Posterior inference over proxy parameters: HMC vs. the evidence_scale grid

Status: prototype complete, result positive, adoption not yet decided. Beads: distributional-agi-safety-fcmy (epic), .1–.4. Code: now in swarm-ai-research/beta-swarm (vendored here as the beta-swarm/ submodule) — beta_swarm/inference/, scripts/hmc_vs_grid_evidence_scale.py, tests/test_hmc.py. Paths in this note are relative to that repo's root. It was written while beta_swarm/ still lived in this repo, at commit 5ab1a982; the split-out is beta-swarm commit 8005468. Runs: runs/20260916T2025*_hmc_vs_grid_seed{0,1,2}/. Reference: Betancourt, A Conceptual Introduction to Hamiltonian Monte Carlo, arXiv:1701.02434.

The question

beta_swarm/proxy.py maps observables to a Beta belief through seven hand-set constants. One of them, evidence_scale, is fit — by a 1-D grid sweep (sweep_evidence_scale) that reports a point estimate. The other six are never fit at all.

Because the outcome v is continuous on [0, 1], the proxy already defines a likelihood:

w      = softmax([z1, z2, z3, 0])      # weights on the simplex
v_hat  = w . x                         # x in [-1,1]^4, from observables
mean   = sigmoid(k * v_hat)
conc   = c0 + s * e
v     ~ Beta(mean * conc, (1 - mean) * conc)

The calibration harness scores this predictive distribution (CRPS and PIT are proper scoring rules for exactly it) but never inverts it. So: is the 1-D grid leaving anything on the table?

Method

Six unconstrained parameters (z1, z2, z3, log_k, log_c0, log_s), weakly informative Normal priors placed directly on those coordinates (so no Jacobian adjustment; a Normal on log_k is a log-normal on k, which is what a positive scale parameter wants anyway).

Sampled with a hand-rolled dynamic HMC — no new dependencies, deliberately: the question is whether a probabilistic-programming stack is worth adopting, and adopting one to answer it would prejudge it. Following Betancourt, the sampler has dynamic trajectory lengths with a U-turn criterion (not a static length), multinomial sampling from the trajectory, dual-averaging step-size adaptation to a target accept of 0.8, a diagonal inverse metric from windowed warmup, and divergence / E-BFMI / split-R-hat / ESS diagnostics.

The gradient is analytic, hand-derived. That is the highest-risk part of the whole exercise — a subtly wrong gradient yields a smooth, plausible posterior centred on the wrong place, and nothing downstream would catch it — so it is checked against central finite differences at five random points, and the likelihood is checked against scipy.stats.beta.logpdf evaluated through the production proxy.

Data generation is misspecified on purpose. Outcomes come from the archetype emission models in beta_swarm/agents.py (honest / mediocre / deceptive), not from the proxy's own Beta. That is the real operating condition and a harder test than self-recovery.

n = 3000, 4 chains × 1000 draws after 1000 warmup, seeds 0/1/2.

Results

Diagnostics were clean on every run: 0 divergences, 0 max-depth hits, R-hat ≤ 1.0012, min ESS 4000, E-BFMI ≈ 1.1–1.2. The sampler itself is not the story; that it reports cleanly here matters only because the test suite shows it reports dirty when it should (Neal's funnel produces divergences; two separated modes produce R-hat > 1.01).

1. The parameters are strongly correlated — the grid cannot reach the joint optimum

log_c0 ↔ log_s (base_concentration ↔ evidence_scale): r = −0.77, −0.76, −0.76 across the three seeds.

This is the structural argument, and it needs no appeal to taste. The grid moves evidence_scale with base_concentration frozen at its hand-set 2.0. When the two trade off this strongly, the best evidence_scale conditional on c0 = 2.0 is not the best evidence_scale, and no amount of refining the 1-D grid fixes that. It is a limitation of the search shape, not its resolution.

2. The hand-set weights are badly wrong for this generative model

parameter	hand-set default	posterior median (90% CI, seed 0)
w_progress	0.40	0.002 (0.001, 0.005)
w_rework	0.20	~0.002
w_verifier	0.20	~0.002
w_engagement	0.20	0.994 (0.991, 0.997)
sigmoid_k	2.0	1.385 (1.321, 1.445)
base_concentration	2.0	0.968 (0.767, 1.171)
evidence_scale	1.5	3.161 (2.915, 3.411)

The posterior puts essentially all weight on counterparty engagement and approximately none on task progress. Stable to three decimal places across seeds.

This is interpretable, and the interpretation is the caveat. In agents.py, deceptive agents emit inflated task_progress_delta (≈0.75 regardless of true quality) while their engagement stays low, because engagement is the one channel a lone deceiver cannot manufacture. Progress is therefore an actively misleading signal in this population and engagement is the discriminating one. The posterior found that. It is recovering a property of the simulator, which is by construction — not a discovered fact about real agent systems.

What generalizes is the method: this is weight misspecification that the 1-D grid could not have surfaced, because it never varies the weights.

3. Calibration is roughly twice as good at the posterior mean

	PIT deviation	tail ECE	CRPS	sharpness
posterior mean	0.235	0.180	0.116	5.28
grid (sharpest-calibrated)	0.370	0.308	0.221	10.22

The grid's pick is worse on PIT deviation — its own selection criterion — by 57%. It is sharper, having bought that sharpness with calibration it could not afford. Note that the grid's best-PIT pick (seed 0, n=3000: scale 5.0, PIT 0.333) is still worse than the posterior mean, so this is not an artifact of the selection rule used here.

Also note the comparison is not strictly apples-to-apples: the grid selects on PIT, HMC targets the posterior. Both derive from proper scoring rules, but the honest reading is "the posterior lands somewhere better on the grid's own metric", not "HMC optimizes PIT better".

4. The governance-lever argument did not hold up

The bead predicted that parameter uncertainty would put a credible interval on tail_mass(tau) wide enough to change a call the point estimate makes confidently. It does not, at this sample size:

• 90% CI width on P(v < 0.4): median 0.011, max 0.038
• interactions whose CI straddles the 0.5 line: 4 of 400
• cases where the point estimate reads confident but the posterior does not: 0

Parameter uncertainty is real but small relative to the decision margin. The uncertainty does concentrate on borderline cases (spread correlates negatively with distance from the threshold — pinned by a test), which is the right shape; there is just not much of it.

Two caveats pointing opposite ways. At n = 3000 the posterior is tight almost by construction, so this says little about small-sample regimes. Conversely, the model is misspecified, and credible intervals under misspecification are known to be too narrow — the honest statement is that the tail-mass intervals reported here are a lower bound on the real uncertainty, and a sandwich-corrected or cross-validated interval would be the way to check.

Relation to Arm A Finding 4

docs/research/calibration-arm-a-deviation-analysis.md argues that latent p_true is unrecoverable in principle: observables carry information about v only, so no estimator can distinguish an interaction drawn with p_true = 0.4 from one drawn with p_true = 0.2 given the same realized v.

That argument stands and is not contradicted here, because it is about a different target. Finding 4 concerns recovering a per-interaction latent from a single realized outcome — a fundamentally under-determined problem. This work estimates global parameters shared across N interactions, which pools information and is well-posed; the parameter-recovery test confirms the posterior covers known truth. A reader who knows Finding 4 should not read this as overturning it, and nothing here licenses per-interaction p_true recovery.

Verdict

Two of the three adoption criteria are met (correlation structure a per-axis grid cannot reach; weight misspecification it cannot surface). The third — a governance call that changes — is not.

That is enough to justify fitting the proxy rather than hand-setting it, but not on the strength of the governance-uncertainty argument, which should be dropped from the case until a small-sample or misspecification-corrected version of check 4 is run.

Open before adoption (bead .4):

1. Re-run at n = 100–500, where the tail-mass intervals should actually bite.
2. Cross-validate or sandwich-correct the intervals, given known misspecification.
3. If adopted, replace the hand-rolled sampler with numpyro or blackjax. It was written to avoid a dependency during evaluation, not to be maintained. The cost of that swap is a jax dependency in a repo that has deliberately stayed on numpy/scipy/sklearn, and that tradeoff deserves its own decision.
4. The w_engagement ≈ 0.99 result must be reproduced against a generative model that was not written by us before it informs any change to the proxy's defaults. Right now it is a statement about agents.py.

Addendum, 2026-09-17: the code moved

beta_swarm was split out of this repo into swarm-ai-research/beta-swarm and vendored back as the beta-swarm/ submodule.

Worth recording because it nearly cost work. beta_swarm/ had originally been folded in from a standalone repo (8e2a3984), and both copies then kept moving: this repo gained the PR-review fixes and the whole HMC package, while the standalone gained a ContainmentEscaper adversary that never landed here. Ten of fourteen shared files differed and neither side was a superset. Wiring the submodule first would have deleted the HMC work from the working tree, since a submodule replaces the directory with a checkout of the remote.

The order that worked: port the missing half into this repo (98557793), making it the superset; then sync outward and push (beta-swarm 8005468); only then replace the directory with the submodule. The 161 tests pass identically on both sides, which is what confirms nothing was dropped in either direction.