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Notebook 10 — Many tests

SWC ENC 2026 · behaviour module · Part 2 (population-level inference)

Modular and skippable, like the rest of Part 2.

Real analyses rarely run one test — they run dozens. The moment you screen many candidate effects at once — several predictors, many conditions, or every strategy in the design matrix — some will look "significant" by pure chance, and you have to account for it. This notebook builds that toolkit on a controlled problem where we know which effects are real, so we can measure whether a correction actually works — something you can never do on real data.

In this notebook you will:

1. Run a t-test and see exactly what its p-value means.
2. Watch false positives pile up when you run many tests.
3. Control them two ways — Bonferroni (FWER) and Benjamini–Hochberg (FDR) — and measure the difference.

Setup

We simulate a batch of independent "candidate effects" — think of them as many possible behavioural predictors we're screening. Each is measured in n_mice animals. Most candidates are truly null (real effect exactly 0); a handful are real. Because we set which is which, we can later grade every method against the truth. This cell always runs.

import numpy as np
import matplotlib.pyplot as plt
from scipy import stats
import swcbehav as sb

rng = np.random.default_rng(0)
n_mice, n_tests, n_real = 15, 200, 20
true_effect = np.zeros(n_tests)
true_effect[:n_real] = 0.9                       # the first 20 candidates are real
is_real = true_effect > 0

# each mouse measures each candidate with noise
data = true_effect[None, :] + rng.normal(0, 1, size=(n_mice, n_tests))
print(f"{n_tests} candidates ({n_real} real, {n_tests - n_real} null), {n_mice} mice each")

1. One t-test

A one-sample t-test asks: is a mean different from a reference value (here, 0), relative to how noisy the measurement is? The statistic is signal over noise,

$$t = \frac{\bar{x} - 0}{s / \sqrt{n}},$$

where $\bar{x}$ is the sample mean, $s$ its standard deviation, and $n$ the number of mice. A large $|t|$ means the mean is many standard errors from 0 — hard to explain as noise. The p-value turns $|t|$ into a probability: if the true mean were 0, how often would we see a $t$ this extreme? We read it from the t-distribution.

Exercise 1 (~5 min). Complete one_sample_t. Compute $t$ yourself; get the two-sided p-value from stats.t.sf (the survival function, $1-\text{CDF}$) with n-1 degrees of freedom.

Check / unstuck. The real candidate should give a small p (~0.006), the null one a larger p. Stuck? scipy.stats.ttest_1samp(x, 0) returns (t, p).

def one_sample_t(x):
    x = np.asarray(x, float)
    n = len(x)
    # YOUR CODE HERE: t = mean / (sample_sd / sqrt(n)) using x.std(ddof=1);
    # two-sided p = 2 * stats.t.sf(abs(t), df=n-1); return t, p
    raise NotImplementedError

print("a REAL candidate :", [round(v, 4) for v in one_sample_t(data[:, 0])])
print("a NULL candidate :", [round(v, 4) for v in one_sample_t(data[:, -1])])

The real candidate has a small p-value; the null one (usually) doesn't. Now compute a p-value for every candidate — scipy will do all 200 at once.

tvals, pvals = stats.ttest_1samp(data, popmean=0, axis=0)
print("first few p-values:", np.round(pvals[:5], 4))

2. The problem with many tests

At a threshold of $\alpha = 0.05$, each null candidate still has a 5% chance of looking "significant" by luck. With many nulls, those add up. Count how many of our truly null candidates cross $p < 0.05$:

raw_hits = pvals < 0.05
false_positives = np.sum(raw_hits & ~is_real)
print(f"'significant' at p<0.05: {raw_hits.sum()} candidates")
print(f"  of which FALSE positives (truly null): {false_positives}")
print(f"  expected by chance: {0.05 * (n_tests - n_real):.0f}")

Those false positives are the price of many tests. Two philosophies control it:

• Bonferroni controls the family-wise error rate (FWER) — the chance of even one false positive — by testing each candidate at $\alpha/m$. Safe, but so strict it also throws away real effects.
• Benjamini–Hochberg controls the false discovery rate (FDR) — the expected fraction of your "discoveries" that are false. More permissive, keeps more real effects, and it's the correction Piet et al. use.

3. Benjamini–Hochberg

Sort the $m$ p-values ascending, $p_{(1)} \le \dots \le p_{(m)}$. Find the largest rank $k$ with $p_{(k)} \le \frac{k}{m}\alpha$, and reject everything up to it. The sliding threshold $\frac{k}{m}\alpha$ is lenient for the smallest p-values and tightens toward $\alpha$ — that's what trades a controlled FDR for more power.

Worked example: with $m=5$ p-values $[0.001, 0.20, 0.01, 0.50, 0.04]$, sort to $[0.001, 0.01, 0.04, 0.20, 0.50]$ and compare each to $\frac{k}{5}\cdot 0.05 = [0.01, 0.02, 0.03, 0.04, 0.05]$: ranks 1 and 2 pass ($0.001\le 0.01$, $0.01\le 0.02$), rank 3 fails ($0.04 > 0.03$). The largest rank that passes is $k=2$, so you reject the two smallest p-values.

Exercise 2 (~8 min · meaty). Complete benjamini_hochberg; it returns a boolean "rejected" mask.

Check / unstuck. Expect BH to reject ~9 candidates (matches the backend). Stuck? Use sb.benjamini_hochberg(pvals, 0.05).

def benjamini_hochberg(pvals, alpha=0.05):
    pvals = np.asarray(pvals, float)
    m = len(pvals)
    order = np.argsort(pvals)
    thresholds = alpha * np.arange(1, m + 1) / m
    # YOUR CODE HERE: find where sorted p-values fall at/under `thresholds`;
    # reject everything up to the LARGEST such rank. Return a boolean mask of len m.
    raise NotImplementedError

print("BH rejects", benjamini_hochberg(pvals).sum(), "candidates")
print("backend check:", sb.benjamini_hochberg(pvals).sum())

It helps to see what BH does. Plot the sorted p-values against their rank, with the sliding threshold $k\alpha/m$ (the BH line) and, for contrast, the flat uncorrected $\alpha$. BH keeps everything up to the last point that lies below the sloped line — a cutoff stricter than the naive $\alpha$ but far more forgiving than Bonferroni's $\alpha/m$.

m = len(pvals)
srt = np.sort(pvals)
k = np.arange(1, m + 1)
n_rej = sb.benjamini_hochberg(pvals, 0.05).sum()
plt.figure(figsize=(6, 4))
plt.plot(k, srt, "o", ms=3, label="sorted p-values")
plt.plot(k, 0.05 * k / m, "r-", label=r"BH threshold  $k\alpha/m$")
plt.axhline(0.05, color="0.6", ls="--", label=r"uncorrected $\alpha=0.05$")
plt.axhline(0.05 / m, color="tab:purple", ls=":", label=r"Bonferroni $\alpha/m$")
plt.axvline(n_rej, color="tab:green", lw=1, label=f"BH cutoff (reject {n_rej})")
plt.xlim(0, 60); plt.ylim(0, 0.06)
plt.xlabel("rank k"); plt.ylabel("p-value"); plt.legend(fontsize=8)
plt.title("Benjamini–Hochberg selects the cutoff")
plt.show()

4. Grading the methods against the truth

Here's the payoff of synthetic data: we know is_real, so we can measure each method's power (fraction of real effects caught) and its false-discovery rate (fraction of discoveries that are actually null). But a single experiment is noisy, and FDR is only controlled on average — so we run many simulated experiments and average.

def run_experiment(seed):
    r = np.random.default_rng(seed)
    d = true_effect[None, :] + r.normal(0, 1, size=(n_mice, n_tests))
    _, pv = stats.ttest_1samp(d, 0, axis=0)
    return {"no correction":      pv < 0.05,
            "Bonferroni":         pv < 0.05 / n_tests,
            "BH":                 sb.benjamini_hochberg(pv, 0.05)}

def fdr_power(rej):
    n = rej.sum()
    return np.sum(rej & ~is_real) / max(n, 1), np.sum(rej & is_real) / is_real.sum()

reps = [run_experiment(s) for s in range(300)]
print(f"{'method':16s}{'mean FDR':>10}{'mean power':>12}")
for name in ["no correction", "Bonferroni", "BH"]:
    fdrs = np.mean([fdr_power(r[name])[0] for r in reps])
    powers = np.mean([fdr_power(r[name])[1] for r in reps])
    print(f"{name:16s}{fdrs:>10.3f}{powers:>12.2f}")

Averaged over experiments the picture is clean: no correction runs a false-discovery rate far above 0.05; Bonferroni drives false discoveries nearly to zero but sacrifices power; BH holds the mean FDR at or just under the target 0.05 while catching far more of the real effects than Bonferroni. That balance — a controlled false-discovery rate with usable power — is why the paper (and most of modern neuroscience) reaches for Benjamini-Hochberg when screening many comparisons.

Wrap-up

You built a t-test from its definition, saw why many tests inflate false positives, and measured how Bonferroni and Benjamini–Hochberg control them. The one piece of structure we set aside here was nesting — we treated each mouse's measurement as one independent number. The last notebook confronts nesting head-on.

Next (Notebook 11): honest error bars for nested data — the hierarchical bootstrap.

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