Free USMLE Step 1 Biostatistics and Epidemiology practice questions

The number needed to treat (NNT) is the reciprocal of the absolute risk reduction (ARR). The ARR is the control event rate minus the treatment event rate: 4.0% minus 3.0% = 1.0%, or 0.01. The NNT is therefore 1/0.01 = 100: 100 patients must take the drug for 3 years to prevent one stroke. The press release reports the relative risk reduction (RRR), ARR divided by the control rate (0.01/0.04 = 25%). The RRR sounds impressive but hides how small the absolute benefit is when the baseline risk is low; the same 25% RRR in a high-risk population with a 20% event rate would give an ARR of 5% and an NNT of 20. The NNT always refers to a specific outcome and time period, and it should be weighed against the number needed to harm (for an anticoagulant, major bleeding).

A. 4 is the reciprocal of the RRR expressed as a fraction (1/0.25), a common error that confuses relative with absolute benefit.

B. 25 is the RRR as a percentage, not a number of patients.

C. 33 is the reciprocal of the treatment-group event rate (1/0.03), which has no meaning as an NNT.

D. 75 is the percentage of residual risk (the relative risk of 0.75 multiplied by 100), not an NNT.

The design is named by where the study starts and in which direction it looks. These investigators began with disease status, selecting children with hepatoblastoma (cases) and children without cancer (controls), and then looked back at prior exposures such as maternal smoking. That is a case-control study. Its measure of association is the odds ratio (ad/bc from the 2 x 2 table); because the investigators chose the numbers of cases and controls, incidence and relative risk cannot be calculated. When the disease is rare, as hepatoblastoma is, the odds ratio approximates the relative risk. This design is efficient for rare diseases, but it is prone to recall bias (mothers of affected children may report exposures differently) and to selection bias in choosing controls.

A. A prospective cohort would enroll pregnant women by smoking status and follow their children forward for new tumors, which would be impractical for so rare a disease.

B. A retrospective cohort uses old records to define groups by exposure and then traces outcomes; here groups were defined by disease.

C. A cross-sectional study measures exposure and disease at a single point in time in a sample of a population and yields prevalence.

D. In a randomized controlled trial the investigator assigns the exposure, which is impossible and unethical for maternal smoking.

A type I error occurs when a study rejects a null hypothesis that is actually true, concluding that a difference exists when it does not: a false positive. Its probability is alpha, the significance level chosen before the study. With alpha set at 0.05, about 1 in 20 trials of a completely ineffective treatment will reach p below 0.05 by chance alone. Here the first trial declared the extract effective, but much larger, well-conducted trials and a meta-analysis show no true effect, so the original result was most likely a chance false positive. The quality features described (blinding, concealment, minimal attrition) argue against bias and point to random error.

B, type II error, is the opposite mistake: failing to reject a false null and missing a real effect (a false negative), usually because of an underpowered study; the first trial did not miss an effect, it found one that does not exist. C, confounding, is a distortion by a third variable related to both exposure and outcome; randomization balances known and unknown confounders, making it an unlikely explanation. D, selection bias, is a systematic error in who enters or stays in a study, and the stem describes concealed allocation and minimal loss to follow-up. E, effect modification, is a true difference in effect across subgroups, not a spurious overall result.

The investigators constructed receiver operating characteristic (ROC) curves, which plot the true-positive rate (sensitivity) against the false-positive rate (1 - specificity) as the cutoff moves. The area under the curve (AUC) summarizes overall discrimination across all cutoffs and equals the probability that a randomly chosen patient with bacterial pneumonia has a more abnormal value than a randomly chosen patient with viral pneumonia. An AUC of 1.0 is perfect discrimination. An AUC of 0.50 means the curve lies on the diagonal: at every cutoff, the true-positive rate equals the false-positive rate, so a positive result is no more likely in diseased than nondiseased patients (LR = 1). Biomarker Z therefore performs no better than a coin flip. Biomarker X, with the curve bowing toward the upper-left corner, discriminates best.

A. On the diagonal, sensitivity varies from 0 to 100% as the cutoff changes; it simply always equals 1 - specificity. C. PPV depends on prevalence and cannot be read from the AUC. D. A test can rule out disease only if a negative result is much less likely in diseased patients (low LR-), which a test on the diagonal cannot achieve. E. The AUC is not the accuracy at a single cutoff; it is a summary over all cutoffs.

This is a case-control study: subjects were selected by outcome (infection vs no infection) and exposure was measured backward. Because the investigators chose how many cases and controls to enroll, incidence cannot be calculated, so the correct measure is the odds ratio.

Set up the 2 x 2 table with exposure in rows: a = exposed cases = 60, b = exposed controls = 30, c = unexposed cases = 40, d = unexposed controls = 70. OR = ad/bc = (60 x 70)/(30 x 40) = 4200/1200 = 3.5. Equivalently, the odds of exposure among cases (60/40 = 1.5) divided by the odds of exposure among controls (30/70 = 0.43) is 3.5. Proton pump inhibitor users had 3.5 times the odds of infection. Because community-acquired infection is uncommon, this OR approximates the relative risk under the rare disease assumption.

A (0.29) is the inverted ratio, bc/ad, which would wrongly suggest protection. B (0.43) is only the odds of exposure among controls (30/70). C (1.5) is only the odds of exposure among cases (60/40), without dividing by the control odds. D (2.0) divides the proportion of exposed cases (60%) by the proportion of exposed controls (30%); a ratio of exposure proportions is neither a relative risk nor the OR.

The outcome is time to an event (death) with censoring: patients were followed for different lengths of time and many were alive at last contact. The investigators also need to adjust for several confounders at once. Cox proportional hazards regression handles both requirements. It models the hazard, the instantaneous death rate among patients still at risk, as a function of several covariates (chemotherapy, age, stage, performance status) and reports an adjusted hazard ratio for each. It is semiparametric: it does not require specifying the shape of the baseline hazard, but it does assume that hazard ratios stay constant over time. Like any regression, it adjusts only for measured confounders.

B. Multiple linear regression is for a continuous outcome such as blood pressure, and it cannot handle censored survival times.

C. Multivariable logistic regression models a binary outcome (dead or alive at a fixed time) and gives an adjusted odds ratio. It discards information on when deaths occurred and handles patients censored before that time point poorly.

D. Spearman correlation measures the strength of a monotonic association between two ranked variables; it does not compare survival or adjust for covariates.

E. The log-rank test has already been done. It compares whole survival curves and returns a single p-value, but it is unadjusted and gives no effect size.

The experiment criterion asks whether changing the exposure changes the risk of the outcome. Evidence can come from randomized trials, from people who remove an exposure themselves (lung cancer risk declines progressively after quitting smoking), or from public health interventions. Here, low folate was the suspected cause, the population's folate intake was deliberately raised by fortification, and neural tube defects fell afterward. Folate supplies one-carbon units for nucleotide synthesis, which the rapidly dividing neuroectoderm needs when the neural tube closes during week 4 of development, before many women know they are pregnant; this is why fortification of a staple food works better than relying on supplements started after pregnancy is recognized. Showing that risk falls when an exposure is altered is among the most persuasive kinds of causal evidence, because it mimics the logic of a trial.

A. Analogy means similar exposures cause similar effects, as when thalidomide made other drugs in pregnancy suspect; the data here concern folate itself. C. Coherence means the association fits known natural history and biology, such as population trends following exposure trends; the key observation is the response to a deliberate intervention. D. Specificity means one exposure causes one disease; it is the weakest criterion, and an unchanged rate of other defects does not show that folate deficiency causes only neural tube defects. E. Temporality, exposure preceding outcome, is the only essential criterion and is satisfied here, but timing alone is not what these data add; the distinctive evidence is that deliberately changing the exposure changed the risk.

The trial's sample size and alpha (usually 0.05) protect only the prespecified primary endpoint. That endpoint failed: the hazard ratio of 0.94 has a CI including 1. Once the primary analysis is negative, any positive secondary endpoint, subgroup or post hoc finding is hypothesis-generating, not confirmatory. With 14 subgroups tested at 0.05, the chance that at least one appears significant by chance alone is about 1 minus 0.95 to the 14th power, or roughly 50%. A Bonferroni threshold would be 0.05 / 14, about 0.0036. A credible subgroup effect should be prespecified, few in number, supported by a significant test of interaction (showing the effect truly differs between women and men), biologically plausible and replicated. The advertisement's "proven" headline built on a subgroup after a failed primary endpoint is a classic red flag.

A is wrong because a single subgroup result from many comparisons after a failed primary endpoint cannot establish efficacy. B is wrong because a smaller or absent benefit in men is not evidence of harm, and no harm data are given. C is wrong because the primary result is the trial's valid, prespecified answer; subgroup findings do not overturn it. D is wrong because the overall hazard ratio of 0.94 is not significant.

Length-time bias arises because slowly progressive tumors have a long detectable preclinical phase, so a periodic screening test is much more likely to catch them. Aggressive tumors have a short preclinical window; they grow from undetectable to symptomatic between scheduled screens and appear as interval cancers. The screen-detected group is therefore enriched for indolent, biologically favorable disease, and its better survival reflects tumor biology rather than any benefit of early detection. The extreme form is overdiagnosis, finding cancers that would never have caused symptoms in the patient's lifetime. The proper way to judge a screening program is by disease-specific mortality in a randomized comparison of screened and unscreened populations.

A, lead-time bias, makes survival look longer because the clock starts earlier at diagnosis even though death is not delayed; the stem states that survival remained better after correcting for the earlier diagnosis date, and the clue here is the difference in tumor grade and growth rate. B, the Hawthorne effect, is a change in subjects' behavior because they know they are being observed. C, recall bias, is differential memory of past exposures in a case-control study. D, Berkson bias, is a selection bias from using hospitalized controls in a case-control study.

Each design has its own success criterion, judged from the confidence interval against the prespecified margin (delta), not from the point estimate or the p-value.

Equivalence requires the entire CI to lie between minus delta and plus delta, showing the new product is neither meaningfully worse nor meaningfully better. Here the lower limit (minus 3) is inside minus 10, but the upper limit (plus 11) extends beyond plus 10, so a clinically meaningful difference in favor of the biosimilar cannot be excluded and equivalence is not established.

Noninferiority requires only that the limit on the unfavorable side stay within the margin. The unfavorable limit is minus 3, well inside minus 10, so the biosimilar is not worse than the reference by more than the acceptable margin. Agreement of intention-to-treat and per-protocol results supports this, because nonadherence pulls ITT toward the null and is anti-conservative in noninferiority and equivalence trials.

Superiority would require the CI to exclude 0, the no-difference value for a difference; this CI includes 0, so superiority is not shown.

A is wrong because equivalence depends on the whole interval, not the point estimate. B is wrong because the CI crosses 0. C is wrong because the entire interval, including the unfavorable limit, lies above minus 10. E is wrong because the noninferiority criterion is clearly met.