Measuring Which Side of the Superset Trap Neural Language Learners Fall On

Children hear only grammatical sentences, yet they end up rejecting sentences they have never heard and accepting rare sentences they have also never heard. Formal learning theory names the difficulty precisely. When the possible languages form a nested chain, each one containing the last, a learner that sees only positive examples faces a dilemma. If it guesses too big a language, no example will ever show it the mistake. If it guesses too small, it must keep revising forever. The union at the top of such a chain is called a limit point. Neural-network studies of the "poverty of the stimulus" (the claim that children's input is too thin to determine their grammar) are testing whether models escape this dilemma, but their standard instrument cannot tell which way a model fails. That instrument is forced-choice minimal pairs: does the model prefer the grammatical sentence over a near-identical ungrammatical one? A model can pass while still putting substantial probability on ungrammatical continuations, which is overgeneralization. It can also pass while putting almost no probability on rare grammatical ones, which is undergeneration.

We propose to measure both failure modes directly. We will embed explicit limit-point chains, built from artificial constructions whose true grammar we control, into developmentally sized English corpora. We then track how much probability a trained model assigns to the "next step up" the chain, the strings in $L_{k+1}$ but not in $L_k$, as exposure grows. The central hypothesis is that neural language models treat absence as evidence of ungrammaticality only when a construction's surrounding frame is frequent enough that absence is surprising. This is the "strong sampling" logic humans use. Where that expected count is low, models behave as if absence carries no information. If true, one quantity, the expected count of an unobserved extension, would explain a pattern that currently looks contradictory. Filtered-corpus training on familiar words succeeds; wug-word induction from syntactically indirect evidence fails; island constraints look learned; parasitic gaps do not.

Core Claim

A minimal-pair score mixes two numbers: how much probability the model leaks into strings just outside the target language, and how much it withholds from rare strings inside it. We call these gap mass and withheld mass. Both can be read off directly when the chain is known. The claim to be tested is that gap mass decays with training exposure at a rate set by the expected frequency of the unobserved extension, as a size-principle learner would predict, rather than by the raw amount of data. Withheld mass behaves the same way in reverse.

We define the gap-mass ratio at training size $N$ as

$$R_k(N) = \frac{\bar p_N(L_{k+1}\setminus L_k)}{\bar p_N(L_k)},$$

where $\bar p_N(S)$ is the model's mean length-normalized probability over held-out strings in set $S$, and the two sets are matched for length and vocabulary. A learner trapped in the superset keeps $R_k$ near a constant. An ideal Bayesian learner that assumes its data are drawn from the true language drives $R_k$ toward zero. For that learner, the posterior odds against the larger language grow by a factor of roughly $|L_k|/|L_{k+1}|$ per relevant observation, so the log of $R_k$ should fall linearly in the number of sentences that could have exhibited the extension but did not. This is the size principle. We compare neural learning curves against this reference rather than against chance.

Relation to Prior Work

The formal side supplies the objects we build. Béchet et al. k-Valued Non-Associative Lambek Categorial Grammars are not Learnable from Strings and Foret et al. Rigid Lambek Grammars Are Not Learnable from Strings construct explicit nested grammar chains to prove unlearnability. Heinz's String Extension Learning shows that local "chunk"-based classes avoid limit points altogether. We reuse the construction style of the first two as a stimulus-design tool and treat Heinz's result as a control: chains built from local n-gram features should be easy, and chains built from non-local structure should be hard. Kleinberg and Mullainathan's Language Generation in the Limit prove that generation, unlike identification, is always possible by retreating to a safe sub-language. They note that this trades validity against breadth, with hallucination on one side and mode collapse on the other. Our gap and withheld masses are empirical measurements of exactly those two quantities, which that paper leaves unmeasured for trained networks. Peng et al. Language Identification in the Limit with Computational Trace dissolve the impossibility by giving the learner execution traces. We deliberately withhold such signals, because children do not receive them.

Several papers motivate the gap in the empirical literature, and they disagree. Filtered Corpus Training (FiCT) removes 15 phenomena from an 83M-token corpus and reports only about a 5% average accuracy drop. By contrast, Can Language Models Induce Grammatical Knowledge from Indirect Evidence? finds near-chance performance for novel words under syntactically indirect evidence, with performance falling as more such evidence is added on the transitive task. Language Models Learn Rare Phenomena from Less Rare Phenomena shows that related frequent constructions carry the generalization. Large Language Models and the Argument from the Poverty of the Stimulus shows parasitic gaps resisting even web-scale training. A Unified Assessment of the Poverty of the Stimulus Argument reports above-chance filtered performance on islands but explicitly does not determine whether models converge to the right language or to an overgeneral one that happens to win forced choices. That open question is precisely what our measurement answers.

Two papers constrain the design. Sampling Assumptions Affect Use of Indirect Negative Evidence shows humans use absence as evidence only under strong-sampling framings. Next-token training is formally a strong-sampling objective, so any weak-sampling behavior in a network must come from how it generalizes, not from its loss. That is a testable distinction. Zuidema's How the Poverty of the Stimulus Solves the Poverty of the Stimulus and Berwick's Computational Analogues of Constraints on Grammars escape the trap by reshaping the language over generations or by restricting the hypothesis space. We do neither. We ask what an unrestricted learner does on a fixed language.

Research Program

First, we build a stimulus library of limit-point chains in which each language adds one structural option to the previous one. Three families span the locality spectrum. The first is a local family, in which $L_k$ permits a novel modifier sequence up to length $k$; it is expressible with n-gram-style chunks and serves as the easy control. The second is a hierarchical family, in which $L_k$ permits extraction of a wug-marked filler out of clauses nested up to depth $k$; this is the island-like case. The third is a coordination family, in which a second gap is licensed only in the presence of a first gap; this is the parasitic-gap-like case. The extensions are designed so that the top of each chain is itself in the class, which gives a true limit point. Vocabulary uses both real English words and wug tokens. This separation lets us test the FiCT-versus-WIDET contrast directly.

Second, we inject sentences sampled from a chosen $L_k$ into BabyLM Strict-Small (10M words) and Strict (100M words) from the BabyLM findings. We cross three factors: the injected count (from tens to thousands of sentences), the depth $k$, and the "frame frequency," meaning how many sentences reach depth exactly $k$ and so make the missing $k+1$ conspicuous. For the undergeneration side, we sample from the top language $L_\infty$ with a naturally skewed depth distribution. We then measure withheld mass on deep strings never shown.

Third, we train GPT-2-small-class and 97M OPT-class models, matching the models in the AANN and POSH-BENCH studies. We save checkpoints so that $R_k(N)$ and withheld mass are learning curves rather than single endpoints; the Pythia tooling can be reused for checkpoint handling. We fit each curve's decay slope against injected count and against frame frequency, and compare the slopes to the size-principle reference.

Fourth, we carry the decomposition back to natural English. For island items and parasitic-gap and across-the-board items, gap mass is estimated as the surprisal of the island-violating gap relative to two references: an extraction that is licit, and the same string with no gap. This extends the bijectivity flip test of Mind the Gap to a continuous measure. Withheld mass is estimated as the surprisal of a licit parasitic gap relative to its licit single-gap counterpart. The question is whether the synthetic families predict which natural phenomena fail and in which direction.

Baselines

The naive reference point is standard minimal-pair accuracy on the same models and items, as reported on BLiMP and POSH-BENCH. It is computed from identical checkpoints at no additional cost. Our decomposition beats it if it separates models or conditions that minimal-pair accuracy scores as tied. A concrete test is a pair of conditions with equal forced-choice accuracy but an order-of-magnitude difference in $R_k$, together with a demonstration that the difference predicts which condition later degrades once more distractor data is added.

The theoretical reference is a Bayesian learner that knows the chain and applies the size principle. It is computed exactly on the same injected samples. It is not a competitor to beat. It defines "ideal" gap-mass decay, and we report each network's slope as a fraction of it.

The surface baseline is a 5-gram model trained on the same corpora. Following Heinz, it should track the ideal learner on the local family and fail on the hierarchical families. If it matches the networks on the hierarchical families too, then network behavior there is only chunk statistics.

The strongest empirical competitors are the published filtered and enriched models, retrained under our exact corpora and token budgets with matched hyperparameter search. The first is the filtered child-directed GPT-2 condition from the unified assessment. It reports 72% on Islands and 80% on Wanna-contraction in the filtered 10M-word condition (POSH-BENCH accuracy, A Unified Assessment). The second is the Lan and Chemla enrichment condition, which reports across-the-board difference-in-differences accuracy rising from 56.7% to 97.2% after 200 injected examples in 90M words of Wikipedia. The third is the AANN counterfactual, at about 47% accuracy against a 20% chance baseline. We do not aim to raise these accuracies. We aim to show that each of them hides a measurable split between overgeneration and undergeneration, and that the frame-frequency variable predicts the split.

The ablation that isolates our key ingredient holds injected count fixed and varies only frame frequency. If gap-mass decay depends on raw count alone, the strong-sampling explanation is wrong.

Why not just…?

Why not just keep using minimal pairs with a better score, such as length-normalized or threshold acceptability? Any score computed on real English lacks ground truth for which strings are in the target language, so leakage cannot be separated from legitimate generalization. This is the unresolved point in the unified assessment. The synthetic chains supply that ground truth. The natural-English step is included only after the decomposition has been validated on chains where the answer is known. If thresholded minimal-pair scores turn out to predict $R_k$ nearly perfectly on the chains, we will say so, and the simpler score wins.

Why not just train on artificial languages alone, without the English corpus? The poverty-of-the-stimulus question is about learning amid rich, related data. The AANN results show that surrounding constructions change what is learned. We run pure-artificial training as a control arm. If its curves match the embedded condition, then the embedding does not matter and the simpler setup suffices.

Why not just enrich the data, as Lan and Chemla did, and count how many examples are needed? Enrichment measures the cost of reaching a forced-choice score. It does not reveal whether the unenriched model was overgenerating or undergenerating, and those two failures call for opposite remedies. Our design contains enrichment as one axis (injected count), so their result appears as a special case.

Why not just add a hierarchical inductive bias? The unified assessment reports that pretraining on Dyck languages (nested-bracket strings), tree-planted attention, and a recency bias improved general syntax but not POSH-BENCH. That result is evidence that the bottleneck is not structural capacity alone. If compute allows, we add the Dyck-pretraining arm. Our prediction is that it shifts withheld mass on the hierarchical families but leaves the frame-frequency dependence of gap mass unchanged.

Decisive Checks

Three results would confirm the proposal. First, on the local family, network gap mass should decay near the ideal slope. Second, on the hierarchical families, decay should be slow or flat for wug vocabulary but faster for real-word vocabulary at matched injected count, reproducing the FiCT-versus-WIDET split inside a single controlled design. Third, raising frame frequency at fixed injected count should steepen decay; this is the strong-sampling signature. On natural English, the prediction is that island items show elevated gap mass, meaning overgeneration hidden by above-chance accuracy, while parasitic-gap items show elevated withheld mass, meaning undergeneration.

The hypothesis is refuted under two conditions. If gap-mass decay is independent of frame frequency, the explanation fails. If withheld and gap mass fail to predict natural-phenomenon failures beyond what minimal-pair accuracy already predicts, the decomposition adds nothing. In that case the conclusion would be that forced-choice scores are adequate after all, which is itself a useful result.