Experiment Design

State a falsifiable hypothesis in this format:

If we [change], then [metric] will [direction] by at least [MDE],
because [reasoning based on user behavior or data].

A hypothesis without a mechanism ("because") is a guess. The mechanism forces you to articulate why the change should work, which informs metric selection and interpretation.

2. Primary Metric + Guardrail Metrics

Primary metric: One metric that decides the experiment. Exactly one — not two, not "primary and secondary." If you cannot pick one, you do not understand the goal yet.

Guardrail metrics: 2-4 metrics that must not degrade. These protect against winning on the primary metric at the cost of something else.

3. Sample Size Calculation

Specify the inputs and the result:

Baseline rate:        3.2%
Minimum detectable effect: +0.5pp (absolute) → 3.7%
Significance level (alpha): 0.05 (two-sided)
Power (1 - beta):    0.80
Sample size per variant: ~14,750 users
Total sample:        ~29,500 users

State the formula or tool used (e.g., Evan Miller's calculator, statsmodels power analysis). If using a ratio metric or non-binomial outcome, note the test type (t-test, Mann-Whitney, etc.).

4. Randomization Unit

Define what gets randomized and how:

• Unit: User-level (most common), session-level, device-level, or cluster-level
• Method: Hash-based assignment (deterministic) vs. random draw (non-deterministic)
• Stickiness: Users must stay in the same variant across sessions. Specify how (user ID hash, cookie, backend assignment table)

Flag risks: if randomizing at user level but the feature affects shared resources (e.g., marketplace supply), consider cluster or switchback designs.

5. Runtime Estimation

Daily eligible traffic:    ~4,200 users
Sample needed:             29,500 users
Estimated runtime:         8 days (to reach sample size)
Recommended minimum:       14 days (to capture weekly seasonality)
Maximum runtime:           28 days (to avoid novelty effect decay)

Always round up to full weeks to account for day-of-week effects. If runtime exceeds 4 weeks, revisit the MDE — you may be trying to detect an effect too small to matter.

6. Stopping Rules

Define in advance when and how the experiment ends:

• Do not peek at results before the planned sample size unless using a sequential testing framework (e.g., group sequential design, always-valid p-values)
• Stop early for harm: If a guardrail metric degrades beyond a pre-defined threshold (e.g., revenue drops > 5%), stop the experiment regardless of primary metric
• No early stopping for success under fixed-horizon testing — a significant p-value at 40% of the sample does not mean the effect is real
• If using sequential testing: Specify the spending function (O'Brien-Fleming, Pocock) and planned interim analysis points

7. Holdout Groups

When the experiment will lead to a permanent rollout, reserve a holdout:

• Size: 5-10% of eligible traffic, withheld from the winning variant after rollout
• Purpose: Measure long-term impact, detect novelty effects wearing off, validate the experiment result in production
• Duration: Minimum 4 weeks post-rollout, ideally one full business cycle

If no holdout is planned, document why (e.g., regulatory requirement to treat all users equally).

8. Analysis Plan

Write this before the experiment starts — never after seeing results:

1. Primary analysis: Compare variant vs. control on the primary metric using [test type]. Report the point estimate, 95% confidence interval, and p-value.
2. Guardrail checks: For each guardrail, confirm the metric did not degrade beyond the threshold. Use one-sided tests where appropriate.
3. Segmentation: Pre-register 2-3 subgroup analyses (e.g., new vs. returning users, mobile vs. desktop). Segments chosen after seeing results are exploratory, not confirmatory.
4. Multiple comparisons: If running more than two variants, apply Bonferroni or Holm correction. State the adjusted alpha.
5. Sample Ratio Mismatch (SRM) check: Verify the actual split matches the intended ratio (chi-square test, p < 0.001 threshold). SRM invalidates the experiment.

9. Reporting Template

Experiment:    [Name]
Dates:         [Start] – [End]
Variants:      Control (50%) vs. Treatment (50%)
Total users:   [N]

Primary metric: Checkout conversion
  Control:     3.18% (n = 14,800)
  Treatment:   3.71% (n = 14,700)
  Difference:  +0.53pp (+16.7% relative)
  95% CI:      [+0.12pp, +0.94pp]
  p-value:     0.011

Guardrails:    All passed (see appendix)
SRM check:     p = 0.42 (no mismatch)
Decision:      SHIP / ITERATE / KILL
Rationale:     [1-2 sentences]

Quality checklist

Before delivering an experiment design, verify:

• Hypothesis includes a falsifiable prediction and a causal mechanism
• Exactly one primary metric is defined — not a composite or a list
• Guardrail metrics cover revenue, performance, and user experience
• Sample size calculation includes all inputs (baseline, MDE, alpha, power)
• Randomization unit matches the unit of analysis (no user-level randomization with session-level metrics without correction)
• Runtime accounts for weekly seasonality (full-week increments)
• Stopping rules are defined before the experiment starts, not improvised mid-flight
• Analysis plan is pre-registered — subgroups and corrections specified in advance
• SRM check is included in the analysis plan

Common mistakes to avoid

• Peeking at results. Checking significance daily and stopping when p < 0.05 inflates false positive rates to 20-30%. Use sequential testing if you need interim looks, or commit to a fixed horizon.
• Underpowered tests. Running an experiment "for a week" regardless of traffic. If you do not have enough sample to detect your MDE, the experiment will almost certainly show "no significant difference" — and you will learn nothing.
• Multiple comparisons without correction. Testing 5 variants against control at alpha = 0.05 gives a ~23% chance of at least one false positive. Apply Bonferroni (alpha / k) or use a hierarchical testing procedure.
• Novelty effects. New UI elements get extra attention simply for being new. If you measure a lift in week 1, it may vanish by week 3. Run experiments long enough and use holdout groups to validate durability.
• Post-hoc segmentation as proof. "It didn't win overall, but it won for mobile users in Germany" is not a valid conclusion — it is hypothesis generation. Pre-register segments or label post-hoc findings as exploratory.
• Ignoring SRM. If your 50/50 split is actually 51/49, something in the assignment or logging pipeline is broken. No amount of statistical analysis can fix corrupted randomization.