Answers for every SmartData Tools calculator
Yes. Every calculator on this site runs entirely as JavaScript in your own browser — there's no signup, no paywall, and no server processing your inputs.
No. Each tool reimplements the relevant statistical formula (Welch's t-test, Schoenfeld's log-rank formula, Simon's two-stage search, BOIN's posterior-probability boundaries, and so on) directly, so you get the same numbers you'd get from statistical software without installing anything.
No. All calculations run client-side in your browser. The one exception, the Optimal Cutoff Point tool, processes your uploaded CSV locally in the browser as well — it is never sent to a server.
Comparing two independent groups' means: Two-Sample T-Test. A single group against a fixed benchmark: One Sample Mean or One Sample Proportion. Comparing two proportions: Comparison of Two Proportions. A time-to-event outcome: Survival Analysis. Planning an early-phase trial: Simon Two-Stage or BOIN.
Yes. The catalog is /tools.json. For most calculators, the math is also available as the ES module /engine/engine.mjs (calculate({ tool, calculator, params })) — importable from Node without a browser. See tools.json's engine.coverage for which calculators are included. Inputs stay on your machine; nothing is sent to a server.
Student’s t-test assumes both groups have the same variance, which is rarely true and can distort your power estimate when it doesn’t hold. Welch’s version handles unequal variances and unequal group sizes correctly, and reduces to the standard t-test as a special case when the variances happen to be equal — so there’s no downside to using it by default.
Set the allocation ratio (group 2 size ÷ group 1 size) to whatever you expect — for example 2 for a 2:1 randomization. The calculator solves for the group 1 size that hits your target power at that ratio; unequal allocation always requires a somewhat larger total sample size than 1:1 for the same power.
From a pilot study, a similar published trial measuring the same outcome, or a conservative estimate from the literature. Because required sample size scales with the square of the SD, an SD that’s too low is the most common reason a study ends up underpowered — when in doubt, round up.
No — this calculator works directly with your two raw means and standard deviations rather than a standardized effect size. If you only have a Cohen’s d value, back out a mean difference by multiplying d by your assumed (pooled) SD, then enter that mean difference and SD directly.
The chi-square (normal-approximation) test is the standard choice for planning when expected cell counts will be reasonably large (a common rule of thumb is at least 5 per cell). For trials that may enroll very few participants per arm or expect proportions very near 0 or 1, Fisher’s exact test is safer for the actual analysis, though it typically requires a somewhat larger sample to reach the same power.
No. The formula here matches the uncorrected Pearson chi-square/z-test. Continuity-corrected versions (e.g. Yates’) generally need a slightly larger sample size for the same power — if your analysis plan specifies a corrected test, budget a small margin above what’s shown here.
It’s the ratio of group 2’s size to group 1’s size (n2 ÷ n1). Use 1 for equal group sizes; use a value like 2 for a 2:1 randomization (e.g. when one arm is more costly or the comparator group is more available).
The normal approximation is least accurate when both proportions are close to 0 or 1 and sample sizes are small. In that regime, treat the result as a starting estimate and consider validating with an exact method before finalizing a small trial’s enrollment target.
A paired design’s power comes from each pair’s within-subject correlation canceling out shared variation. Higher positive correlation shrinks the SD of the difference (and thus the required sample size); a correlation near zero makes pairing offer little advantage over an unpaired design; negative correlation can make pairing worse than an unpaired test.
For repeated measures on the same subject (e.g. pre/post), correlations of 0.3–0.7 are common starting assumptions, but this varies enormously by outcome — check similar published studies reporting a within-subject correlation or the raw paired data if available, and favor a conservative (lower) value if unsure, since it yields a larger, safer sample size estimate.
Whenever you can measure the same experimental unit (person, animal, sample) under both conditions, since it usually needs a much smaller sample than an independent-groups design to detect the same effect — provided the outcome is reasonably correlated across the pair.
Patients who enroll later have less time to reach an event by the study’s end. Uniform accrual over the accrual period plus a fixed additional follow-up is the standard assumption for converting a target number of events into a total enrollment size — entering both separately (rather than one combined duration) lets the calculator account for this correctly.
Either — they’re equivalent under the exponential assumption used here. Switch to "Median survivals" mode if you have (or can estimate) the two arms’ median survival times directly; the hazard ratio is then derived as control-median ÷ treatment-median.
Schoenfeld’s formula for the number of events needed is quite robust to departures from the exponential assumption under proportional hazards. The exponential assumption matters more for converting that event count into a patient sample size — if survival is markedly non-exponential (e.g. a long plateau), treat the resulting sample size as approximate and consider consulting a biostatistician for a piecewise-exponential or Kaplan–Meier-informed calculation.
The log-rank test is powered by the number of observed events, not the number of patients enrolled. Longer follow-up (or accrual) gives each patient more time to have an event, so fewer patients are needed to accumulate the same target event count.
Non-inferiority asks a one-directional question: is the new treatment not meaningfully worse than control (e.g. a cheaper or more convenient treatment that only needs to not underperform)? Equivalence asks a two-directional question: does the difference fall within an acceptable range in either direction (e.g. comparing two formulations expected to behave the same way).
The margin should be a clinically or scientifically meaningful threshold agreed upon before the study, not derived from the data. Regulatory guidance for many disease areas specifies conventional margins; in the absence of a domain standard, a common (though debated) rule of thumb is a fraction (e.g. half) of the effect size the active comparator itself showed over placebo.
Non-inferiority and equivalence tests are inherently one-sided (you only care about one direction, or you're running two one-sided tests for equivalence), and 0.025 one-sided is the conventional regulatory default because it matches the stringency of a standard 0.05 two-sided superiority test.
Leave it at 0 (the default) — this is the most common and conservative assumption for planning a non-inferiority or equivalence trial. A non-zero value is only appropriate if you have prior evidence that the treatments truly differ by some known amount.
Cohen's f is the standard deviation of the group means divided by the common within-group SD. Rather than compute f directly, enter the group means you actually expect (from pilot data or the literature) and the common SD — the calculator derives f for you, so you can reason in the original units of your outcome instead of an abstract effect size.
A significant omnibus ANOVA result only tells you that not all group means are equal — it doesn't say which pairs differ. Planning to follow up with pairwise comparisons (e.g. Tukey's HSD) is standard practice, though this calculator sizes only the omnibus test, not the follow-up comparisons.
No — this calculator assumes equal n per group, the standard and most efficient allocation for a fixed total sample size. If your design requires unequal groups (e.g. a larger control group), treat this result as an approximate starting point.
The formula assumes homogeneous within-group variance (the standard ANOVA assumption). If group variances differ substantially, consider Welch's ANOVA for the analysis itself; this calculator's power estimate will be less accurate in that situation.
Both compare the same subjects under two conditions, but the Paired T-Test is for a continuous outcome (e.g. a measurement) while McNemar's test is for a binary outcome (e.g. present/absent, pass/fail). If your paired outcome is binary, use this calculator instead.
They're the two types of discordant pairs: p₀₁ is the proportion of pairs negative under condition 1 but positive under condition 2, and p₁₀ is the reverse. McNemar's test only uses these discordant pairs — concordant pairs (same outcome under both conditions) contribute no information about a change.
It depends heavily on your outcome's stability between conditions — for a rarely-changing outcome, discordance might be under 10%; for a frequently-changing one, it could be 30% or more. Check similar published studies reporting a 2×2 concordance table for your outcome, and favor a conservative (smaller) estimate if unsure, since a smaller discordant proportion requires a larger total N for the same power.
McNemar's test power depends only on the discordant pairs, so the effect size is naturally expressed as the odds ratio between the two discordant-pair probabilities (ψ = p₀₁/p₁₀), not the overall proportion positive under either condition.
The normal approximation can be noticeably inaccurate when the proportion is near 0 or 1, or when the sample size is small — both common in single-arm studies. The exact binomial test works directly with the binomial distribution, so it stays valid across the full range of proportions and sample sizes.
Because the exact binomial test’s rejection region is a discrete set of integer outcome counts, achieved power increases in steps rather than smoothly as n grows — so the smallest n clearing your target power can jump rather than increase gradually, unlike normal-approximation formulas.
Two-sided is the standard default and detects a difference from the reference proportion in either direction. Use one-sided only when you have committed in advance to a specific direction of effect (e.g. testing only whether a response rate exceeds a historical benchmark, never whether it’s lower).
A one-sample t-test compares your sample’s mean to a single fixed number (e.g. a historical benchmark or regulatory threshold). A paired t-test compares two measurements taken on the same subjects (e.g. before vs. after) — use that calculator instead if every observation has a natural partner.
You almost never do in practice — use your best estimate from pilot data or comparable published studies. The formula here treats it as known for planning purposes, matching standard practice; if your study will instead estimate SD from the same data, your realized power may differ somewhat from the plan.
Two-sided is the conservative, generally-expected default: it detects a difference from the reference value in either direction. Choose one-sided only when a difference in one specific direction has no clinical or scientific relevance and you commit to that direction before seeing any data.
Sample size scales roughly with the square of (zα + zβ), so power near 0.95–0.99 needs meaningfully more subjects per percentage point than power in the 0.80–0.90 range. 80% power is a common convention, not a statistical requirement — raise it when the cost of missing a true effect is high.
Wilson is a widely-recommended general-purpose default: it stays accurate across small samples and proportions near 0 or 1, without being as conservative (overly wide) as Clopper–Pearson. Use Clopper–Pearson when you specifically need a guaranteed-coverage "exact" interval, often required in regulatory or diagnostic-accuracy reporting.
The Wald interval (the textbook ±z·SE formula) is known to perform poorly for small samples or proportions near 0 or 1 — its actual coverage can fall well below the stated confidence level, and it produces a zero-width or out-of-range interval when the numerator equals 0 or the denominator. It’s included here mainly for comparison with textbook formulas, not as a recommended default.
Yes — enter a comma-separated list of numerators (e.g. "3,7,12") that all share the same denominator, and the calculator returns one row per numerator using the selected method.
Both are adjustments designed to fix Wald’s small-sample problems while staying simpler than Clopper–Pearson. Agresti–Coull adds pseudo-observations before applying the Wald formula; Jeffreys uses a Bayesian interval from the Jeffreys prior. Both perform similarly to Wilson in most practical cases; pick whichever your field’s literature conventionally reports.
Minimax minimizes the largest possible sample size the trial could use, useful when enrollment capacity is a hard constraint. Optimal minimizes the expected sample size assuming the treatment is truly ineffective (p0), which tends to save patients on average at the cost of a higher worst-case N — a common choice when protecting patients from an ineffective treatment is the priority.
Widen your N1/N2 search range (a larger maximum sample size gives the search more room to find a design meeting your alpha/power targets), or reconsider whether alpha and power are set realistically tight for the difference between p0 and p1 you’re trying to detect.
The reported design specifies exact stage-1 and final sample sizes and stopping boundaries; deviating from them (e.g. enrolling a slightly different number of patients) changes the design’s actual operating characteristics. Minor deviations are common in practice, but the stated alpha/power apply only to the exact design as specified.
BOIN’s escalation/de-escalation boundaries are derived to minimize incorrect decisions under a range of possible true toxicity curves, and its boundaries don’t depend on the shape of the dose–toxicity curve. It generally identifies the correct maximum tolerated dose more reliably than 3+3 while using a comparable number of patients.
φ₁ (lower bound) and φ₂ (upper bound) define the toxicity range considered acceptably close to your target rate φ; the defaults (0.6×φ and 1.4×φ) work well for most trials. Override them only if your protocol specifies a narrower or wider de-escalation/escalation margin around the target.
These are optional BOIN variants: modifications add extra safety/futility stopping rules on top of the base design, and accelerated titration allows faster initial dose escalation (typically single-patient cohorts) before switching to the standard BOIN rule — use them only if your protocol specifically calls for that variant.
O'Brien-Fleming spends very little alpha at early looks (very high evidence bar to stop early) and most of it near the final analysis, so the final-analysis threshold barely differs from a non-sequential design — a common default. Pocock spends alpha more evenly across looks, making early stopping easier but requiring a stricter final-analysis threshold, which can be preferable when stopping early for a strong effect is a priority.
The classic 1970s-era tables were computed for a fixed, pre-specified number of equally-spaced looks using discrete group sequential theory. This calculator uses the more modern, more flexible Lan-DeMets alpha-spending-function approach, which approximates the same boundary shapes but isn't numerically identical — both control the overall Type I error correctly at the specified alpha.
It means each interim analysis is planned to occur after an equal fraction of the total planned information (roughly, sample size or events) has accrued. If your actual interim timing deviates meaningfully from the plan, the exact boundaries should be recomputed for the observed information fractions — a limitation of this calculator's current equally-spaced-only scope.
No — this tool computes only the stopping boundaries themselves. A full group sequential design also typically inflates the maximum sample size somewhat above the fixed-sample (non-sequential) size to maintain power despite the possibility of early stopping; that inflation factor is not computed here.
Maximizing raw accuracy can pick a degenerate cutoff when the two outcome classes are imbalanced (e.g. always predicting the majority class). Youden’s index balances sensitivity and specificity equally, giving a cutoff that performs well on both classes regardless of their relative prevalence.
It reflects how much the estimated optimal cutoff (and its sensitivity/specificity) might vary if you drew a different sample from the same population — a wide interval signals that your current dataset may be too small to pin down a stable cutoff.
Two columns: a continuous predictor value and a binary outcome (0/1) for each row, with a header row. See the tool’s file-upload area for the exact expected column layout.
It’s a first-order (linearized) approximation and degrades when the denominator Y has a large coefficient of variation relative to its mean (roughly, when Y could plausibly be close to zero) — in that regime the ratio’s distribution becomes heavy-tailed and this formula can understate its true variability.
The correlation between X and Y across the population you’re modeling — e.g. if X and Y are both physiological measurements on the same subjects, they’re often positively correlated, which changes (usually reduces) the variability of their ratio compared to assuming independence.
Fieller’s theorem provides an exact confidence interval for a ratio of two normal random variables and doesn’t rely on the delta method’s linear approximation — consider it when precision matters and the denominator’s variability is not small relative to its mean.
Reliability/agreement studies are usually designed to pin down the ICC to a useful precision (e.g. "within ±0.1") rather than to test a specific hypothesis, since there often isn't a natural null value to test against. Precision-based planning directly answers "how many subjects until my estimate is precise enough to be useful?"
Both help, but with diminishing returns from adding raters: going from 2 to 3 raters per subject usually narrows the CI more than going from 3 to 4, and beyond roughly 4-5 raters, adding more subjects is typically far more efficient than adding more raters.
No — this formula assumes a one-way random-effects model (raters/replicates treated as randomly sampled and not individually distinguished). Two-way models (raters as a fixed factor, or accounting separately for rater bias) have different variance formulas not covered by this calculator.
No — it's a large-sample approximation validated by Bonett to be accurate in typical planning scenarios, but treat it as a planning estimate rather than an exact guarantee, particularly for very small k or ICC values near 0 or 1.
Reference AUC (H₀) is the value you're testing against — almost always 0.5 (a classifier with no discriminative ability, equivalent to chance), though any target AUC works. Anticipated True AUC (H₁) is the AUC you expect your classifier to actually achieve, based on pilot data or prior studies; the calculator sizes the study to reliably distinguish that AUC from the reference.
n1 is the number of subjects with the condition of interest (positive/diseased), and n2 is the number without it (negative/non-diseased) — the two groups whose test results are compared to build the ROC curve. The allocation ratio is n2/n1.
This is expected and matches the literature: near-chance discrimination (AUC close to 0.5) is intrinsically hard to distinguish from true chance and needs a large sample, while a strongly discriminating classifier (AUC near 0.9-1.0) is easy to distinguish from chance with comparatively few subjects.
No — it uses the Hanley-McNeil (1982) approximation to AUC variance (the negative-exponential special case of their formula, expressed purely in terms of AUC) with a normal approximation for power, a standard large-sample method, but treat the result as a planning estimate. Accuracy can degrade for very small groups, AUCs near 0 or 1, or score distributions with substantial ties.
No — this tests a single classifier's AUC against a fixed reference value. Comparing two independent or paired (correlated) AUCs needs a different variance formula and isn't covered by this calculator.