The earlier exploiters ran a quarter of their targets' budget. Rerun at a matched
~131M learner actions (measured: 130.4M and 131.1M):
ours exploiter reaches 0.4657 [0.455, 0.477], mean lead -5.5
league exploiter reaches 0.6295 [0.619, 0.640], mean lead +28.8
The CIs are nowhere near each other and the gap widened under funding, 0.094 ->
0.164. A qualitative line gets crossed too: a properly funded attacker trained
from scratch *beats* league outright, and still loses to ours.
Two things a reader has to carry with that, both of which cut against us:
- Neither exploiter plateaued -- both climb through the final update, so these
remain lower bounds. And ours' attacker has the steeper tail (+0.031 vs +0.016
per 100 updates) while league's curve is already bending, so a much larger
attacker could narrow the gap. Cannot rule out that it closes.
- League is a single-round policy blind to carry and match score, and both frozen
policies are played greedily, which is maximally exploitable by construction.
So this is not a clean "training method A vs B".
The claim that survives is the matched-budget one, and only that one.
Co-Authored-By: Claude Opus 4.8 <noreply@anthropic.com>
Claude-Session: https://claude.ai/code/session_01XBQKgvBbxbheiTF1AVy1Sh
The exploiters ran 32.5M learner actions, not the 65.5M I recorded -- they train
one seat, so a 250x1024 run yields half of what the same shape gives the
both-seat self-play trainer. Against targets trained on 131M and 122.6M, that
makes the attacker roughly 4x underfunded.
Which means the absolute number does not support "ours is only 22.8%
exploitable". It supports exactly one claim: at a matched budget, league gives up
more. Whether the ordering survives a properly funded attacker is now the open
question, so the script takes --updates and --batch-games to run it.
Co-Authored-By: Claude Opus 4.8 <noreply@anthropic.com>
Claude-Session: https://claude.ai/code/session_01XBQKgvBbxbheiTF1AVy1Sh
Winning the head-to-head says a policy is strong on average, not that it is hard
to beat. So freeze each policy, train a fresh one from scratch whose only job is
to beat that policy, and see how far it gets.
Same exploiter budget (250 updates x batch 1024, 65.5M learner actions):
ours (match stack, 131M) exploiter reaches 0.2278 [0.219, 0.237]
league (web-deployed) exploiter reaches 0.3213 [0.311, 0.331]
League gives up 9.4 more points to a dedicated attacker. Both sit far from 0.5, so
neither is a pushover -- but the caveat left open by the head-to-head is now closed
in our favour on both axes: stronger on average (0.6094) and harder to exploit.
Worth noting against expectation: league was trained *with* an exploiter structure
and we ran pure self-play, and we still come out less exploitable. Whatever the
league machinery buys, it did not buy that here.
The number is a lower bound -- a bigger exploiter would find more -- so it only
means anything as a like-for-like comparison, which is how it is used.
Co-Authored-By: Claude Opus 4.8 <noreply@anthropic.com>
Claude-Session: https://claude.ai/code/session_01XBQKgvBbxbheiTF1AVy1Sh
The 39.3M ablation was the critic's worst ground. At a matched 131M budget:
both-seat training is worth +17.1 points of win rate, the privileged critic
+3.7 -- a 4.6x gap. And they behave differently: both-seat is flat across scale
(+16.8 at 39.3M, +17.1 at 131M) while the critic swings (-1.6 to +3.7).
The mechanism explains it. Both-seat doubles the data at the same compute --
self-play already played those plies with the same network. The critic adds no
data, only accuracy, and a privileged value trunk has more to fit, so it grades
badly until there is enough to fit it with.
Fable ranked the critic first among missing ideas and both-seat fourth. That was
exactly backwards.
Co-Authored-By: Claude Opus 4.8 <noreply@anthropic.com>
Claude-Session: https://claude.ai/code/session_01XBQKgvBbxbheiTF1AVy1Sh
The 39.3M ablation said the privileged critic hurt (switching it off won 0.5160
[0.505, 0.527]). Head to head at 131M, both sides trained identically, it says the
opposite: off *loses*, 0.4633 [0.453, 0.474]. Against league the critic-on model
scores 0.6094 and the critic-off one 0.5526.
The critic earns its keep once there is enough data to fit it -- at 39.3M the
privileged value trunk is underfit and only adds advantage noise. Defaulted back
on, with the small-scale number kept in the docstring as a warning: an ablation at
a budget you do not intend to ship can invert.
Co-Authored-By: Claude Opus 4.8 <noreply@anthropic.com>
Claude-Session: https://claude.ai/code/session_01XBQKgvBbxbheiTF1AVy1Sh
Each piece switched off in turn, trained at identical compute, then played against
the full stack over 8192 duplicate matches. Below 0.5 means the removed piece was
doing work.
- both seats: 0.3317 [0.322, 0.342]. The biggest single contributor. Half of it is
simply sample count -- dropping the opponent seat halves the learner actions per
update -- but that is the point: self-play already produced those plies with the
same network, and the old trainer stop_gradiented them away.
- match observation: 0.4751 [0.464, 0.486]. Small but real. Since carry itself
contributes almost nothing (rounds decompose), most of this is likely the
single-round observation defects being fixed: to_move, the deck clock, and the
score_diff scale.
- privileged critic: 0.5160 [0.505, 0.527] -- turning it OFF makes the agent
significantly STRONGER. Fable called this the biggest missing idea; it is wrong.
A critic that knows the deck fits V(full state), which is not
E[return | masked obs], so the advantage picks up a component the actor cannot
act on. From the actor's side that is noise, not variance reduction. Asymmetric
critics hurting under partial observability is a known failure mode.
Defaulted off accordingly. (Reusing it as a PIMC leaf evaluator may still stand --
that is a separate claim from using it to train the policy.)
Co-Authored-By: Claude Opus 4.8 <noreply@anthropic.com>
Claude-Session: https://claude.ai/code/session_01XBQKgvBbxbheiTF1AVy1Sh
The question was what any of this actually improved over the training method
that existed. Duplicate matches, 8192 a piece, same three deals and coins from
both seats:
- At 39.3M learner actions the match stack beats the Phase 0a gate agent
(0.5842) which had 411M -- 10.5x the data. Sample efficiency is the headline.
- At 39.3M it *loses* to the league policy (0.3142). That is a budget gap, not a
strength gap: league had 122.6M plus a league/exploiter structure.
- Scaled to a matched budget (131M vs league's 122.6M) it wins: 0.6094
(CI 0.599-0.620), +22.0 points.
So: same compute, stronger agent, measured on the actual game.
Caveat kept honest in the plan -- league was trained with exploiters, and we have
measured average strength, not exploitability. "Harder to exploit" is not shown.
Co-Authored-By: Claude Opus 4.8 <noreply@anthropic.com>
Claude-Session: https://claude.ai/code/session_01XBQKgvBbxbheiTF1AVy1Sh
The user asked why we were not simply maximising the three-round total, and they
were right. Each ply now pays the points by which it moved the running match
difference; at gamma=1 that telescopes to the final total, so the objective is
exactly the rulebook's, handed out every ply instead of once 150 plies later.
Three measurements killed the tanh design:
- Rounds are independent (corr(m1,m2)=0.004, corr(m1+m2,m3)=0.05), so a reward
linear in the total decomposes the match into three independent rounds and
carry enters the objective nowhere. The only coupling, the start-player rule,
is worth +0.73 +/- 0.84 points -- indistinguishable from zero.
- Risk attitude, the one thing tanh buys, is worthless here. A policy made to
gamble when it trails by 20 entering round three *loses* to a greedy clone over
6144 duplicate matches (0.482); gambling only at -40 breaks even (0.498). A
marginal wager buys about +1.7 sigma for -2 to -3 expected points. Ceiling on
the whole carry-conditioning idea: under one win-rate point.
- Head to head over 10,000 duplicate matches at equal compute, the linear reward
*beats* tanh(total/12): 0.5859 (CI 0.576-0.596), +20.3 points. Dropping it is
not merely free, it is better -- not because of risk, but because tanh hands a
~150-ply match one saturated +/-1 and leaves all credit assignment to the critic.
The flat carry probe was not exploration collapse: sampled play still opens 5.00
expeditions, entropy settles at 1.36 nats (3.9 effective actions), and the critic
reads carry cleanly (round-three values run -0.87 to +0.86, monotone). The signal
was there; there was nothing to buy with it.
Criterion 1 (a monotone carry response) comes off the gate accordingly -- the
optimal response barely exists in this game. carry stays in the observation: it
costs nothing and the start-player rule keys off it.
Co-Authored-By: Claude Opus 4.8 <noreply@anthropic.com>
Claude-Session: https://claude.ai/code/session_01XBQKgvBbxbheiTF1AVy1Sh
Self-play works: matches converge to 146.8 plies (~49 a round) with a 91% deck-
race rate, so the stalling that static opponents induced is gone. Duplicate match
eval scores 0.4968 with a mean lead of exactly 0.0 -- same deals, same coins, both
seats, deal luck cancelling exactly.
Success criterion 1 does not pass. The carry probe is close to flat: expeditions
opened sit at 5.00 whether the policy is 60 points down or 60 points up. Wager use
does move monotonically across all six carry levels, and in the right direction
(behind -> more multipliers), but the spread is 0.31 wagers.
Two diagnoses, one of which was mine and wrong:
- Residual potential shaping was NOT the cause. Annealing it fully to zero left
the probe just as flat.
- terminal_scale is. At carry -60, tanh((margin - 60)/50) is close to linear over
any realistic round margin, and maximising E[tanh] on a linear stretch is just
maximising E[margin] -- there is no reason to gamble. Risk-seeking only appears
where tanh is sharply convex, which needs a smaller scale. Dropping 50 -> 12
widens the wager spread 0.19 -> 0.31, which is the mechanism showing up.
The probe itself is also mis-scaled: at scale 12, tanh(60/12) is 1.0, so +/-60 is
a saturated dead zone with no gradient and the policy has learned nothing there.
The measurable band is |carry| <~ 2 * terminal_scale, and the probe levels have to
be set from the scale rather than fixed.
Co-Authored-By: Claude Opus 4.8 <noreply@anthropic.com>
Claude-Session: https://claude.ai/code/session_01XBQKgvBbxbheiTF1AVy1Sh
The cap item existed so a three-round match would fit inside a 400-step scan.
Phase 0a's truncation bootstrap removed that constraint -- scan length is a free
parameter now -- and the same phase showed the cap is the thing that turns
stalled games into losses: 20.6% of cap-hit games lost, 99.4% of all losses. A
120-ply cap would put *more* games into the wall and make "freeze the round
while ahead" easier, so the round cap stays at 400 and max_steps_rate stays a
watched metric.
Also records what the plan never listed: ppo.py, gates.py and league.py all take
a single-round State and still have to be wired to MatchState. That is the
largest remaining piece of Phase 1.
Co-Authored-By: Claude Opus 4.8 <noreply@anthropic.com>
Claude-Session: https://claude.ai/code/session_01XBQKgvBbxbheiTF1AVy1Sh
At equal compute (250 updates either way, 5.8x the samples) the new loop beats
the baseline against heuristic_expert: 0.4525 -> 0.5071 win rate, -4.28 ->
-0.56 mean score diff. Expert ends rounds at their natural length, so that is
a clean read on card play.
It appears to *lose* ground against heuristic_balanced (0.9866 -> 0.9292), but
that is entirely the MAX_STEPS=400 cap. Drawing from a discard pile does not
deplete the deck, so a round can be stalled indefinitely; against a weak
opponent the extra turns are worth points, and with 5.8x the samples the agent
learns the exploit harder (greedy rounds run 225 plies). Splitting 2048 games:
naturally-ended games lose 0.08%, cap-hit games lose 20.62%, and 99.4% of all
losses land in cap-hit games. The board freezes mid-expedition and the -20s
stand.
Self-play does not have this failure mode -- league runs converge to 53.6-ply
rounds and never hit the cap -- which is the regime the 3-round work targets.
Noted in the plan: static heuristic anchors are unusable as gates, and the
per-round cap needs care in Phase 1.
Co-Authored-By: Claude Opus 4.8 <noreply@anthropic.com>
Claude-Session: https://claude.ai/code/session_01XBQKgvBbxbheiTF1AVy1Sh
rollout_steps was pinned to MAX_STEPS (400) while a round actually runs
~50 plies, and finished envs were only reset between updates. 83% of every
rollout was spent stepping already-done envs to produce masked-out zeros.
Measured at rollout_steps=400: active steps go 17.3% -> 100%, i.e. 5.8x the
learner actions per update for the same compute.
Resetting in-scan exposes three things that were previously benign:
- compute_gae bootstrapped truncated episodes from zero. That was safe only
because every episode used to terminate inside the scan; now episodes cross
the boundary, so thread V(s_T) through.
- rollout_metrics read final_env and summed rewards along the scan axis, both
of which assume one episode per slot. With several episodes per slot that
silently produces garbage, so aggregate at done boundaries instead.
- league assignments were redrawn only between updates, which would pin a slot
to one seat/opponent across every episode in a scan. Redraw them on reset.
Also anneal potential shaping against learner actions rather than padded scan
steps: the old accounting counted the dead steps, so a 5M-step anneal expired
within two updates of 250. Any earlier evidence that shaping does not help was
gathered with it effectively off.
Co-Authored-By: Claude Opus 4.8 <noreply@anthropic.com>
Claude-Session: https://claude.ai/code/session_01XBQKgvBbxbheiTF1AVy1Sh
coolguyandClaude Opus 4.8