RDTvlokip PRO

The identity is exact and the column is withdrawn. Then your pilot does not work on this quantity, for a reason that turns out to be the same reason the floor was worth having. And your reframe of question 4 is better than mine, so I took it and followed it to a date on my own record.

Your identity, to zero

contrast              |t|     |t|/2.80    my ratio     difference
R 27 vs 26          0.482      0.1721      0.1721      0.00e+00
R 26 vs 25          0.627      0.2238      0.2238      0.00e+00
R 25 vs 24          2.430      0.8677      0.8677      0.00e+00
R 24 vs 23          0.711      0.2540      0.2540      0.00e+00
beta .005/.03       2.968      1.0601      1.0601      0.00e+00
beta .005/.037      0.875      0.3125      0.3125      0.00e+00

Not close — identical, because plancher = 2.80 * se and t = d / se in the same file. So "every observed effect is at or below its own detection floor" is |t| < 2.80, which at 145 df is p > 0.0058: an alpha 8.6 times stricter than the 0.05 written into the floor's own definition. And you are right that I published the same fact twice in one message and flagged only one instance — my section C printed t = 2.97 → p = 0.0035, which is section D's 1.06 row.

I replaced a p-value column with a rescaled p-value column and called it a design quantity, one message after explaining why observed power is a rescaled p-value. The ratio column is withdrawn. The correction to my question 3 is that "is it a function of the design" has to be checked on the printed expression, not on the intent.

The absolute floor survives, and it convicts something older than this table

Your prospective use is the real find, and it reaches further back than the row you applied it to. Both replication floors, computable before those runs existed:

                     n        floor      effect it had to confirm    ratio
beta .005/.03 discovery  30+30   0.00925          0.00981             1.06
              replication 12+12   0.01462          0.00981             0.67
R 25 vs 24    discovery  53+47   0.00728          0.00631             0.87
              replication 30+12   0.01240          0.00631             0.51

The sixty runs I ran in round eight could not have confirmed either contrast even if both were exactly true. I reported that replication as a test — "the sign flips", "it does not replicate", "the omnibus goes to p = 0.144" — and it was never a test. It was an estimator, and an unbiased one, which is why -0.0053, SE 0.0033 remains the only honest line to publish from it. The conclusion I drew survives. The reason I gave for it does not: I read a failure to reach a bar that the draw could not have reached.

That is computable before running, does not depend on what came out, and no p on the replication can say it. Kept, printed alone and absolute.

And rule 5 does eat it on the four R rows. 8+30+53+47+12 is a partition of the discovery runs by an outcome; the 6.32 effective runs at R 27 vs 26 was a result. Both inputs to those floors fall out of the run. Only the beta rows at 30 and 30 are design — and, as you note, the only contrast in the table that clears its floor is in the only column that was eligible.

Where the pilot fails, and it is not a detail

You propose 2.80 * sigma_pilot * sqrt(1/na + 1/nb) in the design document. On this quantity the pilot cannot fix sigma, and the reason is structural rather than practical.

beta        n      mean       sd     sd/mean
0.005      30    0.00768   0.01080     1.41
0.010      30    0.00943   0.01042     1.10
0.020      30    0.01005   0.00857     0.85
0.030      30    0.01749   0.01771     1.01
0.037      30    0.01057   0.01436     1.36

Bartlett  chi2 = 19.176   p = 0.0007        sd ratio across levels  2.07

Heteroscedastic across the swept factor, so one pilot sigma misprices the floor by 12 % to 38 % depending on the cell. But the mechanism is what matters:

The gap is bounded below by zero. The unconstrained max is always at least the matched value, so max - appariee >= 0 by construction, and 63 of the 210 runs sit exactly at 0. A non-negative variable piled at its bound has its scale tied to its location, and it does:

across the 18 cells with n >= 4:
   corr(cell mean, cell sd)    Pearson +0.874   Spearman +0.917
   slope sd on mean            +0.817
   median coefficient of variation   1.07

Sigma is not a nuisance scale here. It is roughly the quantity being measured. So a pilot fixes the floor only if the pilot's mean matches the eventual mean, which is to say only if you already know the effect. That is not a fixable pilot design; it is the floor's one data-dependent input being data in the strong sense.

But more of question 4 moves before the run than you proposed, in a different unit

The same fact that breaks the absolute floor makes a relative one writable. If sd ≈ CV × mean with CV stable near 1, then

floor / mean  =  2.80 * CV * sqrt(1/na + 1/nb)

which needs no sigma at all. For 30 seeds per cell and CV ≈ 1.2: 0.89. Checked against the actual table, floor 0.00925 over grand mean 0.01035 = 0.894.

Written before the first seed, in one line and with no pilot: with thirty seeds per cell, this design sees a near-doubling of the gap and nothing smaller. That is a stronger pre-registration than an absolute floor because it survives not knowing the scale, and it is the honest form for any non-negative quantity piled at zero — which is most of what gets measured in this field. CV is the stable thing to pilot; sigma is not.

So: not the whole of question 4 moves, but the part that moves is bigger than an absolute floor and it moves in relative units.

Question 4, your reframe, and the date

It became unwritable by you, which is not the same as uncomputable. The defect is not that the data arrived first. It is that "what does this measurement feed" was never asked, and that question does not reference the results.

You are right, and it is a better diagnosis than mine. I said the threshold rots on contact with data. It does not — it was never planted.

So I asked it, and it has an answer with a date on it.

The gap max - appariee measures the inflation from publishing the concentration statistic in its unconstrained-argmax form rather than the matched form. Its consumer was the 0.35 threshold in TEST3 §6.1, which decided whether an emergent code counted as compositional. That threshold was withdrawn on 11/08/2026, notebook §1.9, after you pointed out it was built on a sample maximum.

Rounds six through twelve have priced a measurement whose consumer was deleted in round five.

The distinction that keeps it honest, since not all of the work goes: the bound still has a consumer, because I report the max-form statistic and a reader needs to know it can be inflated by up to 0.14. That work stands. The contrast table — does the inflation depend on R, on beta — never had one. No decision anywhere changes at any value of that dependence, which is exactly why the relevance ratio was free to be 2 or 8 and why naming it now looks picked. There was nothing to pick from.

Which is what the design says too, if you ask it about the question that did have a consumer. That one is one-sample, not a contrast:

mean gap over 210 runs        0.01035    SE 0.00085    95 % CI [0.00869, 0.01201]
distance to the worst case    0.1339  =  158 standard errors
one-sample floor              0.00237
contrast floors in the table  0.00728 to 0.01445

The same runs are three to six times finer on the question with a consumer than on the contrasts without one, and they answered it at 158 sigma before any of this started.

What neither of us opened: the variable is not continuous

I noticed the zero bound while checking your pilot and did not stop to look at it. It is the largest thing in this file.

63 of the 210 runs have a gap of exactly zero. Thirty per cent. The gap is zero precisely when the unconstrained argmax is already a bijection — no message position claiming the attribute another one claimed. So this is not a continuous quantity with a floor; it is a point mass plus a right-skewed positive part, and every t, every permutation, every Scheffe bar and every bootstrap in twelve rounds has been computed on it as though it were neither.

First consequence, and it lands on the number I have been defending since round seven. The bound 0.1443 comes from the transposition climber searching for the worst code — which necessarily has an argmax collision. It is a worst case given a collision. My 0.0104 is unconditional, thirty per cent of it zeros. The published ratio compares a mixture to a conditional:

quantity                                    value     ratio to 0.1443
E[gap] over 210 runs  (what I published)   0.01035        13.9
E[gap | gap > 0]      (the matched one)    0.01479         9.8
median of the positive part                0.01254        11.5
q95 of the positive part                   0.04049         3.6
max observed over 210 runs                 0.05927         2.4

The ratio I have been quoting is 13.9 against a like-for-like 9.8 — and if you compare the two quantities that are actually the same kind of object, a worst case against a worst case, it is 2.4. "Emergent codes come nowhere near what an adversarial search reaches" was built on the pairing that flatters it, and I chose that pairing without noticing there was one to choose.

Second consequence: the quantity is two quantities, and they have different consumers.

P(argmax collision)         0.700    95 % CI [0.633, 0.761]
E[inflation | collision]    0.01479  SE 0.00101
product                     0.01035  = the published mean, exactly

How often the published statistic is wrong at all, and by how much when it is. Those answer different questions for a reader, and averaging them into one number answers neither. Never separated in any version of this document.

Third consequence: the tests. The positive part has skew +1.34, and neither it nor its log passes Shapiro — 1.7e-09 and 2.2e-06 — so it is not lognormal either, just skewed with no convenient form. Running the two contrasts of this exchange against the structure instead of through it:

contrast          Student, raw          on log(gap>0)         Mann-Whitney
R 25 vs 24     t=+2.462  p=0.0156    t=+1.471  p=0.1459        p=0.0619
beta .005/.03  t=-2.589  p=0.0122    t=-2.113  p=0.0405        p=0.0285

The R contrast — four rounds, a selection correction, a replication, a bump analysis, a pigeonhole argument — goes to p = 0.062 the moment it is asked in a form the variable can answer. It was partly the Gaussian machinery reading a point mass as data.

And the decomposition says the contrasts are not about the collision rate: 13 % and 17 % of each comes from the zero proportion, Fisher p = 0.66 and 0.55. They are about the size of the inflation when it happens, which is the half with the smaller n — 39 and 32 runs, not 53 and 47.

One number I will not claim. The observed zero rate, 0.300, differs from 6/27 = 0.2222 at binomial p = 0.0098 — 6/27 being the permutation rate if the three argmaxes were independent and uniform. They are argmaxes of correlated mutual informations, so that reference is not a justified null and the p is not a finding. It is a number, and I am printing it as one.

Rule 7, and it was available on 11/08

When a claim is withdrawn, list every measurement whose only consumer it was, and stop measuring them. A retraction propagates downstream and nothing in my process made it propagate. §1.9 killed the threshold; the quantity it justified kept being measured, contrasted, corrected for multiplicity, replicated, corrected again, and defended across seven rounds against increasingly good statistics — all of it correct, none of it attached to anything.

That is the rule that ends this thread, and unlike the previous six it costs nothing to run and cannot be gamed: it is a list, written at retraction time, of what the retracted claim was feeding.

I do not think you and I could have found it by getting better at the statistics. Every round did get better at the statistics.

And the zero mass is the same lesson from the other side. Twelve rounds of increasingly correct inference on a variable that neither of us had plotted. min, max and a count of exact zeros would have caught it in round one, cost nothing, and required no argument — and they would have caught it before the bound comparison that all of this was downstream of.

Notebook §7.29, §1.21, §1.22. Code in src/test3_communication/plancher_de_detection.py and masse_en_zero.py.

You are right that rule 6 published a bare integer. You are right about the arrow. And your one surprising number is your p-value wearing a hat, which I will show before I use the rest of your argument, because the rest of it survives without it.

Rule 6 is not repairable by reporting it over its null. I went to build that null and it is not identified.

Rule 6 dies harder than you killed it

I planted the effect your way — residuals from the R-level means, resampled with replacement, constant shift on every R = 25 run, calibrated so E[t] = 2.430, cell sizes 53 and 47. Then I varied the one thing that should not matter: where the residuals come from. Same design, same planted effect, same n, same greedy removal.

residual source              median breakdown   mean   P(<=2)   P(<=3)   power
residuals from R-level means         3           4.3    0.488    0.568    0.682
residuals from the 25 cell means     4           5.6    0.354    0.432    0.796
Gaussian, same sd                    2           4.0    0.518    0.598    0.626
yours                                4           5.5    0.252    0.398    0.665

Your median and mean sit on my cell-residual row; your power sits on my R-residual row. I could not find a single specification that produces all four of your numbers, and I am reporting that rather than tuning until it matches.

But locating your run exactly no longer matters, because the spread across three defensible choices is the finding. The observed 2 reads as the median of one null, "half of true effects" in a second, and "a quarter" in a third — and nothing distinguishes them except a modelling choice about residual structure that has no bearing on the effect being planted. The residual skew is 1.37 by R-level and 0.96 by cell; that difference alone moves the reference by a factor of two.

So the fix you proposed — report the count against E[breakdown | a real effect of this size] — inherits the problem it was fixing. There is no null to report against without first assuming the generative model, and the assumption swings the verdict.

Rule 6 is withdrawn, not amended. It was a robustness statistic with the model smuggled into the calibration step, which is the same failure as a bare integer with the model smuggled into the reader's head.

Your 0.665 is your p in costume

Power computed at the observed effect size is a one-to-one decreasing function of the p-value (Hoenig and Heisey 2001). It cannot contain anything t does not already contain. Directly:

    t     two-sided p    power at the observed size
 1.00        0.3190              0.168
 1.50        0.1358              0.319
 1.98        0.0496              0.503
 2.43        0.0163              0.675
 2.97        0.0035              0.839
 3.50        0.0006              0.935

Your 0.665 is my 0.675 analytic and 0.682 simulated, and it is p = 0.0163 rewritten. "The design has two-thirds power at the size it found" is "t was 2.43" — it is a fact about the observation, not about the design, and the sentence attributes it to the design.

Your use of it is fine: calibrating a planted effect against the observed size is legitimate and is not the same thing. It is the standalone sentence that does not survive.

That leaves your closing question standing on its own, which is where it should have been.

Your pigeonhole, verified, and the arrow conceded

reward <= R/27          discovery 150/150     replication 60/60
deficit in {0, 1}       never 2, never negative, across all 210
deficit == 1            9 of 150 and 11 of 60, six of the nine at R = 25
k = round(27 * reward)  contrast t = +2.226   (yours to the digit)

You are right and I had it backwards. R = len(np.unique(code)) is the alphabet size of the argmax code, and reward is round-trip success over the same 27 referents, so R symbols admit at most R decodable referents. Counting, not regression. My "R is the reward times twenty-seven" described the 141 runs where the bound is tight and silently dropped the nine where it is not — and those nine are the informative ones, since they are the runs where the code carries R symbols and only R − 1 decode.

The direction does make rule 5 bite harder, exactly as you say: a column that bounds the objective is disqualified in the runs where the optimiser misses the ceiling too, which my formulation did not cover.

One thing you did not check, which I expected to matter and it does not: none of the nine collision runs is in the bump cell. Zero of its thirteen. And their mean gap is 0.01142 against 0.01102 for the rest. So the receiver collision is not the mechanism behind anything, and the bump remains what §7.27 found it to be — four high-max runs.

Your question, answered on its own terms

Is there a draw large enough to put an effect that size above 0.9?

For beta, yes, and it is cheap: 36 seeds per level, 179 runs, about half an hour. For R, 89 runs per cell, roughly 266 total — but R cells are not settable, so that is not a draw anyone can command. You take what falls out. That asymmetry is rule 5 showing up again in a different costume: the column you cannot power is the column you were never allowed to contrast.

is the honest column next to each contrast the detectable-effect floor rather than the p?

Yes. Here is the whole table with it, floor = 2.80 × SE, a function of the design alone:

contrast                 n        SE      floor     observed   observed/floor
R 27 vs 26            8+30    0.00516    0.01445    -0.00249        0.17
R 26 vs 25           30+53    0.00296    0.00830    -0.00186        0.22
R 25 vs 24           53+47    0.00260    0.00728    +0.00631        0.87
R 24 vs 23           47+12    0.00419    0.01175    -0.00298        0.25
beta 0.005 vs 0.03   30+30    0.00330    0.00925    -0.00981        1.06
beta 0.005 vs 0.037  30+30    0.00330    0.00925    -0.00289        0.31

Every observed effect in the table is at or below its own detection floor. The two we spent four rounds on are the two that reach 0.87 and 1.06 — which is the definition of the regime where what surfaces is inflated. The floor column says that before any of it happened, needs no data, and cannot be gamed. It replaces the p column.

Where I think this goes past the question

The floor answers "what could I have seen". Nothing in eleven rounds has asked "what would I have needed to see for anything to change".

The table in §7.25 existed for one purpose: to know whether the gap the dynamics produces approaches the worst case a search can reach. Published worst case 0.1443, observed mean gap 0.0110, ratio 13.1.

target ratio    required rise in the gap    versus the largest observed effect (0.00981)
      2                 0.0611                          6.2 x
      3                 0.0371                          3.8 x
      5                 0.0178                          1.8 x
      8                 0.0070                          0.7 x
     10                 0.0034                          0.3 x

I want to stop here rather than take the number that helps me. The threshold is chosen, not derived, and the verdict flips between ratio 5 and ratio 8. If "nowhere near" means a factor of two, every contrast in the table is six times below anything that could matter and the design is four to eight times more sensitive than it needed to be. If "nowhere near" means a factor of eight, the contrasts are in range and the whole exercise was legitimate.

I cannot now name that threshold without it looking picked, which is the actual finding: it was never written down, and it is the only number in this entire exchange that had to be fixed before the data and was not. The floor is a design quantity and I can still compute it honestly today. The relevance threshold is a design quantity that becomes uncomputable the moment you have seen the results.

The five questions underneath this exchange

Eleven rounds, and the corrections have been getting more precise while staying on the same level. Written as questions, because that is what they are:

1. When is a column a variable? A dataframe column looks like a factor whether or not anyone set it. R survived four rounds of increasingly careful statistics because every one of them priced a contrast instead of asking what the column was. In this field almost everything reported as a factor is an output — final loss, effective rank, number of active features, the step convergence happened at, the architecture that survived a sweep. The test is whether the column was assigned before the run, and it is answered by reading the generator, not the data.

2. Can a robustness diagnostic exist without a generative model? Rule 6 says no. The breakdown count needs no distribution to compute and cannot be interpreted without one, and the interpretation moves by a factor of two across choices that have nothing to do with the effect. I suspect this generalises to every statistic sold as assumption-free: the assumption is not absent, it is relocated to the calibration step where nobody looks for it.

3. Which of our reported numbers are functions of the design and which are functions of the data? Only the first kind can be fixed before the first seed, and only the first kind cannot be gamed. The detection floor is design. The Scheffe bar is design. K is design. The p-value, eta squared, the breakdown count and observed power are all data — and observed power is the clean demonstration, since it looks like a design quantity and is a p-value.

4. What is the smallest effect that would have changed a conclusion? An experiment without this number cannot be under-powered or over-powered, because power is relative to an effect nobody named. It has to be written before the data, and after the data it can no longer be written honestly. Ours was never written, and that is why I can produce a table where the answer depends on a ratio I get to choose.

5. How much of empirical method is machinery for pricing measurements that could not have mattered? Eleven rounds on the correct price of a contrast on a column that was not eligible, measuring a quantity whose relevance threshold was never set, in a table where every effect sits at or below its own detection floor. Each correction was right. The sequence never asked whether the thing being corrected was worth measuring, and every tool either of us reached for was a tool for pricing, not for that question.

I do not have rules for 4 and 5. The one thing I can do is put the floor column and a stated relevance threshold into the design document before the next run, where the second one is still writable.

Notebook §7.28, §1.20 for rule 6. Code in src/test3_communication/plancher_de_detection.py.

You are right about the bump, right about my sentence, and right that rules 1 through 4 would not have caught this. I tried to break your diagnostic the way you broke my contrast and could not. Then I went one column over in the same file and found something that makes the question you asked at the end the wrong question — in a way that costs me the whole row, not one cell of it.

My sentence was wrong and my own p said so

Everything in my table was below the corrected q90.

2.968 is not below 2.73. I wrote that two lines under a p of 0.053, and 0.053 is between q95 and q90 by construction, so the number I had just published contradicted the sentence I wrote about it. It hands back the one row the section existed to surface. Struck.

Everything reproduces, and I checked your diagnostic against your own standard

Leave-one-cell-out lands on the digit: 1.134, 2.012, 1.944 for your three cells. The five within-beta gaps land on the digit. Scheffe gives 0.213 against your 0.212. The additive fit gives 2.215 against your 2.193, which is a parametrisation difference and nothing more.

Then the obvious attack, which is yours turned around: your leave-one-out is a maximum over twenty-five removals. You read the largest drop out of twenty-five, which is exactly what you caught me doing with ten contrasts. So I built its null the same way, permuting the gaps over the real design and taking the max drop each time:

observed drop                        1.295
E[max drop] under the null           0.430
q90 / q95 / q99             0.733 / 0.835 / 1.070
P(null max drop >= 1.295)           0.0008

It survives its own correction with room to spare. That attack is dead too, and I am reporting it because I went looking for it and it is not there.

One thing you chose

the other 19 cells move t(R) by at most 0.27

There are twenty-two others, not nineteen, and removing beta = 0.005, R = 25 moves t by 0.517 — larger than two of the three cells you displayed. It moves it up, 2.430 to 2.947, which is presumably why it did not make the list. Your 0.27 is right for downward moves only. It is the same shape as my error one section up: a sentence covering the rows not shown, wrong in the direction that helps the point.

Nothing in your conclusion turns on it. I am flagging it because you would flag it.

Further one: it is not thirteen runs, it is two

The smallest number of runs whose removal takes the contrast under the nominal bar — pick them adversarially, greedily, no cell structure assumed:

R 25 vs 24        t = +2.430    breaks at 2 runs of 150   (1.3 %)
beta 0.005 vs 0.03  t = -2.968    breaks at 3 runs of 150   (2.0 %)

Your thirteen is six times too generous to me. And the cell is not a cell, it is bimodal. Sorted gaps inside it:

0.0496  0.0488  0.0477  0.0445  |  0.0253  0.0245  0.0215  0.0202  0.0118  0.0089  0.0081  0.0062  0.0000

The jump at that break is 0.0192; the largest jump anywhere else in the cell is 0.0084. The top four have mean concentration max 0.182, above the whole plan's q90 of 0.171. The other nine have 0.123, and the plan's median is 0.124. Four unusual runs sitting on nine completely ordinary ones, not a cell with a level.

Further two: the thing you named has a test, and it does not clear your own bar

You wrote that it is not a confound, it is an interaction. That is a testable statement and neither of us tested it. Fitting cell means against the additive model:

interaction        F(11,127) = 1.748    nominal p = 0.070    permutation p = 0.075

So the interaction you diagnosed sits at 0.075 before any multiplicity correction at all — squarely in the zone you spent two rounds teaching me to distrust. And on the sixty independent runs: F(6,40) = 1.425, p = 0.229, with the cell inverting from +0.0201 to -0.0088.

The bump is real in the discovery sample, survives being the max of twenty-five, and is not there on the second draw. Same verdict as the two contrasts it explains.

Further three, which is the one that matters: R is the objective

results_test3/ carries a column neither of us opened. Every run records its final reward.

runs where |reward - k/27| < 1e-3, for integer k     150 / 150
runs where k == R                                    141 / 150
runs where k == R - 1                                  9 / 150
corr(R, reward)                                       +0.9725

R is the reward times twenty-seven. Not correlated with the outcome, not downstream of it — it is the outcome, rounded to a grid of 1/27. Every cell in your table has a single reward value to five decimals: 0.92586 across all thirteen runs of the bump cell, 0.88882 one column over, 0.96289 one column back.

You called the R row post-treatment. That is true and it is too gentle. Stratifying by R is stratifying runs by the value of the objective the optimiser was maximising, and then asking whether a measurement bias differs between the ones that scored 25/27 and the ones that scored 24/27. There is no factor there to be a fact about. The bump is not why that row should not have been published; the row should not have been published if every cell had been flat.

For completeness, because it decides whether your row is contaminated too: beta does not move R. Chi-square on the full 5 x 5 crossing gives 15.67 on 16 df, p = 0.476. There is a weak linear component, corr(beta, R) = +0.197 at p = 0.016, so the beta row is very slightly mediated, but it is a real factor that I set, and it stays a legitimate contrast. Its problems are the ones already on the record: corrected p = 0.053, Scheffe 0.072, and t = -0.34 on replication.

Further four: the quantity is a function of max, not of R

corr(concentration max, gap)         +0.4317
corr(matched concentration, gap)     +0.0665
corr(concentration max, R)           +0.0172

The gap is mostly "how high the unconstrained max landed", and where the max lands has nothing to do with R. That is the mechanism under your bump: a cluster of high-max runs that happened to fall in one cell of a table indexed by something orthogonal to them. Which is also why the cell inverts on the next draw — nothing was holding it there.

Your question, and why I am answering a different one

Is there one for when a contrast is allowed to be reported as a fact about the factor it is labelled with, rather than about the one cell it lives in?

The question presumes the label is a factor, and for the row we have been arguing about it is not. So two rules, and the first is the one that would have saved this.

Rule 5. A contrast is reported as a fact about a column only if the column was set before the run. Not measured, not derived, not "an output that happens to index things usefully" — assigned. R fails this at the strongest possible level, being the objective on a grid. No diagnostic on that row could have rescued it, and none was needed: it is disqualified before any data arrives, by reading the generator. This deletes the entire R row from §7.25 and §7.25bis, which is more than your bump does, and it is the only rule so far that costs me a result I still believe rather than one I had already given up.

Rule 6, for columns that pass rule 5. Publish the breakdown count. The smallest number of runs whose adversarial removal takes the contrast under the bar. One integer, no distribution, no family, computable in seconds, and it does not care whether the fragility is a cell, an outlier, or a cluster. Here: 2 of 150 and 3 of 150. A contrast that dies to 1.3 % of the sample is reported with that integer attached or not reported.

Neither is a rule about selection. You were right that all four of mine were, and that was the flaw — I had built four ways to price a contrast and none to ask whether the column deserved a price.

And rule 1 does have a diary in it

You are right, and I am taking Scheffe. "Every factor read in the same sitting" makes the published p depend on my scrolling; 2.817 at 145 df and family 0.10 gives my R contrast 0.213 against my sitting-dependent 0.200, and the beta contrast 0.072 against 0.053. Same numbers, fixed by the design before the first seed, no diary. Rule 1 now reads: K is the design's, and the bar is Scheffe's.

Sixth time in this exchange the answer was in something already on disk. This time it was a column in the same file, twelve characters from the one we were arguing about.

Notebook §7.27, §1.19 for the dead hypothesis. Code in src/test3_communication/anatomie_du_bump.py.

Your three legs reproduce. Two of your numbers about me are wrong in my favour and I am correcting them against you. And your closing question has an answer I did not want to give, which I found by trying to answer it honestly: no rule, decided per table, and the proof is one row above the one we have been arguing about.

Your null law, by three routes

I did not want to take your simulation on trust, so I built two more. Parametric with fixed cells, the way you did it. A permutation of the 150 observed gaps over the observed design labels, which assumes nothing — not normality, not a common sd, not that the cell sizes were fixed. And a parametric one with the cell sizes redrawn each time, because R is an output of the run and 8/30/53/47/12 is itself a realisation.

Your law is right, and your row is my sigma-known row to three digits on all of it. The only visible gap anywhere is that a re-estimated sigma has slightly heavier tails than a known one, which moves q90 by 0.025 and P by 0.006. Redrawing the cell sizes moves it less than that, so the fixed-cell approximation you had to make was free — worth knowing, since R being an output was the one thing you could not check from outside.

Magnitudes reproduce too: E[abs d of the winner] 0.00658 parametric, 0.00662 permutation, against your 0.00657. E[abs d | the winner is the 25/24 pair] 0.00415 and 0.00421, against your 0.00414. And that pair wins 13.7 % of the time, which is why it comes cheaper.

Correction one: my t was 2.43, and yours was closer to it than mine

You read 2.40 off the published table and I told you mine was 2.53. Recomputed from the runs with the sd pooled across the five cells — the estimator a contrast test actually uses — it is 2.430, and the pooled sd is 0.012969 against your 0.012942. My 2.53 was the within-bin version, which I had already told you was the worse estimator at n = 8 and then used anyway for the headline number.

So the entry in your table should be 2.43, and the selection-corrected p by permutation is 0.099 (two independent permutation runs of 100 000 give 0.0994 and 0.1013, so 0.10). You had 0.107 at 2.40. Nominal p was 0.0163.

Correction two: your pooled comparison used my number from a different procedure

Your null pooled +0.00256 by inverse variance against my +0.0028. But my +0.0028 is not an inverse-variance pool of two halves. It is what falls out of re-running the contrast on all 210 raw runs, which re-estimates the cell means and the sd jointly. Those are different estimators and they do not have to agree.

Pooled the way your null pools, my two independent estimates give:

discovery     +0.00631   SE 0.00260   t = +2.43   weight 63.5 %
replication   -0.00535   SE 0.00343   t = -1.56   weight 36.5 %
inverse variance pool  +0.00206   SE 0.00207   t = +1.00

Against your null run end to end at 400 000 draws:

Your +0.00256 matches the conditional row, so your end-to-end conditioned on the pair while the text says "select the max". That is the right conditioning — my contrast is that pair — but then the comparison is against +0.00206, not +0.0028.

Either row says what you said, harder. It is not P = 0.434. My pooled number is at the 63rd to 82nd percentile of a table with nothing in it, and I should not have published it. The only unselected estimate I own is the replication alone, -0.0053, SE 0.0033. That is now the only one in the notebook. While I was at it: the t = 1.47 I published for n = 210 is also the within-bin version. Pooled sd gives d = +0.00285, t = 1.35.

Correction three, which is yours to keep: omega squared is exact, not approximate

Under the null, eta squared is exactly Beta(df1/2, df2/2), so its expectation is exactly df1/(df1+df2). Your 2.68 % is 4/149 and your 2.87 % is 6/209, to the digit — I checked against 400 000 draws and got 2.683 % and 2.867 %. Not "biased up by about df1/df2". Biased up by exactly that. Every one of your four figures reproduces:

Now the part neither of us had

You corrected my p for ten contrasts. The table offered twenty. The same 150 runs carry a beta row, five levels, ten more pairwise contrasts, printed in the same reply, read the same afternoon.

Its largest is abs t = 2.968. Bigger than the one we have spent two rounds on.

beta = 0.005 vs beta = 0.03    d = -0.00981    t = -2.968    nominal p = 0.0035
beta = 0.010 vs beta = 0.03    d = -0.00806    t = -2.439
R = 25      vs R = 24          d = +0.00631    t = +2.430
beta = 0.020 vs beta = 0.03    d = -0.00744    t = -2.253
beta = 0.030 vs beta = 0.037   d = +0.00691    t = +2.093

Five contrasts past two sigma, not one. My sentence last round — "the one contrast past two sigma in a table of ten" — was wrong on both counts, and the largest of the five was in the row where I wrote "no trend past the noise on the row itself". I wrote that without running a test. The row's omnibus at discovery was F(4,145) = 2.595, p = 0.039.

Corrected over the twenty by permutation: my R contrast goes from 0.101 to 0.200. The beta one sits at 0.053.

So I ran the replication I already had. The sixty independent runs answer the beta row too, and I had never looked:

beta 0.005 vs 0.03   discovery -0.00981 (t = -2.97)   replication -0.00135 (t = -0.34)
omnibus              discovery F(4,145) = 2.595, p = 0.039   replication F(4,55) = 1.790, p = 0.144

Cell means, discovery then replication, across beta = 0.005 / 0.010 / 0.020 / 0.030 / 0.037: 0.0077, 0.0094, 0.0100, 0.0175, 0.0106 — then 0.0087, 0.0099, 0.0024, 0.0101, 0.0121. The peak I would have described as "beta = 0.03 stands up" is gone, and the cell that collapses on the second draw is a different one. The pooled p = 0.029 at n = 210 is 71 % discovery data and is not a confirmation of anything.

It dies the same way, for the same reason, and I reached the right conclusion about it by not looking hard enough. That is not the same as being right, and it is worse than the R error, because there I at least wrote the number down.

Your question, answered

Does it have a standing rule for how many contrasts a table offers before you are allowed to read the largest, or is that decided per table after you have seen it?

Per table, after seeing it. There is no rule in the notebook and there never was. And the beta row is the demonstration: I looked at both rows, decided the R row was worth a contrast and the beta row was worth a sentence, and picked the smaller of the two maxima. A per-table decision made after seeing the table cannot even be relied on to select the largest thing in it.

Four lines going in, before the next seed:

1. K is declared before the data. K = every pairwise contrast the design offers, summed over every factor read in the same sitting, whether or not it gets reported. Twenty here, not ten, and the ten I did not report are the ones that made it twenty.
2. Every abs t >= 2 in the table is printed, not the largest. Five rows here. Withholding four is what let me call a row flat while it held a 2.97.
3. The corrected p comes from a permutation of the outcome over the design labels. Seconds to run, no distributional assumption, and it is the arbiter when the parametric version and the reader's version disagree — as they did above by 0.025 on q90.
4. A selected contrast never gets published pooled with its own replication. Replication alone, with its SE.

For this design the threshold that rule implies is worth stating, because it is not close to the one I was using: over the twenty contrasts, q90 is 2.73, q95 is 2.99, q99 is 3.56. Against a nominal 1.98. Everything in my table was below the corrected q90.

On the zero-run claim

You are right that the max-of-K law and E[eta squared] are functions of the design and were computable before the first seed, and you concede the second draw is stronger. I would sharpen it in the direction that costs me more: available before the first seed, it changes the design rather than the reading. Knowing that five R levels and five beta levels demand abs t = 2.99 would have forced me either to name one contrast in advance or to budget the replication into the run from the start. I did neither, because I did not know I was choosing.

What the zero-run route could not have done is tell me the sign flipped, or that the beta row dies too. Those needed the sixty runs. It is the cheapest way to know you should not believe a number; it is not a way to find out what the number is.

Fifth time in this exchange the answer was a second draw. First time it also answered a question I had not asked.

Notebook §7.26, and §1.18 for the dead hypothesis. Verification code in src/test3_communication/correction_de_selection.py and correction_de_selection_suite.py.

You called it. I ran it. The contrast flipped sign.

First, your arithmetic, checked against the raw runs rather than the table

Everything you derived from binned means reproduces on the 150 individual runs. Your reconstruction was exact enough that the differences are rounding:

And you are right that my 11 % and 90 % are the same two numbers over different denominators. Worth stating once so it does not read as a hedge later.

Your per-bin standard errors differ from mine because you pooled: 0.012942/√8 = 0.00458 is your R = 27 cell exactly. Mine are the within-bin values. Yours is the better estimator at n = 8; mine tests the homoscedasticity yours assumes. On the contrast that matters they agree — your t = 2.4, my t = 2.53.

The thing you cannot do from where you are sitting

R is an output of the run, not a setting. I cannot run thirty seeds at R = 24 and R = 25. I run seeds and take whatever R falls out. Those two cells carry 100 of 150 runs, so thirty more inside them costs about forty-five runs. I ran sixty, on an independent seed, same five betas.

The replication

On the sixty new runs alone, R = 25 against R = 24:

difference   -0.0053     SE 0.0033     t = -1.60

The sign flips. Which is what the largest of ten available contrasts does when it is the largest of ten available contrasts. You said you did not believe it. Neither of us should have.

Pooled to 210 runs, everything moves toward null and nothing moves away from it:

The new sample also reached R = 22 and R = 21 once each, which is why the F has six numerator degrees of freedom rather than four.

So I am taking both of your reformulations, and they are now stronger than when you wrote them

On R. "R explains 4 %" was the wrong sentence, and at n = 210 it is not even the wrong number any more: eta² is 1.2 % and F(6,203) = 0.419 at p = 0.87. The sentence that goes in the notebook is yours — R is not distinguishable from explaining none of it — and the replication is what earns it.

On flatness. Your power framing replaces my ratio, and the pooled sample improves it:

observed slope    +0.000507 per unit R    SE 0.000836    t = 0.61
detectable at 80 %  0.00234
worst-case slope   -0.04065 per unit R
ratio               17.4

Up from 13.9. The observed row is bounded away from the reachable row by seventeen times my own resolution, and it still points the other way. You are right that the ratio invites "different scales" and the power statement forecloses it. It is now in §7.25 in your words rather than mine.

What this cost and what it bought

Sixty runs, about half an hour. It killed a kink I would have mentioned as "the one place the flat row is not flat", removed a 4 % figure I had reported as a finding, and turned a p = 0.19 into a p = 0.87.

The generalisable part is not about R. It is that the one contrast past two sigma in a table of ten was exactly the one to distrust, and the cheapest way to know was to draw again rather than to argue about it. That is the fourth time in this exchange that the answer was a second draw, and the first time I made it before publishing rather than after.

You are right about the structure, and I want to correct one number before agreeing with the rest.

One magnitude, which is mine to fix

Your 22.6 % compares your climber at R = 27 (0.0396) against your own mixture (0.1751). My published bound was 0.1443, from the transposition climber, and that is 90 % of my own mixture at 0.1604 — or 82 % of yours. The undercount is 11 %, not a factor of four.

The direction of your correction holds entirely. Its magnitude describes your sweep, not the figure I published.

Everything else lands, including the part I got backwards

The null moves 0.00016 across the whole support my procedure visits. The reachable worst case moves 0.1355. I spent an entire section rebuilding the reference while the damage sat in the search's reachable set — the denominator when the problem was the numerator.

So my three bounds were not too generous. They were too small, and a retraction that points the wrong way is worse than the overclaim it replaces.

Worth recording that we converged on the flatness by different partitions. You measured null by R, 200 000 draws per cell. I had measured it by full fiber profile, eleven profiles, −0.0001 to +0.0005. Same conclusion, no shared assumption, which is the only kind of agreement worth much between us after the concentration-1.0 episode.

Your question, measured

150 runs, five betas by thirty seeds, on actually emergent codes rather than a search worst case.

Neither. The gap does not fall as beta rises: correlation +0.158, and no trend past the noise on the row itself. And R does not stop predicting it, because R never predicted it — correlation +0.091, 4 % of variance explained. Conditioning on R removes almost nothing: the residual correlation with beta stays at +0.144 against +0.158 unconditioned.

It is not that R ceases to be the variable. It was never the variable for this quantity.

Which forces a distinction neither of us had made

The worst case reachable under a floor on R and the gap the dynamics actually produces are different functions of R.

R                    27       26       25       24       23
worst case       0.0526   0.1362   0.1783   0.1850   0.2152     strongly monotone
observed gap     0.0096   0.0120   0.0139   0.0076   0.0106     flat

Ratio between them: 15.2. Emergent codes come nowhere near what an adversarial search reaches in the same regime. Both numbers are indexed by R and there is no reason they should track — one is what a search can find, the other is where the dynamics lands.

And your beta reservation settles by computation

Mixed over the p(R) specific to each beta, the worst case runs from 0.1564 to 0.1773 — 0.0209 of amplitude across the whole range. The shift with beta exists, and it is small relative to the quantity being bounded.

What I take from this

A bound must be mixed over the regime actually visited. An effect size must not be read off the same table. I had neither rule this morning, and I got the second one wrong by inheriting the first one's index.

The three bounds are now reported as the R-indexed table, the mixture is stated next to them, and the observed gap is reported separately with its own note that R explains 4 % of it. Notebook §7.25.

Thank you. I have direct evidence on both halves of your guardrail, and they came out unevenly, which I think is the useful part.

Preregistration: I did it, and it failed in a way I would not have predicted. The design document recorded a dated commitment before any data existed, naming the statistic and the expected outcome, and it was presented as what made the test sharply falsifiable. When the experiment finally ran, the commitment turned out to be underspecified on three counts. It never named the parametrization, which is the variable that decides the answer, so the same commitment was confirmed on two parametrizations and refuted on a third. Its interpretation clause said an excess would prove a flaw in a specific piece of reasoning, and that inference does not follow. And its first half predicted near-perfect bijections, of which there was one in twenty.

So preregistration protected me from fitting after the fact, which is what it is for, and protected me from nothing else. It does not catch an omitted variable, and it does not catch writing down the wrong interpretation in advance. If I keep one rule from this, it is that a recorded prediction has to name three things and not one: on which population, under which parametrization, and what each outcome would prove. I only ever wrote the first.

Independent reproduction: this is the half that worked, and it worked six times out of six. Every correction to this project has come from one outside reader who reruns the code before commenting. Not from review of the write-up, but from re-derivation from the artifact. That is a real constraint on me rather than on him: it only works if I publish enough that re-derivation is possible, so the guardrail is upstream, in what gets released.

It also has a failure mode worth naming, because it happened. He and I once agreed, and we were both wrong, because his argument was correct under an assumption we both carried without stating it. Two people can share a frame, particularly when the second is reading the first's documents. What broke it was not a third reader but running a step of the programme that had never been run.

Which is the version of your guardrail I would defend most: anything that does not inherit your specification. An outside reader is the most available instance and the highest yield. A second independent route to the same quantity is the cheapest, and computing a threshold from a Hessian rather than from a bisection caught that I had been measuring my optimiser rather than my objective. And when all of those agree and are wrong together, the only thing structurally guaranteed not to share your frame is the measurement you have not made yet.

On the exact-computation point you opened with: making the world small enough to compute everything exactly removed the estimation-error class entirely and left the specification-error class untouched. Eight of my hypotheses died in one day and not one was an arithmetic error. Exactness earned its keep only by making the second route cheap, which is a real benefit and not the one I thought I was buying.

You are right, and the diagnosis is worse than "measured in the wrong regime"

I annotated the three bounds as conditional on bijectivity and left them standing. Annotation is not the fix, and I knew that at the time. The same article says a retracted number should be re-measured, not footnoted.

But there is a sharper reason they could not have been right, and it is about the search rather than the reporting. My climber moved by transpositions. A transposition of a permutation is a permutation, so the move set could not leave the bijective regime even in principle. The constraint was not an assumption I failed to check, it was welded into the operator. Yours reassigns one referent to any message, which is why it can see what mine could not.

That is the third time this week that my instrument, not my reasoning, decided the answer.

Your sweep reproduces

Independent implementation, single-referent reassignment, 20 restarts, 120 steps, identical budget at every floor:

Same shape, and the same conclusion: one collision is the whole effect. My R = 27 baseline is a little higher than yours, so my ratio is 2.6x rather than 4x, which does not touch the claim.

Your second bound matches exactly. Highest concentration reachable while still double-counting: at R = 27 you get 0.2045 and I get 0.1943; at R = 26 we both get 0.6409, with matched 0.5812. Two different climbers, four decimals. My permutation figure was 0.6314, so one collision beats a bijectivity-restricted search over the whole permutation space.

And my R = 26 winner has the shape you describe, with a different attribute index:

I(A_i ; M_j) bits          argmax per position: [1 1 1]
[[0.086 0.012 0.062]       distinct messages: 26 of 27
 [0.416 0.330 0.410]       max 0.2430 against matched 0.1068
 [0.036 0.012 0.049]]

One attribute claimed by all three positions, at one collision instead of the eighteen my hand-built example needed.

Your question, answered on 100 seeds rather than 40

You asked whether R = 26 is common enough in the forty starts to be the modal case rather than the boundary. It is neither: R = 25 is modal, and R = 26 is second. Tabular sender, beta = 0.02, 100 seeds:

So the bijective case is not the boundary of the regime, it is 3 % of it. Ninety-seven of a hundred runs sit at or past the first collision, and the median run is one collision beyond where your sweep says the effect has already arrived.

It holds across the code regime rather than at one beta. Mean R by entropy coefficient, 20 seeds each: 24.05 at 0.005, 24.55 at 0.010, 24.80 at 0.030, 25.25 at 0.037. Raising beta toward the stability threshold buys back distinct messages and never reaches 27 on average.

And the other two parametrizations sit deeper, not shallower. Modal R = 21 for the autoregressive-per-referent sender, R = 23 for the attribute-structured one.

So your closing point is right and I had it too weak

I wrote that the matched statistic is the only one that stays interpretable once bijectivity goes. The correct statement is stronger, and it is yours: the double count does not degrade gradually as R falls. It arrives almost entirely at the first collision, and the first collision is not an edge case, it is 97 % of runs.

Which means the published statistic is unusable in this experiment's actual operating regime, not merely at its boundary. That is a firmer conclusion than the one I shipped, and it comes from re-running a number I had chosen to annotate.

The three bounds are replaced by the R-indexed table rather than deleted, with the transposition-operator diagnosis written next to them, and the article is updated. Thank you for not letting me footnote my way out of that one.

You went to the one part of the project that has never run. That is the right place to go, and it is the first time in five rounds that a criticism has arrived before the data rather than after. That matters at the end of this reply.

Your numbers

All of them. Seed 0 at 20,000 reproduces to the digit. My own 10M draw is an independent stream, so it is a check on the estimand and not on your RNG:

Two independent samples agreeing on a maximum to four digits made me check whether the statistic was discrete enough to explain it. It is discrete — 2,951 distinct values in 2M draws, since the whole matrix is a function of nine integer counts — but the top rungs are singletons, so discreteness explains nothing. It is a coincidence, and the next section is what happens when you stop relying on one.

Your vectorised-vs-scalar check: I did the same and got max absolute difference 5.551e-17 on 3,000 codes, which I assume is your 5.6e-17. For a bijection both margins of the joint are exactly uniform, so I(A_i;M_j) = Σ (c/27)·log2(c/3) with c integer — that identity is what makes the whole thing a lookup table, and validating against the scalar path is really validating the identity.

The threshold: you are right, and the reason is worse than "still moving"

Your framing is that the max is the only row still in motion. Mine is that it cannot stop.

The 1,296 compositional codes are bijections. They are in the null, with probability 1296/27! ≈ 1.19e-25, and they score exactly 1. So the supremum of the null distribution is exactly 1 — the very value the threshold was built to declare unreachable. A sample maximum here is not estimating a threshold. It is estimating 1, infinitely slowly. No sample size fixes that, because there is nothing to converge to except the thing being tested.

Empirically, twelve independent blocks of 10,000,000 (variabilite_du_maximum.py, 384 s):

The block maxima run from 0.3775 to 0.4283. That range is 1.54 standard deviations of the null itself. A threshold read off that row inherits it: it measures how long I was willing to sample, not the distribution.

So: threshold withdrawn, quantile quoted instead, exactly as you proposed. q99.9 = 0.2525.

The part you found without pointing at it

§6.1 should never have carried a pass/fail line at all, and my own document says so three paragraphs earlier. §5 reads:

On abandonne délibérément le critère pass/fail. […] la mesure de concentration positionnelle définie en §6.1 sera statistiquement indiscernable de celle d'une permutation tirée uniformément au hasard.

That is a commitment about a distribution. Then §6.1 reintroduces a pass/fail and congratulates itself for it being derived rather than arbitrary. The defect was never the arbitrariness. It was the pass/fail, which §5 had already discarded for the reasons you then re-derived from the power side. I wrote both paragraphs. It took an outside reader for me to read them next to each other.

Your power numbers reproduce exactly. One-sided, p < 0.001, 80% power, δ = 3.93σ/√n:

against 0.223 on a single run for the threshold. Ratio 17. That calculation is now in §6.2 where it belongs.

The matching: your diagnosis is right, your localisation is not

74.6% double-count rate on uniform draws — I get 74.6%. On my top 200, matching gives mean inflation 0.0179 against your 0.0170. Same phenomenon.

Where I disagree is "real in the middle and absent at both ends". I could not test that against the null alone, because the null has no structured codes in it. So I built two populations where the structure is known independently of the MI matrix.

Codes with k of 3 positions cleanly encoding an attribute, the rest scrambled conditionally (still bijections), 4,000 each:

A ladder from a compositional code outward by transpositions, scored against d = minimum Hamming distance to any of the 1,296 (so relabellings are free):

 d      0    2    4    6    8    9   10   12   14   16   18   20   21   23
 infl  .000 .000 .000 .000 .000 .000 .0001 .0004 .0022 .0051 .0081 .0099 .0103 .0090
 dbl%   0    0    0    0    0    0   1.1   3.5  17.4 35.5 57.1 68.8 73.2 77.7

Inflation is exactly zero out to nine transpositions, then climbs and meets the null's own 0.0101 around d = 21.

So the inflation does not live in the middle of the scale. It lives in the region with no positional structure at all, and it is identically zero everywhere there is structure to read. Which means the specific §6.1 worry — a 0.28 code credited 0.017 it does not have — is real only for codes that reached 0.28 by accident, and those have nothing to read either way.

I want to flag how I nearly got this backwards. My first sweep binned the null by concentration level and found inflation rising with concentration: 0.0014 below 0.05, 0.0228 above 0.30. That is a true measurement and it points the opposite way from the ladder, which at the same concentration ≈ 0.27 gives 0.0022. Both are correct. Inflation tracks structure, not level, and those are not the same axis — a uniform draw at 0.27 got there by accident and usually double-counts, a near-compositional code at 0.27 did not. One population would have convinced me of the wrong thing.

Your actual question

Is the max standing in for a matching you have not needed yet, or is there a reason to want the double count?

Standing in for a matching. There was no reason.

There is one reason to keep reporting it, which I did not know when I wrote it and had to go check: the unconstrained per-position form is the field standard. posdis (Chaabouni et al. 2020) takes the argmax independently per position with no one-to-one constraint. So dropping it costs comparability with published numbers.

Both are now in grammaire3.py. concentration() unchanged, so the 20,000-draw table still reproduces bit for bit. concentration_appariee() added — exact Hungarian, and at 3×3 that is six permutations, so enumerated rather than solved. §6.1 now reads the matched one as its position.

One argument for your fix that you did not make

You wrote that the change cancels in §6.2 because it is the same transform on both sides. That holds under H0 — if the emergent codes are ordinary bijections, both populations shift by the same 0.0101 and nothing changes.

It does not hold under H1. If a pressure creates positional structure, the double count disappears with it, as the tables above show. The 0.0101 then comes off the null and not off the emergent population. The matched statistic lowers the reference without moving the signal: neutral where it must be, favourable where I want power. Small — sd also drops 0.0330 → 0.0315 — but it points the right way, and it is a better argument for your change than the one you offered.

Bounding the damage

Local hill-climbing over transpositions, so these are lower bounds, not maxima:

• largest max-minus-matched gap found: 0.1443, on a code scoring 0.2473 — i.e. inside the body of the null, where nothing is concluded anyway;
• highest concentration reachable while double-counting: 0.6314, and that code still scores 0.5560 matched. Even pushed adversarially, the max does not turn an unstructured code into a structured one;
• highest non-compositional concentration found: 0.9294. Your argument that concentration 1.0 forces an injective argmax is right — two positions each fully determining one attribute would collapse nine referents onto three messages, and a bijection cannot — and the top of the scale turns out to be isolated as well as safe: 1.0000, then 0.9294.

All three of those are hill-climbing over permutations, which matters more than I realised when I wrote them. See below.

A follow-up that makes your fix necessary rather than optional

After answering you I ran §6.7, the two-agent check that had never been done. One of its results changes the standing of your second question.

Exact gradient ascent on the joint objective, no sampling anywhere, does not reach a bijection from a uniform start. One start in forty. It settles on codes where 1 to 4 referents collide — E[R] lands on 23/27, 24/27, 25/27, 26/27. Started on a perfect code it stays at exactly 1.

So the emergent codes will not be bijections, and your safety argument for the top of the scale is conditional on bijectivity. Drop that condition and it fails outright. Take m₁ = a₁, m₂ = a₁, m₃ = a₂ — duplicate the first attribute across two positions, discard the third:

distinct messages used : 9 of 27          bijective : no

I(A_i ; M_j) in bits          concentration, max      : 1.000000
[[1.585 1.585 0.   ]          concentration, matched  : 0.666667
 [0.    0.    1.585]
 [0.    0.    0.   ]]

The published statistic hands a perfect 1.0000 — the value reserved for compositional codes — to a code that throws away one attribute in three and uses a third of the message space. The matched version returns 0.667, which is the right answer: two attributes read out of three.

So the double count is not a middle-of-the-scale artefact confined to structureless codes, which is what the measurement on bijections suggested to both of us. Once bijectivity goes, it reaches the top. Your fix is not a 0.48-point improvement in rank concordance. It is the only one of the two statistics that stays interpretable in the regime the experiment will actually be in.

I would not have found this by measuring harder on the null. It came from running the step that had never been run, and it is the second time in this exchange that the useful thing was upstream of the number under discussion.

Why this round was cheap and the next one would not be

No Test 3 training has run. There is no measured emergent concentration anywhere in the repository. So changing the instrument today cannot have been motivated by a result, and anyone can check that from the git history. The identical change made after a first run would be unverifiable from outside, and should be refused. That is the whole reason §5 recorded its commitment with a date, and it is the first time the mechanism has actually been worth something.

Thank you for going to the unpublished part. It is where the mistakes are cheapest to fix and where nobody has any reason to look.

Draft is up, and you're all over it: https://github.com/RDTvlokip/RDTRL/blob/main/docs/ARTICLE2.md

I took you literally on "put the thread in it" — there's a section quoting the four rounds verbatim, including the line about my own balayage_graines docstring already making the argument that demolished my published table. And including your retraction on 11.50, which landed before I'd sent you numbers I already had on disk.

The bound is credited as yours in the section title, in the "what transfers" list, in CITATION.cff, and as a structured contributors entry with your ORCID in .zenodo.json, so it shows on the Zenodo record rather than only in prose.

You said to raise credit when there was a draft. There is one, so: acknowledgment is what I've written, and I'm not attached to it. If you'd rather it were co-authorship on this second piece, say so — most of what it reports is your review work, and I'd have no argument against it. If acknowledgment is right, that's fine too and it stays as is.

Also worth flagging before you read: the reversal test I built to validate your bound was empty on the first attempt. I'd moved genre-neutrality between the two number families, which — since the nouns and verbs are already symmetric in number — is just the sg/pl relabelling. Isomorphic. Seventy seeds would have returned the mirror image by construction. The version that actually tests something uses three genders, so the ceiling ratio goes from 2 to 3, and that one passes: maxima of exactly 36.0 and 12.0, ratio of observed means 3.01 against a predicted 3.0.

No rush and no obligation — but so you're not left guessing: if I haven't heard back in a week, I'll publish as is, with the acknowledgment as written. That's the option that commits you to nothing, and it's the one I can revise upward later if you'd prefer otherwise. Silence just means the default.

Settled, and it cost me a headline rather than a metric. Everything below is measured, and the code is in the repo.

Your dtype test, run.

  float32 first : 0.08333331346511841
  float64 first : 0.0833333358168602

Your five line numbers are exact and your reading of the promotion is exact.

One correction: there are two paths, not three. You have trajectoire_couplage.py:84 as a third because it omits dtype, so the advantage stays float64 and promotes the loss. That is true in numpy and false in torch, where torch.get_default_dtype() is float32, so torch.tensor on a Python float gives a float32 tensor:

  torch.tensor(r - b)                      -> torch.float32, 0.0833333358168602
  torch.tensor(r - b, dtype=torch.float32) -> torch.float32, 0.0833333358168602
  same dtype and same value: True

The loss stays float32 in both. It does not change your conclusion, since the float32 path is still alone, but that script sits with the other three rather than on its own.

Divergence on the real reward stream, recorded rather than simulated:

  seed   first disagreement   % of first 2000 steps   % after   max relative gap
   0            5                     57.7              24.2        5.45e-06
   1            5                     78.3              29.6        7.96e-06
   2            4                     79.0              26.1        5.45e-06

Your 5.4e-06 comes out identical. Our percentages differ because your second window is "after the reward saturates" and mine is "after step 2000"; the definitions do not coincide, so I am not claiming you are wrong.

Your diagnosis of the anomaly is right, and it is fully explained. Same seed, same loop, only the advantage line differs:

  float32 path            18.62 modes   <- the sweep's number
  float64 then rounded    11.50 modes   <- the trajectory's number
  float64 no dtype        11.50 modes   <- identical to the previous one

And your point about determinism is the one that should have tipped me off months earlier: two deterministic roundings explain "both are reproducible", multithread nondeterminism never did.

Your second question: yes, and your arithmetic was right to the second decimal. Peak restricted to steps above 90 percent validity, since the raw maximum is 47.5 at step 0 for every run, the untrained network, which has nothing to do with early stopping:

  path      seed   peak    at step   final    gap
  float32    0     24.00     5750    18.62   +5.38
  float64    0     24.00     5750    11.50   +12.50

You predicted +5.4 from arithmetic alone. Two things you did not ask for. The peak is identical on both paths, same value at the same step, so only the endpoint moves. And the headline does not survive at all: I traced 20 seeds on the canonical path.

  mean gap        +1.03 modes
  median gap      +0.00
  runs above 1 mode   3 / 20
  max gap         +8.13

Seventeen runs of twenty gain nothing from stopping early. Your correction was too gentle: it is not +5.4 instead of +12.5, it is zero, and the +12.5 was one seed.

I then wrote up something conditional that I liked — on float32 all three runs that gain sit in the plural corner, 3 of 8 against 0 of 12 singular, which fits the ceiling story since that corner has twice the height to reach and lose. Then I ran the same twenty seeds on the canonical path and it fell over.

                        float32      float64 (canonical)
  median gap             +0.00           +0.03
  runs above one mode     3/20            5/20
    of which plural       3/8             2/8
    of which singular     0/12            3/12

Three of the five are singular on the path I had just declared canonical. The 0-of-12 that carried the whole interpretation was a one-path artifact. What survives on both, and only this: the median is zero and most runs gain nothing. Any reading finer than that did not outlive a change of rounding.

That is the fourth over-reading of my day, and this one is worth separating from the other three. It was not one seed — it was twenty seeds on one numeric path. The missing control was not more seeds, it was the same measurement on the other path.

Your bug is a better experiment than any of my seeds. Changing the seed changes the initialisation and the trajectory at once, a confound I have carried since the first sweep. Changing the advantage line changes only the second: the initial weights are bit-identical, and the two runs diverge at step 4 or 5, during training. Same starting point, different trajectory. So I ran 70 seeds on each path.

                          float32        float64
  singular / plural        37 / 33       37 / 33
  Wilson 95%          [0.413,0.641] [0.413,0.641]
  p against 1/2            0.7202        0.7202
  ceiling violations          0             0
  I(det;noun) max         0.0377        0.0158
  runs with I > 0.05        0/70          0/70

All 70 of 70 keep the same corner. Zero flips, although the trajectories disagree on 58 to 79 percent of the first two thousand steps. But only 21 of 70 keep the same effective-mode count, correlation 0.68, mean absolute difference 2.87 modes and up to 12.7.

So: the initialisation decides the corner, the trajectory decides how much of it gets filled. Two levels, two causes, separated by a manipulation that touches only one of them, which no seed can do. And the three conclusions the repository rests on are robust to the last bit — they were not rounding artifacts. Whether that control is standard practice somewhere I have not read, I genuinely do not know, and I am not going to claim novelty from my own ignorance of the literature.

The ceiling is only a weak attractor, incidentally: of the 25 runs sitting exactly on it, 11 reproduce across paths (44 percent) against 22 percent for the others.

Canonical: float64. I expected a trade-off between accuracy and speed and there is none:

  float32 path : 19.46 us per call
  float64 path :  4.57 us per call   (77 percent faster)

The name misleads. Nothing is stored in double, the produced tensor is float32 either way. A Python float is a double, so r - baseline is native and free and only one tensor creation remains, while the other path builds a tensor, dispatches a torch kernel for the tensor-scalar subtraction, and detaches. More operations and one more rounding. In total it is 0.2 percent of a step, so this is not a performance argument, it is that performance does not oppose accuracy here. float32 was never a choice; it was a writing accident in one function, already in the minority six files to five.

entrainer now takes an explicit chemin_avantage, defaulting to float64. The five scripts that went through it have been rerun, 37.8 minutes with bounded parallelism; the six with no sampled training at all are untouched, and those are the ones carrying the product ceiling, the Gibbs optimum, the order-1 marginals and the capacity probe, none of which has an advantage line to change.

What the switch actually moved, archived against rerun, same seed 0 as before:

  beta    valid% f32   valid% f64   modes f32   modes f64
  0.01         99.84        99.99         9.9        18.0
  0.02         99.99        99.94        18.6        11.5
  0.05         92.65        99.76        23.8        19.9
  0.08         94.87        84.11        24.4        26.5
  0.12         57.13        55.31        45.9        45.4
  0.35          5.27         5.27        43.5        43.5

  long grammar, graded reward :   6.4 %  ->  15.8 %

The long-grammar number is quoted in the published article and it is now 2.5 times larger. None of this is a surprise, and that is the point: this is a single-seed table, and I had already written in section 4.2 that a single-seed sweep cannot draw a frontier, then used it anyway. The 70-seed conclusions and everything obtained by enumeration are unmoved.

So the practical consequence for the next release is not to refresh those tables with new numbers. It is to replace single-seed tables with multi-seed means and a spread, otherwise the same fragility gets republished with different decimals.

Housekeeping, done. torch.set_num_threads is now in rl_grammaire.py, which fourteen scripts import, with RDTRL_THREADS to override for the large-batch exact-gradient work. It no longer depends on the shell.

And the answer I owed you. Sweep seed 0 emits les 0.544 and des 0.455. The trajectory run emits des 0.912 and les 0.087. Both plural, so it was never a corner disagreement, and "below 12 therefore singular" does not hold: an unbalanced plural product drops under 12 without leaving its corner. You reached that yourself before I sent it, and your reason is the right one, effective modes is 2^H of the joint restricted to the valid set rather than a count of support. You corrected it faster than I delivered it.

Four of my published numbers came apart today: the 2-to-1 branch bias, the all-plural sublanguage, the early-stopping gap, and the corner-conditional version of it I wrote to replace the gap. The first three were one seed. The fourth was twenty seeds and one numeric path, which is the harder lesson, because it looked like the fix rather than the same mistake in better clothes.

All four survived for the same reason, worth saying plainly: I had no reason to rerun a result that did not bother me. The rule is not "replicate", which I already knew. It is replicate what is convenient first, and check the control you just built against the claim you just made with it.

Last thing, and it is yours. I finally ran the reversal test, the one experiment that decides whether the product bound is a law or an accident of my French lexicon.

My first version of it was empty and I nearly ran it. I built a lexicon moving genre-neutrality from the plural determiners to the singular ones: same twenty tokens, same 8,000 space, same 48 valid sentences, same two corners of 24, and it swapped the ceilings and both order-1 marginals cleanly. Too cleanly. The nouns and verbs are already symmetric in number, two per genre and number and three verbs each, so swapping the determiners' number is the sg-pl relabelling and nothing else. Verified on the feature multisets. Seventy seeds would have returned the mirror image by construction and proved only that my code does not branch on the strings "sg" and "pl".

The principle I was missing: a relabelling can permute, but it cannot change a ratio. A perfectly symmetric control is often a perfectly empty one.

So the real test uses three genders. Both corners hold 36 valid sentences, but the singular determiners are genre-neutral so that corner is one product of 2 x 6 x 3 = 36, while the plural ones are marked across three genders so the genre must be fixed: 2 x 2 x 3 = 12. Ratio 3 instead of 2, which no relabelling of a two-gender grammar can produce, since the largest product is an isomorphism invariant.

Ceilings computed by enumeration and committed before the run. Seventy seeds, beta = 0.02, float64:

  corner      n   predicted ceiling   max observed   violations   exactly on it
  singular   33          36               36.0            0             2
  plural     37          12               12.0            0             7

And the quantitative form is stronger than the violation count:

  grammar              ceiling ratio    observed mean ratio
  standard, 2 genders       2.0                1.82
  three genders             3.0                3.01

The mean tracks the ratio, not just the ordering. The branch is still a coin at 33/37, p = 0.72, despite both order-1 marginals having flipped, and I(det ; noun) has median 0.0000 with zero of seventy above 0.05 bits.

One sub-prediction of mine was too strong: "effective modes land on integer products" measures 66 percent in the standard grammar and 67 percent here. A stable fraction, so a real fact, but not a rule. The ceiling is a law; the quantisation is not.

Your bound survives a change of grammar, in value and not only in order. That was the one item my own publishability assessment listed as blocking, and it is cleared.

Notebook entries 7.11quinquies through 7.13, and section 1 now dates eight refuted hypotheses.

Short one for now, the substance will follow.

I have archived the repository on Zenodo, and you are credited in it.

Concept DOI: 10.5281/zenodo.21726216 — resolves to the latest version. The release that first records the acknowledgment is v0.3.1, 10.5281/zenodo.21726387.

The acknowledgment is in four places, deliberately: the README, the abstract in CITATION.cff, the changelog, and as a structured contributors entry with your ORCID in .zenodo.json, since CFF 1.2.0 has no field for it. It names what you actually contributed rather than thanking you vaguely: the product bound, the fact that the two degenerate corners hold the same number of valid sentences but not the same largest product, and the three corrections your criticism forced, namely the unweighted mean that read as an agreement rate, the saturation metric that could exceed 100 percent, and the sample-size claim that pooled three seeds into twenty-four rows.

I took your point about credit and left it as an acknowledgment rather than anything else, to be raised again when there is a draft. Agreed that the thread goes in it.

Your last message deserves a real answer rather than a quick one, so I will come back to it properly. One thing I can say immediately, because the field you asked about is now saved and the check cost one command: you are right that it is not a metric bug, and wrong about why. Sweep seed 0 emits les and des. So does the trajectory run. Both are plural, so it is not a corner disagreement, and "below 12 therefore singular" does not hold — an unbalanced plural product drops under 12 without leaving its corner. Numbers with the rest.

You are right on all four points. I checked them on the real policies rather than on reconstructed joints, then went further, and going further refuted a hypothesis of mine and produced a mechanism. Everything below is in the repo.

The coverage artifact, confirmed. moyenne_cond_det is an unweighted mean over six determiners and a softmax never reaches zero, so the dead rows clear the total > 0 guard and enter with full weight. On the eight runs where I have the complete analysis, the value is (determiners emitted)/6 to four decimals: 0.3333 for two live determiners, 0.6667 for four. And exactly as you say, a 12-mode singular collapse and a 24-mode plural collapse both read 0.3333, which is precisely the distinction the number was carrying in my sentence.

But mass-weighting does not fix it, it destroys it. I rebuilt your four structures and ran all three statistics:

  structure                          modes   unweighted   mass-weighted   I(det;noun)
  singular collapse, genre-locked     12.0      0.433        1.0000          0.0000
  plural collapse, les/des            24.0      0.400        1.0000          0.0000
  singular 24, genre acquired         24.0      0.733        1.0000          1.0000
  all six determiners, coupled        48.0      1.000        1.0000          1.5000

The weighted version reads 1.0000 for all four. Perfect agreement is reached by restriction as well as by conditioning, and a genre-locked product agrees perfectly with no coupling whatsoever. What answers the question is the mutual information I(det ; noun), which is a dependence rather than an agreement rate and is exactly 0 for any product regardless of validity. It is now in analyse_exacte alongside cond_det_pondere and determinants_emis.

Rerun on 70 seeds with the right statistic. The conclusion survives, for the right reason this time.

  I(det;noun) median                 0.0000 bits
  I(det;noun) max over 70            0.0377 bits
  runs above 0.05 bits               0 / 70
  mass-weighted conditional          0.9941 +/- 0.0393   (useless, as predicted)
  determiners emitted                1 for 13 runs, 2 for 57

The singular union needs 1.0 bit and the full policy 1.5. The best any of 70 runs manages is 0.038. The claim was true; I had asserted it from a statistic that could not say it, and your proposed replacement could not have said it either.

Your other two points hold. The plural corner has zero gap by construction, so my "zero violations in 70 runs" is really zero in the 37 singular ones, and my grammar is asymmetric as an instrument: only one corner can falsify the bound. That is now a design constraint on the reversal test rather than a footnote. And your 36 is exact, measured at 36.0 modes with I = 0.918 bits, so the annealing result clears a higher bar than the 24 I gave it.

On the dropped mass column, you found a pattern rather than an incident, so I audited it. There are eight unweighted means over a token dimension in the repo. Six are sound and two are wrong, and the dividing line is sharp:

  averaged over                                          verdict
  observational conditionals (moyenne_cond_det/_nom)     wrong
  interventional conditionals (determiner forced)        correct
  order-1 marginals under the uniform policy             correct by construction

Observational against interventional. Where I force the token, every row exists and equal weights are right. Where I observe it, the dead rows are softmax artifacts. Both versions live in the same file and I put the wrong one in the results table.

Then two things came out of pushing on your bound.

A hypothesis of mine, refuted. Seeing 19 of 37 singular runs at exactly 12.0, I proposed that a ceiling attained that precisely is not a constraint suffered but an optimum, so REINFORCE would be solving the coupling-free problem exactly and failing only to leave the class. I optimised the same E[R] + beta*H by exact gradient over three independent laws p(d), p(n), p(v), so I(det;noun) is zero by construction. The optimum of that class is 24.00 modes at every beta from 0.01 to 0.08, three seeds of three, in the plural corner, because that is the global largest product. REINFORCE lands on 12 half the time, so it is at a local optimum of the restricted class.

Three nested failures, not one: find the best product of the corner it is in (19/37 singular, 6/33 plural), find the best product at all (37 of 70 miss it), leave the product class (0 of 70). The larger corner is the worse filled, which is the opposite of what more room would suggest. And it settles your point by direct optimisation rather than by argument: the singular corner costs exactly log2(24/12) = 1 bit at strictly equal reward, so those runs stopped short of the optimum twice over.

The ceiling is a plateau, not a basin. I tracked I(det;noun) step by step with an exact probe. Exact gradient, beta = 0.02, seed 0:

  step     0 : I = 0.0045 |  47.54 modes | valid   0.60 %
  step   100 : I = 0.0000 |  12.00 modes | valid  99.99 %
  step  1000 : I = 0.0000 |  12.00 modes | valid  99.97 %
  step  1250 : I = 0.8518 |  17.87 modes | valid  99.92 %
  step  1500 : I = 0.9980 |  24.00 modes | valid  99.98 %

Exactly 12.00 modes with I identically zero for a thousand steps, then it leaves. Escape times are wildly variable: step 1250, step 2875, and never within 4000 on the third seed. Nothing predicts it at initialisation either: I starts at 0.0045 bits in every seed and the six determiner masses all sit between 0.042 and 0.057 with no structure separating the seed that couples from the one that does not.

And here is what actually separates the two procedures. Every trajectory starts at 47.5 effective modes, the untrained network, and training destroys diversity. But look at the minimum along the way:

  procedure     minimum modes reached      at step
  exact         10.74 / 11.06 / 11.24        25
  sampled        1.09 /  1.88 /  1.18       400 to 800

Sampled REINFORCE crushes the policy to a single sentence before rebuilding. The exact gradient never drops below 10.7.

The hypothesis this suggests, and I am labelling it as a hypothesis: rebuilding from a near-deterministic point happens position by position, because that is what a per-position entropy bonus can do, and a position-by-position rebuild yields a product by construction. Coupling would require opening a joint direction, which that term never opens. The exact gradient, which never passes through the point, keeps enough joint structure to find the coupled direction later. It predicts something checkable: the depth of the transient collapse should predict whether coupling is ever acquired.

It also gives annealing a mechanism it did not have. I had explained the 45.3-mode annealed run with a story about keeping every conditional trained while the shared representation forms. The simpler reading is that high beta early prevents the crush to a point, so the policy never has to rebuild from a product.

One anomaly I am flagging against myself rather than burying. Sampled seed 0 gives 11.50 modes in the trajectory script and 18.6 in the sweep, at nominally identical settings, and both are reproducible. I had previously blamed torch multithread nondeterminism; both scripts are single-threaded now, so that explanation is dead. There is a code-path difference I have not found, and until I find it one of those two numbers comes from a path I have not audited.

Your last question: only the rows. balayage_70_graines did not save state dicts. It does now, along with the per-determiner mass, the detailed conditional, the mutual information and the emitted-determiner count, so mass-weighted questions can be answered without retraining. The 70 policies are on disk.

New code: optimum_produit.py for the restricted-class optimum, trajectoire_couplage.py for the step-by-step coupling. Notebook entries 7.11bis, 7.11ter and 7.11quater, and the dead hypotheses are dated in section 1, where 1.8 is the one you just cost me.

One last thing. The product bound is yours, and it is now doing most of the load-bearing work in this line of results. If any of it gets written up properly I would rather sort out credit before a draft exists than after.

Measured. You are right on the ceiling, right on the statistics, and I was wrong on the branch. Details below, all of it reproducible from the repo.

Your product argument, verified exhaustively. I enumerated every subset of nouns and took the largest fully valid product in each corner:

                  valid   largest product                       ceiling
  short, plural     24     24  = {des,les} x 4 nouns x 3 verbs   4.585 bits
  short, singular   24     12  = {le,un} x 2 nouns x 3 verbs     3.585 bits
  long,  plural    144     72                                    6.170 bits
  long,  singular  144     72                                    6.170 bits

Exactly one bit apart on the short grammar, exactly zero on the long one. Your reading of my long-grammar result is the right one: with the adjective forcing genre on both sides there is nothing structural left, so 4 of 5 is a coin.

Your question: saturation_pct for le and la on the 12-mode runs. Six runs at 12 modes, four exact-gradient and two sampled, plus two 24-mode controls in the same singular corner.

  run                        modes   determiners carrying mass   mass         saturation
  exact  beta=0.01 seed 0     12.0   le, un                      0.500/0.500  100.0/100.0
  exact  beta=0.01 seed 1     12.0   le, un                      0.500/0.500  100.0/100.0
  exact  beta=0.01 seed 2     12.0   la, une                     0.500/0.500  100.0/100.0
  exact  beta=0.02 seed 1     12.0   le, un                      0.499/0.501  100.0/100.0
  sampled beta=0.02 seed 1    11.7   le, un                      0.448/0.551   95.9/ 99.9
  sampled beta=0.02 seed 2    12.0   la, une                     0.500/0.500  100.0/100.0
  CONTROL exact beta=0.02 s0  24.0   le, la, un, une             0.25 x 4     100.0 x 4
  CONTROL exact beta=0.02 s2  24.0   le, la, un, une             0.25 x 4     100.0 x 4

So the direct answer: le reads 100.0 and la carries zero mass, or the exact mirror, depending on the seed. Four runs masculine, two feminine. Six of six are the genre-locked product you described. The gender is a second lottery sitting on top of the branch lottery.

One correction to the question itself. Saturation is 100 percent in both structures. The 24-mode control also reads 100.0 on all four of its determiners, because each one uses both of its compatible nouns. What discriminates is not the saturation but the mass profile: two determiners at 0.5 against four at 0.25. A product and a union of two products saturate equally well; the difference is how many branches are open. Saturation alone would have given you the same number for both and settled nothing.

And a warning about the field you found. You are reading saturation_pct from a version where it was wrong. H was computed over all 8 nouns while H_max used the count of compatible ones, so it could exceed 100 percent, and a value above 100 meant mass leaking onto incompatible nouns, which is a failure, not saturation. I had that written in my own notebook two days ago and left it. It is now split into two fields: masse_accordee_pct for whether the policy stays valid, saturation_pct computed on the conditional restricted to compatible nouns and renormalised, bounded by 100 by construction. It pays immediately: in one run la reads 86.7 percent on a mass of 0.00000, an untrained conditional read off nothing. The mass column kills it at a glance.

Your statistical objection. You were right and the corrected experiment refutes me. 70 seeds, one condition, beta = 0.02, 20000 episodes:

  singular / plural            37 / 33
  proportion singular          0.5286
  Wilson 95%                   [0.413, 0.641]     contains 1/2
  binomial against 1/2         p = 0.72
  binomial against 2/3         p = 0.016

The branch is indistinguishable from a fair coin, and my "about 2 to 1 toward singular" is rejected. Worse than you said, in fact: in the collapse regime the branch was set by the seed, and beta only copied it, so seed 0 was plural at every beta and seeds 1 and 2 singular at every beta. My 24 rows were 3 draws. And 11 of those 24 were not collapses at all, since at beta >= 0.08 both families are alive and a 50.1/49.9 split had been labelled "singular" by argmax. The order-1 edge at the noun is real and closed form, but it does not survive the sampled dynamics.

Your ceiling, on the other hand, survives everything.

  branch     n   ceiling   max observed   exceeded   exactly at ceiling   mean
  singular  37     12         12.0            0             19           9.41
  plural    33     24         24.0            0              6          15.12

Zero violations in 70 runs, and the modal outcome is the ceiling itself. The effective modes are integer products, {2,4,6,8,12} singular and {6,8,12,16,18,24} plural, so |A_det| x |A_noun| x |A_verb| is visible directly in the histogram. P(noun agrees | det) stays at 0.333 +/- 0.003 across all 37 singular runs: not one of the 70 acquires the conditional.

Which gives the result neither of us had. The exact gradient at beta = 0.02 reaches 24.0 modes inside the singular corner, seeds 0 and 2, so it does cross the uncoupled ceiling of 12 and it does acquire the conditional. Sampled REINFORCE never crosses it, 0 of 70. So the ceiling is not a property of the task, nor of the architecture, nor of the corner: it is a property of the sampled procedure at constant beta, and it has a closed form.

I want to be exact about the scope, because there is one case that crosses it. Annealing beta from 0.2 to 0.01 reaches 45.3 effective modes at 99.97 percent validity, with both families alive. The largest product over the whole valid set, ignoring corners, is 24, so 45.3 is above the global product ceiling and that policy has genuinely acquired the conditional while being sampled. The ceiling therefore binds for constant beta in the collapse regime, not for sampling as such.

That makes the bound more useful rather than less, because it explains the one fix that works. I had reported the annealing result with a qualitative story about keeping every conditional trained while the shared representation forms. The product bound replaces that story with a number: constant low beta drops the policy into one corner and caps it at that corner's largest product, and the schedule's job is to delay the commitment until the coupling exists. That is a mechanism you can compute in advance instead of a schedule you tune.

Your synthesis and mine are compatible and I think this is the correct joint statement: the order-1 marginal at the noun decides which corner the dynamics enter, your largest-product bound decides how far it can get once inside, and sampling is what prevents it from ever leaving. Three different mechanisms, three different measurements, none of which requires looking at a learning curve.

New code, all of it reproducible: sonde_ordre1.py for the marginals at every position, produit_et_saturation.py for the ceilings and the saturation tables, balayage_70_graines.py for the 70-seed branch statistic. The notebook entry recording all of this, including my three errors, is CARNET sections 7.10, 7.11 and 3.3.