 ). A comprehensive list of signalling questions has recently been compiled by the developers of the Cochrane risk of bias assessment tool for nonrandomised studies of interventions (ROBINS-I) [ 56 ], and a similar tool is in development for nonrandomised studies of exposures [ 58 ]. These lists and tools will be useful, but reviewers should think about further questions that may be relevant in the context of their review. Cooper and colleagues compiled a list of questions relating to study sensitivity [ 23 ].

4. Separate assessments may have to be made for different outcomes

The risk of bias will often differ across different outcomes. For example, bias in the ascertainment of death from all causes is much less likely than for a subjective outcome, such as quality of life or pain, or for an outcome that relies on clinical judgment, such as pneumonia.

5. Assessments should be documented

It is good practice to copy and archive the text from the article on which an assessment regarding the risk of bias is based. Such documentation increases transparency, facilitates discussion in case of disagreement, and allows for replication of assessments.

6. Summary scores should be avoided

Summary scores involve weighting of bias domains; typically, each item in a score is weighted equally (0 or 1 point), but the importance of a bias will depend on the context, and one bias may be more important than another [ 59 , 60 ]. The situation is made worse if the scale includes items that are not consistently related to bias. For example, the Newcastle-Ottawa Scale includes quality items of questionable validity, such as comparable nonresponse among cases and controls [ 61 ]. Rather than calculating summary scores, a conservative approach classifies the study at the level of risk of bias corresponding to the highest risk identified for individual domains.

7. Thinking about a hypothetical, unbiased trial may be helpful

It may useful, as a thought experiment, to think of a hypothetical RCT that would answer the review question posed in the systematic review [ 56 ]. Such a trial will often be unfeasible and unethical, but the thought experiment may help to sharpen the review question and clarify the potential biases in the observational studies. S3 Box gives an example.

Reporting biases, P hacking, and analytic choices

An important source of bias that may undermine conclusions from any systematic review or meta-analysis is the selective publication of studies. It is known that studies with ‘positive’ results (i.e., statistically significant effects) are more likely to be published than negative studies, introducing a distorted overall picture of an association. There is robust evidence of publication bias and other reporting biases for RCTs [ 62 , 63 ]: positive trials are more likely to be published, to be published quickly, to be published more than once, and to be cited, making it more likely that they will be included in systematic reviews.

Selective publication of results may also be a problem within studies, when many different exposures and outcomes were examined. If only the statistically significant associations are fully analysed, written up, and published, the results of systematic reviews will be distorted. A related issue arises when the selection of the study population or statistical model is chosen based on the P value (‘ P hacking’) [ 64 ].

How to deal with risk of bias?

Results from the risk of bias analysis should be presented in a transparent way, tabulating risk of bias elements for each included study. An important consideration is how to deal with studies at high risk of bias. If the aim is to present the best available evidence on the efficacy of a medical intervention, the review is often restricted to studies at low risk of bias. For systematic reviews of observational studies of etiology, we generally advise against excluding studies based on risk of bias assessments. Including all studies and exploring the impact of the risk of different biases and of study sensitivity on the results in stratified or regression analyses will often provide additional insights, as discussed below.

Exploring and exploiting heterogeneity

The studies included in a systematic review will generally vary with respect to design, study populations, and risk of bias [ 1 ]. Mapping of heterogeneity between studies [ 65 ] may not only provide a useful overview but also help decide whether or not to combine studies statistically in a meta-analysis. Such diversity may provide opportunities for additional insights and can explicitly be exploited [ 66 ]. For example, the association of Mycobacterium avium subspecies paratuberculosis (MAP) with Crohn disease was examined in a review of case-control studies that compared cases of Crohn disease with controls free of inflammatory bowel disease or with ulcerative colitis patients [ 67 ]. The association was strong for both comparisons, indicating that the association with MAP is specific to Crohn disease and not a general (epi)phenomenon in inflammatory bowel disease (see also Box 4 on negative controls).

Diversity in study settings also may provide insights. Lifestyle factors such as smoking, physical activity, sexual behaviour, or diet are exposures of interest in many observational studies, but they are highly correlated in Western societies. Their independent effects, for example, on cancer risk, are therefore difficult to disentangle. The inclusion of studies in special populations, for example, defined by religion or geographical regions with different lifestyle patterns, may therefore help understand (residual) confounding. Similarly, studies that measured exposures and confounding factors more or less precisely, used different methods to adjust for confounding variables ( Box 4 ), or were generally at higher or lower risk of bias will be valuable in this context. For example, a meta-analysis showed that the relationship between induced abortion and breast cancer was evident in case-control studies but not in cohort studies [ 68 ]: the association observed in case-control studies was probably due to recall bias.

The thoughtful exploitation of sources of heterogeneity at the design stage or exploration in the analysis are therefore an important part of systematic reviews and meta-analyses of observational studies of etiology. Analyses should either be prespecified in the study protocol or interpreted in the spirit of exploratory data analyses. Exploration of heterogeneity starts with the visual inspection of forest plots and funnel plots. Statistical techniques include subgroup analyses and metaregression, as discussed below.

Meta-analysis: To pool or not to pool?

After careful examination of risk of bias and other sources of heterogeneity, reviewers must consider whether statistically combining effect estimates is appropriate for all studies, for a subgroup of studies, or not appropriate at all. Authors provide different reasons for not pooling data [ 69 ], and different opinions exist on how to approach this question [ 18 ]. Considerations for or against pooling should be based on judgments regarding study diversity, sensitivity, and risk of bias rather than solely on statistical measures of heterogeneity (see below) for two reasons. First, in the absence of statistical heterogeneity, combining results from biased studies will produce equally biased combined estimates with narrow confidence intervals that may wrongly be interpreted as definitive evidence. The inclusion of studies at high risk of bias will often, but not always, introduce heterogeneity. For example, the protective effect of a diet rich in beta-carotene on cardiovascular mortality shown in observational studies was very consistent across studies. However, randomised trials of beta-carotene supplementation did not show any benefit, making it likely that the results of observational studies were confounded to a similar extent by other aspects of a healthy diet and lifestyle [ 41 ]. Second, even in the presence of statistical heterogeneity, combining studies may be appropriate if studies are at low risk of bias and results are qualitatively consistent, indicating some degree of benefit or risk. If authors decide not to provide one overall pooled estimate, stratified meta-analyses (by study design or population) may be considered. Be mindful that a systematic review that documents heterogeneity and risk of bias will still provide a valuable contribution even without a formal meta-analysis.

Statistical analysis

Fixed- versus random-effect models in the context of observational studies.

Once the decision has been made that (some) studies can be combined in a meta-analysis, reviewers need to decide whether to use a fixed-effect or a random-effects model or both. These models have been described extensively [ 70 ]. In short, fixed-effect analyses assume that all studies estimate the same underlying effect and that differences between effect estimates are due to sampling variation. In contrast, random-effects models assume that underlying true effects vary between studies. In the presence of statistical heterogeneity, effect estimates will differ because smaller studies receive more weight in the random-effects than in the fixed-effect model, and the random-effects confidence interval will be wider because it additionally incorporates the between-study variation. In the absence of statistical heterogeneity, results from random- and fixed-effect models will be identical.

In observational studies, population characteristics and exposure or outcome definitions will likely differ across studies. The assumption that all these studies estimate the same underlying effect is rarely justified, and using a random-effects model for combining observational studies therefore seems reasonable [ 18 ]. An important consideration in this context is the question of whether, for a given research question, smaller or larger studies are at greater risk of bias. In clinical research, large multicentre trials tend to be at lower risk of bias than small single-centre studies, supporting the use of fixed-effect models. The opposite may be the case in observational etiological research, for which smaller studies may have collected better data on exposures and confounders. The model to be used should be specified in advance, but presenting results from both models in a sensitivity analysis may be informative. Of note, although random-effects models allow for between-study heterogeneity, they do not help to understand the sources of heterogeneity [ 71 ].

Statistical measures of between study heterogeneity

Methods to assess statistical heterogeneity include the I 2 statistics and Cochrane’s Q test for heterogeneity. The Q test assesses whether variation between effect estimates is likely due to chance alone; the I 2 statistic quantifies the amount of variation between studies that cannot be attributed to chance [ 72 ]. These measures should be interpreted with caution: the I 2 statistic is captured with uncertainty [ 73 ], and Cochrane’s Q test has limited power to detect heterogeneity when the number of included studies is low [ 74 ]. Since the number of studies included in a review of observational studies is typically 10 to 20 [ 1 ], statistical power will generally be low. Moreover, the statistical verdict on presence or absence of heterogeneity does not need to coincide with the reviewers’ judgment on presence or absence of study diversity or risk of bias. It might be that important study diversity does not translate into statistical heterogeneity.

Funnel plot (a)symmetry

A funnel plot is a graphical tool to investigate whether estimates from smaller studies differ from those of larger studies. Effect sizes are plotted against the standard error or precision of the estimate (which relate to study size) [ 75 ]. If estimates from different studies differ only because of random variation, then they will scatter symmetrically around a central value, with variation decreasing as precision increases. The plot will thus resemble an inverted funnel. Asymmetry of the funnel plot means that there is an association between study size and effect estimates or a ‘small study effect’ [ 76 ], with smaller studies typically showing larger effects. This may be due to several reasons, including true heterogeneity (i.e., smaller studies differ from larger ones in terms of study population, exposure levels, etc.), selection bias (i.e., the selective publication of small studies showing an effect), bias in design or analysis, or chance [ 77 , 78 ]. Asymmetry should not be equated with publication bias. Particularly in the context of observational studies, there are many other sources of heterogeneity and funnel plot asymmetry.


Metaregression is used to investigate whether study characteristics are associated with the magnitude of effects and whether specific study characteristics can explain (some of) the observed statistical heterogeneity. The presence of heterogeneity motivates metaregression analyses, and random-effects metaregression should therefore always be used. The use of fixed-effect metaregression is conceptually nonsensical and yields a high rate of false-positive results [ 79 ].

Variables included in a metaregression model may be study features, such as study design, year of publication, or risk of bias; or characteristics of the people included in the different studies, such as age, sex, or disease stage. These variables are potential effect modifiers. For example, the risks of smoking decrease with advanced age. Only a few variables should be included in a metaregression analysis (about one variable per 10 studies), and they should be prespecified to minimise the risk of false-positive results [ 80 ]. In multivariable metaregression, the model presents mutually adjusted estimates, and permutation tests to adjust for multiple testing can be considered [ 80 ]. When including characteristics of study participants, note that associations observed at the study level may not reflect those at the individual level—the so-called ecological fallacy [ 81 ]. This phenomenon is illustrated in Fig 3 for trends in the CD4 positive lymphocyte count in HIV-positive patients starting antiretroviral therapy (ART): in five of the six studies, the CD4 cell count at the start of ART increased over time, which was not shown in metaregression analysis at the study level. A graphical display of the metaregression is informative [ 82 ]. Such a graph shows for each study the outcome (e.g., a relative risk or a risk difference) on the y-axis, the explanatory variable on the x-axis, and the regression line that shows the association between two variables. In a metaregression graph, the weight of the studies is preferably shown by ‘bubbles’ around the effect estimates, with larger bubbles relating to studies with more weight in the analysis ( Fig 3 provides a schematic example).

An external file that holds a picture, illustration, etc.
Object name is pmed.1002742.g003.jpg

Hypothetical example of aggregate and individual level CD4 cell count data at the start of ART. Adapted from [ 83 ]. ART, antiretroviral therapy.

Combining different metrics

Meta-analyses depend on how data are presented in individual articles. Especially in the context of observational studies, researchers may face the problem that different metrics are used for the same exposure–outcome association, depending on study design or statistical models used. Consider the association between smoking (exposure) and blood pressure (outcome). In cohort studies, hazard ratios, incidence rate ratios, risk ratios, or odds ratios can be estimated when the outcome is dichotomized, whereas mean difference or standardised mean difference may be reported if this is not the case.

How can different metrics be combined in meta-analysis? There are two issues to consider, one conceptual, one more technical. When studies report different ratio metrics, for example, hazard ratios, risk ratios, or odds ratios, they may be combined ignoring the differences in metrics. This may be appropriate depending on which study designs were included (cohort studies or case-control studies) and how participants were sampled in case-control studies [ 84 , 85 ]. As a general rule, the different ratio metrics can be combined if the outcome under study is rare (<5%), which is often the case in etiologic studies. If the outcome is not rare, researchers must be more careful because the odds ratio will substantially overestimate the relative risk. This property of the odds ratio is a reflection of the fact that for non-rare outcomes, the odds is larger than the risk (for example, if the risk is 0.8, the corresponding odds is 4).

It is also possible to combine relative risks with other metrics like standardised mean differences or correlation coefficients. This requires transformation from an odds ratio in a standardised mean difference (or vice versa) [ 86 ] or an odds ratio in a correlation coefficient [ 87 , 88 ]. For example, in a meta-analysis of the association between fibrinogen levels on postoperative blood loss, studies reported odds ratios, regression coefficients, correlation coefficients, and/or P values [ 89 ]. All effect measures were transformed into correlation coefficients and subsequently combined in a meta-analysis [ 89 ].

Dose-response meta-analysis

In many epidemiologic studies, several levels of exposure are compared. For example, the effect of blood glucose on cardiovascular outcomes can be studied across several groups of glucose levels, using one category as reference. However, different studies may report different categories of the exposure variable (tertiles, quartiles, or quintiles). One approach is to meta-analyse the estimates by comparing the lowest and highest category. This is not recommended because the meaning of lowest versus highest differs across studies. A more sophisticated approach is to model the association between the exposure and outcome to estimate the increase (or decrease) in risk associated with one unit (or other meaningful incremental) increase in exposure. See references for technical details [ 90 , 91 ]. For example, a meta-analysis of the association between Homeostasis Model Assessment Insulin Resistance (HOMA-IR) and cardiovascular events used dose-response modelling to estimate that the cardiovascular risk increased by 46% per one standard deviation increase in HOMA-IR [ 24 ].

Interpretation and discussion of results

Reviewers should discuss their results in a balanced way: many of the included studies might be far from perfect, even if the overall estimate comes with a narrow confidence interval [ 41 ], and researchers should keep in mind that statistical significance is not an indicator of whether a true relation exists or not. Big numbers cannot compensate for bias. If included studies have a low risk of bias and heterogeneity does not seem large, researchers may conclude that the main results provide reasonably valid estimates. On the other hand, if many studies are at high risk of bias, researchers should conclude that the true effect remains uncertain. The Grades of Recommendation, Assessment, Development, and Evaluation (GRADE) system can be helpful to formally judge ‘the extent of our confidence that the estimates of an effect are adequate to support a particular decision or recommendation’ [ 92 ], taking into account study design, risk of bias, degree of inconsistency, imprecision and indirectness (applicability) of results, and reporting bias [ 93 ].

One or a few studies might suffice to demonstrate that a relevant bias likely exists and that all other studies suffer from it. For example, many cohort studies have shown that higher C-reactive protein (CRP) levels are associated with cardiovascular risk. However, other cardiovascular risk factors, including smoking, obesity, and physical activity, are associated with higher CRP levels, and these may confound the association with cardiovascular disease levels [ 94 ]. No association was seen in mendelian randomisation studies [ 94 ], which used genetic variants that are related to CRP levels but independent of the behavioural or environmental risk factors that confound the association in epidemiological studies [ 95 ] (see Box 1 ). Mendelian randomisation studies and classic cohort studies in fact estimate different ‘effects’: lifelong exposure in mendelian randomisation versus exposure from a certain (often not well-defined) time-point onward. It should be noted that when mendelian randomisation studies include participants later in life, selection bias may occur [ 96 ]. Evidence from mendelian randomisation studies, if available, should always be taken into account when interpreting the results from systematic reviews of epidemiological studies. A useful guide for reading mendelian randomisation studies has recently been published [ 97 ].

When assessing causality, integration of different sources of evidence (e.g., ecological studies, basic research on mechanisms) may facilitate a final judgement; trying to obtain an integrated verdict based on results from different analytic or epidemiologic design approaches, for which each approach has different and preferably unrelated sources of potential bias, is called triangulation [ 98 ]. If different approaches all point to the same conclusion, this strengthens confidence that the finding may be causal [ 98 ]. For example, in the discussion on smoking and lung cancer, time trends in lung cancer were an important argument against the hypothesis that an inherited trait would cause lung cancer as well as smoking [ 99 ]. Discussing competing explanations systematically will add value to the interpretation of the results [ 100 ]. Especially in the field of toxicology, mechanistic evidence plays an important role in causal inference, and systematic review of this literature is encouraged [ 17 ]. Clearly, understanding pathways requires more than quickly searching for a few articles that support the hypothesis ('cherry picking') [ 17 ]. Systematic reviews on insulin-like growth factor or adiposity and cancer risk took laboratory, animal, and human evidence into account to judge the plausibility of different mechanisms [ 40 , 101 ].

Finally, the importance of the results in terms of clinical and public health relevance should be discussed. The identification of likely causes does not necessarily translate into recommendations for interventions [ 102 ]. For example, based on epidemiological and other evidence, obesity probably increases the risk of several cancers [ 101 , 103 ], but this does not mean that losing weight will reduce cancer risk. Obesity may have exerted its detrimental effect, and different interventions to reduce obesity have different effects on cancer risk [ 104 ].

An important strength of systematic reviews is that they generate a clear overview of the field and identify the gaps in the evidence base and the type of further research needed. The usual statement that 'more research is needed' can thus be replaced by detailed recommendations of specific studies. Furthermore, having assessed the strengths and limitations of many studies, reviewers will be in an excellent position to name the pitfalls that need to be avoided when thinking about future research.

Supporting information


Douglas Altman died on June 3, 2018. We dedicate this paper to his memory.


Funding statement.

ME was supported by special project funding (Grant No. 174281) from the Swiss National Science Foundation. The funders had no role in study design, data collection and analysis, decision to publish, or preparation of the manuscript

Provenance : Not commissioned; externally peer reviewed.

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Systematic review of case-control studies: oral contraceptives show no effect on melanoma risk


Background: Parallel to the rising incidence of malignant melanoma in fair-skinned populations, intensive efforts are currently devoted to identifying risk factors for melanoma in addition to the well-known cutaneous factors and those variables related to UV-exposure.

Objective: Systematic review of published results to elucidate the role of oral contraceptives in the development of malignant melanoma.

Data sources: Literature retrieval systems MEDLINE and CANCERLIT as well as reference lists of already collected studies.

Study selection: All 18 (non-duplicate) case-control studies on the above relationship.

Data extraction: From the published data, study-specific odds ratios (OR) and accompanying confidence intervals (CI) were recalculated. For a quantitative meta-analytical summarisation two different models have been applied: a "fixed effects" (FE) and a "random effects" (RE) model.

Data synthesis: Study-specific ORs ranged from 0.13 up to 1.85; however, the majority of studies (14 of 18) yielded similar ORs within the interval [0.82, 1.15]. The summary ORs estimated from FE- and RE-models were both 0.95 (95% CI: [0.87, 1.04] for the FE-model, [0.87, 1.05] for the RE-model).

Conclusion: The systematic review of case-control studies revealed no evidence for an aetiological role of oral contraceptives in the development of malignant melanoma.

PIP: A systematic review of the research literature was conducted to elucidate the role of oral contraceptives (OCs) in the development of malignant melanoma. The retrieval systems MEDLINE and CANCERLIT identified 18 case-control studies of this relationship and study-specific odds ratios (ORs) were recalculated in the meta-analysis. These ORs ranged from 0.13 to 1.85; however, the majority of studies yielded ORs within the 0.82-1.15 range. The summary ORs estimated from both fixed effects and random effects models were each 0.95; the 95% confidence intervals were 0.87-1.04 and 0.87-1.05, respectively, indicating no association. Separate analyses of the OC-malignant melanoma association by year of study publication, type of case group, source of the control group, and type of exposure ascertainment corroborated this lack of significant effect.

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Systematic Reviews: Levels of evidence and study design

Levels of evidence.

"Levels of Evidence" tables have been developed which outline and grade the best evidence. However, the review question will determine the choice of study design.

Secondary sources provide analysis, synthesis, interpretation and evaluation of primary works. Secondary sources are not evidence, but rather provide a commentary on and discussion of evidence. e.g. systematic review

Primary sources contain the original data and analysis from research studies. No outside evaluation or interpretation is provided. An example of a primary literature source is a peer-reviewed research article. Other primary sources include preprints, theses, reports and conference proceedings.

Levels of evidence for primary sources fall into the following broad categories of study designs   (listed from highest to lowest):

Based on information from Centre for Reviews and Dissemination. (2009). Systematic reviews: CRD's guidance for undertaking reviews in health care. Retrieved from http://www.york.ac.uk/inst/crd/index_guidance.htm

Hierarchy of Evidence Pyramid

"Levels of Evidence" are often represented in as a pyramid, with the highest level of evidence at the top:

what is a systematic review of case control studies

Types of Study Design

The following definitions are adapted from the Glossary in " Systematic reviews: CRD's Guidance for Undertaking Reviews in Health Care " , Centre for Reviews and Dissemination, University of York :

EBM and Study Design

Edith Cowan University acknowledges and respects the Noongar people, who are the traditional custodians of the land upon which its campuses stand and its programs operate. In particular ECU pays its respects to the Elders, past and present, of the Noongar people, and embrace their culture, wisdom and knowledge.

Effect of childhood BMI on asthma: a systematic review and meta-analysis of case-control studies

BMC Pediatrics volume  18 , Article number:  143 ( 2018 ) Cite this article

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Asthma is a multifactorial syndrome that threatens the health of children. Body mass index (BMI) might be one of the potential factors but the evidence is controversial. The aim of this study is to perform a comprehensive meta-analysis to investigate the association between asthma and BMI.

Electronic databases including, Web of Science, Pubmed, Scopus, Science Direct, ProQuest, up to April 2017, were searched by two researchers independently. The keywords “asthma, body mass index, obesity, overweight, childhood and adolescence” were used. Random and fixed effects models were applied to obtain the overall odds ratios (ORs) and standardized mean difference (SMD). Heterogeneity between the studies was examined using I 2 and Cochrane Q statistics.

After reviewing 2511 articles, 16 studies were eligible for meta-analysis according to inclusion/exclusion criteria. A meta-analysis from 11 case-control studies revealed OR of asthma and overweight as OR = 1.64; (95% Confidence Interval (CI): 1.13–2.38) and from 14 case-control studies, OR for asthma and obesity was OR = 1.92 (95% CI: 1.39–2.65), which indicated that risk of asthma in overweight and obese children and adolescence was significantly higher (1.64 and 1.92 times) than that of individuals with ( p -value < 0.01 for underweight/normal weight in both cases). Furthermore, there was a significant relationship between asthma and BMI > 85 percentile according to SMD SMD = 0.21; (95%CI: 0.03–0.38; p-value = 0.021).


The results showed a significant relationship between BMI (obesity/overweight) and asthma among children and adolescents. It is important to study the confounding factors that affect the relationship between asthma and BMI in future epidemiological researches.

Peer Review reports

There are some hypotheses for the relationship between asthma and obesity since the number of the cases diagnosed with these two disorders over the last two decades has increased [ 1 ]. Asthma is a chronic clinical respiratory syndrome that is accompanied by the inflammation of respiratory ducts, obstruction, and airway hyper responsiveness [ 2 ]. It is caused by a combination of factors and complicated interaction between hereditary traits, air pollution, respiratory tract infection, and exposure to triggers such as cigarette smoking [ 3 ]. These factors influence the response of the disease to treatment and its severity [ 4 ]. It is estimated that 7.1 million individuals under 18 years of age were currently afflicted with asthma and 4.1 million suffered from periodic asthma or asthma attack in 2011 (United States) [ 5 ]. Over the last three decades, prevalence of obesity has doubled and quadrupled among children and adolescents [ 6 , 7 ] and along with other mechanisms, obesity may cause shortness of breath as well. It is known that aggregation of soft fatty tissues around the chest increases pressure on the lungs, increases blood volume at the area, and consequently, decreases the capacity of the respiratory system. Furthermore, other mechanical effects of obesity may cause limitations to airways and hypersensitivity [ 1 ]. So, lack of enough physical activity among asthma patients and physiological respiratory changes of obese patients may cause the two diseases to be interrelated [ 8 ].

There are four previous meta-analyses conducted by Chen [ 9 ], Flaherman [ 10 ], Egan [ 11 ] and Mebrahtu [ 12 ] in which Relative Risk (RR) or Odds Ratio (OR) for relationships between asthma and overweight among children were reported. Three of these meta-analyses are based on cohorts (Chen, Egan and Flaherman) and the other one is based on any observational studies including cohort, case-control, and cross-sectional. Chen and Egan applied subgroup analysis just for gender but they didn’t conduct a cumulative meta-analysis. Flaherman considered studies that reported both high birth weight and high BMI in school aged children for cumulative meta-analysis and they reported OR and RR and applied subgroup analysis for physician diagnosis. Mebrahtu was more consistent in investigating this association by determining OR in different weight categories. We applied an intensive search and employed comprehensive analyses not only based on OR estimates, but also we considered SMD analysis, cumulative meta-analysis and adjusted ORs. Subgroup analyses for gender, age, continents, and asthma diagnosis method, year of publication and sample size were applied. In addition, case-control studies have been considered for risk ratio assessment.

This systematic review was based on Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) guidelines [ 13 ] (Additional file 1 : PRISMA Checklist S1).

Criteria of research

All case-control studies on the relationship between BMI and asthma among childhood and adolescence regardless of time and place of study were considered, language was limited to English.

Search strategy

A comprehensive search was undertaken via Web of Science (1983 to 10 April of 2017), PubMed /Medline (1966 to 10 April of 2017), Scopus (1960 to 10 April of 2017), Science Direct (1823 to 10 April of 2017), ProQuest (1993 to 10 April of 2017), Google Scholar ( web search engine ), and Eastern Mediterranean Region databases (IMEMR) (1984 to 10 April of 2017). Medical subject headings (MeSH) keywords such as “asthma, BMI, obesity, overweight, childhood and adolescence” were used for our search in scientific journals, conferences, dissertations, theses and reports. All references to relevant articles (manually) were also investigated.

For example, the following box represents the search strategies in PubMed

“Asthma” [MeSH]

Childhood [MeSH]

Adolescence [MeSH]

#1 AND #2 AND #3

“Body mass Index” [MeSH]

“Obesity” [MeSH]

“Overweight” [MeSH]

Asthma diagnosis

The case group (asthmatic) was diagnosed either by a physician or by completion of the ISSAC (The International Study of Asthma and Allergies in Childhood) questionnaire by a parent or adolescent. The control group (non-asthmatic) consisted of those who were not diagnosed with asthma.

BMI criteria

The following criteria were considered in assessing the exposure factor (BMI): 1. Age-sex-specific BMI percentiles were obtained based on Centers for Disease Control and Prevention (CDC) growth chart (see Table  1 ). 2. Age-sex-specific cut-off points (underweight18.5 kg/m 2 , overweight: 25 kg/m 2 and obesity 30 kg/m 2 ) by the International Obesity Task Force (IOTF) [ 14 ]. 3. Reference data for obesity with normal being < 85 th , obese > 85 th - <95th and very obese ≥95 th [ 15 ]. 4. The BMI percentile values with underweight being ≤P5, Malnutrition >P5- ≤ P15, normal >P15- < P85, overweight ≥P85- < P95, obese ≥P95 [ 16 ]. 5. The BMI-Z score based on CDC growth chart. 6. The overweight/obesity when the BMI- standard deviation score (SDS) units (z-score) was ≥2 [ 17 ]. (It is notable that we used BMI percentiles based on the CDC growth chart (2014) where underweight < 5th, normal ≥5th- < 85th, overweight≥85th- < 95th and obese ≥95th [ 18 ] and the categorization method of the IOTF for exposure (BMI)).

Article selection

Searching databases using keywords and extracting data from articles were done independently by two researchers (Azizpour and Sayehmiri) in order to avoid risk of bias. An abstract of each article was screened for eligibility according to inclusion/exclusion criteria and then the full text was reviewed for data extraction. In cases of disagreement between the two reviewers, a third researcher reviewed the article and a final decision was made after careful discussion. The relevant articles were selected according to inclusion/exclusion criteria. Inclusion criteria were case-control studies on the relationship between asthma and BMI, studies on children and adolescents (2–19 years old), and in the English language. Studies on adults, irrelevance of the subject, the relationship between BMI and asthma severity, cross-sectional and cohort studies and any relationship between breast feeding and asthma were excluded. For the quality assessment of studies we used, the Joanna Briggs Institute (JBI) Critical Appraisal Tools [ 19 ]. The quality score is determined by the range 67–100 (good), 34–66 (average), and 0–33 (bad).

Data extraction

An appropriate data extraction form was designed including author (s) name, sample size, country of study, age group (case and control), method of asthma diagnosis, year of publication, time of study, and the exposure assessment method (BMI). The following data, if available, are extracted to evaluate the association between BMI and asthma.

Frequency of obesity, overweight and underweight/normal in childhood and adolescence (based on CDC growth chart (2014), and IOTF) in both case and control groups (binary outcome) to obtain OR and RR.

Mean and standard deviation (M ± SD) of BMI based on BMI or BMI-Z score in case and control groups (continuous measure) to obtain SMD.

Adjusted OR to evaluate the association between BMI and asthma.

The above data were also collected for different gender, age, continents, and asthma diagnosis method, year of publication and sample size for the purpose of subgroup analyses.

Statistical analyses

The following three methods were employed to aggregate the extracted data and drive the summary effect of an association between asthma and BMI:

Method 1: OR and RR were calculated when classified BMI (overweight/obesity) for control and case groups were reported ( \( {OR}_i=\frac{a_i{d}_i}{b{{}_ic}_i} \) , \( RR=\frac{a/\left(a+b\right)}{c/\left(c+d\right)} \) ), then Der Simonian and Laird method (random effects model) were used to combine the OR S or RR S .

Cumulative meta-analysis was used for pooled estimates to show whether the year of publication or year of the new study has any essential effect on the final results.

Method 2: To derive the summary effects for studies that reported the effect size for case and control groups based on the mean and standard deviation (SD) of BMI, or BMI-Z score, we first calculated the mean difference of each study as follows:

SMD: standardized mean difference.

SD: pooled standard deviation

S 1 2 : Variance of the case group

S 2 2 : Variance of the control group

n 1 : Number of samples in the case group

n 2 : Number of samples in the control group

Afterwards, to find the overall SMD of all articles, Der Simonian and Laird method (random effects model) was used to combine the result of studies with the “metan” command (from STATA).

Method 3: Ln transformation, Ln ( OR ) of each adjusted OR and associated confidence interval was calculated by using the following formula for standard error:

where OR Upper is upper limit of OR and OR Lower is lower limit of OR [ 20 ].

Then the inverse variance method (fixed effect model) was used to obtain the overall effect size (ES), and the anti-log of the overall ES was taken to come back to the original OR, ( e ln (OR) ).

Subgroups analyses were performed for gender, age, continent, sample size, year of publication and asthma diagnosis methods.

In addition, I 2 and Cochrane Q Statistics were used [ 21 ] to investigate the heterogeneity of the data. I 2 was considered in four levels; I 2  = 0% indicated no heterogeneity, 25% to − 50% for low, 50% to 75% for moderate, and more than 75% for high heterogeneity [ 22 ]. A random or fixed model was used according to the heterogeneity factor whereas random effects models [ 23 , 24 ] were used for heterogeneous studies and fixed effects models otherwise.

Begg’s test was used to check publication bias. All data analyses were performed in STATA version 10 and a p -value < 0.05 was considered as statistically significant.

Literature search and data collection

In total, 2511 titles were found from which 2348 were removed after reviewing abstracts. Out of 163 potentially related articles, 30 were duplicates and 14 were removed since the ages of the participants were out of our scope. In addition, 69 cross-sectional and 23 cohort studies were also removed. Afterwards, out of 27 articles, 11 case-control studies were removed for the following reasons: Two articles were not in English (One in Romanian [ 25 ] and the other in Portuguese [ 26 ]), the population of one study was breastfeeding [ 27 ], one article studied the relationship between asthmatic with current and no current wheeze and BMI [ 28 ], four studies were on age range childhood-adult [ 29 , 30 , 31 , 32 ], one in which case-control groups were asthmatic with and without allergic rhinitis [ 33 ], and finally two studies focused on persistent asthma as the case group and Intermittent asthma as the control group [ 34 , 35 ] (2001 to 2016). Finally, 16 case-control articles from 1998 to 2017 were entered into the study (Fig.  1 ).

Flowchart of selecting the article

Overall, 9 studies in the United States of America and Canada (North America), 2 in Peru and Brazil (South America), 3 in Montenegro, Greece and Italy (Europe) and 2 in Iran and Saudi Arabia (Asia) were identified with an age range of 2.2–18 years of age in case group and 2.4–18 years of age in control groups; in total 3577 individuals were in the case group and 4820 individuals were in the control group. In 13 studies, asthma was diagnosed by a physician, in 2 studies by a parent and in 1 study asthma was reported by adolescents. In 8 studies exposure was assessed according to BMI percentiles based on CDC growth charts, one study in which BMI-Z score was based on CDC growth chart, 4 studies in which BMI cut off point was based on IOTF, one study was based on reference data, one study was based on the BMI percentile values and one study was based on BMI- SDS units (z-score); also quality scores of the whole manuscript were good, see Table 1 .

Overall OR for overweight individuals

Meta-analysis derived OR = 1.64 (95% CI: 1.13–2.38, p -value = 0.01) from 11 case-control studies reported OR of asthma and overweight; moderate heterogeneity was observed between studies (Heterogeneity chi-squared = 35.91 (df = 10) p -value = 0.0001 and I 2  = 72.2%) (Fig.  2a ); However the reported relative risk was RR = 1.26 (95% CI: 1.07–1.48, p-value = 0.006). A cumulative meta-analysis showed that by combining the studies that were done before 2007, there was a significant association between overweight and asthma. By adding new studies from 2007 to 2012 to previous studies the cumulative effect of being overweight on asthma was not significant, while by adding studies that were done from 2013 to 2016 to previous studies, the cumulative effect of being overweight on asthma showed significant effects. (Fig. 2b ). Meta-regression analysis showed that there was no significant statistical relationship between OR of asthma in overweight individuals and the year of publication. This means that the year of publication is not a reason for heterogeneity. (Correlation Coefficient = − 0.10, p -value = 0.260) (Fig. 2c ).

Meta-analysis based on 11 case-control studies which reported asthma in overweight individuals. a Forest plots of estimate of overall odds ratio asthmatic b cumulative meta-analysis and c meta-regression analysis with OR of asthma in overweight individual and year of publication

Overall OR for obesity

In total, 14 case-control studies reported OR of asthma and obesity; meta-analysis revealed an association between them; OR = 1.92; (95% CI: 1.39–2.65, p-value = 0.0001). Furthermore, high heterogeneity was observed between studies (chi-squared = 50.49 (df = 13) p -value = 0.0001 and I2 = 74.3%) (Fig.  3a ), as well as relative risk which was RR = 1.40; (95%CI: 1.19–1.63, P -value =0.0001). Cumulative meta-analysis showed that one study was done in 1998 with significant association between obesity and asthma. Adding new studies from 2005 to 2008 to previous studies showed that the cumulative effect of obesity on asthma was not significant. On the other hand, adding studies from decade of 2008 to 2017 to previous ones; a significant association was observed based on the cumulative effect of obesity on asthma (Fig. 3b ). Meta-regression analysis didn’t identify any significant statistical relationship between OR for asthma in obese individuals and the year of publication. This means that the reason of heterogeneity is not the year of publication (Correlation Coefficient = − 0.15, p-value = 0.08) (Fig. 3c ). Overall ES of asthma based on adjusted OR.

Meta-analysis based on 14 case-control studies which reported asthma in obesity individuals. a Forest plots of estimate of overall odds ratio asthmatic b cumulative meta-analysis and c meta-regression analysis with OR of asthma in obese individual and year of publication

Three studies with 740 cases and 1169 controls were reported ES = 1.30 (95% CI: 1.12–1.49; p -value < 0.001), that confirm a significant increased risk of asthma for individuals with BMI greater than the 85th percentile.

Overall SMD for asthma and BMI

The overall standard mean difference (SMD) based on 10 studies with 2761 cases, and 3281 controls, and the results showed a significant relationship between asthma and BMI (SMD = 0.21; 95% CI: 0.03–0.38; p -value = 0.021), for individuals with BMI greater than the 85th percentile.

Subgroup analyses for asthma and overweight / obesity

Analysis showed that the risk of asthma in obese and overweight children during 2009–2017 was increased in comparison with the decade of 1998–2008. Furthermore, the risk of asthma in obese and overweight girls was greater than the risk of asthma in obese and overweight boys. Asian children and adolescents had a risk of asthmatic attacks three times more likely than children in the American continent (Table  2 ).

Subgroup analyses based on SMD

We found that there were significant relationships between BMI (greater than the 85th percentile) and asthma in a) both genders, b) results reported in 2009–2017, c) America and the Asian continent, d) children younger than 11 years old and e) groups of children whose asthma were reported by Physicians (Table  3 ) according to SMD.

In order to evaluate the publication bias of studies, Begg’s test and the Funnel plot were employed. For articles related to overweight children, the p -value = 0.312 (Fig.  4a ); for articles related to obesity the p -value =0.090 (Fig. 4b ) and this identified that publication bias was not significant which shows that the majority of the query articles had the same opportunities to be published.

Begg’s funnel plot (pseudo 95% confidence limits) showings the effect of publication bias. a Overweight group and b Obese group

We determined that the risk of asthma in individuals who were overweight and obese was 1.64 times and 1.92 times more likely than individuals who were underweight/normal weight respectively. The ES obtained from a combination of adjusted the OR in BMI > 85 percentile was 1.30 (significant difference). Moreover, according to SMD, the relationship between asthma and BMI was significant. Beuther et al. noted that, based on the studies of animals, inflammation of airways due to allergic/non-allergic factors increased through the use of leptin from internal and external sources [ 36 ]. The relationship between obesity and asthma could be explained by a number of hypotheses, for example, obesity through hormonal influences or mechanisms of genetic factors which may have direct effects on immune system response or phenotype of asthma. Furthermore, an increased risk of asthma may be explained by a combination of genetic predisposition factors with birth weight, movement of the body that uses energy, and nutrition, as potentially linked to obesity [ 37 ]. So asthma is an outcome of a complicated combination of environmental and genetic factors for which we do not have thorough knowledge [ 38 , 39 ]. However, the key point is that along with the increased risk of asthma with obesity, there are internal and external factors that count as confounders which might influence the relationship between asthma and BMI. The results from our meta-analyses showed a significant relationship between overweight/obesity and asthma, but the important result is that by removing the confounding factors, the effect size was reduced from 1.64 and 1.92 (in the overweight/obese) to 1.30. In this review, five studies reported adjusted OR according to different sets of confounding factors. The confounding factors in Henkin’s research were atopic dermatitis, allergic rhinitis, and other allergies [ 40 ]; in Papoutsakis’ research OR was adjusted for age, gender, education, atopic background of parents, calorie intake, breastfeeding, and physical activity score [ 41 ]; Forno et al. considered family income, the asthma record of parents, age, gender, and race to adjust the OR [ 42 ]; Also Nahhas considered the parents’ age, birth weight, education, smoker parents, physical activity, exposure to animals, watching TV, allergens, and gender as confounding factors [ 43 ]. Lawson et al. considered age, gender, mother’s education, having a asthmatic record in the family, early respiratory illness, smoker mother, smoking during pregnancy, dog at home in last 12 months, cleaning or playing in pens or corrals regularly and farm dwelling as factors to adjust the OR [ 44 ].

Analyses based on OR in the subgroups showed that overweight and obesity increased the risk of asthma in both genders (girls more than boys); however, the relationship was not significant, probably due to a small number of studies and sample size, so we need more studies dealing with a larger sample size to obtain more accurate results. Moreover, a significant association was identified between BMI and the risk of asthma in both genders (girls more than boys) based on SMD. The SMD is a calculated quantitative index based on the difference between the means in the case and control groups (continuous variable) which follows a normal distribution. This index has more precision than OR since OR is calculated on the basis of frequency of variables. In addition, the two articles that found significant SMD are different from the articles which found insignificant OR in terms of the exposure factor. Chen et al. reported that obese and overweight boys were at higher risk of asthma compared to girls [ 9 ] but the results of Egan et al. found a significant relationship between overweight and asthma in boys and obesity and asthma in girls [ 11 ].

Obesity is firmly connected to breathing disorders and influences the function of the lungs. In fact, the high percentage of excessive body fat compresses the lungs and limits the free air movement because of its mechanical effect on the airways via central body fat [ 45 ]. Gender, atopy, family history of asthma (non-modifiable), and obesity (one of the few modifiable) are risk factors for asthma [ 46 ]. Even though exercise has minimal impact on lung function in asthmatic children, it should still be recommended by health care providers [ 47 ]. The difference in risks by continent may indicate the effect of the environment or race on the hazard of asthma. In general, healthcare providers overseeing obese kids and wishing to control their asthma should consider interventions such as weight loss, physical activity, and normalization of nutrient levels. Monitoring of complications related to obesity with designed prospective and clinical trial studies should also be taken into account.


One of the main limitations of this research was the variety of methods used in reporting the results e.g., some studies reported M ± SD (mean ± standard deviation) and others reported OR. In addition, definitions of obesity and overweight were not consistent over different studies. The number of studies was also another limitation. Furthermore, meta-analysis for case-control studies cannot identify the causal-temporal relationships between BMI and asthma.

Based on our findings, we noted that BMI is a significant factor when it comes to asthma. We found that obesity and being overweight increase the risk of asthma. A thorough investigation to recognize the confounding factors on the relationship between asthma and BMI is also important for future epidemiological research.


Centers for Disease Control and Prevention

Confidence interval

Effect size

International Obesity Task Force

The International Study of Asthma and Allergies in Childhood

Joanna Briggs Institute

Medical subject headings

Odds ratios

Preferred Reporting Items for Systematic Reviews and Meta-analyses

Relative risk

Standard deviation

Standard deviation score

Standardized mean difference

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Kourosh Sayehmiri

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YA, KS conceived the idea and preformed the literature search. YA, AD, KS contributed to the literature search, data extraction and study selection. KS preformed all the statistical analyses. YA, KS interpreted the results. YA wrote the manuscript. ZM and BD contributed in designing the study, and were involved in drafting and revising the manuscript it. All authors approved the final version of the manuscript.

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Azizpour, Y., Delpisheh, A., Montazeri, Z. et al. Effect of childhood BMI on asthma: a systematic review and meta-analysis of case-control studies. BMC Pediatr 18 , 143 (2018). https://doi.org/10.1186/s12887-018-1093-z

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what is a systematic review of case control studies

Study Design 101

A study that compares patients who have a disease or outcome of interest (cases) with patients who do not have the disease or outcome (controls), and looks back retrospectively to compare how frequently the exposure to a risk factor is present in each group to determine the relationship between the risk factor and the disease.

Case control studies are observational because no intervention is attempted and no attempt is made to alter the course of the disease. The goal is to retrospectively determine the exposure to the risk factor of interest from each of the two groups of individuals: cases and controls. These studies are designed to estimate odds.

Case control studies are also known as "retrospective studies" and "case-referent studies."


Design pitfalls to look out for

Care should be taken to avoid confounding, which arises when an exposure and an outcome are both strongly associated with a third variable. Controls should be subjects who might have been cases in the study but are selected independent of the exposure. Cases and controls should also not be "over-matched."

Is the control group appropriate for the population? Does the study use matching or pairing appropriately to avoid the effects of a confounding variable? Does it use appropriate inclusion and exclusion criteria?

Fictitious Example

There is a suspicion that zinc oxide, the white non-absorbent sunscreen traditionally worn by lifeguards is more effective at preventing sunburns that lead to skin cancer than absorbent sunscreen lotions. A case-control study was conducted to investigate if exposure to zinc oxide is a more effective skin cancer prevention measure. The study involved comparing a group of former lifeguards that had developed cancer on their cheeks and noses (cases) to a group of lifeguards without this type of cancer (controls) and assess their prior exposure to zinc oxide or absorbent sunscreen lotions.

This study would be retrospective in that the former lifeguards would be asked to recall which type of sunscreen they used on their face and approximately how often. This could be either a matched or unmatched study, but efforts would need to be made to ensure that the former lifeguards are of the same average age, and lifeguarded for a similar number of seasons and amount of time per season.

Real-life Examples

Boubekri, M., Cheung, I., Reid, K., Wang, C., & Zee, P. (2014). Impact of windows and daylight exposure on overall health and sleep quality of office workers: a case-control pilot study . Journal of Clinical Sleep Medicine : JCSM : Official Publication of the American Academy of Sleep Medicine, 10 (6), 603-611. https://doi.org/10.5664/jcsm.3780

This pilot study explored the impact of exposure to daylight on the health of office workers (measuring well-being and sleep quality subjectively, and light exposure, activity level and sleep-wake patterns via actigraphy). Individuals with windows in their workplaces had more light exposure, longer sleep duration, and more physical activity. They also reported a better scores in the areas of vitality and role limitations due to physical problems, better sleep quality and less sleep disturbances.

Togha, M., Razeghi Jahromi, S., Ghorbani, Z., Martami, F., & Seifishahpar, M. (2018). Serum Vitamin D Status in a Group of Migraine Patients Compared With Healthy Controls: A Case-Control Study . Headache, 58 (10), 1530-1540. https://doi.org/10.1111/head.13423

This case-control study compared serum vitamin D levels in individuals who experience migraine headaches with their matched controls. Studied over a period of thirty days, individuals with higher levels of serum Vitamin D was associated with lower odds of migraine headache.

Related Formulas

Related Terms

A patient with the disease or outcome of interest.


When an exposure and an outcome are both strongly associated with a third variable.

A patient who does not have the disease or outcome.

Matched Design

Each case is matched individually with a control according to certain characteristics such as age and gender. It is important to remember that the concordant pairs (pairs in which the case and control are either both exposed or both not exposed) tell us nothing about the risk of exposure separately for cases or controls.

Observed Assignment

The method of assignment of individuals to study and control groups in observational studies when the investigator does not intervene to perform the assignment.

Unmatched Design

The controls are a sample from a suitable non-affected population.

Now test yourself!

1. Case Control Studies are prospective in that they follow the cases and controls over time and observe what occurs.

a) True b) False

2. Which of the following is an advantage of Case Control Studies?

a) They can simultaneously look at multiple risk factors. b) They are useful to initially establish an association between a risk factor and a disease or outcome. c) They take less time to complete because the condition or disease has already occurred. d) b and c only e) a, b, and c

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Hypertension and the risk of endometrial cancer: a systematic review and meta-analysis of case-control and cohort studies

Scientific Reports volume  7 , Article number:  44808 ( 2017 ) Cite this article

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A history of hypertension has been associated with increased risk of endometrial cancer in several studies, but the results have not been consistent. We conducted a systematic review and meta-analysis of case-control and cohort studies to clarify the association between hypertension and endometrial cancer risk. PubMed and Embase databases were searched up to 27 th of February 2016. Prospective and case-control studies which reported adjusted relative risk estimates and 95% confidence intervals of endometrial cancer associated with a hypertension diagnosis were included. Summary relative risks were estimated using a random effects model. Nineteen case-control studies and 6 cohort studies were included. The summary RR was 1.61 (95% CI: 1.41–1.85, I 2  = 86%) for all studies, 1.73 (95% CI: 1.45–2.06, I 2  = 89%) for case-control studies and 1.32 (95% CI: 1.12–1.56, I 2  = 47%) for cohort studies. The association between hypertension and endometrial cancer was weaker, but still significant, among studies with adjustment for smoking, BMI, oral contraceptive use, and parity, compared to studies without such adjustment. This meta-analysis suggest an increased risk of endometrial cancer among patients with hypertension, however, further studies with more comprehensive adjustments for confounders are warranted to clarify the association.


Hypertension is a major cause of morbidity and mortality worldwide and is an established risk factor for coronary heart disease and stroke 1 , 2 . Globally a high systolic blood pressure accounted for 10.4 million deaths and 208.1 million disability-adjusted life-years (DALYs) in 2013 3 . Important risk factors for hypertension include overweight and obesity 4 , low physical activity 5 , 6 , high alcohol consumption 7 , dietary factors 8 , 9 , 10 , 11 , and use of non-narcotic analgesics 12 .

Endometrial cancer is the eighth most common type of cancer in women with approximately 320 000 cases recorded in 2012, accounting for about 4.8% of all cancers in women (2.3% overall) 13 . It is more common in high-income countries than in low-income countries, however, its incidence has been increasing in populations undergoing urbanization and economic growth, in parallel with increasing obesity rates and sedentary lifestyles 14 , 15 . Several risk factors for endometrial cancer have been established including excess body weight 16 , low physical activity 17 , diabetes history 18 , and use of unopposed hormone replacement therapy 19 . A history of hypertension has been evaluated as a risk factor for endometrial cancer in several case-control 20 , 21 , 22 , 23 , 24 , 25 , 26 , 27 , 28 , 29 , 30 , 31 , 32 , 33 , 34 , 35 , 36 , 37 , 38 and cohort studies 39 , 40 , 41 , 42 , 43 , 44 , and many 20 , 21 , 24 , 25 , 26 , 28 , 30 , 32 , 33 , 34 , 35 , 36 , 37 , 38 , 39 , 42 , 44 , but not all 22 , 23 , 27 , 29 , 31 , 39 , 42 , 44 of these found an increased endometrial cancer risk. Because obesity and diabetes are important risk factors for both hypertension 45 , 46 and endometrial cancer 16 , 18 it is not clear whether the association between hypertension and endometrial cancer could be due to confounding by these factors because some studies did not adjust for BMI 20 , 21 , 25 , 33 , 35 , 38 or diabetes 20 , 21 , 24 , 25 , 28 , 29 , 33 , 35 , 38 . We conducted a systematic review and meta-analysis of case-control and cohort studies that had investigated the association between hypertension and endometrial cancer risk with an aim of clarifying the strength of the association, possible sources of heterogeneity and potential confounding by other risk factors.

Search strategy and inclusion criteria

We searched the PubMed and Embase databases up to 27 th February 2016 for eligible studies. We used the following search terms in the PubMed search: (hypertension OR high blood pressure OR blood pressure OR risk factor) AND (endometrial cancer OR uterine cancer). We followed standard criteria for reporting meta-analyses 47 .

Study selection

We included published retrospective case-control studies and cohort studies that investigated the association between hypertension and the risk of endometrial cancer. Adjusted estimates of the relative risk (odds ratios and hazard ratios which were considered to be approximately equal given that endometrial cancer is a relatively uncommon cancer) had to be available with the 95% CIs in the publication. A list of excluded studies and exclusion reasons is provided in Supplementary Table 1 . DA and AS conducted the study selection.

Data extraction

The following data were extracted from each study: The first author’s last name, publication year, country where the study was conducted, study period, sample size, number of cases/controls, exposure and subgroups of tumor characteristics (low, moderate or high aggressiveness) or cancer type (type 1 vs. type 2), relative risks and 95% confidence intervals for the association and variables adjusted for in the analysis. Data were extracted by one reviewer (DA) and checked for accuracy by a second reviewer (AS).

Statistical methods

We calculated summary relative risks of developing endometrial cancer by history of hypertension using the random-effects model by DerSimonian and Laird 48 which takes into account both within and between study variation (heterogeneity). The average of the natural logarithm of the relative risks was estimated and the relative risk from each study was weighted by the inverse of its variance 49 .

Heterogeneity between studies was evaluated using Q and I 2 statistics 50 . Cochran’s Q is calculated as the weighted sum of squared differences between individual study effects and the pooled effects across studies, with weights being those in the pooling method. I 2 is a measure of how much of the heterogeneity that is due to between study variation rather than chance. I 2 -values of 25%, 50% and 75% indicates low, moderate and high heterogeneity respectively. We conducted main analyses (all studies combined) and stratified by study design (cohort studies, case-control studies) because of the greater potential for recall and selection bias in retrospective case-control studies and to investigate sources of potential heterogeneity. We also conducted subgroup analyses by other study characteristics such as sample size, number of cases, geographic location, and by adjustment for confounding factors. We also conducted a stratified analysis by whether the articles explicitly stated that participants with prevalent hysterectomies at baseline were excluded, and/or whether participants with incident hysterectomies were censored during follow-up in cohort studies, or excluded from the control group in case-control studies.

Publication bias was assessed using Egger’s test 51 and Begg-Mazumdar’s test 52 and by inspection of funnel plots. Study quality was assessed using the Newcastle-Ottawa scale which ranks the studies on a scale from 0 to 9 based on the selection of the study population, comparability between cases and non-cases and the assessment of the outcome 53 . The statistical analyses were conducted using the software package Stata, version 13.0 software (StataCorp, Texas, US).

Out of a total 7879 records identified by the search we included 25 studies with 28385 cases and 300598 participants in the meta-analysis of hypertension and endometrial cancer risk, including six cohort studies 39 , 40 , 41 , 42 , 43 , 44 and nineteen case-control studies 20 , 21 , 22 , 23 , 24 , 25 , 26 , 27 , 28 , 29 , 30 , 31 , 32 , 33 , 34 , 35 , 36 , 37 ( Fig. 1 and Tables 1 and 2 ). Fourteen of the studies were from North-America, seven were from Europe, and four were from Asia ( Tables 1 and 2 ).

figure 1

Flow-chart of study selection.

The summary RR for all studies was 1.61 (95% CI: 1.41–1.85, I 2  = 86%), and it was 1.73 (95% CI: 1.45–2.06, I 2  = 89%) for case-control studies and 1.32 (95% CI: 1.12–1.56, I 2  = 47%) for cohort studies ( Fig. 2 ), however, the test for heterogeneity by study design was not significant, p = 0.19. In sensitivity analyses excluding one study at a time the summary RR ranged from 1.49 (95% CI: 1.34–1.65) when excluding the study by Zhang et al . 33 to 1.65 (95% CI: 1.41–1.94) when excluding the study by Trabert et al . 36 . There was evidence of publication bias with Egger’s test, p = 0.005 ( Fig. 3 ), however, when stratified by study design this was observed among case-control studies, p = 0.007, but not among cohort studies, p = 0.78.

figure 2

Hypertension and endometrial cancer, forest plot.

figure 3

Hypertension and endometrial cancer, funnel plot.

Subgroup and sensitivity analyses, study quality assessment

There were positive associations in almost all subgroup analyses ( Table 3 ), and although there was no heterogeneity when stratified by study design, geographic location or number of cases, there was indication of heterogeneity when studies were stratified by confounding factors including smoking (p = 0.02), BMI (p = 0.003), oral contraceptive use (p = 0.02), hormone replacement therapy (p = 0.08), parity (p = 0.03), and age at menopause (p = 0.07), with weaker, but still significant associations among studies with such adjustments. When we conducted sensitivity analyses removing one study at a time, the size of the summary estimate persisted and did not vary substantially ( Supplementary Table 2 ).

In a further sensitivity analysis we also conducted a subgroup analysis by whether the studies explicitly stated that they excluded participants with prevalent hysterectomies at baseline and/or stated that they censored participants at the time of incident hysterectomy (cohort studies) or excluded participants who had undergone hysterectomy from the control group (case-control studies). The summary RR was 1.51 (95% CI: 1.28–1.78, I 2  = 88.5%) for studies with such exclusions or censoring and 1.81 (95% CI: 1.49–2.20, I 2  = 56.5%) for studies without such exclusions or censoring.

In a sensitivity analysis we also included a pooled analysis which assessed the association between quintiles of systolic blood pressure and endometrial cancer risk 54 , using the relative risk for the highest vs. the lowest quintile of systolic blood pressure. The results were not materially altered, summary RR = 1.61 (95% CI: 1.42–1.83, I 2  = 38%) for all studies and 1.33 (95% CI: 1.16–1.52, I 2  = 86%) for cohort studies. Further including another cohort study 55 which reported on elevated blood pressure (≥130/≥85 vs. <130/<85 mm/Hg) or self-reported hypertension, not only hypertension, did also not substantially alter the results, summary RR = 1.57 (95% CI: 1.38–1.78, I 2  = 85%) for all studies and summary RR = 1.28 (95% CI: 1.12–1.48, I 2  = 46%) for cohort studies. Mean (median) study quality scores were 7.3 (7.0) for all studies combined, 7.3 (7.0) for case-control studies, and 7.3 (7.0) for cohort studies).

To our knowledge this is the first meta-analysis of published observational studies of hypertension and the risk of endometrial cancer and our results confirm that hypertension is a strong risk factor for endometrial cancer with a 61% increase in the relative risk, however, the association was weaker in cohort studies (RR = 1.32) than among case-control studies (RR = 1.73). These findings are consistent with a large cohort study of 290 000 women in Austria, Norway and Sweden which found an increased endometrial cancer risk with increasing levels of diastolic blood pressure and in particular, systolic blood pressure 54 . The results also persisted in a sensitivity analysis including the results from this cohort study 54 as well as the EPIC study 55 , which reported on elevated blood pressure or hypertension.

The present meta-analysis has some limitations. As hypertension is a condition that is strongly related to lifestyle factors and some medical conditions including diet, BMI, physical activity, and diabetes we cannot entirely exclude the possibility that the observed association between hypertension and endometrial cancer risk at least partly could be due to confounding. We found that the association was weaker, but still statistically significant, among studies that adjusted for smoking, BMI, oral contraceptive use, hormone replacement use, parity and age at menopause (RR = 1.14–1.34 for studies with such adjustment vs. 1.74–2.10 for studies without such adjustment). However, because there was still a significant association in subgroups that adjusted for these factors it could indicate that there is an adverse effect of hypertension on endometrial cancer risk, but that it may be slightly weaker than what was suggested from the overall summary estimates. Because the original studies did not stratify for BMI or diabetes it was not possible for us to investigate whether the association was limited to specific weight classes or if it was modified by diabetes status.

We also found that the positive association between hypertension and endometrial cancer persisted when the studies were stratified by whether participants with prevalent hysterectomies at baseline were excluded and/or whether participants with incident hysterectomies were censored, or whether prevalent hysterectomies were excluded from the control group. Hypertension may also be related to hysterectomies 56 , 57 , 58 , and could potentially bias the risk estimates, however, any bias would most likely be toward the null. We cannot exclude the possibility of residual confounding from other risk factors such as use of intrauterine device 59 , polycystic ovarial syndrome 60 , or other potential risk factors that the original studies may not have adjusted for.

Case-control studies are more likely to be affected by certain biases, such as recall bias and selection bias. Because we included both case-control and cohort studies there is a possibility that recall or selection bias might have affected the results in the case-control studies and the overall summary estimate. Although the association appeared to be stronger in case-control studies than among cohort studies, there was still a significant association among cohort studies, which suggest that recall bias or selection biases does not entirely explain the observed association. In addition, there was some indication of publication bias with Egger’s test, but this appeared to be restricted to the analyses of case-control studies and all studies combined, and was not observed among the cohort studies.

The biological mechanism(s) that may explain an adverse effect of hypertension on endometrial cancer risk are unclear at present. It has been suggested that long-term hypertension may lead to cellular senescence and inhibition of apoptosis 61 . It has also been suggested that medications used for the treatment of hypertension could increase cancer risk, however, a meta-analysis found little evidence of an association with overall cancer 62 , and a cohort study found no relation with female genital cancers 63 , although few studies have specifically investigated endometrial cancer.

Strengths of the present meta-analysis include the comprehensive search strategy, the detailed subgroup and sensitivity analyses, and the large sample size providing a more robust estimate of the association between hypertension and endometrial cancer risk. To date relatively few studies have investigated the association between hypertensive disorders of pregnancy and endometrial cancer risk with one study suggesting an increased risk with hypertensive disorders overall 64 , while another study found no association with preeclampsia overall, although an increased risk was observed with early-onset preeclampsia 65 . Any further studies could better assess the causality of the observed association between hypertension and endometrial cancer by using genetic risk scores for hypertension 66 , 67 . In addition, clarification of potential effect modification by age at exposure, BMI and diabetes status, and further studies of the association with subtypes of endometrial cancer are needed.

In conclusion, the results from this systematic review and meta-analysis suggest that women with hypertension may have a 61% increase in the relative risk of developing endometrial cancer. Any further studies should clarify potential effect modification by age, BMI and diabetes status, and the causality of the observed association, as well as the potential underlying mechanism(s).

Additional Information

How to cite this article: Aune, D. et al . Hypertension and the risk of endometrial cancer: a systematic review and meta-analysis of case-control and cohort studies. Sci. Rep. 7 , 44808; doi: 10.1038/srep44808 (2017).

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Change history

06 april 2018.

A correction has been published and is appended to both the HTML and PDF versions of this paper. The error has not been fixed in the paper.

Scientific Reports 7: Article number: 44808; published online: 07 April 2017; updated: 06 April 2018. In this Article, Abhijit Sen and Lars J. Vatten are incorrectly listed with ‘Department of Epidemiology and Biostatistics, Imperial College, London, UK’. The correct affiliation for these authors islisted below:

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This work has been supported by funding from the Liaison Committee between the Central Norway Regional Health Authority (RHA) and the Norwegian University of Science and Technology (NTNU) and by the Imperial College National Institute of Health Research (NIHR) Biomedical Research Centre (BRC).

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Dagfinn Aune, Abhijit Sen & Lars J. Vatten

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Aune, D., Sen, A. & Vatten, L. Hypertension and the risk of endometrial cancer: a systematic review and meta-analysis of case-control and cohort studies. Sci Rep 7 , 44808 (2017). https://doi.org/10.1038/srep44808

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Cohort, cross sectional, and case-control studies are collectively referred to as observational studies. Often these studies are the only practicable method of studying various problems, for example, studies of aetiology, instances where a randomised controlled trial might be unethical, or if the condition to be studied is rare. Cohort studies are used to study incidence, causes, and prognosis. Because they measure events in chronological order they can be used to distinguish between cause and effect. Cross sectional studies are used to determine prevalence. They are relatively quick and easy but do not permit distinction between cause and effect. Case controlled studies compare groups retrospectively. They seek to identify possible predictors of outcome and are useful for studying rare diseases or outcomes. They are often used to generate hypotheses that can then be studied via prospective cohort or other studies.


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Cohort, cross sectional, and case-control studies are often referred to as observational studies because the investigator simply observes. No interventions are carried out by the investigator. With the recent emphasis on evidence based medicine and the formation of the Cochrane Database of randomised controlled trials, such studies have been somewhat glibly maligned. However, they remain important because many questions can be efficiently answered by these methods and sometimes they are the only methods available.

The objective of most clinical studies is to determine one of the following—prevalence, incidence, cause, prognosis, or effect of treatment; it is therefore useful to remember which type of study is most commonly associated with each objective (table 1)

While an appropriate choice of study design is vital, it is not sufficient. The hallmark of good research is the rigor with which it is conducted. A checklist of the key points in any study irrespective of the basic design is given in box 1.

Study purpose

The aim of the study should be clearly stated.

The sample should accurately reflect the population from which it is drawn.

The source of the sample should be stated.

The sampling method should be described and the sample size should be justified.

Entry criteria and exclusions should be stated and justified.

The number of patients lost to follow up should be stated and explanations given.

Control group

The control group should be easily identifiable.

The source of the controls should be explained—are they from the same population as the sample?

Are the controls matched or randomised—to minimise bias and confounding.

Quality of measurements and outcomes

Validity—are the measurements used regarded as valid by other investigators?

Reproducibility—can the results be repeated or is there a reason to suspect they may be a “one off”?

Blinded—were the investigators or subjects aware of their subject/control allocation?

Quality control—has the methodology been rigorously adhered to?


Compliance—did all patients comply with the study?

Drop outs—how many failed to complete the study?

Missing data—how much are unavailable and why?

Distorting influences

Extraneous treatments—other interventions that may have affected some but not all of the subjects.

Confounding factors—Are there other variables that might influence the results?

Appropriate analysis—Have appropriate statistical tests been used?

All studies should be internally valid. That is, the conclusions can be logically drawn from the results produced by an appropriate methodology. For a study to be regarded as valid it must be shown that it has indeed demonstrated what it says it has. A study that is not internally valid should not be published because the findings cannot be accepted.

The question of external validity relates to the value of the results of the study to other populations—that is, the generalisability of the results. For example, a study showing that 80% of the Swedish population has blond hair, might be used to make a sensible prediction of the incidence of blond hair in other Scandinavian countries, but would be invalid if applied to most other populations.

Every published study should contain sufficient information to allow the reader to analyse the data with reference to these key points.

In this article each of the three important observational research methods will be discussed with emphasis on their strengths and weaknesses. In so doing it should become apparent why a given study used a particular research method and which method might best answer a particular clinical problem.


These are the best method for determining the incidence and natural history of a condition. The studies may be prospective or retrospective and sometimes two cohorts are compared.

Prospective cohort studies

A group of people is chosen who do not have the outcome of interest (for example, myocardial infarction). The investigator then measures a variety of variables that might be relevant to the development of the condition. Over a period of time the people in the sample are observed to see whether they develop the outcome of interest (that is, myocardial infarction).

In single cohort studies those people who do not develop the outcome of interest are used as internal controls.

Where two cohorts are used, one group has been exposed to or treated with the agent of interest and the other has not, thereby acting as an external control.

Retrospective cohort studies

These use data already collected for other purposes. The methodology is the same but the study is performed posthoc. The cohort is “followed up” retrospectively. The study period may be many years but the time to complete the study is only as long as it takes to collate and analyse the data.

Advantages and disadvantages

The use of cohorts is often mandatory as a randomised controlled trial may be unethical; for example, you cannot deliberately expose people to cigarette smoke or asbestos. Thus research on risk factors relies heavily on cohort studies.

As cohort studies measure potential causes before the outcome has occurred the study can demonstrate that these “causes” preceded the outcome, thereby avoiding the debate as to which is cause and which is effect.

A further advantage is that a single study can examine various outcome variables. For example, cohort studies of smokers can simultaneously look at deaths from lung, cardiovascular, and cerebrovascular disease. This contrasts with case-control studies as they assess only one outcome variable (that is, whatever outcome the cases have entered the study with).

Cohorts permit calculation of the effect of each variable on the probability of developing the outcome of interest (relative risk). However, where a certain outcome is rare then a prospective cohort study is inefficient. For example, studying 100 A&E attenders with minor injuries for the outcome of diabetes mellitus will probably produce only one patient with the outcome of interest. The efficiency of a prospective cohort study increases as the incidence of any particular outcome increases. Thus a study of patients with a diagnosis of deliberate self harm in the 12 months after initial presentation would be efficiently studied using a cohort design.

Another problem with prospective cohort studies is the loss of some subjects to follow up. This can significantly affect the outcome. Taking incidence analysis as an example (incidence = cases/per period of time), it can be seen that the loss of a few cases will seriously affect the numerator and hence the calculated incidence. The rarer the condition the more significant this effect.

Retrospective studies are much cheaper as the data have already been collected. One advantage of such a study design is the lack of bias because the outcome of current interest was not the original reason for the data to be collected. However, because the cohort was originally constructed for another purpose it is unlikely that all the relevant information will have been rigorously collected.

Retrospective cohorts also suffer the disadvantage that people with the outcome of interest are more likely to remember certain antecedents, or exaggerate or minimise what they now consider to be risk factors (recall bias).

Where two cohorts are compared one will have been exposed to the agent of interest and one will not. The major disadvantage is the inability to control for all other factors that might differ between the two groups. These factors are known as confounding variables.

A confounding variable is independently associated with both the variable of interest and the outcome of interest. For example, lung cancer (outcome) is less common in people with asthma (variable). However, it is unlikely that asthma in itself confers any protection against lung cancer. It is more probable that the incidence of lung cancer is lower in people with asthma because fewer asthmatics smoke cigarettes (confounding variable). There are a virtually infinite number of potential confounding variables that, however unlikely, could just explain the result. In the past this has been used to suggest that there is a genetic influence that makes people want to smoke and also predisposes them to cancer.

The only way to eliminate all possibility of a confounding variable is via a prospective randomised controlled study. In this type of study each type of exposure is assigned by chance and so confounding variables should be present in equal numbers in both groups.

Finally, problems can arise as a result of bias. Bias can occur in any research and reflects the potential that the sample studied is not representative of the population it was drawn from and/or the population at large. A classic example is using employed people, as employment is itself associated with generally better health than unemployed people. Similarly people who respond to questionnaires tend to be fitter and more motivated than those who do not. People attending A&E departments should not be presumed to be representative of the population at large.

How to run a cohort study

If the data are readily available then a retrospective design is the quickest method. If high quality, reliable data are not available a prospective study will be required.

The first step is the definition of the sample group. Each subject must have the potential to develop the outcome of interest (that is, circumcised men should not be included in a cohort designed to study paraphimosis). Furthermore, the sample population must be representative of the general population if the study is primarily looking at the incidence and natural history of the condition (descriptive).

If however the aim is to analyse the relation between predictor variables and outcomes (analytical) then the sample should contain as many patients likely to develop the outcome as possible, otherwise much time and expense will be spent collecting information of little value.

Cohort studies

Cohort studies describe incidence or natural history.

They analyse predictors (risk factors) thereby enabling calculation of relative risk.

Cohort studies measure events in temporal sequence thereby distinguishing causes from effects.

Retrospective cohorts where available are cheaper and quicker.

Confounding variables are the major problem in analysing cohort studies.

Subject selection and loss to follow up is a major potential cause of bias.

Each variable studied must be accurately measured. Variables that are relatively fixed, for example, height need only be recorded once. Where change is more probable, for example, drug misuse or weight, repeated measurements will be required.

To minimise the potential for missing a confounding variable all probable relevant variables should be measured. If this is not done the study conclusions can be readily criticised. All patients entered into the study should also be followed up for the duration of the study. Losses can significantly affect the validity of the results. To minimise this as much information about the patient (name, address, telephone, GP, etc) needs to be recorded as soon as the patient is entered into the study. Regular contact should be made; it is hardly surprising if the subjects have moved or lost interest and become lost to follow up if they are only contacted at 10 year intervals!

Beware, follow up is usually easier in people who have been exposed to the agent of interest and this may lead to bias.

There are many famous examples of Cohort studies including the Framingham heart study, 2 the UK study of doctors who smoke 3 and Professor Neville Butler‘s studies on British children born in 1958. 4 A recent example of a prospective cohort study by Davey Smith et al was published in the BMJ 5 and a retrospective cohort design was used to assess the use of A&E departments by people with diabetes. 6


These are primarily used to determine prevalence. Prevalence equals the number of cases in a population at a given point in time. All the measurements on each person are made at one point in time. Prevalence is vitally important to the clinician because it influences considerably the likelihood of any particular diagnosis and the predictive value of any investigation. For example, knowing that ascending cholangitis in children is very rare enables the clinician to look for other causes of abdominal pain in this patient population.

Cross sectional studies are also used to infer causation.

At one point in time the subjects are assessed to determine whether they were exposed to the relevant agent and whether they have the outcome of interest. Some of the subjects will not have been exposed nor have the outcome of interest. This clearly distinguishes this type of study from the other observational studies (cohort and case controlled) where reference to either exposure and/or outcome is made.

The advantage of such studies is that subjects are neither deliberately exposed, treated, or not treated and hence there are seldom ethical difficulties. Only one group is used, data are collected only once and multiple outcomes can be studied; thus this type of study is relatively cheap.

Many cross sectional studies are done using questionnaires. Alternatively each of the subjects may be interviewed. Table 2 lists the advantages and disadvantages of each.

Any study with a low response rate can be criticised because it can miss significant differences in the responders and non-responders. At its most extreme all the non-responders could be dead! Strenuous efforts must be made to maximise the numbers who do respond. The use of volunteers is also problematic because they too are unlikely to be representative of the general population. A good way to produce a valid sample would be to randomly select people from the electoral role and invite them to complete a questionnaire. In this way the response rate is known and non-responders can be identified. However, the electoral role itself is not an entirely accurate reflection of the general population. A census is another example of a cross sectional study.

Market research organisations often use cross sectional studies (for example, opinion polls). This entails a system of quotas to ensure the sample is representative of the age, sex, and social class structure of the population being studied. However, to be commercially viable they are convenience samples—only people available can be questioned. This technique is insufficiently rigorous to be used for medical research.

How to run a cross sectional study

Formulate the research question(s) and choose the sample population. Then decide what variables of the study population are relevant to the research question. A method for contacting sample subjects must be devised and then implemented. In this way the data are collected and can then be analysed

The most important advantage of cross sectional studies is that in general they are quick and cheap. As there is no follow up, less resources are required to run the study.

Cross sectional studies are the best way to determine prevalence and are useful at identifying associations that can then be more rigorously studied using a cohort study or randomised controlled study.

The most important problem with this type of study is differentiating cause and effect from simple association. For example, a study finding an association between low CD4 counts and HIV infection does not demonstrate whether HIV infection lowers CD4 levels or low CD4 levels predispose to HIV infection. Moreover, male homosexuality is associated with both but causes neither. (Another example of a confounding variable).

Often there are a number of plausible explanations. For example, if a study shows a negative relation between height and age it could be concluded that people lose height as they get older, younger generations are getting taller, or that tall people have a reduced life expectancy when compared with short people. Cross sectional studies do not provide an explanation for their findings.

Rare conditions cannot efficiently be studied using cross sectional studies because even in large samples there may be no one with the disease. In this situation it is better to study a cross sectional sample of patients who already have the disease (a case series). In this way it was found in 1983 that of 1000 patients with AIDS, 727 were homosexual or bisexual men and 236 were intrvenous drug abusers. 6 The conclusion that individuals in these two groups had a higher relative risk was inescapable. The natural history of HIV infection was then studied using cohort studies and efficacy of treatments via case controlled studies and randomised clinical trials.

An example of a cross sectional study was the prevalence study of skull fractures in children admitted to hospital in Edinburgh from 1983 to 1989. 7 Note that although the study period was seven years it was not a longitudinal or cohort study because information about each subject was recorded at a single point in time.

A questionnaire based cross sectional study explored the relation between A&E attendance and alcohol consumption in elderly persons. 9

A recent example can be found in the BMJ , in which the prevalence of serious eye disease in a London population was evaluated. 10

Cross sectional studies

Cross sectional studies are the best way to determine prevalence

Are relatively quick

Can study multiple outcomes

Do not themselves differentiate between cause and effect or the sequence of events


In contrast with cohort and cross sectional studies, case-control studies are usually retrospective. People with the outcome of interest are matched with a control group who do not. Retrospectively the researcher determines which individuals were exposed to the agent or treatment or the prevalence of a variable in each of the study groups. Where the outcome is rare, case-control studies may be the only feasible approach.

As some of the subjects have been deliberately chosen because they have the disease in question case-control studies are much more cost efficient than cohort and cross sectional studies—that is, a higher percentage of cases per study.

Case-control studies determine the relative importance of a predictor variable in relation to the presence or absence of the disease. Case-control studies are retrospective and cannot therefore be used to calculate the relative risk; this a prospective cohort study. Case-control studies can however be used to calculate odds ratios, which in turn, usually approximate to the relative risk.

How to run a case-control study

Decide on the research question to be answered. Formulate an hypothesis and then decide what will be measured and how. Specify the characteristics of the study group and decide how to construct a valid control group. Then compare the “exposure” of the two groups to each variable.

When conditions are uncommon, case-control studies generate a lot of information from relatively few subjects. When there is a long latent period between an exposure and the disease, case-control studies are the only feasible option. Consider the practicalities of a cohort study or cross sectional study in the assessment of new variant CJD and possible aetiologies. With less than 300 confirmed cases a cross sectional study would need about 200 000 subjects to include one symptomatic patient. Given a postulated latency of 10 to 30 years a cohort study would require both a vast sample size and take a generation to complete.

In case-control studies comparatively few subjects are required so more resources are available for studying each. In consequence a huge number of variables can be considered. This type of study is therefore useful for generating hypotheses that can then be tested using other types of study.

This flexibility of the variables studied comes at the expense of the restricted outcomes studied. The only outcome is the presence or absence of the disease or whatever criteria was chosen to select the cases.

The major problems with case-control studies are the familiar ones of confounding variables (see above) and bias. Bias may take two major forms.

Sampling bias

The patients with the disease may be a biased sample (for example, patients referred to a teaching hospital) or the controls may be biased (for example, volunteers, different ages, sex or socioeconomic group).

Observation and recall bias

As the study assesses predictor variables retrospectively there is great potential for a biased assessment of their presence and significance by the patient or the investigator, or both.

Overcoming sampling bias

Ideally the cases studied should be a random sample of all the patients with the disease. This is not only very difficult but in many instances is impossible because many cases may not have been diagnosed or have been misdiagnosed. For example, many cases of non-insulin dependent diabetes will not have sought medical attention and therefore be undiagnosed. Conversely many psychiatric diseases may be differently labelled in different countries and even by different doctors in the same country. As a result they will be misdiagnosed for the purposes of the study. However, in reality you are often left studying a sample of those patients who it is possible to recruit. Selecting the controls is often a more difficult problem.

To enable the controls to represent the same population as the cases, one of four techniques may be used.

A convenience sample—sampled in the same way as the cases, for example, attending the same outpatient department. While this is certainly convenient it may reduce the external validity of the study.

Matching—the controls may be a matched or unmatched random sample from the unaffected population. Again the problems of controlling for unknown influences is present but if the controls are too closely matched they may not be representative of the general population. “Over matching” may cause the true difference to be underestimated.

The advantage of matching is that it allows a smaller sample size for any given effect to be statistically significant.

Using two or more control groups. If the study demonstrates a significant difference between the patients with the outcome of interest and those without, even when the latter have been sampled in a number of different ways (for example, outpatients, in patients, GP patients) then the conclusion is more robust.

Using a population based sample for both cases and controls. It is possible to take a random sample of all the patients with a particular disease from specific registers. The control group can then be constructed by selecting age and sex matched people randomly selected from the same population as the area covered by the disease register.

Overcoming observation and recall bias

Overcoming retrospective recall bias can be achieved by using data recorded, for other purposes, before the outcome had occurred and therefore before the study had started. The success of this strategy is limited by the availability and reliability of the data collected. Another technique is blinding where neither the subject nor the observer know if they are a case or control subject. Nor are they aware of the study hypothesis. In practice this is often difficult or impossible and only partial blinding is practicable. It is usually possible to blind the subjects and observers to the study hypothesis by asking spurious questions. Observers can also be easily blinded to the case or control status of the patient where the relevant observation is not of the patient themselves but a laboratory test or radiograph.

Case-control studies

Case-control studies are simple to organise

Retrospectively compare two groups

Aim to identify predictors of an outcome

Permit assessment of the influence of predictors on outcome via calculation of an odds ratio

Useful for hypothesis generation

Can only look at one outcome

Bias is an major problem

Blinding cases to their case or control status is usually impracticable as they already know that they have a disease or illness. Similarly observers can hardly be blinded to the presence of physical signs, for example, cyanosis or dyspnoea.

As a result of the problems of matching, bias and confounding, case-control studies, are often flawed. They are however useful for generating hypotheses. These hypotheses can then be tested more rigorously by other methods—randomised controlled trials or cohort studies.

Case-control studies are very common. They are particularly useful for studying infrequent events, for example, cot death, survival from out of hospital cardiac arrest, and toxicological emergencies.

A recent example was the study of atrial fibrillation in middle aged men during exercise. 11


Pre-existing databases provide an excellent and convenient source of data. There are a host of such databases and the increasing archiving of information on computers means that this is an enlarging area for obtaining data. Table 3 lists some common examples of potentially useful databases.

Such databases enable vast numbers of people to be entered into a study prospectively or retrospectively. They can be used to construct a cohort, to produce a sample for a cross sectional study, or to identify people with certain conditions or outcomes and produce a sample for a case controlled study. A recent study used census data from 11 countries to look at the relation between social class and mortality in middle aged men. 12

These type of data are ordinarily collected by people other than the researcher and independently of any specific hypothesis. The opportunity for observer bias is thus diminished. The use of previously collected data is efficient and comparatively inexpensive and moreover the data are collected in a very standardised way, permitting comparisons over time and between different countries. However, because the data are collected for other purposes it may not be ideally suited to the testing of the current hypothesis, additionally it may be incomplete. This may result in sampling bias. For example, the electoral roll depends upon registration by each individual. Many homeless, mentally ill, and chronically sick people will not be registered. Similarly the notification of certain communicable diseases is a statutory responsibility for doctors in the UK: while it is probable that most cases of cholera are reported it is highly unlikely that most cases of food poisoning are.

Causes and associations

Because observational studies are not experiments (as are randomised controlled trials) it is difficult to control many external variables. In consequence when faced with a clear and significant association between some form of illness or cause of death and some environmental influence a judgement has to be made as to whether this is a causal link or simply an association. Table 4 outlines the points to be considered when making this judgement. 13

None of these judgements can provide indisputable evidence of cause and effect, but taken together they do permit the investigator to answer the fundamental questions “is there any other way to explain the available evidence?” and is there any other more likely than cause and effect?”

Qualitative studies can produce high quality information but all such studies can be influenced by known and unknown confounding variables. Appropriate use of observational studies permits investigation of prevalence, incidence, associations, causes, and outcomes. Where there is little evidence on a subject they are cost effective ways of producing and investigating hypotheses before larger and more expensive study designs are embarked upon. In addition they are often the only realistic choice of research methodology, particularly where a randomised controlled trial would be impractical or unethical.

Cohort studies look forwards in time by following up each subject

Subjects are selected before the outcome of interest is observed

They establish the sequence of events

Numerous outcomes can be studied

They are the best way to establish the incidence of a disease

They are a good way to determine causes of diseases

The principal summary statistic of cohort studies is the relative risk ratio

If prospective, they are expensive and often take a long time for sufficient outcome events to occur to produce meaningful results

Cross sectional studies look at each subject at one point in time only

Subjects are selected without regard to the outcome of interest

Less expensive

They are the best way to determine prevalence

The principal summary statistic of cross sectional studies is the odds ratio

Weaker evidence of causality than cohort studies

Inaccurate when studying rare conditions

Case-control studies look back at what has happened to each subject

Subjects are selected specifically on the basis of the outcome of interest

Efficient (small sample sizes)

Produce odds ratios that approximate to relative risks for each variable studied

Prone to sampling bias and retrospective analysis bias

Only one outcome is studied


The inclusion of subjects or methods such that the results obtained are not truly representative of the population from which it is drawn

The process by which the researcher and or the subject is ignorant of which intervention or exposure has occurred.

Cochrane database

An international collaborative project collating peer reviewed prospective randomised clinical trials.

Is a component of a population identified so that one or more characteristic can be studied as it ages through time.

Confounding variable

A variable that is associated with both the exposure and outcome of interest that is not the variable being studied.

A group of people without the condition of interest, or unexposed to or not treated with the agent of interest.

False positive

A test result that suggests that the subject has a specific disease or condition when in fact the subject does not.

Is a rate and therefore is always related either explicitly or by implication to a time period. With regard to disease it can be defined as the number of new cases that develop during a specified time interval.

A period of time between exposure to an agent and the development of symptoms, signs, or other evidence of changes associated with that exposure.

The process by which each case is matched with one or more controls, which have been deliberately chosen to be as similar as the test subjects in all regards other than the variable being studied.

Observational study

A study in which no intervention is made (in contrast with an experimental study). Such studies provide estimates and examine associations of events in their natural settings without recourse to experimental intervention.

The ratio of the probability of an event occurring to the probability of non-occurrence. In a clinical setting this would be equivalent to the odds of a condition occurring in the exposed group divided by the odds of it occurring in the non-exposed group.

Is not defined by a time interval and is therefore not a rate. It may be defined as the number of cases of a disease that exist in a defined population at a specified point in time.

Randomised controlled trial

Subjects are assigned by statistically randomised methods to two or more groups. In doing so it is assumed that all variables other than the proposed intervention are evenly distributed between the groups. In this way bias is minimised.

Relative risk

This is the ratio of the probability of developing the condition if exposed to a certain variable compared with the probability if not exposed.

Response rate

The proportion of subjects who respond to either a treatment or a questionnaire.

Risk factor

A variable associated with a specific disease or outcome.


The rigour with which a study has been designed and executed—that is, can the conclusion be relied upon?


The usefulness of the findings of a study with respect to other populations.

A value or quality that can vary between subjects and/or over time

Study design for cohort studies.

Study design for cross sectional studies

Study design for case-control studies.

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Evidence based practice toolkit.

Levels of Evidence Table

Evidence pyramid (levels of evidence), definitions.

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This level of effectiveness rating scheme is based on the following: Ackley, B. J., Swan, B. A., Ladwig, G., & Tucker, S. (2008).  Evidence-based nursing care guidelines: Medical-surgical interventions.  (p. 7) .  St. Louis, MO: Mosby Elsevier.

Different types of clinical questions are best answered by different types of research studies.  You might not always find the highest level of evidence (i.e., systematic review or meta-analysis) to answer your question. When this happens, work your way down to the next highest level of evidence.

This table suggests study designs best suited to answer each type of clinical question.

Evidence Pyramid

" Evidence Pyramid " is a product of Tufts University and is licensed under BY-NC-SA license 4.0

Tufts' "Evidence Pyramid" is based in part on the  Oxford Centre for Evidence-Based Medicine: Levels of Evidence (2009)

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