Case-Control
Studies
Evaluating Epidemiological Research
Kiffer G. Card, PhD, Faculty of Health Sciences, Simon Fraser University
Learning objectives for this lesson:
- Describe the major design features of risk-based and rate-based case-control studies
- Identify hypotheses and population types consistent with each design
- Differentiate between primary-base and secondary-base case-control studies
- Elaborate the principles used to select and define the case series
- Explain the principal features for selecting controls in open and closed populations
- Design and implement a valid case-control study to meet specific objectives
This course was developed by Kiffer G. Card, PhD, as a companion to Dohoo, I. R., Martin, S. W., & Stryhn, H. (2012). Methods in Epidemiologic Research. VER Inc.
Glossary — Key Terms, People & Concepts
📚 Reference page — available throughout the lesson
This glossary collects the key concepts, people, and ideas you will meet in this lesson. Use it as a reference while you work through the material, or as a review before assessments. Type in the search box to filter entries.
Introduction & The Study Base
⏱ Estimated reading time: 15 minutes
Introduction and Overview
Modern teaching of case-control design follows the “study base” framework laid out by Vandenbroucke and Pearce (2012). Lesson 3 introduced the three sampling approaches that organize observational analytic studies: cross-sectional (sample without regard to disease), case-control (sample on the disease), and cohort (sample on the exposure). It walked through the cross-sectional design in detail. This lesson does the same work for case-control studies. The four content sections proceed from the most general design choices to the most specific: Section 1 sets up the basic logic and the concept of the study base; Section 2 covers how cases are identified and how controls are selected; Section 3 distinguishes the two main flavors (risk-based and rate-based) and shows what the odds ratio actually estimates under each; Section 4 closes the loop on comparability, analysis, and reporting.
Two ideas from Lesson 3 carry over directly. First, the cross-sectional limit of measuring prevalence rather than incidence is one of the things case-control studies are designed to overcome. Second, the unified-approach discipline (think experiment first, fix design before seeing data, project forward to alternative results) applies just as much here as it did to cross-sectional designs — arguably more, because the choice of cases and controls creates more opportunities for things to go wrong.
Learning Objectives
- Describe the fundamental logic of the case-control study design.
- Distinguish between primary-base and secondary-base case-control studies.
- Explain the concept of nested case-control studies.
- Identify when case-control designs are performed prospectively vs. retrospectively.
What Is a Case-Control Study?
The basis of the case-control study design is to select individuals who have newly developed the disease or outcome of interest (the cases) and, as a comparison, individuals who have not developed the disease at the time of selection (the controls). We then contrast the frequency of exposure factors in the cases with the frequency of exposure factors in the controls.
Walk through the 1950 Doll & Hill (1950) case-control study scene by scene. Next ▶ advances at your pace.
A 7-scene reenactment of the first major case-control study: the rising lung-cancer ward, the backward-looking design, case and control interviews, the 2×2 table populating live, the tilting scale, and the moment OR ≈ 14 lands in print.
Key Distinction
A case-control study is not a comparison between a set of cases and a set of ‘healthy’ subjects. It is a comparison between a set of cases and a set of non-case subjects (people who have not developed the specific disease but may have other diseases) whose exposure to the factors of interest reflects the exposure in the source population.
The controls would have been included as cases if they had developed the outcome (disease) of interest. Most frequently, individual people are the units of interest, but the design also applies to aggregates of individuals.
Figure — The logic of case-control design: select cases and controls from the same source population, then compare their exposure histories.
Usually, case-control studies are performed retrospectively since the outcome (usually disease) has occurred when the study begins. However, it is possible to conduct case-control studies prospectively; in these, the cases have not yet developed until after the study begins, so the cases are enrolled as they occur over time.
The diagram makes the logic look simple, but it conceals a hard question: which source population? In case-control studies that question has a name and three standard answers, and the rest of the lesson essentially turns on getting it right.
The Study Base
The study base is the population from which the cases and (possibly) the controls are obtained. The nature of the study base determines how controls should be selected. The three flip cards below introduce the standard typology — primary base, secondary base, and the special case of nested designs. Click each one and notice that they differ in how directly the source population can be enumerated, which in turn determines how easy it is to draw a valid control sample.
The three study-base types make more sense when you can see them in published studies. The four examples below recur throughout the rest of the lesson; expand each one to see how the design choices were made and which combination of features (primary vs. secondary base; risk-based vs. rate-based; nested or not) the investigators chose. We will refer back to these examples by number in Sections 2–4.
Key Examples
Dorgan et al (2010) used serum samples from a secondary-base case-control study. A total of 6,915 women who were free of cancer donated blood between 1977–1989. Of the 6,720 women in extended follow-up, 1,751 were identified as deceased. For each of the 117 potential cases, 2 potential controls were matched on age (±2 years), date (±1 year), and menstrual cycle day (±2 days). This is a risk-based sampling strategy. Conditional logistic regression was used to evaluate the association.
Dore et al (2004) conducted a rate-based study in Alberta, British Columbia, and Saskatchewan, Canada (Dec 1999–Nov 2000). Eligible cases had diarrheal illness with S. Typhimurium from stool samples. Controls were matched 1:1 on age and province of residence, randomly selected from provincial health registries. Cases and controls were interviewed by telephone using a pre-tested, standardised questionnaire covering demographics, health history, medication use, travel history, and animal contact.
Magura et al (2008) used a risk-based, secondary-base case-control design. Cases were men newly diagnosed with prostate cancer at Meritcare hospital between 2004–2006. Controls were identified from the primary-care database of the same hospital: men without cancer, aged 50–74, who had annual physicals and lipid profiles within a year. Exclusion criteria included other cancers and non-Caucasian race. The authors used a widely accepted definition of hypercholesterolemia (total cholesterol >5.17 mmol/l) and estimated odds ratios using multiple logistic regression.
Rodrigo et al (2011) conducted a community-based (primary-base), nested, rate-based case-control study within a larger randomised controlled trial in South Australia. 300 households maintained weekly health diaries. The outcome — highly credible gastroenteritis (HCG) — was defined as 2+ loose stools, 2+ vomiting episodes, or combinations with abdominal pain/nausea in 24 hours. Controls were matched to cases by study week. Logistic regression was used, allowing for familial clustering and repeated observations.
Key Takeaways
- Case-control studies select subjects based on disease status and look backward at exposure.
- The study base can be a primary base (enumerable population) or secondary base (clinic/registry).
- Nested designs allow estimation of disease frequency by exposure — a unique advantage.
- Controls should represent the exposure experience of the source population that gave rise to the cases.
Now that you can see the design's full logic and a handful of working examples, the next box brings the analysis back to the 2×2 contingency table you met at the end of Lesson 3. The same structure shows up — but because we sampled on case status this time, the only valid summary measure is the odds ratio.
What you'll do: read a fictional smoking/lung-cancer 2×2 table into R, compute the cross-product odds ratio, and add a 95% confidence interval using the Woolf method. What to take away: the OR you compute here is the standard summary measure for every case-control study you will read in this course; Lesson 5 will show how its meaning changes again when sampling is by exposure rather than by case status.
Case-control studies are summarized by an odds ratio (OR), the only measure of association you can compute when you've sampled by case status. The arithmetic is just the cross-product of a 2×2 table.
# Hypothetical study: 50 lung cancer cases + 150 controls; smoking status known.
# Smoker Nonsmoker
# Cases (lung Ca) 45 5
# Controls 60 90
tab <- matrix(c(45, 60,
5, 90),
nrow = 2, byrow = FALSE,
dimnames = list(Status = c("Case", "Control"),
Smoke = c("Yes", "No")))
tab
# Odds ratio = (a*d) / (b*c)
a <- tab["Case", "Yes"]; b <- tab["Case", "No"]
c <- tab["Control", "Yes"]; d <- tab["Control", "No"]
OR <- (a * d) / (b * c)
OR
# 95% CI from the log-OR (Woolf method)
log_se <- sqrt(1/a + 1/b + 1/c + 1/d)
ci <- exp(log(OR) + c(-1, 1) * 1.96 * log_se)
round(c(OR = OR, lower = ci[1], upper = ci[2]), 2)Reading the OR. Cases had ~13.5 times the odds of being smokers compared with controls. Because we sampled on case status, this OR — not a risk ratio — is the appropriate measure. Later in HSCI 341 you'll meet epitools::oddsratio() which produces the same result with one line of code.
R Reflect on what you just ran
Use the questions below to interpret the output you produced. Look at your console before answering.
1. The computed OR was 13.5 with a 95% CI of (5.10, 35.71). State in plain language what that OR means about the odds of being a smoker among lung-cancer cases versus controls. Does the CI exclude the null value of 1, and what does that tell you about statistical significance?
2. The CI is very wide (about a sevenfold range). Looking at the four cell counts (a=45, b=5, c=60, d=90), which cell is driving the imprecision — and how does the Woolf formula sqrt(1/a + 1/b + 1/c + 1/d) make that intuitive?
3. Why is the OR — and not a risk ratio or risk difference — the only valid measure of association here? Reference how the data were sampled.
The reflection below is a personal application of the primary/secondary distinction. After working through it and the knowledge check, Section 2 takes the same design logic one level deeper: how do you actually identify cases, and how do you choose controls so that the comparison is fair?
Reflection
Reflection
Consider a disease that is of interest to you. Would a primary-base or secondary-base case-control study be more feasible? What would be the advantages and trade-offs of each approach for your specific research question?
Minimum 20 characters required.
1. In a case-control study, what do we compare between cases and controls?
2. What distinguishes a primary study base from a secondary study base?
3. What unique advantage does a nested case-control study provide?
4. Case-control studies are most commonly performed:
The Case Series & Principles of Control Selection
⏱ Estimated reading time: 15 minutes
Introduction and Overview
Section 1 set up the design at the level of the source population. This section steps inside it. The two halves of a case-control study — the case series and the control group — each carry their own design decisions, and historically far more case-control studies have been ruined by control selection than by anything else. We start with the case series, where the choices are mostly about definition and ascertainment, then turn to the harder problem of choosing controls.
Learning Objectives
- Describe the key elements in selecting and defining the case series.
- Discuss the importance of diagnostic criteria and case ascertainment.
- Articulate the four major principles of control selection.
- Compare different sources of controls and their strengths and limitations.
The Case Series (Section 9.3)
Key elements in selecting the case series include: specifying the disease (including diagnostic criteria), identifying the source(s) of the cases, deciding whether only incident or both incident and prevalent cases are to be included, and estimating the required number of cases and total sample size.
Incident vs. Prevalent Cases
There is virtually unanimous agreement that, when possible, only incident cases should be used. There are specific circumstances where prevalent cases may be justified, but this would be the exception, not the rule. Usually, only the first occurrence of the outcome in each study subject is included (Examples 9.1 and 9.3); however, multiple occurrences of the same disease can be included (Example 9.4).
Where Do Cases Come From?
The primary/secondary distinction we met in Section 1 also shapes how cases themselves are identified. The two tabs below revisit each option with the case series specifically in view; notice how the source choice creates a very different downstream problem for control selection.
Primary-base cases come from a specific registry that contains virtually all cases for a defined population (e.g., provincial or state disease registries). Sampling or taking a census of cases directly from the primary source population avoids a number of potential selection biases, but may be more difficult to implement and more costly.
Primary-base designs are moderately common because provincial or state records allow complete enumeration of people and their health events.
Secondary-base cases are obtained from a physician’s clinic, one or more hospitals, or registries. A major challenge is to conceptualise the actual source population from which the cases arose. A common solution is to select controls from records at the same source (e.g., the same hospital; see Example 9.3).
Every effort should be made to obtain complete case ascertainment. In secondary-base studies, the set of cases from a tertiary care facility could become increasingly different from cases in the broader source population.
Diagnostic Criteria
The diagnostic criteria for a subject to become a case should include specific, well-defined manifestational (i.e., clinical) signs where appropriate and, when possible, clearly documented diagnostic criteria (e.g., laboratory test results) that can be applied to all study subjects in a uniform manner. In some instances, it might be desirable to subdivide the case series into subgroups based on differences in disease characteristics.
Diagnostic criteria settle who counts as a case. The harder question — the one that makes or breaks a case-control study — is who counts as an appropriate comparison. That is the rest of this section.
Principles of Control Selection (Section 9.4)
The selection of appropriate controls is often one of the most difficult aspects of a case-control design. The key guideline is that controls should be representative of the exposure experience in the population which gave rise to the cases.
The Four Major Principles
Wacholder, McLaughlin, Silverman, & Mandel (1992a; 1992b; 1992c) provide the classic discussions of control selection. The four principles below act together — not independently — to ensure that the controls' exposure experience really does mirror the population that gave rise to the cases.
Sources of Controls
The four principles tell you what valid controls look like in the abstract. In practice, every choice of control source trades a different strength against a different bias. The table below catalogues the six most common sources; the column to read most carefully is the third one, because the limitation of each source is exactly the kind of bias that source most often produces.
| Source | Strengths | Limitations |
|---|---|---|
| Population controls | Representative of source population | Low response rates; recall bias; less motivated |
| Hospital controls | Accessible; cooperative; similar recall ability | Exposure may be related to hospitalisation |
| Friend controls | Similar recall; willing to participate | Over-matching; biased estimates (Bunin et al, 2011) |
| Neighbourhood controls | Similar socioeconomic background | If neighbourhood related to exposure, causes bias |
| Random digit dialling (RDD) | Population-representative sampling | Business vs. home phone issues; declining response rates |
| Partner controls | Shared environment; cooperative | Age-sex distribution differs; over-matching on exposures |
Key Takeaways
- Incident cases are strongly preferred over prevalent cases.
- Cases can come from primary bases (registries) or secondary bases (clinics/hospitals).
- Controls must represent the exposure experience of the source population.
- The four key principles: same study base, closed/open population rules, and temporal eligibility.
The reflection below asks you to make a real control-selection decision and defend it against the biases the table above just named. Once you have done that and the knowledge check, Section 3 turns to a parallel choice: should the design be risk-based or rate-based, and how does that decision change what the odds ratio actually estimates?
Reflection
Reflection
Imagine you are studying whether a specific dietary factor is associated with colorectal cancer. You plan to recruit cases from a hospital. What type of control group would you select (hospital, population, friend, etc.) and why? What biases might arise from your choice?
Minimum 20 characters required.
1. In case-control studies, which type of cases should preferably be used?
2. The key guideline for valid control selection is that controls should be:
3. What is a major limitation of using hospital controls?
4. Using friend controls in a case-control study can lead to:
Controls in Risk-Based & Rate-Based Designs
⏱ Estimated reading time: 15 minutes
Introduction and Overview
Sections 1 and 2 settled how the case series and the control group are assembled. The remaining design choice is how time enters the picture — specifically, whether the controls are people who survived the whole study period without becoming cases (a closed-population, risk-based design) or people sampled from the population at the moment each case occurs (an open-population, rate-based design). That choice changes what the odds ratio you eventually compute actually means. The two halves of this section unpack each design in turn, ending in matched 2×2 tables and the equations that connect them to risk and rate ratios.
Learning Objectives
- Describe the data layout and sampling approach for risk-based case-control studies.
- Derive and interpret the odds ratio (OR) in a risk-based design (Eq 9.1).
- Describe the data layout and incidence density sampling for rate-based case-control studies.
- Explain why the OR estimates the risk ratio in risk-based designs and the rate ratio in rate-based designs.
Risk-Based Case-Control Designs (Section 9.5)
The traditional approach to case-control studies has been risk-based (cumulative incidence) design. Controls are selected from among the people that did not become cases by the end of the study period. A subject can be selected as a control only once.
Design Requirements
This design is appropriate if the population is closed and is most informative if the risk period for the outcome has ended before subject selection begins. It fits situations such as outbreaks from infectious or toxic agents where the risk period is short and essentially all cases have occurred within the defined study period.
2×2 Table: Risk-Based Case-Control Design
The closed-source population can be categorised with respect to exposure and outcome (upper-case = population, lower case = sample):
| Exposed | Non-exposed | Total | |
|---|---|---|---|
| Cases | a1 | a0 | m1 |
| Controls (Non-cases) | b1 | b0 | m0 |
The cases (M1) are those that arose during the study period, while the controls (M0) are those that remained free of the outcome. Usually all or most cases are included (sampling fraction sf among cases approaches 1). We select controls independently of exposure status so that the sampling fractions in the two exposure groups should be equal:
The measure of association in risk-based designs is the odds ratio (OR):
What Does the OR Estimate?
The OR is a valid measure of association in its own right. It also estimates the ratio of risks (RR) if the outcome is relatively infrequent (e.g., <5%) in the source population. Whether the OR approximates the RR or rate ratio depends on the study design and assumptions about the source population (Knol, Vandenbroucke, Scott, & Egger, 2008).
The risk-based design works beautifully when the population stays put for the whole study window — an outbreak investigation, a closed cohort with short follow-up. Most of the populations epidemiology actually studies do not behave that way: people enter, leave, age, and accumulate exposure over time. For those populations the case-control design has to be rebuilt around person-time rather than head counts.
Rate-Based Case-Control Designs (Section 9.6)
Because the populations we study are often open, the case-control designs for these populations should use a rate-based approach (incidence density sampling), which ensures that the time-at-risk is taken into account when control subjects are selected.
2×2 Table: Rate-Based Case-Control Design
| Exposed | Non-exposed | Total | |
|---|---|---|---|
| Cases | A1 | A0 | M1 |
| Person-time at risk | T1 | T0 | T |
Recall that in a cohort study, the two rates of interest would be:
In a rate-based case-control study, we select controls using a sampling rate (sr) that is equal in exposed and non-exposed populations:
Therefore, the ratio of exposed to unexposed controls equals the ratio of the cumulative exposed and unexposed subject times:
This means the OR from the case-control data estimates the incidence rate ratio (IR) in the source population:
Key Advantage of Rate-Based Design
In this design, the OR estimates the IR (from a cohort study) and no assumption about rarity of outcome is necessary for a valid estimate. This is a major advantage over risk-based designs where the rare disease assumption is needed for the OR to approximate the RR.
Equations 9.2–9.5 describe the relationship between the case-control sample and the underlying source-population rates. The practical question is how to draw the control sample so those equations actually hold. The answer is a specific sampling rule.
Incidence Density Sampling
The most common method of obtaining controls is by selecting a specified number of non-cases from the risk set, matched time-wise to the occurrence of each case. This is called incidence density sampling. At each time a subject develops the outcome, we choose b controls from the non-case subjects that exist in the source population at that point. Key features:
- We do not need to know the time-at-risk for potential controls.
- We do not need to assume the population is stable.
- The number of controls per case can vary.
- Subjects initially identified as controls can subsequently become cases.
- Controls can subsequently become cases (and vice versa in rate-based designs).
Key Takeaways
- Risk-based designs use closed populations; the OR estimates the RR when the outcome is rare (Eq 9.1).
- Rate-based designs use open populations and incidence density sampling (Eqs 9.2–9.5).
- In rate-based designs, the OR directly estimates the IR with no rarity assumption needed.
- Incidence density sampling matches controls to cases by time of occurrence.
The reflection below pulls Sections 1–3 together: it asks you to make the design-flavor choice explicitly and trace its consequences for interpretation. Section 4 then closes out the lesson with the four practical questions that any case-control investigator has to answer once the design is chosen — how many controls, whether to use multiple control groups, how to assess exposure, how to keep cases and controls comparable, and how to report the result honestly.
Reflection
Reflection
Why is the distinction between risk-based and rate-based case-control designs important for interpreting the odds ratio? In what situations would you recommend a rate-based design over a risk-based design, and how would this affect control selection?
Minimum 20 characters required.
1. In a risk-based case-control study, controls are selected from:
2. The odds ratio in a risk-based case-control study estimates the risk ratio when:
3. What is the key advantage of the rate-based OR over the risk-based OR?
4. In incidence density sampling, at each time a case occurs we select controls from:
Comparability, Analysis & Reporting
⏱ Estimated reading time: 15 minutes
Introduction and Overview
Sections 1–3 walked through the major design choices: study base, case ascertainment, control selection principles, and the risk-based/rate-based split. By the time you get here, the design is essentially set. This section is about the practical implementation choices that follow — how many controls, whether to use more than one control group, how to assess exposure, how to maintain comparability, how to analyse the resulting data, and how to report it. Each of these is a place where a sound design can still be undermined.
Learning Objectives
- Discuss the number of controls per case and the use of multiple control groups.
- Describe exposure and covariate assessment in case-control studies.
- Explain the three approaches to keeping cases and controls comparable.
- Describe the analysis of case-control data and STROBE reporting guidelines.
Number of Controls per Case (Section 9.8)
Most studies use a 1:1 case-control ratio; however, other than being statistically efficient, there is nothing magical about this ratio. If the information on covariates and exposure is already recorded (i.e., exposure data is ‘free’), one might use all qualifying non-cases as controls to avoid sampling issues.
Practical Guidelines
When the number of cases is small, the precision of association measures can be improved by selecting more than one control per case. There are formal approaches for deciding the optimal number (Schlesselman, 1974), but usually the benefit of increasing the number of controls per case is small; often 3–4 controls per case is the practical maximum.
Number of Control Groups (Section 9.9)
Beyond the question of how many controls per case is the related question of how many control groups. Some researchers use multiple control groups to balance a perceived bias with one specific control group (Examples 9.5 and 9.6). However, this should be clearly defined, as it adds complexity and can be difficult to interpret if the different control groups produce different results. The two examples below show the strategy in practice; in both cases the second control group functioned mainly as a robustness check on the first.
Example 9.5 — Secondary-Base Study with Population Controls
Abubakar et al (2007) studied Crohn’s disease risk factors from 9 hospitals in England using both hospital-derived and community controls. The a priori design was matched with 104 cases. For community controls, 2 general practitioners per Crohn’s patient were randomly selected, matched by age (±1 year) and gender. The authors noted that the choice of control group had little impact on their results.
Example 9.6 — Primary-Care and Population-Based Controls
Brenner et al (2010) evaluated lung cancer risk factors in never-smokers in Toronto. They used both population-based controls (randomly sampled from property tax files, n=425) and hospital-based controls (from a family medicine clinic, n=523). Unconditional logistic regression models were used. A separate analysis based on 156 non-smoking cases with 466 non-smoking controls confirmed the main findings.
Once you have settled how many controls and how many control groups, the next implementation question is how exposure and covariates are actually measured — and, especially in retrospective designs, how to keep that measurement from being shaped by case status itself.
Exposure & Covariate Assessment (Section 9.10)
Most case-control studies are retrospective, so a concise, workable definition of ‘exposure’ (and also of confounders) is needed when implementing the study design. When ascertaining exposure status and information on confounders, it is preferable to obtain the greatest accuracy possible using the same process for both cases and controls.
General Rules for Exposure Assessment
When possible, have data collectors blinded to case status. As a general rule, the exposure status of cases should be the exposure category that existed at the time of outcome occurrence. For controls, their exposure status reflects their exposure situation at the time of their selection.
Keeping Cases and Controls Comparable (Section 9.11)
Accurate exposure measurement is necessary but not sufficient. Even with perfect measurement, a confounded comparison gives biased answers. The three flip cards below describe the three standard tools for preventing that — restriction, matching, and analytic control. They are not interchangeable, and a well-designed case-control study often uses two or three of them in combination.
With design choices and comparability tools in place, what remains is the analysis itself — and, just as importantly, what the resulting odds ratio means under each combination of design and sampling decision we have made so far.
Analysis of Case-Control Data (Section 9.12)
The data format and analysis for both risk-based and rate-based designs proceeds in a similar manner. In a 2×2 table:
| Exposed | Non-exposed | Total | |
|---|---|---|---|
| Cases | a1 | a0 | m1 |
| Controls | b1 | b0 | m0 |
Remember that we cannot directly estimate disease frequency (unless the study is nested) because the m1:m0 ratio was fixed by the sampling design. Chapter 6 outlines the analysis including hypothesis testing, estimating the odds ratio, and developing confidence intervals.
The three tabs below summarize what the OR estimates under each of the design combinations we have built up across this lesson. The pattern to read away with: the same number, computed from the same 2×2 table, is interpreted differently depending on the sampling decisions you made before any data were collected.
With risk-based designs and sampling of controls at the end of the follow-up period, the odds ratio estimates the risk ratio if the frequency of disease in the source population is low (e.g., below 10%), and censoring is unrelated to exposure.
If concurrent sampling (incidence density sampling) is used, the odds ratio estimates the rate ratio in both closed and open populations. For validity, stability of exposure is needed in the closed population but not in the open population.
When controls are selected from an open population without concurrent sampling of controls, the odds ratio estimates the rate ratio only if the population is stable, otherwise it is just the odds ratio. If matching is used to select controls but is ignored in the analysis, the impact depends on the extent of exposure changes during the study period (Knol, Vandenbroucke, Scott, & Egger, 2008).
The final piece of the implementation puzzle is making the design transparent to the next reader. The STROBE statement, which we previewed in Lesson 1 and then introduced in Lesson 3, has a case-control extension that names the items most likely to go missing in a write-up.
Reporting Guidelines (Section 9.13)
Vandenbroucke et al (2007) described the key elements of case-control studies that should be reported (STROBE). The complete listing is in Table 7.3; items specific to case-control studies are included in Table 9.1, expanded in the accordion below.
Methods:
- Item 6a: Give the eligibility criteria, and the sources and methods of case ascertainment and control selection. Give the rationale for the choice of cases and controls.
- Item 6b: For matched studies, give matching criteria and the number of controls per case.
- Item 12: If applicable, explain how matching of cases and controls was addressed.
Results:
- Item 15: Report numbers in each exposure category, or summary measures of exposure.
Key Takeaways
- 3–4 controls per case is usually the practical maximum for improving precision.
- Multiple control groups add complexity; the general experience is that more than one control group has limited value.
- Exposure assessment should use the same process for cases and controls, with blinding when possible.
- Comparability is achieved through exclusion, matching, or analytic control (multivariable techniques).
- What the OR estimates (RR or IR) depends on the study design and sampling approach.
The reflection below is the section's payoff — a short colleague-asks-you-a-question prompt that requires you to use everything in this lesson to give a careful answer. Once you have worked through it and the knowledge check, the lesson moves to its final assessment, which integrates Sections 1–4.
Reflection
Reflection
A colleague presents a case-control study with an odds ratio of 2.5 and asks: “Does this mean exposed people have 2.5 times the risk?” How would you respond? Consider the study design (risk-based vs. rate-based), the rarity of the outcome, and what the OR actually estimates under different conditions.
Minimum 20 characters required.
1. What is the practical maximum number of controls per case in most case-control studies?
2. What approach to preventing confounding is ‘most often relied upon’ in case-control studies?
3. When concurrent (incidence density) sampling is used, the OR estimates:
4. According to STROBE guidelines for case-control studies, which of the following should be reported?
Final Review & Assessment
⏱ Estimated time: 20 minutes
Bringing It All Together
This lesson worked from the inside out. Section 1 fixed the conceptual core — cases and controls must arise from a single, well-defined study base, and getting that right is what separates a clean primary-base design from a shaky secondary-base one. Sections 2 and 3 then translated that core into mechanics: how to define and recruit a case series, the four principles of control selection, and the choice between risk-based sampling (which gives you the OR as an approximation of the risk ratio) and rate-based / incidence density sampling (which gives you the OR directly as a rate ratio).
Section 4 closed the loop by moving from design to execution and reporting — choosing the number of controls, deciding when to use multiple control groups, ensuring comparability through exclusion, matching, and analytic control, and then communicating the whole package transparently using STROBE. Read end-to-end, the lesson is a single argument: case-control studies are powerful precisely because they are efficient, but every efficiency has a price, and the design choices you make have to be explicit, defensible, and reported.
The final reflection asks you to put that argument to work by sketching a brief case-control proposal of your own. The 15-question assessment then checks the conceptual content directly. From here, Lesson 5 turns the design around to follow exposed and unexposed people forward in time — cohort studies — and a lot of the vocabulary you just built (study base, comparability, sampling logic) will travel with you.
Key Takeaways from Lesson 4
- A valid case-control study begins with a clearly specified study base; primary-base designs make it explicit, secondary-base designs reconstruct it.
- Cases must satisfy a stable diagnostic definition; whether you use incident or prevalent cases changes what your odds ratio means.
- Controls must be sampled from the same source population as the cases, independently of exposure — the four principles of control selection are non-negotiable.
- Risk-based sampling and rate-based (incidence density) sampling answer different questions; the OR estimates a risk ratio in one and a rate ratio in the other.
- Comparability is engineered, not assumed — through exclusion, matching, and analytic control — and matched designs require matched analyses.
- Transparent reporting using STROBE is the bridge between a defensible design and a study other people can appraise, replicate, or extend.
The companion R script r-activities/HSCI_230_Lesson_4_Case_Control_Studies.R walks you through the canonical case-control analysis: build a 2x2 table of cases and controls by exposure, compute the odds ratio as (a*d)/(b*c), and bracket it with a 95% confidence interval using the Woolf (log-OR) method. A short stretch block at the end repeats the same calculation with epitools::oddsratio() so you can compare the by-hand answer to a packaged one.
tab <- matrix(c(45, 60,
5, 90),
nrow = 2, byrow = FALSE,
dimnames = list(Status = c("Case", "Control"),
Smoke = c("Yes", "No")))
tab
# Odds ratio = (a*d) / (b*c)
a <- tab["Case", "Yes"]; b <- tab["Case", "No"]
c <- tab["Control", "Yes"]; d <- tab["Control", "No"]
OR <- (a * d) / (b * c)
OR
# 95% CI from the log-OR (Woolf method)
log_se <- sqrt(1/a + 1/b + 1/c + 1/d)
ci <- exp(log(OR) + c(-1, 1) * 1.96 * log_se)
round(c(OR = OR, lower = ci[1], upper = ci[2]), 2)
## -----------------------------------------------------------------------------
## Stretch: same analysis with epitools::oddsratio()
## -----------------------------------------------------------------------------
# install.packages("epitools") # uncomment if not already installed
# library(epitools)
# oddsratio(tab, method = "wald")
Final Reflection
Design a brief case-control study proposal for a health question of your choice. Specify: (1) the research question, (2) whether you would use a primary or secondary study base and why, (3) how you would define and identify cases, (4) how you would select controls and from what source, (5) whether a risk-based or rate-based design is more appropriate, and (6) how you would ensure comparability.
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Final Assessment
This assessment covers all sections of Lesson 4. You must score 100% to complete the lesson. Review the feedback after each attempt.
1. The fundamental logic of a case-control study is to:
2. A case-control study is NOT a comparison between cases and:
3. A secondary study base refers to a source population that is:
4. A unique advantage of a nested case-control study is that it can:
5. Why are incident cases preferred over prevalent cases?
6. According to the principles of control selection, controls should:
7. The odds ratio in a risk-based case-control study (Eq 9.1) is calculated as:
8. In rate-based case-control designs, the OR estimates the incidence rate ratio because:
9. What is incidence density sampling?
10. What is the practical maximum number of controls per case before benefits diminish?
11. Why might using friend controls lead to biased estimates?
12. In Example 9.3, the secondary-base case-control study of prostate cancer used controls from:
13. When ascertaining exposure in case-control studies, what is recommended?
14. The general experience regarding multiple control groups is that:
15. According to STROBE, which item is specific to case-control study reporting?