18.1 Study Design, Bias & Causation

18.1 Study Design, Bias & Causation

Quick Answer: Match design to question: prevalence → cross-sectional; rare disease/multiple exposures → case-control (OR); incidence/multiple outcomes → cohort (RR); efficacy with least confounding → RCT. ARR = CER − EER; NNT = 1/ARR. Randomize to balance confounders, blind to reduce observer bias, analyze by intention-to-treat, and do not confuse earlier diagnosis (lead-time) or indolent disease detection (length-time) with longer life.

Biostatistics and epidemiology on the CBSE (and Step 1–style exams) reward disciplined labeling: name the design, name the measure, name the bias, then compute. This section builds the design hierarchy, risk metrics with worked numbers, bias taxonomy, mitigation strategies, and light causal reasoning including screening artifacts.

Hierarchy of Study Designs

Think of designs as tools ordered by how strongly they support causal inference when well executed—not as a moral ranking of investigators.

Case reports and series describe unusual presentations or clusters. They cannot estimate incidence or prove causality, but they generate hypotheses (e.g., a new drug rash series).

Cross-sectional studies measure exposure and disease at the same time (surveys, screening camps). They estimate prevalence and associations, but cannot establish whether exposure preceded disease. Classic trap: concluding that low exercise "causes" obesity from a one-time survey when reverse causation or confounding is equally plausible.

Case-control studies start with cases (disease) and controls (no disease), then compare prior odds of exposure. Ideal for rare outcomes and when many exposures are of interest. You generally cannot compute incidence from the sample (you fixed the number of cases), so the natural measure is the odds ratio (OR).

Cohort studies start with exposed vs unexposed people free of the outcome and follow them forward (or reconstruct forward with historical records). You observe incidence, so relative risk (RR) is natural. Good for rare exposures and multiple outcomes; expensive and slow for rare diseases with long latency unless the cohort is huge or retrospective.

RCTs assign intervention by chance, balancing known and unknown confounders in expectation. Blinding and allocation concealment protect against performance and detection bias. Ethics limit RCTs when the intervention is clearly harmful or when the outcome is extremely rare.

Meta-analyses combine quantitative results. Quality tracks the underlying studies: pooling biased observational studies yields a precise but still biased summary.

Relative Risk vs Odds Ratio

Definitions

Build a classic 2×2 from a cohort or trial (rows = exposure/treatment; columns = disease yes/no):

• Incidence in exposed = a / (a + b)
• Incidence in unexposed = c / (c + d)
• Relative risk (RR) = [a/(a+b)] ÷ [c/(c+d)]
• Odds of disease in exposed = a/b; in unexposed = c/d
• Odds ratio (OR) = (a/b) ÷ (c/d) = ad/bc

Rule for exams:

• Cohort / RCT with incidence data → prefer RR (and absolute measures).
• Case-control → OR (incidence usually not estimable).
• When disease is rare (roughly <10% in both groups), OR ≈ RR; when common, OR exaggerates the association relative to RR.

Worked example 1 — Cohort RR and OR

In a 5-year cohort of 2,000 smokers and 2,000 nonsmokers:

Incidence smokers = 80/2000 = 0.040 (4.0%)
Incidence nonsmokers = 10/2000 = 0.005 (0.5%)
RR = 0.040 / 0.005 = 8.0
OR = (80 × 1990) / (1920 × 10) = 159,200 / 19,200 ≈ 8.29

Disease is uncommon, so OR ≈ RR. Interpretation: smokers had eight times the risk of lung cancer versus nonsmokers over follow-up (observational—confounding by other factors still possible).

Worked example 2 — When OR diverges from RR

Common outcome (e.g., any infection after surgery):

RR = (40/100) / (20/100) = 2.0
OR = (40×80)/(60×20) = 3200/1200 ≈ 2.67

Same data, different numbers: reporting OR as if it were RR overstates relative effect when the outcome is common.

Worked example 3 — Case-control OR only

Investigators identify 100 myocardial infarction (MI) cases and 100 controls, then ascertain prior NSAID exposure:

OR = (30×85)/(15×70) = 2550/1050 ≈ 2.43

You cannot say "2.43 times the risk" as a population RR without incidence data; say "odds of prior NSAID use were 2.43-fold higher among cases than controls" (still subject to confounding and selection of controls).

Absolute Risk Reduction, NNT, and NNH

Relative measures hide baseline risk. Always recover absolute metrics for clinical meaning.

• Control event rate (CER) = outcome rate in control arm
• Experimental event rate (EER) = outcome rate in treatment arm
• Absolute risk reduction (ARR) = CER − EER (for beneficial reduction of bad outcomes)
• Relative risk reduction (RRR) = ARR / CER = 1 − RR
• Number needed to treat (NNT) = 1 / ARR (round up to whole patients for teaching)
• Absolute risk increase (ARI) = EER − CER when treatment raises harm
• Number needed to harm (NNH) = 1 / ARI

Worked example 4 — NNT with high baseline risk

In a secondary-prevention RCT, 5-year MI rates:

• Placebo: 20/100 = 0.20
• Drug X: 12/100 = 0.12

ARR = 0.20 − 0.12 = 0.08
RR = 0.12/0.20 = 0.60 (RRR = 40%)
NNT = 1/0.08 = 12.5 → 13 patients treated for 5 years to prevent one MI

Worked example 5 — Same RRR, different NNT (low baseline risk)

Primary prevention, same relative effect:

• Placebo event rate 2% (0.02)
• Drug event rate 1.2% (0.012)

ARR = 0.008; RRR still 40%; NNT = 1/0.008 = 125

Marketing may advertise "40% fewer events" in both trials; NNT shows far less absolute benefit when baseline risk is low—high-yield exam contrast.

Worked example 6 — NNH

Serious bleed rates: drug 3/100, placebo 1/100.
ARI = 0.03 − 0.01 = 0.02; NNH = 50.
If NNT for benefit is 13 and NNH is 50, roughly four patients benefit per one harmed for those endpoints (crude comparison—time frame and severity must match).

Bias Taxonomy

Bias is systematic error; it does not average out with larger n (unlike random error).

Confounding vs bias language: Confounding is a mixing of effects; it can sometimes be controlled in analysis if measured. Selection and information biases often cannot be fully fixed after the fact.

Confounding worked sketch

Crude data: heavy coffee drinkers have higher MI rates. Smokers drink more coffee and have higher MI rates. After stratification by smoking, coffee–MI association shrinks toward null → smoking was a confounder. Randomization aims to balance smoking (and unmeasured factors) across arms so crude treatment effects are unconfounded in expectation.

Mitigating Bias and Confounding

Per-protocol / as-treated analyses estimate effect among adherers but reintroduce selection confounding (who adheres differs). Exams often ask why ITT is preferred for primary superiority analyses of pragmatic trials.

Worked conceptual example — ITT vs per-protocol

RCT of exercise counseling: many assigned to exercise drop out. ITT still counts them in the exercise arm (conservative if dropouts do poorly). Per-protocol keeps only completers, who may be healthier → exaggerated benefit.

Causation: Hill Criteria (Light)

Bradford Hill viewpoints help judge whether an association is likely causal (none is absolute proof):

1. Strength — large RR/OR more suggestive (not required)
2. Consistency — repeated in different populations/methods
3. Specificity — one exposure–one effect (weak criterion; many causes are multifactorial)
4. Temporality — exposure before outcome (essential)
5. Biological gradient — dose–response
6. Plausibility — fits known biology
7. Coherence — consistent with natural history/lab data
8. Experiment — removal of exposure reduces disease; RCT evidence
9. Analogy — similar to other causal pairs

Exam use: absence of temporality kills causal claims; large, consistent, dose-responsive associations with experimental support are strongest narratives.

Lead-Time and Length-Time Bias (Screening Intro)

Lead-time bias: Screening diagnoses disease earlier. Survival measured from diagnosis appears longer even if death occurs at the same age. Fix: compare mortality rates (deaths per population-time), not survival from diagnosis alone.

Example sketch: Untreated aggressive cancer kills at age 60 whether diagnosed at 58 (2-year survival) or screened at 55 (5-year survival). Lead time = 3 years; true life span unchanged.

Length-time bias: Slowly progressive disease spends more time in a detectable preclinical phase, so screening disproportionately finds indolent cases with better prognosis. Aggressive interval cancers present clinically between screens. Fix: randomized screening trials with mortality endpoints; beware survival comparisons of screen-detected vs symptom-detected cases.

Integration for CBSE Vignettes

• Stem samples by disease and looks backward → case-control → OR.
• Stem follows exposed workers for incidence → cohort → RR, watch healthy-worker selection.
• Stem randomizes drug vs placebo → compute ARR/NNT; if they give only RRR, recover absolute rates if possible.
• Positive association disappears after adjusting for smoking → confounding.
• Unblinded radiologists more often call "progression" on new drug → observer bias.
• Screening program boasts longer 5-year survival without mortality drop → lead-time (and possibly length-time/overdiagnosis).

Map design → valid measure → absolute impact → residual bias. That sequence solves most study-design items on the CBSE.