A model can score highly against the brain—or transfer beautifully across languages—while the score mostly reflects something other than the structure researchers hoped to measure. This paper tests exactly how much correspondence survives when that structure is removed.

Representational similarity has become a common currency for relating models to one another and to the brain. Language models are scored by how well their activations predict neural recordings; cross-lingual models are probed for shared subspaces; interpretability work reads structure off learned directions.

The tempting inference is that measured correspondence—to the brain, across languages, or to a reference geometry—is evidence of a functionally meaningful and usable property. That inference becomes a research program: if the correspondence is real, it might become a training signal that improves the model or a causal handle that steers behavior.

The step rarely taken is to treat a correspondence score as a measurement that might register something other than the intended quantity. Three failure modes matter: a score can be insensitive, returning nearly the same value whether or not the reference structure is present.

The instrument can also vary in reliability along the axis being studied, so a gradient partly tracks measurement quality instead of the phenomenon. Finally, the units can be miscounted when a design generates many observations from few independent entities; none of these problems is visible from the score alone, but each admits a direct test.

The tests are applied in two settings, followed by a utility question about whatever survives them. The settings are deliberately different: one compares a shared direction across languages, and the other aligns a model to the brain. The dominant failure differs between them: the typological gradient is compromised mainly by its instrument, while the alignment score is compromised mainly by insensitivity.

Both studies follow one template. A model carries an internal structure S, such as a layer’s representational geometry or a linear direction, and that structure is brought into correspondence with a reference R. The reference can be fMRI response geometry or another language’s grammaticality contrast, and C of S and R is the score reporting that correspondence.

The audit has three parts, in an order that makes each next step interpretable. First, a content ablation rebuilds the reference so it keeps incidental properties but loses the correspondence itself, using shuffled rows, same-dimension noise, and a same-sized random direction.

Re-measuring the score against those controls estimates the share attributable to content rather than form, rank, or scale. Second, an instrument check asks whether the score has comparable reliability everywhere; a failed probe cannot support transfer, and reliability that co-varies with the predictor mixes signal with measurement quality.

Third, an inference check counts units correctly: pairwise designs generate many observations from few entities, so significance must be assessed by permuting entities, not pairs. Only after the audit comes the functional question: does exploiting surviving correspondence change downstream behavior beyond matched controls?

Running the audit first keeps a null interpretable, because a null is uninformative if the intervention never installed the content. A positive result is also uninformative if the score never measured the intended content. Table 1 summarizes each check and what it found in both studies.

Read across each row to compare the two studies: the content-ablation row uses different matched controls, while the instrument-check row reports either probe reliability or a noise ceiling. The inference-check row likewise shows that the authors test the statistical structure separately in each study, rather than treating the two audits as interchangeable.

In XGLM-1.7B, chosen because it covers all seventeen languages, a logistic-regression classifier is trained to distinguish grammatical from ungrammatical subject-verb agreement. The probe reads the residual stream at the middle decoder layer, at the verb carrying agreement, and uses sixty percent of each language’s pairs for training and the rest for testing.

The data are minimal pairs from MultiBLiMP for seventeen languages that mark agreement on the verb. For every ordered language pair, transfer measures how accurate language A’s probe is on language B, while steering adds A’s direction as B is read and asks whether B’s grammatical preference strengthens.

That preference is the margin between the total log-probability of the grammatical sentence and its ungrammatical twin, measured in nats; a zero margin means indifference. Transfer accuracy decreases with typological distance, with a correlation of minus zero point six six and an explained variance of zero point four three.

That relationship reproduces the pattern motivating URIEL-based transfer prediction. The probe’s own accuracy also falls, and transfer accuracy is interpretable only where the probe being transferred from works. In four of seventeen languages—Hindi, Urdu, Turkish, and Arabic—the probe does no better than guessing in its own language, against a chance level of zero point five.

These failures are not scattered randomly: a language’s probe gets worse as it differs more from the rest of the sample, with a correlation of minus zero point seven four. Probe reliability therefore co-varies with the predictor, so the gradient mixes signal with measurement quality.

Restricting the analysis to thirteen languages whose probes clear chance halves the explained variance, from the full relationship to a correlation of minus zero point four seven and an explained variance of zero point two two. In panel b, the black line uses all seventeen languages, while the blue line uses only pairs whose probes clear chance; the two lines separate most noticeably toward the higher-distance, lower-accuracy region.

The legend identifies these fits as minus zero point six six and minus zero point four seven, respectively. Steering shows no trend with distance: raw steering benefit has a correlation of plus zero point zero eight and a p-value of zero point five eight six.

A random-direction baseline points the same way, suggesting typologically unusual languages may be more perturbable by any intervention, though the language-level result is only a trend. After removing that nuisance with a per-target random baseline, an apparent source-specific advantage does not survive the language-level null, with a p-value of zero point one five five.

Partialling out probe-transfer accuracy leaves nothing, and restricting to thirteen languages produces a corrected correlation of minus zero point zero nine with a p-value of zero point seven zero four. No stage produces a distance-graded steering effect once the seventeen languages, rather than the 272 pairs, are treated as the units.

For brain alignment, Pythia models at 160 million, 410 million, and 1.4 billion parameters are fine-tuned on 627 sentences from the fMRI benchmark. A second objective pulls the model’s internal geometry toward the fMRI responses.

The similarity measure is linear centered kernel alignment, or CKA, which compares how two representation sets arrange the same sentences and returns one for identical arrangements. Each training batch holds sixteen sentences, and the model representation has one row per sentence.

Targets permuted across sentences and rank-matched Gaussian noise both reach CKA of zero point three one, recovering between eighty-three and ninety-two percent of the brain-aligned score. The brain-attributable increment is the difference over those controls: zero point zero two eight, zero point zero six eight, and zero point zero six four at the three model scales, or five to thirteen percent of the ceiling.

That increment is reliably nonzero, so brain-specific structure was installed, but it is small enough that the score is dominated by something else. A shuffled target scores CKA of zero point two zero four against the real target, while a noise target scores zero point one eight six, meaning the measure returns a large number when there is no correspondence at all.

Across target ranks, the measured values match rank divided by the number of sentences to within one percent, so the authors recommend reporting that baseline and scoring a shuffled target before training. Across all three model groups, the red shuffled and orange random bars sit nearly level, with closely overlapping confidence intervals.

The dashed reliability ceiling remains visibly above every bar, while the blue brain-aligned bar is separated from the two matched controls by a modest vertical gap. Brain alignment does not improve BLiMP: at 160 million parameters it reaches seventy-four point five percent versus seventy-four point one percent for language-model-only training, a difference that is not significant.

It is also not significantly above the shuffled or random controls, and the same pattern repeats at 410 million and 1.4 billion parameters. The equivalence test bounds the true 160-million-parameter effect between minus zero point four and plus one point four BLiMP points.

The null is not explained by excessive noise, a mistuned alignment weight, models being too small, or inert training: fine-tuning moves BLiMP by three to six points, while the aligned condition buys no detectable gain. For this operationalization, the objective did what such an objective does and bought no detectable gain; brain-specific utility is bounded more loosely because only five to thirteen percent of the ceiling was brain-specific.

The clearest added evidence is in the CKA columns: brain alignment raises CKA from 0.10 to 0.34 at 160M, from 0.25 to 0.41 at 410M, and from 0.27 to 0.42 at 1.4B. The delta column records corresponding brain-specific increments of plus 0.028, plus 0.068, and plus 0.064, while shuffled and random controls remain nearly identical.

The two correspondence measures were tested after removing the correspondence they were meant to detect or making it unreliable, and in neither case did score magnitude mean what it suggested. A permuted or noise target reproduced eighty-three to ninety-two percent of a brain-alignment score, leaving only five to thirteen percent of the reliability ceiling as brain-specific.

Across languages, four of seventeen probes sat at or below chance, and probe reliability declined along the same axis as the predictor. Counting seventeen languages rather than 272 pairs removed the significance of the causal leg entirely, while the design could not recover the gradient’s magnitude.

No downstream or distance-graded causal benefit was detected from what survived, although these are failures to detect effects of the size the designs resolve, not proofs of absence. The checks were cheap and decisive about what each score meant, so a correspondence score reported without them is a number whose units are unknown.

The big lesson is simple: before interpreting a correspondence score, destroy the correspondence and test the instrument. Here, most brain-alignment score survived broken targets, while the cross-lingual gradient was entangled with unreliable probes and vanished as a causal claim.