Slides (PDF) · Student tasks · Български
Set aside about 15 minutes to read and reflect. The text follows the presentation “Epidemiological study designs”. Class 8 taught us to count — prevalence, incidence, person-time — and Class 9 applied the counts to oral diseases. This class shows how studies are built to answer questions with those counts. Afterwards you should be able to name the design of a study, calculate and interpret a relative risk, a risk difference and an odds ratio, and say what could make an association misleading.
Three questions identify almost any design
First, did the investigator assign the exposure? If not, the study is observational: conditions are studied as they occur. If yes, it is experimental — a trial. Second, is there a comparison group? Without one, the study is descriptive (who, where, when) and generates hypotheses; with one, it is analytic and tests hypotheses about determinants. Third, where does the study start? A case–control study starts with the outcome and looks back for the exposure; a cohort study starts with the exposure and follows people forward to the outcome; a cross-sectional study measures both at the same time. A good analytic design compares an outcome between groups, quantifies the comparison, manages errors and confounding, and establishes that the exposure came before the outcome (Burt & Eklund, 2021, ch. 12).
Descriptive studies
A case report describes one unusual patient and a case series several. They are the first signal of something new: the fluoride story began when Frederick McKay described Colorado children with “brown stain” — later recognised as fluorosis — who had less caries. A series has no comparison group and no denominator, so it cannot test a cause.
The cross-sectional survey is the main descriptive design and the basis of the WHO oral health surveys of Class 9. Exposure and outcome are measured at the same moment, which gives prevalence. In a hypothetical survey of 300 twelve-year-olds, 50 of 100 daily drinkers of sugary drinks and 40 of 200 others had untreated caries: 50% against 20%, a prevalence ratio of 2.5. The association is real in the sample, but the survey cannot show whether the drinks came before the caries — the main limitation of a snapshot.
An ecological study measures exposure and outcome for whole groups — towns, regions, countries. Studies of water fluoridation and hip fractures compared communities. They are quick and cheap, and suitable when the exposure is a group property such as a fluoridation policy, but they risk the ecological fallacy: an association between groups does not show that the same people had both the exposure and the outcome.
Cohort and case–control studies
Analytic studies speak the language of the 2 × 2 table, with the exposure in the rows and the outcome in the columns (cells a, b, c, d).
A cohort study starts with people free of the outcome, classified as exposed or unexposed, and follows them over time. Because new cases are counted, risks are compared directly. In a hypothetical cohort of 1000 adults aged 25, 60 of 400 smokers and 30 of 600 non-smokers developed periodontitis in five years: risks of 15% and 5%. The relative risk (RR) is 15/5 = 3.0 — smokers had three times the risk — and the risk difference is 10 percentage points over five years. That excess is associated with smoking in these data; calling it preventable by removing smoking needs causal assumptions and control of other explanations. A cohort can be prospective (exposure measured now, outcome later) or retrospective (past records identify the exposed and unexposed, who are followed up to the present). In the Dunedin birth cohort in New Zealand, cannabis use between ages 18 and 32 was associated with new periodontal attachment loss, with an adjusted RR of about 2.2 for the heaviest users (Thomson et al., 2008). Cohorts show temporality and give incidence, but they are slow, expensive, inefficient for rare outcomes and vulnerable to losses to follow-up.
A case–control study starts at the other end: people with the outcome (cases) and comparable people without it (controls), whose past exposure is compared. The investigator decides how many cases and controls to take, so risks cannot be calculated; instead the odds ratio OR = ad/bc is used. It approximates the RR only when the outcome is rare in the source population: with risks of 2% and 1%, RR = 2.00 and OR = 2.02, but with risks of 40% and 20%, RR is still 2.00 while OR = 2.67 — odds are not risks. With 60 smokers among 100 patients with oral cancer and 50 among 200 controls, OR = (60 × 150)/(50 × 40) = 4.5. Case–control studies are the design of choice for rare diseases such as oral cancer, and Doll and Hill’s work on smoking and lung cancer was one (Doll & Hill, 1950). Their weak points are the measurement of past exposure (recall bias) and the choice of controls (selection bias); a factor used for matching can no longer be studied, which is why matching on smoking would have hidden its effect.
Experimental studies
In a randomised controlled trial (RCT) the investigator assigns the intervention by random allocation, so each participant has the same chance of either group and unknown factors are balanced on average. If the groups differ at the end, the difference can be attributed to the intervention — the RCT is the “gold standard” for testing whether it works, for example whether fluoride varnish prevents caries. Randomisation must be protected by allocation concealment: whoever enrols a child must not know the next allocation. A placebo keeps participants unaware of their group, but the control need not be a placebo: when withholding an established benefit would be unethical, the control group receives the standard product, for example the standard varnish (an active control). Blinding should name who is unaware — participants, care providers, outcome assessors, analysts — because an examiner who expects a product to work may score the control group more strictly. A placebo is impossible for water fluoridation, sealants or a visible school brushing programme, but the outcome assessors can still be kept unaware.
When an intervention acts on groups, whole schools or towns are randomised (community or cluster trials). Weaker designs are common in dentistry: non-randomised trials such as the Vipeholm diet study, and before–after studies without a concurrent control, such as the Grand Rapids fluoridation trial, where other changes during the study can explain the result. If untreated caries falls from 40% to 30% in a programme school but also from 35% to 30% in a comparison school, the extra change is (30 − 40) − (30 − 35) = −5 percentage points, not −10 — and even that assumes similar background trends. Crossover trials, in which each participant is their own control, suit short trials of reversible conditions such as gingivitis but not caries. Efficacy asks whether an intervention works under ideal conditions; effectiveness whether it works in everyday practice.
Errors, causation and evidence
An association may be wrong for three reasons. Random error (chance) shrinks with larger samples. Bias — systematic error from non-comparable groups (selection bias) or from measuring exposure or outcome differently (information bias) — does not. Confounding comes from a third factor linked with both exposure and outcome: drinkers have more oral cancer partly because they also smoke more. In a hypothetical cohort, new tooth loss over five years affects 34% of mouthrinse users and 16% of non-users (crude RR 2.125), yet within each age group the risks are equal (10% under 50, 40% from 50) and RR = 1: users are simply older. Stratification reveals the confounder. Randomisation balances confounders, even unknown ones; observational studies can only restrict, match, stratify or adjust for those that were measured — and a larger sample improves precision, not validity.
To judge whether an association is causal, Bradford Hill’s viewpoints ask about temporality, strength, consistency, dose–response, plausibility, coherence and experimental evidence (Hill, 1965); only temporality is required. The viewpoints guide reasoning; they are not a score, and neither a large RR nor many satisfied viewpoints proves causation. For the effects of prevention and treatment, a well-conducted randomised comparison usually protects best against confounding, and the classic scale runs from RCTs and their systematic reviews (level I), through non-randomised controlled trials (II-1), cohort and case–control studies (II-2) and time series (II-3), to descriptive studies and expert opinion (III). But the strength of evidence depends on the question and on how well the study was done: burden needs a representative examination survey, rare harms a good case–control or cohort study, and many questions — are amalgams harmful? — cannot be tested in a trial at all.
Before opening the student tasks, remember the three questions of the class: who decided the exposure, is there a comparison group, and which came first?