Composed Pipeline Type I Error Simulator

2.1 Trial structure

Two-arm Phase II oncology design with binary endpoint (e.g., ORR). The default schedule mirrors the JSM 2026 reference design: monitoring looks at $n \in \{30, 45, 60, 90\}$, planned final at $n_{\text{base}} = 90$, cap at $N_{\max} = 150$, and SSR firing at $n = 45$ via blinded pooled response. Treatment and control arms accrue concurrently; allocation is either fixed 1:1 alternation (when RAR is off) or Thompson Sampling after a 10-patient burn-in (when RAR is on).

2.2 MAP prior

Method background: Bayesian Historical Borrowing (MAP priors, robustification, prior-data conflict).

The control prior is a Beta mixture

fitted with RBesT from the historical cohorts ($n = 50, 40, 60$; response rates 26%, 25%, 25%; pooled 38/150 = 0.2533), giving the three-component default $w = 0.5887,\ \mathrm{Beta}(18.403, 53.273)$; $w = 0.2113,\ \mathrm{Beta}(1.956, 4.703)$; and a flat robustifying $w = 0.2000,\ \mathrm{Beta}(1, 1)$. Mixture weights are updated at each interim via the log marginal likelihood. The treatment-arm posterior uses an independent Jeffreys prior — historical borrowing applies only to control.

The reference rate is ambiguous, so name it explicitly. The threshold is calibrated at the design anchor $p_0 = 0.25$, which is not the mean of any prior in play: the dominant informative component has mean 0.2568, the full robustified mixture has mean 0.3132, and the historical pooled rate is 0.2533. Describe $p > 0.25$ as departure of the baseline rate from the calibration anchor, never as “$k$ percentage points above the prior mean.”

2.3 Bayesian monitoring

Method background: Bayesian Sequential Monitoring (posterior-probability stopping rules).

At each scheduled look the calculator computes

by deterministic Gauss–Legendre quadrature (400 nodes) as $\int f_e(x) F_c(x)\,dx$, where $f_e$ is the Jeffreys treatment posterior density and $F_c$ the control posterior mixture CDF. Stop for efficacy if this posterior probability exceeds $\gamma^*$. Quadrature replaced an earlier 2,000-draw Monte Carlo estimate: the monitoring rule takes a maximum over interim looks, so Monte Carlo noise inflates that maximum and identical trial data could otherwise yield different decisions. The default $\gamma^* = 0.96566$ comes from a grid-free binary search with the blinded nuisance SSR active, and gives in-sample T1E = 0.0248 (MCSE 0.0011, $N = 20{,}000$) at the design anchor $p_0 = 0.25$ with no trend. Note this is in-sample calibration: the search targets the empirical calibration sample exactly, not the population Type I error, so out-of-sample behaviour is unverified.

2.4 Blinded SSR

Method alignment: Blinded SSR and this composed pipeline now use the same core principle: re-estimate a binary nuisance level from blinded pooled outcomes while holding the planned treatment effect fixed. This is consistent with the binary internal-pilot framework of Friede–Kieser (2004). The implementation here remains a conventional-style working rule embedded in a different pipeline: its planning calculation assumes 1:1 allocation, whereas the simulated trial can use Thompson-sampling RAR and a Bayesian posterior-probability final decision. Its reference Wald power is therefore not the exact power of the full composed design.

At $n_{\text{ssr,trig}}$ the pooled response count $x_{\text{pool}} = x_e + x_c$ defines$\hat p_{\text{pool}}$. With planned effect$\Delta = 0.20$, working rates are imposed symmetrically around the blinded estimate:

The target is not an arbitrary 80% conditional-power threshold. It is the one-sided fixed-sample Wald power implied by the original$N=90$ design at $(p_c,p_e)=(0.25,0.45)$, which is 0.5296. The recalculated working 1:1 total is

and $N_{\mathrm{final}}=\min\{N_{\max},\max(N_{\mathrm{base}},N_{\mathrm{work}})\}$. Only $(x_{\mathrm{pool}},n_{\mathrm{int}})$enters the rule; arm labels, arm-specific outcomes, posterior probabilities, and the realized allocation ratio do not. At the default $n=45$ look, exhaustive evaluation of all pooled counts maps to final $N=90$through 100.

2.5 Response-Adaptive Randomization

Method background: Adaptive Randomization (Thompson sampling, DBCD, Neyman, Pocock–Simon).

Thompson Sampling: at each enrollment after a 10-patient burn-in, sample one Beta variate from each arm's posterior and allocate to whichever variate is larger. This is the canonical TS reference implementation; it converges toward complete allocation to the better arm (a fundamentally different limit from the Rosenberger DBCD target).

2.6 Time trend

Linear drift on a fixed per-patient scale anchored to the planned horizon: $p_{\text{arm}}(t) = p_{\text{arm,base}} + \delta \cdot t$ with $t = i / (n_{\text{base}} - 1)$. Both arms drift in parallel under H₀, so the data-generating null is preserved. Coupling RAR with this drift can create allocation imbalance that affects the final analysis, although the experiment does not isolate an RAR-specific trend channel.

Note $t$ is not capped at 1: when SSR extends enrollment past $n_{\text{base}}$ drift keeps accruing at the same per-patient rate, which is intended — a longer trial spans more calendar time. (A trial expanded to $n = 100$ accrues total drift $0.05 \times 99/89 \approx 0.056$, not 0.05.) Only the resulting probability is clamped to $[0, 1]$. Dividing by the re-estimated sample size instead would make normalized time jump backward the moment SSR fires, an SSR-induced artifact.

Each preset on the calculator runs a multi-scenario batch corresponding to a table in the JSM paper.

4.1 The estimand

On the constant-rate boundary — $p_e = p_c$ with no time trend — the reported rejection rate is the frequentist Type I error rate, not a posterior predictive error rate conditional on prior beliefs. When a shared trend is active the rate over calendar time is no longer constant, so the manuscript reports those cells as rejection probabilities rather than Type I error. The prior–data conflict scenarios are realistic situations where the historical prior is misspecified relative to the current trial population, but H₀ still holds in the current data. The inflation we report is the false-positive rate under the current trial's data-generating null — the regulatory-relevant quantity, not a Bayesian robustness diagnostic.

4.2 Monte Carlo uncertainty

The simulator reports the rejection rate, its binomial Monte Carlo standard error $\text{MCSE} = \sqrt{\hat p (1 - \hat p) / N_{\text{sim}}}$, and a 95% Wald CI. At $N_{\text{sim}} = 5{,}000$ with $\hat p \approx 0.08$, MCSE ≈ 0.0038 and the CI half-width is about ±0.0075. To halve MCSE, run at $N_{\text{sim}} = 20{,}000$ in the Advanced panel.

4.3 How this engine compares to the paper's R runs

The paper's reference numbers were generated in R (Mersenne Twister PRNG); this calculator is a Python/NumPy (PCG64) port. Same seed values give different streams, so a single-seed run drifts by a few MCSE even when two engines are mathematically equivalent. The calculator presets are pinned to the final published design and compare each run with the manuscript value using the combined Monte Carlo uncertainty from both simulations. Treat a few-MCSE single-seed discrepancy as a prompt to increase replications and compare independent seeds, not as deterministic non-reproduction.

Two details of the reference implementation matter enough to call out, because getting either wrong shifts results in trend-active scenarios specifically. First, calendar drift accrues on a fixed per-patient scale anchored to the planned horizon. If the denominator tracked the re-estimated sample size instead, normalized time would jump backward the moment SSR fired and the response probability would fall — an artifact induced by SSR that contaminates both the SSR effect and the departure × trend interaction. Second, the monitoring posterior is computed by deterministic quadrature, not Monte Carlo: because the monitoring rule takes a maximum over interim looks, MC noise inflates that maximum and identical trial data could otherwise yield different decisions.

4.4 Interaction term

When the Departure × Trend 2×2 preset finishes, the calculator displays $\Delta_{\text{interaction}}$ below the results table. A positive value would mean the joint effect exceeds the sum of the independent contributions. The paper's departure × trend reference value is −0.0006 — essentially additive. (The separate SSR × RAR interaction, pooled across two seed blocks, is −0.0077 with SE 0.0041; the paper draws no directional conclusion from either.)

Two caveats attach. It is a risk-difference interaction at the specific factor levels evaluated, not a scale-free mechanistic claim. And because drift is anchored to the planned horizon $n_{\text{base}} = 90$, a trial expanded to $n = 100$ accrues total drift of about 0.056 rather than 0.05 — so the interaction includes the extra secular-trend exposure created by extending enrollment, not only a mechanism interaction.

• Two-arm, binary endpoint. Continuous and survival are on the roadmap but not implemented in v1; the JSM paper itself is binary-only.
• Blinded SSR with pooled response. The calculator uses aggregate counts at the SSR look (the "single-arm in the sense that SSR uses only aggregate counts, not treatment-arm allocation" phrasing from the paper). Unblinded treatment-arm-specific SSR is not modeled.
• Thompson Sampling RAR only. DBCD, Neyman, and other allocation rules are not exposed in this calculator. Use the dedicated RAR calculator for those.
• MAP prior is pre-pooled. The prior is supplied as a set of $(w_i, a_i, b_i)$ mixture components via prior_components. To fit a MAP prior from historical cohort data, use the Bayesian Borrowing calculator first and copy the fitted hyperparameters across.
• Linear time trend only. Sigmoidal, step, or non-linear trends would require code changes.
• The supremum is not estimated. A grid exhibits points at which control fails and establishes that the supremum of the Type I error is at least the largest value observed (0.2786, at the upper grid boundary, where the curve was still rising). It does not locate the worst case.
• The SSR rule is a working nuisance calculation. It uses blinded pooled outcomes and a prespecified 1:1 planning allocation, while the full design may realize unequal Thompson- sampling allocation and uses Bayesian monitoring. This makes the SSR operationally blinded, but its preserved Wald power is not the exact power of the composed analysis. Results remain conditional on the chosen planned effect and working model.
• Calibration is in-sample. The binary search targets the empirical calibration sample exactly; out-of-sample behaviour is unverified.