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Among patients still alive at the same time after surgery, chemotherapy has an estimated lung-cancer death rate 3.71 times that of radiotherapy, assuming proportional cause-specific hazards. The estimated 95% confidence interval for this hazard ratio is $(1.583,8.697)$. Thus the fit suggests a higher instantaneous lung-cancer death rate on chemotherapy, with appreciable uncertainty in its size.

The null hypothesis of no treatment effect on that hazard is $H_0:{\gamma }_1=0$ against ${\gamma }_1\ne 0$. Its Wald test uses $Z=1.3113/0.4346\simeq 3.018$, approximately standard normal under the null hypothesis, with two-sided $p=0.00255$. This is evidence against equal lung-cancer death hazards in the fitted model. It is not a statement that five-year lung-cancer death probability is multiplied by 3.71 or that survival duration is divided by 3.71. The cumulative incidence function depends on both cause-specific hazards, and the model needs proportional-hazards and independent observation-censoring assumptions. In a randomised comparison the assigned treatment contrast is protected against baseline confounding, but the instantaneous comparison concerns the groups who have survived to the time in question; it does not identify a treatment effect within a common latent survivor subgroup.

Randomization makes assignment independent of the participants' pre-existing potential outcomes, giving an unbiased comparison of allocation groups under the usual trial assumptions. It therefore protects against baseline confounding, including from unmeasured factors, and supplies an assignment distribution for inference. Allocation concealment protects this step from recruitment decisions based on the upcoming assignment. It does not guarantee exact balance in every realized sample.

Use a randomized complete block design, with day as block and each biological cell as an experimental unit. Each day should contain two biological cells at each of the five dose levels. Each level then has ten replicates overall and occurs equally often in every day: the resulting block design is an orthogonal block design.

This spreads any day-to-day changes in preparation, temperature or measurement across all levels instead of confounding dose with day. Treat the zero level as a control with otherwise comparable handling. Keep the treatment-to-measurement delay standardized because the response variable is a diffusion rate measured immediately after preparation.

Write $y_{WP}$ and $y_{AP}$ for the estimated log odds ratios relative to the common control. Indirect treatment comparison uses the consistency relation ${\delta }_{WA}={\delta }_{WP}-{\delta }_{AP}$. For independent trials, subtraction adds their variances, givingThe substantive assumption is transitivity in network meta-analysis: the study populations, outcome definitions and follow-up are sufficiently comparable, particularly in their distributions of effect modifiers, that the two control comparisons estimate effects applicable to the same target population. The common control's name alone does not justify that assumption. This also assumes comparable marginal odds ratios; these need not equal covariate-adjusted odds ratios even without confounding.

Using the supplied rounded variances and the given standard normal quantile, the approximate confidence interval isOn the odds ratio scale this is $e^{-1.26}\simeq 0.284$, with approximate limits $(0.104,0.771)$. The estimated odds of recurrent stroke under treatment $W$ are about 28% of those under $A$, a reduction of about 72% in odds. The interval excludes equal odds, so this comparison provides evidence of lower odds under $W$ if the indirect treatment comparison assumptions hold. These are odds, not a 72% reduction in probability; a confidence interval describes the long-run coverage of the procedure, not a posterior probability for this particular interval.

Let $Y(1)$ and $Y(0)$ be the potential outcomes for the same individual under well-defined interventions setting the binary exposure to 1 and 0. The average treatment effect, also called the average causal effect on the additive scale, isThe average is over the target population. This compares hypothetical outcomes under two interventions, rather than the observed difference $\mathbb{E}[Y\mid X=1]-\mathbb{E}[Y\mid X=0]$, which can be distorted by confounding. For binary $Y$, the displayed contrast is a causal risk difference. Consistency in causal inference and a well-defined intervention, including an appropriate no-interference in causal inference assumption, give these potential outcomes their meaning.

For the electronic-record observational study, three strengths are:

Three weaknesses are:

For two-sample Mendelian randomization, three strengths are:

Three weaknesses are:

Thus the agreement supports the hypothesis, but does not establish the effect of a dietary intervention.

Two useful ways to strengthen the causal inference are:

These are complementary: the first changes the proposed exposure experimentally, and the second probes the validity and reproducibility of its genetic evidence.

The first model alone would suggest that more cycling is beneficial, but cycling was not randomized in that model: its coefficient can be distorted by confounding or reverse causality. The randomized incentive both substantially increased cycling and substantially increased asthma episodes.

If the incentive affects asthma only through cycling, it is an instrumental variable, and the corresponding Wald estimator of the effect per additional weekly mile isadditional episodes. Under that exclusion assumption the evidence therefore advises against cycling to work more often for this population. Without the exclusion assumption, the experiment establishes the harmful effect of the incentive itself but cannot by itself distinguish an effect of cycling from a direct effect of the monetary incentive.

Education is a causal risk factor if an intervention that changes educational exposure changes the distribution of the corresponding potential outcome for myopia. An observed statistical association need not have that interpretation. Shared causes such as socioeconomic circumstances, parental behavior, genetic traits, or preference for indoor near work can confound education and myopia. Reverse causality is also possible: children with impaired distance vision may select more reading and indoor study, which can increase educational attainment without education causing the impairment.

Restricting to pupils who already attended a Catholic middle school improves covariate balance: the treatment-group differences in family income, urban residence, and prior mathematics score are all much smaller. This makes severe extrapolation and measured confounding less prominent.

The restriction reduces the sample from $11,839$ to $1,006$, so estimates are less precise. It also changes the target population to Catholic-middle-school pupils, reducing external validity for all United States pupils.

In the full sample, covariate adjustment moves the estimated coefficient from $0.73$ to $0.32$, a large change consistent with substantial measured confounding. In the Catholic-middle-school subsample the estimates remain between $0.48$ and $0.60$, supporting the claim that restriction has already improved comparability. The cost is visible in the standard errors, which rise from about $0.08$--$0.09$ to $0.13$--$0.15$ despite similar coefficient magnitudes.

First, an observational study can suffer from confounding or reverse causality. Ill health may both lower circulating vitamin D and raise mortality, while lifestyle, socioeconomic status, and comorbidity may affect both variables. Randomization breaks these baseline associations in expectation.

Second, the interventions answer different questions. Supplementation may be too small, too late, too short, or poorly adhered to, and an average effect can be nearly zero when benefit is confined to people with severe deficiency. Such heterogeneous treatment effects can coexist with a strong observational gradient.

If sex predicts apprenticeship uptake, extreme UTC sex ratios create both confounding and weak overlap. Matching only the aggregate percentage of boys may leave no genuinely comparable control, and an additive distance can hide a large imbalance in this influential variable. Sex may also be an effect modifier, so the UTC effect can differ across these unusual compositions. One should enforce close sex-ratio balance and estimate sex-specific effects before standardizing them to the intended policy population.

Population stratification is systematic variation in allele frequencies between subpopulations. If those subpopulations also differ in outcome causes, genetic variant associations can exhibit confounding, violating instrumental-variable independence in Mendelian randomization.

Put $p_B={\mathrm{logit}}^{-1}(\eta +B)$ and $M(\eta )=\mathbb{E}(p_B)$. Differentiation gives $M^{\prime }=\mathbb{E}[p_B(1-p_B)]=M(1-M)-\mathrm{Var}(p_B)$. Hence the displayed derivative lies between zero and one, strictly below one for a nondegenerate random intercept. A marginal logit is therefore generally nonlinear and its slope differs from the conditional slope even without confounding. This is a precise instance of noncollapsibility of the odds ratio.

A statistical association is a systematic dependence between variables. It need not represent a causal effect, because it may arise from confounding, selection, or reverse causation.

Divide studies by a specified characteristic and estimate an effect in each subgroup, then test the difference using an independent subgroup contrast in meta-analysis or an appropriate interaction model. The test of a between-group difference is distinct from separate tests against no effect within each group. Exploratory splits can be affected by multiple testing and by confounding between study characteristics.

Treatment contamination occurs when participants in one arm of a randomized controlled trial receive an intervention assigned to another arm. This is distinct from contamination in robust estimation. The intention-to-treat analysis still compares randomized assignments, but intervention receipt becomes less separated between the arms, often diluting the assignment effect. Receipt-based comparisons can introduce confounding because receipt need not be randomized.