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Under review as a conference paper at ICLR 2027

Large-scale factor analysis shows machine intelligence is only partially interpretable

Abstract

A common assumption in language model development is that cognitive abilities are organized around a general, domain-free intelligence factor, like fluid intelligence in humans. This assumption is rarely tested directly, and prior attempts have done so only at a much smaller scale. We take a latent variable approach to intelligence in language models, similar to how psychometricians study psychological constructs. Performance in every specific problem set is influenced by a domain-specific and a domain-agnostic latent factor. Using factor analysis as a dimension-reduction technique, we analyzed 13,251 published evaluation scores covering 1,618 language models across 456 different text-only benchmarks. Due to the super-sparse nature of the dataset, we triangulate our analysis across different data densifiers and imputation methods. A robust pattern across different modes of bias is that 1. A general intelligence factor accounts for 70.8% of variance in model performance at our most generous estimate, and far less than that in most of our solutions, 2. Content-similar benchmarks do not necessarily cluster together, and 3. The factor is not dominated by any common theme, and there is a lack of evidence that it is well-proxied by standard "intelligence" benchmarks. Our findings go against current endeavors of defining, identifying, and targeting general intelligence as a tangible construct in language model development. This leaves the strategy of targeting a single conceptual ability without support, since the first-order abilities it would have to reach are often partially idiosyncratic and not identifiable in practice.

Primary area:
interpretability and explainable AI
Keywords:
large language models, factor analysis, psychometrics, general intelligence, evaluation, benchmarks, construct validity

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_XgsZOpenReview ↗
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Paper summary

This paper analyzes the evaluation scores of a large number of models and argues that model capabilities cannot be summarized by a single "general intelligence," and popular assessments such as mathematics and reasoning may not necessarily represent overall intelligence.

Critical strengths

The research question is worth discussing. It examines a common assumption: whether improved math and reasoning scores truly translate to improved general abilities.

Critical weaknesses

This paper is extremely difficult to understand, and its experiments are unreliable, making its conclusions unconvincing. Firstly, the data is extremely sparse. Only about 1.8% of the original score matrix has available data, with many relationships relying on algorithmic estimation. Covering a large number of assessments does not equate to reliably estimating the relationships between them. There are data processing issues affecting the core results. The lack of a unified "higher is better" and "lower is better" metric orientation may make assessments measuring similar abilities appear far apart in the graph, weakening the argument that "similar tasks do not cluster." Finally, the conclusions exceed the scope of the evidence. The paper analyzes the correlation between scores without verifying ability transfer through training intervention; therefore, it is insufficient to conclude that a unified ability structure is unfeasible or that training around general abilities lacks promise.

Questions for authors

See weaknesses.

1 comment

We thank the reviewer for their feedback. We agree that the data is very sparse (only 1.8% of the matrix is observed). Below, we explain how we changed the imputation and fixed other issues.

Metric orientation

We have fixed the metric orientation: all 27 benchmarks where lower is better are now sign-flipped so that higher always means better, and all imputations and factor analyses in this revision use the corrected data. This changes ωh\omega_h by at most 0.02 in every solution. The fix mainly affects semantic labels that contain flipped benchmarks. For example, 3 of the 4 benchmarks labeled likelihood_probe are lower-is-better, where this label now clusters (p=0.001p = 0.001) but did not before the fix (p=0.41p = 0.41). Overall, the number of labels that cluster barely changes (13 to 14 of 39 for SoftImpute on the S table), and depending on the imputer 16–49% of labels cluster, so our conclusion is unchanged.

Imputation Trustworthiness

The key improvement is that imputation is now run sequentially, imputing a higher-density, smaller subset to prefill the next lower-density and bigger subset. For the 0.1 table, we first impute the 0.5 subset, use it to prefill the 0.4 subset, and continue down to 0.1.

Using this sequential imputation, we changed our evaluation strategy for real data. We score each run with a weighted R2R^2 (wR2wR^2): the held-out R2R^2 of each step, averaged with weights equal to the number of new columns that step adds. This method has precedent in sequential least-squares imputation [1] and denoising-autoencoder imputation [2]. Overall, our new pipeline improves the trustworthiness of our imputations, as shown in both simulated and real data performance below.

Simulated MNAR Data Performance

Please refer to our reply to reviewer rXDF, where we describe our simulation imputation and performance.

Real Data Performance

Below is how our imputation methods perform on our real data. As shown, we achieved considerably better evaluation than the non-sequential step in our original draft. This allows us to increase the R2R^2 gate to 0.4 (the table only shows results with wR2≥0.4wR^2 \geq 0.4).

datasetmethodvar%ωh\omega_hECVϕˉ\bar{\phi}wR2wR^2
S_all_standardmissForest88.2%0.7600.5010.2150.455
C_all_standardkNN77.4%0.7310.4510.2160.442
C_all_standardmissForest88.0%0.7130.520-0.0880.566
C_all_standardSoftImpute96.3%0.3670.1260.0380.586
R_all_aggressiveSoftImpute97.8%0.2870.3210.0280.441
S_all_standardSoftImpute92.7%0.0440.1140.0410.428

Overclaiming Issues

We agree that observational evidence does not constitute experimental evidence. Due to poor wording, we may not have communicated this clearly in the original draft. We have restricted Sections 5.1–5.3 to descriptive claims, and statements about the effects of targeted training are now framed as hypotheses. A more conclusive claim would require empirical training experiments. A direct test would train models on one domain and measure the change on other domains, as in human cognitive-training studies.

The closest experimental evidence we know of is Meng et al. (2026), cited in Section 5, who find that input-similarity measures identify the best transfer source for at most 2 of 8 target tasks, and that semantic content does not predict transfer well, suggesting that transfer does not follow semantic similarity. This finding aligns with our results, but a more thorough experiment would be needed to test this directly.

Paper Revision

Since replies are limited in length, we are revising the manuscript to include all of these changes and will upload it before the discussion period ends, so that reviewers can take these into account.

References

[1] X. Zhang, X. Song, H. Wang, and H. Zhang. Sequential local least squares imputation estimating missing value of microarray data. Computers in Biology and Medicine, 38(10):1112–1120, 2008.

[2] Q. Ma, W.-C. Lee, T.-Y. Fu, Y. Gu, and G. Yu. MIDIA: Exploring denoising autoencoders for missing data imputation. Data Mining and Knowledge Discovery, 34(6):1859–1897, 2020.

Reviewer_8Mu7OpenReview ↗
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3
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3
Informativeness
2
Presentation
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2
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Paper summary

This paper applies factor analysis, a classic psychometric technique, to a very large collection of published LLM evaluation results: over 13,000 scores covering 1,618 models and 456 text-only benchmarks. Because the data matrix is extremely sparse and missingness is not random, the authors triangulate across multiple data densification strategies and imputation methods, validating each imputation on held-out scores.

Critical strengths

The scale and diversity of the benchmark corpus is the paper's biggest asset. It spans medical, legal, cultural, low-resource language, safety, and humor benchmarks, far beyond the usual math and reasoning suite, which is exactly what a content-indifferent general factor demands. The handling of missing data is unusually honest: multiple densifiers, multiple imputers, held-out validation, sensitivity analyses, and frequency adjustment for the benchmark rankings. The proposed follow-up experiment, fine-tuning on one task family and measuring transfer to others, is concrete and falsifiable. The data provenance documentation in the appendices is thorough and reusable.

Critical weaknesses

The headline variance figure leans on the least trustworthy imputations. The highest general-factor estimates come from crude fillers like mean-fill and zero-fill, which are well known to artificially inflate shared variance. The imputations the paper's own validation ranks best give much lower estimates, around a quarter of variance. The abstract should lead with the defensible number rather than the most generous one. The sign-flip issue undercuts the clustering claim. The paper admits that lower-is-better metrics were never oriented, which distorts the loading-space distances behind the "same-domain benchmarks don't cluster" finding. Since this is one of three headline results, it must be fixed and re-run before the claim stands.

Questions for authors
  1. Do any high-quality imputations produce a strong general factor, or do all the high estimates come from crude fillers?

  2. What do the specific factors load on in your best solution? A table of top benchmarks per factor would show whether the structure is more interpretable than claimed.

  3. Did you test whether the general factor correlates with model size within families?

1 comment

We thank the reviewer for the feedback and the concrete questions. Some points overlap with the other reviews, so we refer to those replies where the details are already given.

Headline estimate

We agree that the abstract should not lead with the highest estimate. In the revised pipeline, we only factor imputations that pass the R2R^2 gate (SoftImpute, missForest and kNN; see our reply to reviewer XgsZ). The abstract will report the range of ωh\omega_h across these imputers instead of a single value, together with the share of common variance explained by the general factor (ECV; see our reply to reviewer rXDF).

Metric orientation

See our reply to reviewer XgsZ. Orientation barely changes ωh\omega_h, and same-domain benchmarks still cluster only partly.

Q1. Do high-quality imputations give a strong general factor?

Some do. Among the imputations that pass the R2R^2 gate, missForest and kNN give a strong general factor (ωh\omega_h around 0.7), while SoftImpute, which has the best imputation quality on the C table, gives a much weaker one. Our simulation shows that missForest tends to overestimate ωh\omega_h and SoftImpute tends to underestimate it (see our reply to reviewer rXDF), so the true value likely lies between them.

We computed Pearson correlations between the estimated ωh\omega_h and wR2wR^2 for both the simulated and real datasets. For simulated data (n=96n = 96), we found a moderate correlation (r=0.399r = 0.399). For the real dataset, where we only factor imputations that pass the wR2wR^2 gate (n=6n = 6), we found a modest correlation (r=0.2106r = 0.2106).

A strong general factor therefore does not come only from mean-fill or zero-fill, but its size depends on the imputer, which is why we report a range.

Q2. What do the specific factors load on?

We will add an appendix table with the top benchmarks per factor for each solution, and we will release the full loadings. Many group factors follow a language or a benchmark suite rather than a capability. For example, Arabic benchmarks, Thai and Southeast Asian benchmarks, safety red-teaming, and long-context reading QA each form their own factor. Other factors mix unrelated tasks, such as math with instruction following and chatbot ratings. In most solutions, the general factor loads most on broad knowledge and reasoning benchmarks (e.g., MMLU, GSM and OpenBookQA). This is what we mean by partially interpretable: the structure is readable where it follows benchmark suites, but much less so for the capability labels.

Q3. Does the general factor track model size within families?

Mostly yes. We computed general-factor scores and compared them with parameter counts within model families that have at least three sizes. In most families, larger models get higher scores, and the within-family correlation is clearly positive on the C table for all imputers, but weaker on the S table. The exceptions are older families whose models all score near the floor (e.g., OPT and Pythia) and families where a newer small model beats an older large one. This supports reading the general factor as capability-related and fits our claim: a general factor exists, and the open question is how much of the benchmark variance it explains.

Paper Revision

Since replies are limited in length, we are revising the manuscript to include all of these changes and will upload it before the discussion period ends, so that reviewers can take these into account.

Reviewer_rXDFOpenReview ↗
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1
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3
Informativeness
2
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1
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Paper summary

The paper compiles 13,251 published evaluation scores covering 1,618 language models and 456 text-only benchmarks to study the latent structure of model performance. Because the raw matrix has approximately 1.8% density, the authors combine variant- and family-level model aggregation, three matrix-densification strategies, and several score- or correlation-imputation methods. Completions passing a held-out prediction threshold are analyzed using minimum-residual exploratory factor analysis, promax rotation, and a Schmid–Leiman decomposition. The paper reports 20 accepted dataset–imputer combinations, with omega hierarchical values ranging from 0.014 to 0.708; the completion with the highest predictive R-squared gives 0.257. It also analyzes semantic-label cohesion and benchmark rankings by general-factor loadings, with coverage adjustments and supplementary sensitivity analyses. The intended contribution is a broad, exploratory test of whether a coherent general intelligence factor and conventional domain abilities organize LLM benchmark performance. The authors argue that the recovered structure provides little support for a practically targetable hierarchical general-intelligence construct.

Critical strengths
  1. The benchmark compilation has substantial potential value. The paper assembles published results across a much broader range of tasks than a small leaderboard battery and documents source verification, deduplication, metric selection, and model-identity handling. This breadth is useful for studying how benchmark selection changes conclusions about model capabilities. The resource and its provenance work could support a meaningful contribution even if the current substantive interpretation needs revision.

  2. The authors explicitly attempt to expose dependence on analytical choices. Multiple densifiers and imputers, held-out prediction checks, coverage-stratified label-cohesion tests, frequency-adjusted rankings, and supplementary sensitivity analyses address real challenges in benchmark meta-analysis. These checks make the dependence on analytical choices visible and provide a useful starting point for validating the pipeline, although they do not establish recovery of the latent structure.

Critical weaknesses
  1. Latent-structure recovery remains unvalidated, and the reported estimates are strongly method-dependent. The raw matrix is approximately 98.2% missing, and the densified matrices retain only about 10–14% observed entries (Table 2). The concern is whether the pipeline reliably recovers the target structure under these conditions. Masking approximately 20% of already observed entries (Section 3.2; Appendix H) tests score prediction within the observed evaluation regime. It does not establish covariance or factor recovery for systematically unreported model–benchmark combinations.

    Table 3 illustrates this gap on the same S Std. dataset: score-level SoftImpute and missForest achieve predictive R-squared values of 0.504 and 0.471, yet yield omega hierarchical values of 0.257 and 0.032. Correlation-level SoftImpute yields 0.676 with predictive R-squared 0.378. These discrepancies demonstrate substantial uncertainty about the estimated structure; they do not establish that the underlying structure itself is weak or incoherent. The leave-one-benchmark-out analysis in Appendix O measures sensitivity to deleting a column, not recovery under the full missingness process. In the aggressive aggregation specifically, different benchmark entries within a family-level row can also represent different mixtures of model sizes and generations (Section 3.2); the impact needs checking.

    Recovery experiments with known general and domain factors under realistic sparsity and selective observation, supported by checks on a denser, evaluation-consistent subset, are needed to distinguish a weak underlying structure from failure to recover an existing one. Until then, the central negative findings remain insufficiently supported.

  2. Metric orientation, the variance estimand, and the interpretation of the results compromise the main claims. Appendix A explicitly states that metric direction is recorded but not applied, and Appendix I.3 reports no sign flipping. A column sign reversal can be accommodated by corresponding factor loadings, but the downstream cosine distances in Sections 3.4 and 4.2 are sensitive to it: two otherwise identical loading vectors with opposite signs have maximal cosine distance. The authors acknowledge this distortion and its effect on mean-filled correlations. The magnitude of the effect on semantic cohesion remains unquantified. The claim that same-domain benchmarks lack coherent structure therefore requires reanalysis with metrics oriented according to their documented scoring semantics.

    Section 4.1 describes omega hierarchical as indicator variance explained by the general factor. In standard usage, omega hierarchical concerns the general-factor contribution to the variance of an aggregate score; this differs from average variance explained across benchmark indicators, as documented in the psych package's omega documentation. The exact computation and estimand need clarification before interpreting the reported values. This concern does not establish a numerical implementation error. Metric orientation may also change aggregate-score omega through the combination of signed loadings. Moreover, the maximum reported estimate, 0.708, is a maximum across the analyzed pipelines; it does not establish the universal upper bound implied by Section 4.1.

    Finally, the observational factor structure does not identify the effect of training a model on one capability and testing transfer to others. Section 5.3 acknowledges the correlational nature of factor analysis, but the broader implications in Sections 5.1–5.3 about a causally targetable general capability exceed the evidence. These issues affect the interpretation of the paper's central findings and require substantive reanalysis and narrower claims.

Questions for authors
  1. Additional evidence essential to the current assessment: recovery under realistic missingness. Can the complete pipeline recover known general-factor strength and domain structure under sparsity matched to the corpus and plausible selective observation mechanisms? In particular, does it reliably recover a strong general factor and coherent domains when these are present in the generating data? A comparison on a denser, evaluation-consistent subset would also help. The relevant outcomes are factor strength, loadings, and domain-cohesion recovery. These checks would determine whether the central negative findings reflect the underlying structure or limitations of its recovery.

  2. Clarification and reanalysis essential to the current assessment: the estimand and metric orientation. What exact expression or software output produces the reported omega hierarchical values, and what scalar composite or multivariate variance does the denominator represent? Please report an appropriate indicator-level general-factor variance measure alongside omega, and rerun the main analyses after orienting metrics using their documented higher-/lower-is-better semantics. How much do the omega values, semantic-label cohesion, and benchmark rankings change? Which conclusions remain stable across the corrected analyses?

  3. Clarification of the claimed causal conclusion. What evidence distinguishes an absence of transferable causal capabilities from failure of a particular latent model fitted to heterogeneous observational evaluations? Would the authors restrict the conclusion to descriptive structure in this corpus and treat claims about the consequences of targeted training as hypotheses? This change would materially affect my evaluation of the paper's soundness and contribution.

A comprehensive causal study of training interventions would be a separate research project. I am not requesting that project for this submission; the current claims should instead remain within what the observational design can establish.

3 comments

We thank the reviewer for the detailed feedback. In response, we tested our imputation on simulated data with MNAR missingness, added an indicator-level measure (ECV) next to ωh\omega_h, fixed the metric orientation, and narrowed our causal claims.

Simulated study

As described in our reply to reviewer XgsZ, imputation is now sequential, so the simulation uses the same nested subsets at densities 0.5 to 0.1.

We generate data with a known structure: 5 or 10 factors with weak (0.1–0.5) or strong (0.5–0.9) cross-loadings, plus three clusters of benchmarks, similar to the benchmark suites in the real data. The mean correlation between benchmarks is 0.3 or 0.5 (the real data is close to 0.5). This gives 8 settings with known ωh\omega_h and clusters.

Each matrix is masked with logit P(observed)=ai+bj+sij\mathrm{logit}\,P(\text{observed}) = a_i + b_j + s_{ij}, where aia_i and bjb_j give each model and benchmark as many observed scores as in the real data. We test MCAR (s=0s = 0); "cell", where reporting depends on the score itself (s=γzijs = \gamma z_{ij}); and "popularity", where strong models are more often evaluated on benchmarks that correlate with the general factor (s=κρjgis = \kappa \rho_j g_i).

Uncertainty of true factor structure

We ran factor analysis on the simulated imputations above. To evaluate accuracy, we compare ωh\omega_h using the full, ground-truth dataset and calculate the delta relative to the estimate from the sparse data. To save space, we show only results from imputations with wR2>0.4wR^2 > 0.4 from SoftImpute and missForest in this reply.

methodtablemaskcellfull ωh\omega_hest. ωh\omega_hΔωh\Delta\omega_hwR2wR^2
missForestCpopularityf5_weak_r500.7400.8060.0660.496
missForestSpopularityf10_weak_r500.7070.8480.1420.456
missForestCpopularityf10_weak_r500.7300.8560.1260.450
SoftImputeCmcarf5_weak_r500.7400.7020.0380.449
missForestSpopularityf5_loud_r500.7750.8620.0870.448
missForestSmcarf10_weak_r500.7070.8860.1790.424
missForestSpopularityf5_weak_r500.6930.8040.1110.414
missForestCpopularityf10_loud_r500.7750.8390.0640.411
missForestCpopularityf5_loud_r500.7420.8350.0940.409
SoftImputeCcellf5_weak_r500.7400.7180.0220.402
missForestCmcarf5_weak_r500.7400.8360.0960.401

SoftImpute recovers ωh\omega_h nearly exactly on its cells, where its estimate tracks the full-set ωh\omega_h to within 0.02–0.04 under both MCAR (0.70 vs 0.74) and the cell mechanism (0.72 vs 0.74). On the other hand, missForest tends to overshoot the full set: nine estimates exceed the former, with Δ\Delta between +0.06 and +0.18, and estimates of 0.80–0.89 against planted 0.69–0.78. Its bias is largest under MCAR (up to Δ=+0.18\Delta = +0.18 on S_all/f10_weak) and smallest under the popularity mechanism (Δ≈+0.06\Delta \approx +0.06 on two C_all popularity cells). Nevertheless, our simulation results yield estimates of ωh\omega_h close to the full-set ωh\omega_h. We can conclude that our blockwise sequential imputation can perform reasonably effectively, and is fit for use for our main analysis.

Other issues

  • Upper bound: We agree that our maximum estimate is not a truly reliable upper bound, as it is not calculated probabilistically as confidence interval bounds should. We will revise to report the range across imputers instead.
  • ** ωh\omega_h estimand:** We use psych::omega, ωh=(∑iλg,i)2/1⊤R 1\omega_h = (\sum_i \lambda_{g,i})^2 / \mathbf{1}^\top R\,\mathbf{1}, which is the general factor's share of the summed score, not of each benchmark. We will also report ECV=∑iλg,i2/∑ihi2\mathrm{ECV} = \sum_i \lambda_{g,i}^2 / \sum_i h_i^2, which ranges from 0.11 to 0.52 across imputers (ωh\omega_h 0.04 to 0.76). The two-factor solutions in Table 3, where ωh\omega_h is not identified, will be removed.
  • Metric orientation: See our reply to reviewer XgsZ.
  • Aggressive aggregation: We agree that family-level rows can mix model sizes and generations. These tables are also hard to impute (no aggressive C or S table reaches wR2=0.4wR^2 = 0.4), so we will move them to the appendix.
  • Stable conclusions: After these changes, ωh\omega_h still depends strongly on the imputer (0.04 to 0.76) and only 16–49% of semantic labels cluster, so our main conclusion holds.
  • Causal claims: We agree that observational factor analysis cannot show whether training on one ability transfers to others. We will restrict Sections 5.1–5.3 to descriptive claims about this corpus.

Paper Revision

Since replies are limited in length, we are revising the manuscript to include all of these changes and will upload it before the discussion period ends, so that reviewers can take these into account.

Thank you for the detailed response and the additional analyses. I appreciate the metric-orientation correction, the clarification of omega hierarchical, and the commitment to narrow the causal claims. My remaining concerns are mainly the following three points.

First, the simulations with known structure are a useful addition, and using a predictive-quality threshold such as weighted R² > 0.4 to select imputations for further analysis is reasonable. However, the reported results do not yet provide sufficient evidence of reliable structural recovery. Only two successful SoftImpute cases are shown, which cannot establish its performance across the different subsets and missingness mechanisms. For missForest, overestimation of omega hierarchical reaches approximately 0.18, which is substantial for the general-factor strength the paper seeks to interpret. The full-data omega hierarchical values in the table are also concentrated around 0.69–0.78, limiting the range of structures covered by the displayed evidence. Moreover, the response mainly reports recovery of one aggregate statistic, without showing whether factor loadings and domain clusters are recovered.

I cannot determine the coverage of the displayed cases without the results before filtering. Please report the total number of runs, the number passing the threshold, and structural-recovery errors for both passing and non-passing runs, broken down by generating condition, missingness mechanism, and imputation method. In particular, are the two SoftImpute cases all of its passing results? Why are the conditions with a mean benchmark correlation of 0.3 absent from the table? If multiple random repetitions were conducted, please provide error distributions rather than only individual point estimates. My concern is not the use of a threshold itself, but whether the validation establishes the reliability and applicability of the procedure after that selection.

Second, although the imputation pipeline and evaluation metric have changed, the real-data estimates remain highly method-dependent. On the S standard table, missForest and SoftImpute obtain similar weighted R² values, 0.455 and 0.428, while their omega hierarchical estimates are 0.760 and 0.044, respectively. This disagreement does not establish that the substantive conclusion about the underlying capability structure remains valid. The current evidence does not distinguish between different methods failing to produce a consistent structural estimate and model capabilities themselves lacking a clear structure.

Third, at a broader level, the methods and results do not support a general conclusion that a coherent general-intelligence structure is absent or untenable. The data are extremely sparse and selectively observed, and the sharply different factor-strength estimates primarily demonstrate uncertainty in estimation. They do not provide a sufficient basis for rejecting a general-intelligence structure. Even if the methods and estimates were reliable, an unclear hierarchical factor structure in this benchmark corpus would not establish that LLMs lack general capabilities. These arguments cross distinct levels: the correlation structure of benchmark scores, the existence of latent capabilities, and the causal effects of training interventions. I welcome the commitment to restrict the claims, but the broader conclusions in the original manuscript need to be reconsidered throughout in light of these distinctions.

For these reasons, I will maintain my original rating of 1 (Clear rejection). Thank you again for the additional work and for addressing the concerns raised in the review.

We thank the reviewer for the follow-up reply.

Clarification Regarding The Paper Claims

We want to clarify that our paper is an exploratory study that analyzes large-scale LLM benchmark results by triangulating several densification and imputation pipelines and focusing on conclusions that hold across methods. Therefore, our approach is bottom-up, and we analyze and interpret the results as they are, specifically ω_h, without aiming for or arguing for a high or low value. Across all of them, our main finding that the factor structure of LLM benchmark scores is only partially interpretable still holds, even after the revision. Our evidence for this is as follows: most capability labels do not form coherent clusters, and the benchmarks that load most on G are mixed in content. The ω_h estimate itself depends on the pipeline (0.04 to 0.76), so the data cannot settle how strong a general factor is. We acknowledge that our stance may not be written clearly and some wordings may lead to an overclaim understanding. We will revise and ensure this claim is properly written and well under the given scope.

Simulation results

We ran 96 imputations (2 methods × 2 tables × 8 generating conditions × 3 masks) with one seed per condition, so we cannot report error distributions over repetitions. missForest passes the quality filter in 9 runs and SoftImpute in 2; the two SoftImpute cases shown earlier are all of its passing runs. No run with a mean correlation of 0.3 passes (highest wR² 0.25 for missForest and 0.28 for SoftImpute), which is why these conditions were absent. The reference ω_h is that of the full simulated data (0.58 to 0.78), not a planted value. The table below summarises all runs by method and mask: how many pass the quality filter, their weighted R², and the ω_h error for runs that pass and runs that do not.

MethodMaskPass / runswR² mean (max)|Δω_h| pass|Δω_h| fail
missForestMCAR2/160.26 (0.42)0.140.13
missForestcell0/160.23 (0.40)–0.19
missForestpopularity7/160.33 (0.50)0.100.11
SoftImputeMCAR1/160.29 (0.45)0.040.11
SoftImputecell1/160.24 (0.40)0.020.05
SoftImputepopularity0/160.23 (0.36)–0.23

|Δω_h|: mean absolute difference between the estimated ω_h and the ω_h of the full simulated data.

G loadings are recovered only partly (correlation with the full-data G loadings 0.40 and 0.61 in passing runs, against 0.22 to 0.34), in part because the full-data G loadings vary little across benchmarks.

missForest overestimates ω_h in every passing run, and SoftImpute never passes on the S table or under the popularity mask. For this reason the paper does not read any single ω_h value as the strength of G. The full per-run results, by condition and table, are now in Table A5 of the simulation appendix.

Method dependence on the real data

We agree that ω_h on the S table depends on the method. Since the paper makes no claim about the underlying capability structure, we read this disagreement as part of the finding: the public scores do not identify how strong G is. The two S solutions place G differently (congruence 0.09), while the three C solutions agree more closely (0.71 to 0.88). The finding we interpret holds in nearly all solutions: capability labels cluster only partly.

Comments on the paper

1 comment

Dear Area Chair and Reviewers,

We thank all reviewers for their insightful feedback. We would like to summarize the contributions of our paper and how we have revised our paper to addresses the raised concerns.

We present a factor analysis of 13,230 published evaluation scores covering 1,618 language models and 456 text-only benchmarks, triangulated across densifiers and imputers. The reviewers acknowledged the breadth of the corpus, the thorough data provenance work, the effort to expose dependence on analytical choices, and the relevance of the research question.

All three reviewers questioned the reliability of the pipeline on a matrix that is about 98% missing, and the unoriented lower-is-better metrics.

First, to adress the common concern over the imputation reliability, we have improved our imputation pipeline to be sequential over nested density slices, and only imputations with weighted held-out R² ≥ 0.4 are subject to factor-analysis (6 of 18; Section 3.2, Table A16). Notably, this means raw-data analyses are omitted, and no priot correlation-level imputers exceed the acceptability threshold.

Following Reviewer rXDF's useful suggestions, we have added a simulation study under plausible MNAR processes, reporting all 96 runs (Tables A3 to A5). It shows that missForest overestimates ω_h and SoftImpute only rarely passes the filter, so we do not accept any single ω_h estimate as true, rather that our multiple results suggest a range of plausible values. Furthermore, all metrics now have correct orientation so that higher is better (Section 3.2).

Following Reviewers rXDF and 8Mu7, Section 3.3 defines ω_h as computed (the general factor's share of the summed score) and adds ECV, and the abstract and Section 4.1 report ranges (ω_h 0.04 to 0.76, ECV 0.11 to 0.52) instead of the maximum. Following Reviewers rXDF and XgsZ, we have clarified that our claims are limited by the correlational nature of our study, and effects of targeted training are stated as hypotheses (Section 5.2, Table 6). Following Reviewer 8Mu7, we added the top benchmarks per factor (Table A19) and a within-family comparison with model size (Table A12).

We acknowledge that, given the nature of our data, no single result can be taken as face value. Rather, and we would like to emphasize this, our conclusions are drawn from patterns that recur robustly across different sources of analysis and modes of bias: the multiple different imputation methods and the dataset combinations, the near-chance label cohesion metrics, and average normalized GG rankings of the analyzed benchmarks, all triangulate together suggesting that our claim is robust, and our study possess merit.

We are grateful that the Area Chair and Reviewers for their time, and hope that revisions and considerations are taken into account in the final evaluation.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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