Empirical Systems Evaluation

Empirical Systems Evaluation

Design, execute, and report experiments that measure multi-agent coordination systems with statistical rigor. Every claim backed by confidence intervals. Every comparison backed by effect sizes. Every threat to validity stated honestly.

When to Use

• Benchmarking coordination protocols, salvage policies, and scheduling strategies
• Measuring recovery latency, throughput, crash handling, or coordination overhead
• Running human-evaluation studies for output fidelity, handoff quality, or usefulness
• Writing reproducible comparative reports with power, confidence intervals, and effect sizes

NOT for Boundaries

• ML model evaluation such as accuracy, perplexity, BLEU, or leaderboard benchmarking
• Web-product A/B testing for funnels, click-through, or growth optimization
• Survey design, psychometrics, or instrument validation
• General-purpose data science, feature engineering, or predictive modeling

1. Experiment Design Decision Tree

START: "I want to measure X about system Y"
  |
  +-> Is X a latency / throughput / count?
  |     YES -> Automated metric (Section 2)
  |     NO  -> Is X a quality judgment (fidelity, correctness, usability)?
  |              YES -> Human evaluation (Section 3)
  |              NO  -> Is X a binary outcome (crash/no-crash, success/fail)?
  |                       YES -> Proportion test (Section 4)
  |                       NO  -> Reconsider what you're measuring.
  |
  +-> How many conditions are you comparing?
  |     1 (just characterizing) -> Descriptive stats + CI (Section 5)
  |     2 -> Pairwise test (Section 6)
  |     3+ -> Omnibus test + post-hoc (Section 7)
  |
  +-> Do you have paired or independent observations?
        Paired (same scenarios, different systems) -> Paired tests
        Independent (different scenarios) -> Independent tests

2. Automated Metrics Protocol

For latency, throughput, recovery time, message counts, resource usage:

1. Define the metric precisely. "Salvage latency" = wall-clock ms from agent death detection to first recovered work unit passing validation.
2. Instrument, don't approximate. Timestamps at event boundaries, not log-line scraping.
3. Run enough trials. See Section 8 for sample size calculation.
4. Report median + IQR for skewed distributions (latency almost always is). Report mean + SD only if distribution is approximately normal.
5. Always report bootstrapped 95% CI (Section 9).

3. Human Evaluation Protocol

For recovery fidelity, code quality, correctness of salvaged work:

3a. Rater Selection

• Minimum 2 independent raters. 3+ preferred.
• Raters must not know which condition produced which output.
• Document rater expertise level.

3b. Rating Scale Design

• Use concrete anchored scales (not "1=bad, 5=good").
• Example for recovery fidelity:
  • 1: Output is unrelated to original task
  • 2: Output addresses the right task but is mostly wrong
  • 3: Output is partially correct, major gaps remain
  • 4: Output is mostly correct, minor issues only
  • 5: Output is equivalent to or better than pre-crash state

3c. Inter-Rater Reliability

• Compute Cohen's kappa (2 raters) or Fleiss' kappa (3+ raters).
• Thresholds:
  • kappa < 0.40: Poor -- stop, revise rubric, retrain raters
  • 0.40 <= kappa < 0.60: Moderate -- proceed with caution, report prominently
  • 0.60 <= kappa < 0.80: Substantial -- acceptable
  • kappa >= 0.80: Near-perfect -- strong results

3d. Resolving Disagreements

• For 2 raters: third rater breaks ties
• For 3+ raters: majority vote, or discussion-to-consensus with documentation

4. Proportion Tests

For binary outcomes (crash recovered: yes/no):

Is n >= 30 per group AND expected count >= 5 per cell?
  YES -> Chi-squared test or Z-test for proportions
  NO  -> Fisher's exact test

Report: proportion, 95% CI (Wilson interval, not Wald), and odds ratio with CI.

5. Parametric or Non-Parametric? Decision Tree

START: "Which test do I use?"
  |
  +-> Is the data continuous (latency, throughput)?
  |     |
  |     +-> Check normality: Shapiro-Wilk test (n < 50) or
  |     |   Anderson-Darling (n >= 50). Also: inspect Q-Q plot.
  |     |
  |     +-> Normal (p > 0.05)?
  |     |     YES -> Check equal variances: Levene's test
  |     |     |        Equal? -> t-test (2 groups) or ANOVA (3+)
  |     |     |        Unequal? -> Welch's t-test or Welch's ANOVA
  |     |     NO  -> Can you transform to normality (log, sqrt)?
  |     |              YES -> Transform, then parametric
  |     |              NO  -> Non-parametric:
  |     |                     2 groups paired -> Wilcoxon signed-rank
  |     |                     2 groups independent -> Mann-Whitney U
  |     |                     3+ groups -> Kruskal-Wallis + Dunn's post-hoc
  |     |
  +-> Is the data ordinal (human ratings 1-5)?
  |     -> Non-parametric always:
  |        2 groups paired -> Wilcoxon signed-rank
  |        2 groups independent -> Mann-Whitney U
  |        3+ groups -> Kruskal-Wallis
  |
  +-> Is the data counts/proportions?
        -> See Section 4

6. Pairwise Comparisons (2 Conditions)

1. Choose test from Section 5.
2. Report: test statistic, p-value, effect size, CI.
3. Effect size (Cohen's d):
   • d = (mean1 - mean2) / pooled_SD
   • For non-parametric: use rank-biserial correlation r
   • Thresholds: |d| < 0.2 negligible, 0.2-0.5 small, 0.5-0.8 medium, > 0.8 large
4. Always report CI for the effect size, not just the point estimate.

7. Multiple Comparisons (3+ Conditions)

3+ conditions?
  |
  +-> Run omnibus test first (ANOVA or Kruskal-Wallis)
  |     p > 0.05? -> STOP. No post-hoc tests. Report null result honestly.
  |     p <= 0.05? -> Proceed to pairwise post-hoc.
  |
  +-> How many pairwise comparisons?
        k conditions -> k*(k-1)/2 comparisons
        Apply Bonferroni correction: alpha_adj = 0.05 / num_comparisons
        |
        Alternative: Holm-Bonferroni (less conservative, still controls FWER)
        Alternative: Tukey's HSD (for ANOVA, all-pairs)

Bonferroni in practice: 3 conditions = 3 comparisons, alpha = 0.0167. 4 conditions = 6 comparisons, alpha = 0.0083. If this feels too strict, Holm-Bonferroni is the standard alternative.

8. Sample Size: "How Many Runs for p < 0.05?"

For a two-sample t-test with power = 0.80, alpha = 0.05:

Formula (approximate): n = (Z_alpha/2 + Z_beta)^2 * 2 * sigma^2 / delta^2

For coordination systems, a medium effect (d = 0.5) is the minimum interesting difference. Plan for at least 30 runs per condition as a floor; 50+ preferred.

If you cannot run 30+, state this as a limitation and widen your CI interpretation.

Pilot study approach: Run 10 trials, estimate variance, then calculate the sample size needed for your target effect size. This is always better than guessing.

9. Bootstrapped Confidence Intervals

Use when: distribution is unknown, sample is small, or you want distribution-free CIs (which is almost always).

Procedure

1. From your n observations, draw n samples with replacement. Compute statistic.
2. Repeat B = 10,000 times (minimum 2,000; 10,000 is standard).
3. Sort the B bootstrap statistics.
4. 95% CI = [2.5th percentile, 97.5th percentile] (percentile method).
5. For bias-corrected accelerated (BCa) intervals: use when bootstrap distribution is visibly skewed. Most stats libraries implement this.

When to Use Percentile vs BCa

• Percentile: simple, adequate for symmetric distributions
• BCa: handles skew, preferred for latency data
• If results differ substantially, report BCa and note the discrepancy

10. Meaningful vs Strawman Baselines

A comparison is only as strong as the baseline it beats.

Baseline Strength Tiers

Rules:

• You MUST include at least one Tier A or S baseline.
• A Tier B baseline is acceptable as a second comparison point.
• A Tier F baseline alone is scientific malpractice. Never report only "vs no system."
• If no Tier S exists, say so explicitly and explain why your Tier A is the strongest available.

11. Quality Gates

Before any result leaves your desk, verify ALL of the following:

• Every metric has a confidence interval (bootstrap or analytical)
• Every comparison has an effect size (Cohen's d or rank-biserial r)
• Every effect size has its own CI
• Multiple comparisons are corrected (Bonferroni or Holm)
• Human evaluations report inter-rater reliability (kappa)
• Sample size justification is stated (power analysis or pilot-informed)
• Baselines are at least Tier A strength
• Distribution assumptions are checked (normality, variance homogeneity)
• Threats to validity section exists and is honest
• Raw data or summary statistics are available for reproduction
• Code for analysis is provided or described precisely

12. Failure Modes (Anti-Patterns)

12a. P-Hacking

What it looks like: Running many statistical tests, trying different subsets, transformations, or exclusion criteria until p < 0.05. Reporting only the "significant" result.

Detection: Ask "was this comparison pre-registered or decided after seeing the data?" If the answer is after, it is exploratory, not confirmatory.

Fix: Pre-register your hypotheses and analysis plan. If you explore post-hoc, label it clearly as exploratory and apply stricter alpha (0.01). Never present exploratory findings as confirmatory.

12b. Strawman Baselines

What it looks like: Comparing your coordination system to "no coordination" and celebrating the win. Or comparing to a deliberately misconfigured alternative.

Detection: Would a skeptical reviewer say "of course it's better than nothing"?

Fix: See Section 10. Include the strongest available alternative. If your system only beats a strawman, that is not a publishable result -- it is a sanity check.

12c. Reporting Means Without Variance

What it looks like: "System A achieved 340ms recovery latency vs 890ms for System B." No standard deviation, no CI, no indication of spread.

Detection: Can a reader assess whether the difference is reliable?

Fix: ALWAYS report: central tendency + spread + CI. For example: "System A: median 340ms (IQR 280-410, 95% CI [310, 370]) vs System B: median 890ms (IQR 720-1100, 95% CI [810, 970]), Mann-Whitney U = 42, p < 0.001, r = 0.83 [0.71, 0.92]."

12d. Ignoring Multiple Comparisons

What it looks like: Testing 10 metrics across 4 conditions, finding 3 "significant" results at p < 0.05. With 10 tests you expect ~0.5 false positives by chance.

Fix: Bonferroni or Holm-Bonferroni. Distinguish pre-registered primary metrics (corrected) from exploratory secondary metrics (uncorrected but flagged).

12e. Confounding Experimental Conditions

What it looks like: System A on fast hardware, System B on slow. Or easy scenarios for A, hard for B.

Fix: Same hardware, same scenarios, same network. If infrastructure differs, run both systems on both and analyze as a crossed design.

13. Threats to Validity Checklist

Every report must address four categories:

• Internal: confounds controlled, randomization applied, instrumentation non-intrusive, no unexplained exclusions
• External: scenarios representative, scale stated (8 agents != 800), hardware/network documented, generalization boundaries explicit
• Construct: metrics measure what you claim, definitions concrete not hand-waved, rubrics aligned with rater task
• Statistical: sufficient power, test assumptions met, effect sizes practically meaningful (not just p < 0.05)

14. Worked Examples

• Load references/bonded-commons-crash-recovery.md for a full pre-registered crash-recovery comparison across three coordination protocols.
• Start from templates/evaluation-report-template.md when writing a report, preregistration, or experiment memo.
• Minimal case: characterize one system honestly with descriptive stats and confidence intervals before claiming superiority over any baseline.

16. Quick Reference Card

Decision Points

flowchart TD
  A[Incoming request for Empirical Systems Evaluation] --> B{Within this skill's scope?}
  B -->|No| C[Redirect using NOT-for boundaries]
  B -->|Yes| D[Assess inputs, constraints, and current state]
  D --> E{Which path fits best?}
  E -->|Plan or design| F[Choose the simplest viable pattern]
  E -->|Migration or change| G[Protect compatibility and rollout safety]
  E -->|Debug or evaluate| H[Localize the failing boundary first]
  F --> I[Apply the domain-specific guidance below]
  G --> I
  H --> I
  I --> J[Validate against the quality gates]

Use this as the first-pass routing model:

• Confirm the request belongs in this skill before doing deeper work.
• Separate planning, migration, and debugging paths before choosing a solution.
• Prefer the simplest correct path that still survives the quality gates.

Failure Modes

• Treating an out-of-scope request as if this skill owns it.
• Choosing a pattern before checking the actual constraints and current state.
• Returning an answer without validating it against the acceptance criteria for this skill.

Worked Examples

• Minimal case: apply the simplest in-scope path to a small, low-risk request.
• Migration case: preserve compatibility while changing one constraint at a time.
• Failure-recovery case: show how to detect the wrong path and recover before final output.

Quality Gates

• The recommendation stays inside the skill's stated boundaries.
• The chosen path matches the user's actual constraints and current state.
• The output is specific enough to act on, not just descriptive.
• Any major trade-offs or failure conditions are called out explicitly.