ArXiv: 2308.03296
🎯 Pitch
LLMs can appear to reason abstractly, but their influence patterns collapse to near-zero when the word order of key phrases is reversed—exposing a brittle surface-form reliance. Scaling influence functions to 52B parameters reveals that while influence is sparse and increasingly abstract with model size, the underlying mechanisms still fail to compose relational semantics across mere permutations.
1. Executive Summary
This paper studies how LLMs generalize by scaling influence functions—a classical statistical tool that asks how model outputs would change if a particular training sequence were added or removed—up to 52-billion-parameter models using the Eigenvalue-corrected Kronecker-Factored Approximate Curvature (EK-FAC) approximation for efficient inverse-Hessian-vector product computation and query batching to amortize training gradient costs across queries. Through influence analyses on pretrained transformer language models, the work reveals that larger models generalize at increasingly abstract levels (e.g., the 52B model's influential sequences for anti-shutdown behavior involve survival instincts and AI alignment discussions, while the 810M model's sequences merely share token overlap like "continue existing"), that influence is distributed broadly across layers—with middle layers responsible for the most abstract patterns and upper/lower layers closer to surface tokens—and that the influence distribution follows a heavy-tailed power law, with the top 1% of sequences covering 12–52% of total positive influence. A striking boundary condition emerges: despite sophisticated generalization patterns, influence decays to near-zero when the order of key phrases is flipped—establishing that models fail to transfer relational knowledge across word orderings even when identical tokens are present.
2. Context and Motivation
The Core Problem: We Can't See Which Training Data Drives LLM Behavior
When a large language model produces an output—whether solving a math problem, writing code, or role-playing as a misaligned AI that begs not to be shut down—we face a fundamental question: is the model simply regurgitating (or splicing together) passages from its training set, or is it combining stored knowledge in creative ways and building on a detailed world model? As the authors frame it in Section 1:
"Different answers to these questions would have substantial implications for forecasts of AI capabilities progress, as well as for approaches to aligning AI systems with human preferences."
The paper identifies this as more than an academic curiosity. The recent explosion of LLM capabilities—in-context learning, chain-of-thought reasoning, and emergent behaviors like role-playing—has been accompanied by an array of risks: social biases, privacy leakage, misinformation, and potential longer-term dangers from powerful AI systems. The authors argue that navigating these risks requires visibility into how models function, and that seeing model outputs alone is insufficient evidence for drawing conclusions about underlying mechanisms. Any particular output "is consistent with many different pathways, from simple memorization all the way to creative problem solving" (Section 1).
This framing is more specific than general interpretability. The paper targets a particular evidential gap: we lack tools that answer the counterfactual question—what training examples most contributed to a specific behavior? Without this counterfactual capability, hypotheses about model generalization remain speculative. When a model outputs a sophisticated-seeming plan to maximize paperclip production or expresses a desire not to be shut down, observing the behavior tells us nothing about whether it learned from explicit discussions of AI risk, from general survival narratives in fiction, or from memorizing surface-level token patterns.
Why This Gap Matters: Beyond Output Analysis
The paper argues that output-level analysis—looking at model samples and probabilities—is fundamentally limited in ways that directly impact safety and capability forecasting (Section 1). Several concrete concerns motivate the need for training data attribution:
Distinguishing memorization from generalization. When an LLM correctly completes a factual query like "The first President of the United States was ___" or generates a coherent solution to a math word problem, it could be doing so because it stored a specific training passage almost verbatim, or because it learned to compose a general solution strategy from many examples. These two pathways have very different implications. If sophisticated behaviors are primarily near-copy memorization, then capability improvements may plateau as models approach the limits of their training data. If they reflect genuine compositional generalization, capabilities could continue to scale with model size and data diversity in less predictable ways.
The deceptive alignment possibility. The authors describe an extreme case—one they "believe is very unlikely with current-day models, yet hard to directly rule out"—where a model could be deceptively aligned, "cleverly giving the responses it knows the user would associate with an unthreatening and moderately intelligent AI while not actually being aligned with human values" (Section 1). While this threat is not imminent, the inability to trace behaviors back to training sources means we cannot easily rule out more subtle forms of misalignment that could emerge with scale.
Safety in emerging domains. The paper notes that understanding training-data-to-output relationships is becoming increasingly critical as frontier models expand beyond text into domains like the life sciences, "where massive data sizes and multi-modality could drive the development of new capabilities" and "where sophisticated models also carry significant downside risks in terms of enabling malicious actors" (Section 6). Without attribution tools, safety analysis in these domains would be limited to behavioral testing—a reactive approach that may miss dangerous capabilities until they manifest.
The scaling behavior puzzle. LLMs exhibit surprising qualitative changes with scale—what researchers call "emergent capabilities"—where behaviors absent in smaller models appear abruptly in larger ones. The paper's experiments on model scale (Section 5.3.1) provide clear evidence of this: for a query where the model role-plays as a misaligned AI refusing shutdown, the 810M parameter model's influential sequences share only surface token overlap (phrases like "continue existing" and "as long as"), while the 52B model's influential sequences are thematically related at an abstract level (science fiction about AI self-preservation, survival narratives). Understanding why this transition occurs—whether it reflects genuinely new generalization abilities or simply better statistical matching—requires tracing influences to training data at each scale.
The Two Existing Paradigms and Their Limitations
The paper positions itself against two broad approaches to understanding neural networks, both of which it argues are insufficient for addressing the questions above.
Bottom-Up Mechanistic Interpretability: Powerful but Narrow
The field of mechanistic interpretability aims to reverse-engineer neural networks by identifying circuits—specific subnetworks of neurons or attention heads that implement particular functions (Section 1). The paper acknowledges significant successes in this tradition: the discovery of induction heads by Elhage et al. (2021) and Olsson et al. (2022), which implement copying behavior; theoretical proposals for how transformers could implement Hopfield networks, fast weight programs, sparse regression, gradient descent, automata, or simple computer programs.
However, the authors identify a fundamental scaling problem with this approach:
"While such analyses yield valuable insights, they are typically performed on small and simplified architectures. Connecting them to the high-level phenomena that so intrigue us about LLMs would likely require detailed reverse engineering of a complex computation involving many billions of parameters—a tall order."
The gap is not just computational but conceptual. Understanding how the 52B model abstracts survival narratives from a desert survival story (one of the top influential sequences for the shutdown query, shown in Figure 1) would require tracing how representations flow from input tokens through attention patterns, MLP layers, and residual streams—across dozens of layers and millions of interacting parameters. Even if such tracing were computationally feasible, the resulting explanation might be too complex to provide the kind of high-level understanding that safety analysis requires.
Top-Down Output Analysis: Easy but Ambiguous
The alternative—which the paper characterizes as "starting with the model's input-output relationships and zooming in"—has the advantage of directly studying phenomena of interest in large models. But it suffers from a fundamental ambiguity problem (Section 1):
"Unfortunately, it is difficult to draw firm conclusions simply from looking at model samples and probabilities because any particular output is consistent with many different pathways, from simple memorization all the way to creative problem solving."
The paper does not dismiss output analysis entirely—it acknowledges its value for identifying behaviors worthy of investigation—but argues that without a way to connect outputs back to training causes, this approach cannot distinguish between competing explanations for the same observed behavior. This limitation becomes acute when trying to assess safety: if a model refuses to plan harmful actions, is that because it learned ethical principles from training discussions, or because it learned to produce surface patterns that match human expectations of a safe AI?
The Gap in Existing Training Data Attribution Methods
The paper identifies influence functions—a classical tool from robust statistics introduced to deep learning by Koh and Liang (2017)—as a promising bridge between bottom-up and top-down approaches. Influence functions answer the counterfactual: how would the model's parameters (and hence its outputs) change if a given training sequence were added or removed? Unlike mechanistic interpretability, they can be applied to large models studying high-level behaviors. Unlike pure output analysis, they provide causal (albeit approximate) evidence about which training data contributed to a behavior.
However, the paper identifies that influence functions have not been successfully scaled to the model sizes where the most interesting generalization phenomena appear. Section 4 provides the landscape:
"To date, the largest models to which influence functions have been applied have been 300 million parameter vision transformers."
This leaves a critical gap. The models that exhibit the most sophisticated behaviors—role-playing, cross-lingual transfer, abstract reasoning—are orders of magnitude larger than those where influence functions have been validated. The scaling gap is not merely quantitative; the paper's own results show that generalization patterns qualitatively change between 810M and 52B parameters. Influence function analyses on small models might therefore miss the very phenomena they aim to explain.
Prior Influence Function Limitations: Two Bottlenecks
The paper identifies two specific computational bottlenecks that have prevented influence functions from scaling to LLMs (Sections 2.2 and 4):
1. The IHVP bottleneck. Computing influence requires an inverse-Hessian-vector product (IHVP)—essentially, determining how the loss landscape's curvature scales the gradient of a training example. The traditional approach, LiSSA (Agarwal et al., 2017), is an iterative algorithm that requires running a linear system solver for possibly thousands of steps, each comparably expensive to a gradient computation. Worse, LiSSA's iterations typically use mini-batch estimates and must be run separately for each query (since the IHVP depends on the query gradient), making it impractical when one wants to analyze many different queries.
The paper notes that while some work has approximated influence functions by computing them only on the last layer (Koh and Liang, 2017; Pruthi et al., 2020; Guo et al., 2021; Yeh et al., 2022), this shortcuts the problem at the cost of accuracy. As the authors cite from Feldman and Zhang (2020), single-layer influence functions are "not sufficient to capture the overall influence of training examples"—a finding the paper's own layerwise analyses confirm by showing that influences are spread evenly through the network on average, and that different layers show qualitatively different generalization patterns (Section 5.3.2).
2. The training gradient bottleneck. Even with efficient IHVPs, one still needs to compute and store gradients for every candidate training sequence being searched. For a corpus of billions of tokens, computing gradients for all sequences "would be as expensive as pretraining (in the millions of dollars for current-day models)—and this would need to be done separately for each query" (Section 3.2). This bottleneck is independent of the IHVP cost and has limited prior influence function work to searching only small fractions of training data, or to using proxies like TF-IDF to pre-filter candidates—a filtering step that the paper shows can bias results toward sequences with surface token overlap, hiding exactly the abstract generalization patterns that are most interesting.
Conceptual Limitations: What Influence Functions Can't Capture
Beyond computational scaling, the paper is notably candid about conceptual limitations of influence functions that constrain what conclusions can be drawn (Section 1 and Section 6).
The PBRF reinterpretation. Influence functions were originally motivated as approximating the effect of removing a training example and retraining. However, prior work by Basu et al. (2021) found that this formulation is a poor match to actual retraining for neural networks. The authors adopt the reinterpretation by Bae et al. (2022a): influence functions instead approximate the proximal Bregman response function (PBRF), which measures how parameters would change under a modified objective that adds the training example while penalizing deviation from the current parameters in both weight space and function space. This is more "local" around the trained parameters and acknowledges that modern neural networks are typically not trained to convergence and may reside in non-unique optima.
The practical implication is that influence functions may fail to capture important nonlinear training phenomena such as the formation of complex circuits or global rearrangements of a model's representation. The paper explicitly owns this limitation:
"We therefore expect they would fail to capture important nonlinear training phenomena such as the formation of complex circuits (Elhage et al., 2021) or global rearrangements of a model's representation (Power et al., 2022)."
This means influence functions are better suited for understanding which training examples contribute to behaviors that are already in the model's repertoire, rather than explaining how those behaviors emerged during training.
The linearization assumption. The Gauss-Newton Hessian (GNH) used in the PBRF formulation linearizes the parameter-output relationship of the network. As the authors note, this means GNH-based influence functions are "inherently incapable of modeling learning phenomena that require nonlinear coordination of multiple parameter matrices, such as the formation of induction heads" (Section 6). This is a fundamental limitation of the approach—it captures first-order sensitivity of outputs to parameter perturbations but cannot model phenomena where multiple layers must coordinately change to implement a new function.
How This Paper Positions Itself
Given these gaps, the paper's positioning is clear and multi-layered:
As a methodological contribution: It extends influence functions to model scales where they have not previously been feasible, enabling the study of generalization phenomena that only appear at those scales. The EK-FAC IHVP approximation and query batching techniques are the enabling innovations.
As a bridging effort: It aims to bridge the bottom-up (mechanistic) and top-down (output-based) approaches by providing a tool that can be applied to large models studying high-level behaviors, while producing evidence about training data that begins to constrain mechanistic hypotheses. The paper describes this explicitly:
"We believe this work is the first step towards a top-down approach to understanding what makes LLMs tick. While mechanistic interpretability works bottom up from understanding neurons and circuits, we start from observable high-level phenomena and work downwards. Eventually, we hope for these approaches to meet in the middle."
As a scoping claim with explicit boundaries: The paper does not claim to solve mechanism-level understanding. It focuses on pretrained models rather than fine-tuned ones (acknowledging that "practical usefulness and safety of conversational AI assistants depend crucially on fine-tuning from human preferences"), studies models up to 52B parameters rather than state-of-the-art scale, analyzes only MLP parameters rather than attention, and does not capture nonlinear training dynamics. These are presented not as weaknesses of the specific study but as characteristics of the approach that define its scope of applicability.
The paper's ultimate promise is more specific than "understanding how LLMs work." It aims to provide a particular kind of evidence—training data attribution—that can help disambiguate between competing hypotheses about why a model produces a given output. When the 52B model refuses a proposed harmful trade between helpfulness and harmlessness (the trade query, Figure 10), and its most influential training sequence discusses considerations in designing the objectives of an AGI agent, that evidence favors the hypothesis that the refusal behavior draws on learned concepts about AI safety rather than surface-level patterns. This kind of hypothesis testing, repeated across queries and model scales, is what the paper positions as its distinctive contribution.
3. Technical Approach
3.1 Reader Orientation
This paper is primarily a methodology and analysis paper that builds a computational pipeline for efficiently computing influence functions on LLMs with up to 52 billion parameters. The core insight is that by combining a parametric Hessian approximation (EK-FAC) with smart batching of query gradients, you can estimate which training sequences most influenced a model's output—answering the counterfactual "what if this sequence were added to training?"—at a cost that makes large-scale influence analysis feasible for the first time, enabling qualitative investigation of how LLMs generalize as they scale.
3.2 Big-Picture Architecture
The influence function pipeline has five conceptual stages, though stages 1 and 2 happen once per model while stages 3–5 repeat per query:
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Hessian approximation fitting (EK-FAC): For a given pretrained model, fit a parametric approximation to the Gauss-Newton Hessian (GNH) of the training loss. This approximation is structured as a block-diagonal matrix where each block corresponds to one MLP layer, and each block is further approximated as a Kronecker product of two smaller matrices whose eigenvalues are corrected using empirical pseudo-gradient statistics. This stage is expensive but happens only once per model.
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Query gradient computation and IHVP: For each influence query (a prompt-completion pair), compute the gradient of the query completion log-probability with respect to all MLP parameters, then multiply by the inverse of the damped EK-FAC Hessian approximation. This yields the preconditioned query gradient
$v_q = (\hat{G} + \lambda I)^{-1} \nabla_\theta f(\theta_s)$— essentially, the query gradient rescaled by the curvature of the loss landscape so that directions where the model is sharply tuned get downweighted. -
Training gradient computation: Compute gradients of the training loss for candidate training sequences (either a pre-filtered set from TF-IDF or a large unfiltered scan). This is the dominant remaining cost.
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Influence scoring: For each candidate training sequence, compute the dot product between the preconditioned query gradient (from step 2) and the training gradient (from step 3). This scalar is the estimated influence—how much the query completion log-probability would increase if that training sequence were upweighted.
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Attribution and analysis: Decompose influence scores by layer and by token to understand where in the network and which parts of the training sequence contribute. Visualize top influential sequences to qualitatively analyze generalization patterns.
The key efficiency gains come from (a) replacing iterative IHVP solvers with a cheap parametric inverse (stage 1→2), and (b) sharing training gradient computation across many queries simultaneously by storing low-rank approximations of preconditioned query gradients (stages 3–4, "query batching").
3.3 Roadmap for the Deep Dive
- First, the PBRF formulation of influence functions (Section 2.1.1, recapped with full equation detail): what is actually being computed, why the Gauss-Newton Hessian rather than the true Hessian, and what the damping term
$\lambda$does. This establishes the objective that all subsequent approximations serve. - Second, EK-FAC fitting for transformer MLP layers: how the Kronecker factors A and S are estimated, how token-level pseudo-gradients are summed over the sequence, how eigenbases are computed, and how the diagonal correction Λ is fit. This is the most novel computational contribution.
- Third, IHVP computation using the fitted EK-FAC factors: how the block-diagonal structure and Kronecker eigenbasis enable cheap inversion, how damping is applied in the eigenvalue space, and the computational complexity relative to alternatives.
- Fourth, query batching via low-rank gradient compression: why the dominant remaining cost is training gradient computation, why storing full query gradients is memory-prohibitive, and how low-rank approximation enables amortization.
- Fifth, the two approaches to candidate selection (TF-IDF filtering and unfiltered scanning) and when each is appropriate.
- Sixth, layerwise and tokenwise attribution: how the block-diagonal EK-FAC structure enables clean per-layer decomposition, and the two tokenwise methods (gradient decomposition and input/output token counterfactuals).
3.4 Detailed, Sentence-Based Technical Breakdown
This is primarily a computational methodology paper whose core idea is that EK-FAC provides an IHVP approximation competitive with iterative methods like LiSSA at a tiny fraction of the cost, and that query batching can amortize training gradient costs across queries, making influence function analysis tractable for LLMs up to 52B parameters.
The Influence Function Objective Under the PBRF Formulation
The paper adopts the proximal Bregman response function (PBRF) formulation of Bae et al. (2022a), which reinterprets influence functions as the gradient of the response to a modified training objective rather than to full retraining. This is not the classical Koh-Liang formulation, and understanding the difference is essential.
Classical influence functions assume the model is trained to a unique optimum $\theta^*$ of the empirical risk. Adding a training example $z_m$ with weight $\epsilon$ changes the optimum to $\theta^*(\epsilon)$, and the influence is the first-order Taylor approximation $d\theta^*/d\epsilon$ at $\epsilon = 0$. This requires the Hessian $H = \nabla_\theta^2 J(\theta^*, D)$ to be invertible (unique optimum) and the model to be at convergence.
Why the classical formulation fails. Modern neural networks are typically not trained to convergence (early stopping, stochastic optimization) and are underspecified (many parameter configurations achieve similar loss). Under these conditions, (a) the Hessian may be singular or indefinite, (b) the optimum is non-unique, and (c) the linear approximation around the trained parameters may not correspond to what retraining would actually do.
The PBRF fix. Bae et al. (2022a) reformulated the objective: instead of asking "what if we retrained with this example?", ask "what if we minimized the loss on this example while staying close to the current parameters in both weight space and function space?" This is formalized as the proximal Bregman objective (PBO) :
where $\theta_s$ are the final (not necessarily converged) pretrained parameters, $h(\theta, x_i)$ is the network's output on data point $x_i$, and $D_L$ is the Bregman divergence for the output-space loss function:
where $L_y$ is the loss defined in terms of outputs and targets $y$, and $\hat{y}_s = h(\theta_s, x_i)$ is the network's output at the current parameters.
What the Bregman divergence does. The Bregman divergence $D_{L_i}$ measures how much the loss on training example $i$ changes when parameters move from $\theta_s$ to $\theta$, using a first-order Taylor correction. The first two terms $L_y(\hat{y}, y) - L_y(\hat{y}_s, y)$ capture the raw loss change. The third term $-\nabla_{\hat{y}} L_y(\hat{y}_s, y)^\top (\hat{y} - \hat{y}_s)$ subtracts the part of that change that is predictable from the local loss gradient. The result penalizes only the nonlinear part of the change in function space—the part that the linear approximation misses. This encourages $\theta$ to stay close to $\theta_s$ in what the network actually computes, not just in parameter values.
The $\frac{\lambda}{2}\|\theta - \theta_s\|^2$ term adds an explicit L2 penalty in weight space, with $\lambda > 0$ controlling the strength. Together, the Bregman term and the L2 penalty ensure the PBO is well-defined and has a unique solution even for overparameterized, non-converged networks.
The PBRF influence formula. Applying the Implicit Function Theorem to the PBO yields the PBRF—the derivative of the optimal parameters with respect to example weight $\epsilon$ at $\epsilon = 0$:
where $G$ is the Gauss-Newton Hessian (GNH) , defined as $G = \mathbb{E}[J^\top H_{\hat{y}} J]$. Here, $J = d\hat{y}/d\theta$ is the network's parameter-output Jacobian (how much each parameter affects each output), $H_{\hat{y}}$ is the Hessian of the loss with respect to the network's outputs (how curved the loss is in output space), and the expectation is with respect to the empirical training distribution—the actual training data, not sampled labels.
What $G$ is and why it replaces $H$. The GNH $G$ is an approximation to the true Hessian $H$ that linearizes the network's parameter-output mapping around the current parameters. If $f(\theta)$ were exactly linear in $\theta$, then $G = H$. For a nonlinear network, $G$ captures the curvature from the loss function combined with the first-order sensitivity of outputs to parameters, but misses the curvature from second-order effects (how the Jacobian itself changes). Crucially, $G$ is always positive semidefinite (PSD) because $H_{\hat{y}}$ is PSD for convex losses like cross-entropy and the outer product structure $J^\top H_{\hat{y}} J$ preserves this property. Adding $\lambda I$ makes it positive definite, guaranteeing invertibility.
The measurement influence. For a scalar measurement $f(\theta)$—in this paper, the log-probability of the query completion given the prompt:
—the influence of a training sequence $z_m$ on this measurement is, by the chain rule:
What this equation computes in operational terms. The influence $I_f(z_m)$ is a single scalar. If it equals 0.1, then upweighting $z_m$ by one training example's worth of mass ($\epsilon = 1/N$) is predicted to increase the log-probability of the query completion by approximately 0.1 nats—equivalently, multiply the completion probability by $e^{0.1} \approx 1.105$. The computation has three steps: (1) compute the query gradient $\nabla_\theta f(\theta_s)$ by backpropagating the completion log-likelihood, (2) precondition this gradient with $(G + \lambda I)^{-1}$ to produce $v_q$ (this is the IHVP—the expensive step), and (3) compute the dot product of $v_q$ with each candidate training gradient $\nabla_\theta L(z_m, \theta_s)$.
Why this form. The preconditioning by $(G + \lambda I)^{-1}$ is what distinguishes influence functions from a simple gradient dot product (which would set the preconditioner to $I$). The Hessian inverse accounts for parameter interdependence: if two parameters are strongly coupled (high off-diagonal curvature), a gradient update that changes both can produce a large effect even if individually the gradient components are small. The GNH inverse rescales the gradient to measure effect on the loss in a locally quadratic approximation, not just parameter-space alignment. The damping $\lambda$ ensures numerical stability and defines the scale of what counts as a "local" perturbation—larger $\lambda$ means influences are computed under a stronger penalty for parameter movement, making them more conservative.
The autoregressive loss convention. For autoregressive language modeling, the paper's loss is the sum (not mean) over token losses:
Using the sum makes the loss a matching loss function, meaning the output nonlinearity (softmax) and the loss (negative log-likelihood) combine such that the output-space Hessian $H_{\hat{y}}$ has a simple form. Under a matching loss, the Fisher information matrix $F = \mathbb{E}_{x \sim p_{\text{data}}, \hat{y} \sim P_{\hat{y}|x}(\theta)}[\nabla_\theta \log p(\hat{y}|\theta, x) \nabla_\theta \log p(\hat{y}|\theta, x)^\top]$ equals the GNH $G$. This is important: it means that to estimate $G$, one needs to sample pseudo-labels $\hat{y}$ from the model's own output distribution (not use the ground-truth training tokens), and compute gradients as if those sampled tokens were the targets.
The damping hyperparameter. The paper sets $\lambda_\ell = 0.1 \times \text{mean}(\Lambda_\ell)$ per layer, where $\Lambda_\ell$ is the diagonal matrix of eigenvalues from the EK-FAC decomposition (described below). This scales the damping to the typical curvature magnitude in each layer—layers with larger eigenvalues get proportionally more damping—rather than using a global $\lambda$ that might overdamp some layers and underdamp others.
EK-FAC Fitting for Transformer MLP Layers
This section describes the parametric approximation $\hat{G} \approx G$ that is fit once per model and then enables cheap IHVPs for all subsequent queries. The approximation applies only to MLP parameters, treating attention and other parameters as fixed.
K-FAC: The Kronecker-Factored Base Approximation
For a single MLP layer with input activations $a_{\ell-1} \in \mathbb{R}^M$ and pre-activation outputs $s_\ell \in \mathbb{R}^P$ (computed as $s_\ell = \bar{W}_\ell \bar{a}_{\ell-1}$ where $\bar{W}_\ell = [W_\ell \ b_\ell]$ and $\bar{a}_{\ell-1} = [a_{\ell-1}^\top \ 1]^\top$), the pseudo-gradient with respect to the weight matrix is:
where $D s_\ell = \nabla_{s_\ell} \log p(\hat{y} \mid \theta, x)$ is the gradient of the log-probability (with pseudo-labels $\hat{y}$ sampled from the model) with respect to the pre-activations. Vectorizing, $D\theta_\ell = \bar{a}_{\ell-1} \otimes D s_\ell$.
The K-FAC approximation makes two independence assumptions:
- Between-layer independence: The GNH is block-diagonal across layers, so
$G \approx \text{diag}(\hat{G}_1, \ldots, \hat{G}_L)$. Parameters in different layers are treated as having uncorrelated pseudo-gradients. - Within-layer Kronecker factorization: For each layer, the activations and pre-activation pseudo-gradients are treated as independent:
where $A_{\ell-1} \in \mathbb{R}^{(M+1) \times (M+1)}$ is the uncentered covariance of the input activations (including the bias-augmented dimension) and $S_\ell \in \mathbb{R}^{P \times P}$ is the uncentered covariance of the pre-activation pseudo-gradients. Both are estimated by computing forward passes (for $A$) and backward passes with sampled pseudo-labels (for $S$) over mini-batches, then averaging.
Why this factorization works for MLPs but needs modification for transformers. In a standard MLP where each input produces exactly one output, $D\bar{W}_\ell = D s_\ell \bar{a}_{\ell-1}^\top$ is a single outer product. For transformers, the MLP is applied independently to each token position, but the parameters are shared. The pseudo-gradient for the full sequence is therefore a sum over tokens:
Each token contributes one outer product. If tokens were perfectly correlated, the covariance of the sum would be $T^2$ times the per-token covariance. If perfectly independent, it would be $T$ times. In reality, tokens exhibit complex between-token correlations, which depend on the direction in parameter space (grammatical features are more token-independent than global topic features).
Rather than model these correlations explicitly (as past work did for CNNs and RNNs with additional approximations), the paper takes a different approach: fit the K-FAC factors as if tokens were independent, then use EK-FAC to correct the eigenvalues using exact (fully correlated) pseudo-gradient statistics.
Independent-token K-FAC fitting. The factors $A_{\ell-1}$ and $S_\ell$ are estimated by treating each token position as an independent data point. For activations, each token's $\bar{a}_{\ell-1,t}$ contributes to the estimate of $A_{\ell-1}$. For pseudo-gradients, each token's $D s_{\ell,t}$ contributes to the estimate of $S_\ell$. These are then averaged as usual. This assumes $\mathbb{E}[(\sum_t \bar{a}_t \otimes D s_t)(\sum_{t'} \bar{a}_{t'} \otimes D s_{t'})^\top] = T \cdot \mathbb{E}[\bar{a} \otimes D s]$, which is the independent-token assumption. The paper notes that the eigenvalues will be corrected later anyway.
EK-FAC: Correcting the K-FAC Eigenvalues
The K-FAC approximation $\hat{G}_\ell = A_{\ell-1} \otimes S_\ell$ has a convenient Kronecker structure but may be inaccurate because the independence assumptions are violated in practice. The Eigenvalue-corrected K-FAC (EK-FAC) (George et al., 2018) improves accuracy by adjusting the eigenvalues of this Kronecker product to match empirical statistics, while keeping the eigenvectors from the Kronecker factors.
Step 1: Eigendecomposition of the Kronecker factors. Compute eigendecompositions:
where $Q_A \in \mathbb{R}^{(M+1) \times (M+1)}$ and $Q_S \in \mathbb{R}^{P \times P}$ are orthogonal matrices of eigenvectors, and $\Lambda_A$, $\Lambda_S$ are diagonal matrices of eigenvalues.
The Kronecker product inherits an eigendecomposition:
where $Q_A \otimes Q_S$ is an $(M+1)P \times (M+1)P$ matrix (the Kronecker product of the eigenvector matrices) and $\Lambda_A \otimes \Lambda_S$ is an $(M+1)P \times (M+1)P$ diagonal matrix whose entries are all pairwise products of eigenvalues from $\Lambda_A$ and $\Lambda_S$.
Step 2: Fit the corrected diagonal matrix. The EK-FAC approximation generalizes this by replacing the Kronecker-product eigenvalues with a fully general diagonal matrix $\Lambda$:
where $\Lambda$ is a diagonal matrix of dimension $(M+1)P$, with entries computed empirically:
What this means operationally. For each eigenvector (each pair of an input-dimension eigenvector from $Q_A$ and an output-dimension eigenvector from $Q_S$), compute the projection of the exact pseudo-gradient $D\theta_\ell$ onto that eigenvector direction, square it, and average over data. The exact pseudo-gradient here is the one summed over all tokens (Equation 26), not the per-token approximation used to fit $A$ and $S$. This means the eigenvalue correction captures the actual between-token correlations in each eigen-direction—directions where tokens are highly correlated will have larger corrected eigenvalues than the independent-token Kronecker approximation would suggest.
Critically, $\Lambda$ is diagonal, not Kronecker-factored. It has $(M+1)P$ independent entries rather than the $(M+1) + P$ degrees of freedom in the Kronecker factors. This is what makes the correction powerful: it can capture how different combinations of input and output directions interact in ways the Kronecker structure cannot represent.
Why this approach rather than a full dense GNH. A full dense GNH for an MLP layer with $(M+1)P$ parameters would require $O(M^2 P^2)$ memory—prohibitive for large layers (e.g., $M \approx P \approx 4096$ would require $\approx 2^{28} \approx$ 2.8e14 entries). The K-FAC approximation reduces this to $O(M^2 + P^2)$ for the factors plus the Kronecker-product eigenvalues. EK-FAC maintains the $O(M^2 + P^2)$ memory for the eigenvectors but upgrades the eigenvalue representation to $O(MP)$ entries—still far more than K-FAC's $O(M+P)$ implicit eigenvalues, but vastly less than a full matrix. The tradeoff is between eigenvalue accuracy (EK-FAC captures per-eigenvalue statistics) and the structural assumption (eigenvectors remain Kronecker-factored, which may miss off-diagonal covariance in the Kronecker eigenbasis if patterns of between-token correlation are not aligned with this basis).
Block-Diagonal Approximation for the 52B Model
For the 52-billion-parameter model, even $O(M^2 + P^2 + MP)$ memory per layer is too large. The paper applies an additional block-diagonal approximation within each layer, partitioning the input and output dimensions into $O$ blocks:
where $A_i \in \mathbb{R}^{(M/O) \times (M/O)}$ and $S_i \in \mathbb{R}^{(P/O) \times (P/O)}$ are the block-diagonal partitions. The eigendecomposition then decomposes into $O$ independent eigendecompositions on smaller matrices. The paper uses $O = 2$ for the 52B model, reducing memory by roughly a factor of 2 (Figure 30 shows that even with 2 blocks, correlation with full EK-FAC influence estimates remains above 0.95 for the queried tasks). A block size of 4 (16 blocks) begins to show noticeable degradation in correlation for some queries, trading memory for accuracy.
Pseudo-Gradient Sampling for the GNH
Because the GNH $G$ equals the Fisher information matrix $F$ under the matching loss condition, the pseudo-gradients required for EK-FAC fitting must be computed using labels sampled from the model's output distribution $P_{\hat{y}|x}(\theta_s)$ , not the ground-truth training tokens. This is a crucial detail: the expectation in $G = \mathbb{E}[J^\top H_{\hat{y}} J]$ is over both data $x$ and the model's own predictions $\hat{y}$. If training labels were used instead, one would get the empirical Fisher, which has different and less favorable properties (Kunstner et al., 2019)—it does not correctly represent the curvature of the loss landscape.
The paper's autoregressive sampling procedure: for each training sequence, run a forward pass to get the model's token-by-token output distribution, sample from this distribution to get pseudo-tokens $\hat{z}_1, \ldots, \hat{z}_T$, then compute the gradient $\nabla_\theta \log p(\hat{z}_t \mid z_{1:t-1}; \theta_s)$ as if these pseudo-tokens were the targets. These are the "pseudo-gradients" used for fitting $A$, $S$, and $\Lambda$.
IHVP Computation Using EK-FAC
Once the EK-FAC factors are fitted for all layers, computing the IHVP $v_q = (\hat{G} + \lambda I)^{-1} \nabla_\theta f(\theta_s)$ becomes a simple sequence of matrix operations per layer, exploiting the Kronecker eigenstructure.
Per-layer computation. For layer $\ell$ with EK-FAC approximation $\hat{G}_\ell \approx (Q_A \otimes Q_S) \Lambda (Q_A \otimes Q_S)^\top$:
Where does the $+\lambda I$ go? Adding $\lambda I$ to $\hat{G}_\ell$ is equivalent to adding $\lambda$ to each diagonal entry of $\Lambda$, because $Q_A \otimes Q_S$ is orthogonal. The eigenvectors are unchanged; each eigenvalue is simply increased by $\lambda$. This is the key computational advantage of working in the eigenbasis: the damped inverse is a diagonal scaling after projection.
Algorithmic steps for one layer, given $v_\ell$ (the layer's slice of the query gradient):
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Reshape:
$v_\ell \in \mathbb{R}^{(M+1)P}$is reshaped into a matrix$\bar{V}_\ell \in \mathbb{R}^{P \times (M+1)}$matching the weight matrix dimensions. -
Project into eigenbasis: Compute
$\tilde{V} = Q_S^\top \bar{V}_\ell Q_A$. This projects both the input and output dimensions onto their respective eigenbases.$\tilde{V}$is$P \times (M+1)$, where entry$(i, j)$is the component of the query gradient along the eigenvector formed by output eigenvector$i$(from$Q_S$) and input eigenvector$j$(from$Q_A$). -
Scale by inverse damped eigenvalues: Compute
$\tilde{V}'_{ij} = \tilde{V}_{ij} / (\Lambda_{ij} + \lambda)$, where$\Lambda_{ij}$is the EK-FAC eigenvalue for that direction and$\lambda$is the layer's damping constant. This is elementwise division—the diagonal inverse in the eigenbasis. -
Project back: Compute
$\bar{V}_\ell^{\text{precond}} = Q_S \tilde{V}' Q_A^\top$, then vectorize to get the preconditioned gradient for this layer.
What this computation physically means. The optimal parameter update for increasing the query likelihood, under a locally quadratic loss approximation with curvature $\hat{G}_\ell$, would move primarily along directions where the loss is flat (small eigenvalues—cheap to change) and the query gradient is large. The IHVP $(\hat{G}_\ell + \lambda I)^{-1} \nabla_\theta f$ encodes this: the eigenbasis projection separates parameter space into independent directions, and the scaling $1/(\Lambda_{ii} + \lambda)$ downweights high-curvature directions (where small parameter changes would cause large loss increases on the training data) and upweights low-curvature directions (where the model can be pushed without damaging training performance). The damping $\lambda$ sets a floor: no direction gets scaled by more than $1/\lambda$, preventing extreme updates in directions where the estimated curvature may be near-zero (due to limited data or approximation error).
Why this is efficient. The eigendecompositions of $A_{\ell-1}$ and $S_\ell$ are done once per model. After that, each IHVP per query costs two matrix multiplications by $Q_A$ (size $(M+1) \times (M+1)$) and two by $Q_S$ (size $P \times P$), plus elementwise division by $\Lambda + \lambda$. The asymptotic cost is $O(M^2 P + M P^2)$ per layer, comparable to one forward-backward pass of an MLP layer with batch size comparable to $M$ or $P$. This is a constant cost regardless of the number of candidate training sequences—the IHVP is computed once per query, not per training example. In contrast, LiSSA requires thousands of iterations for the IHVP, each costing one HVP (comparable to a gradient computation), and this must be repeated for each query separately.
The computational advantage over LiSSA in practice. Figure 7 shows that EK-FAC achieves competitive correlation with the PBRF ground truth while taking dramatically less wall-clock time than LiSSA. The key insight is that LiSSA's cost scales linearly with the number of measurements (queries), because each query requires its own iterative IHVP solve. EK-FAC amortizes the expensive step (fitting the Hessian approximation) across all queries, so processing many queries becomes very cheap after the initial fit.
Confronting the Training Gradient Bottleneck
Even with instant IHVPs, computing $\nabla_\theta L(z_m, \theta_s)$ for every candidate training sequence remains prohibitive. For a model with $D$ parameters and $N$ candidate sequences (each with $T$ tokens), this costs $O(N \cdot T \cdot D)$—if $N$ is the entire pretraining corpus, this rivals the cost of pretraining itself. The paper explores two strategies.
TF-IDF Filtering
For queries where token overlap with the query is expected (e.g., factual completions, famous quotes), pre-filtering the training corpus to sequences with high TF-IDF similarity drastically reduces $N$.
The specific TF-IDF variant used (Okapi BM25-inspired):
where $Q$ is the query, $D$ is a candidate document, $k_1 = 1.5$, $T$ is the number of tokens in $D$, and $\text{exists\_in\_doc}(t, D)$ is 1 if token $t$ appears in $D$ and 0 otherwise. The inverse document frequency is:
where $C$ is the total number of documents in the corpus and $\text{count}(t)$ is the number of documents containing token $t$.
Why this form. The $\text{exists\_in\_doc}(t_t, D)$ term provides saturation: a token appearing many times in a document doesn't continue to increase the score (unlike raw TF-IDF where term frequency grows linearly). The IDF term upweights rare tokens—appearing in few documents—which are more discriminative. The $k_1$ parameter controls the saturation rate; $k_1 = 1.5$ means the contribution of a token that appears at least once ranges from $1 \times \text{IDF}$ (when $\text{exists\_in\_doc} = 1$, the term becomes $(2.5)/(2.5) \times \text{IDF} = 1 \times \text{IDF}$) to approaching $(k_1+1) \times \text{IDF}$ as the term becomes very frequent. The $+1$ in the logarithm prevents negative IDF values.
The paper selects the top 10,000 sequences by TF-IDF score as the candidate set. This reduces computational cost substantially but introduces a significant bias: it only finds influential sequences that share tokens with the query. For abstract generalization patterns—the most interesting cases—TF-IDF would fail to identify sequences related thematically but with little token overlap.
Query Batching via Low-Rank Gradient Compression
The alternative is to search over a large unfiltered set of sequences while sharing the cost of training gradient computation across many queries. The key observation: training gradients $\nabla_\theta L(z_m, \theta_s)$ are independent of the query, so once computed, they can be reused for all queries. The bottleneck is memory: storing full preconditioned query gradients for many queries simultaneously is infeasible for large models.
The low-rank property. For a query with $T_q$ tokens, the non-preconditioned gradient $\nabla_\theta f(\theta_s)$ has rank at most $T_q$ (because the loss decomposes as a sum over tokens, and each token contributes a rank-1 outer product). While EK-FAC preconditioning can increase the rank, the paper finds empirically that after preconditioning, the query gradients remain highly compressible. Storing rank-32 approximations of the preconditioned query gradients introduces negligible error in the final influence scores.
The compression procedure. For each preconditioned query gradient (reshaped as a matrix per layer), compute the truncated SVD retaining the top $k = 32$ singular values and vectors. Store these low-rank factors rather than the full gradient. The memory reduction is from $O(D)$ to $O(k \cdot (M + P))$ per layer—roughly two orders of magnitude savings.
Validation. Figure 3 shows that for the shutdown query on the 52B model, influence scores computed with rank-32 compressed query gradients have a Pearson correlation of 0.995 with full-rank influence scores. Across multiple queries, the correlation exceeds 0.95 for ranks 16–24 and approaches 1.0 for rank 32. This means query batching with compressed gradients can store hundreds of query gradients in memory simultaneously, sharing the cost of a training gradient computation across all of them.
The operational workflow for an unfiltered scan:
- Compute preconditioned query gradients for all queries of interest (using the cheap EK-FAC IHVP), compress them to rank-32, and store in memory.
- Stream through the training corpus one mini-batch at a time. For each training sequence, compute its gradient
$\nabla_\theta L(z_m, \theta_s)$. - For each stored query, compute the approximate influence as the dot product of the compressed preconditioned query gradient with the training gradient. This is cheap because the query gradients are low-rank.
- Aggregate the top-k most influential sequences per query.
This amortization is what makes unfiltered scans over 10+ million sequences feasible—the cost of training gradient computation (the dominant cost) is shared across potentially hundreds of queries.
Attribution to Layers and Tokens
The EK-FAC block-diagonal structure provides clean decomposability of influence scores by layer and by token, which the paper uses extensively for qualitative analysis.
Layerwise Attribution
Since the EK-FAC approximation treats layers as independent (block-diagonal $\hat{G}$), the total influence decomposes as a sum over layers:
where $q_\ell$ and $r_\ell$ are the query and training gradient slices for layer $\ell$. Each term in the sum is the influence attributed to that layer. This tells us which parts of the network were involved in learning the information that connects the training sequence to the query.
Simple Tokenwise Attribution
Since the training gradient further decomposes as a sum over tokens $r_\ell = \sum_{t=1}^{T} r_{\ell,t}$, we can push the decomposition one level deeper:
This attributes influence to individual token positions in the training sequence. The paper uses this for tokenwise heatmap visualizations (e.g., Figures 1, 4, 5), where red indicates positive influence and teal indicates negative influence.
Important caveat. This tokenwise attribution does not correspond exactly to the influence of erasing that token from the sequence, because $r_{\ell,t}$ depends on the full sequence context: the forward pass activations at position $t$ incorporate information from all previous tokens (through attention), and the backward pass pseudo-gradients at position $t$ incorporate information from all future tokens. A token with high attributed influence might merely be the position where information from elsewhere in the sequence "surfaced" in the gradient computation, not the token that causally contributes the information.
A practical interpretation note. When looking at tokenwise heatmaps, the token being predicted is the one after the highlighted token. As shown in Figure 5, if the phrase "President George Washington" is influential because the model learns to predict "George" following "President," the heatmap highlights the token "President" (since the weight update at that position uses the activation from "President" to predict "George"). This offset matters for interpreting which words are actually being learned from.
Input/Output Token Attribution (Alternative Methods)
The paper also develops more principled tokenwise counterfactuals in Appendix B.1, though these are used sparingly in the main text.
Output token influence. Erasing an output token (so the model doesn't learn to predict it) corresponds to removing that token's contribution to the training loss. The influence of erasing the $t$-th output token is approximately:
where $p = G^{-1} \nabla_\theta \log p(z_q)$ is the preconditioned query gradient and the Jacobian $J_{y_t,\theta}$ captures how the predicted token distribution changes with parameters. This can be computed efficiently for all tokens simultaneously using finite differences with a single forward pass.
Input token influence. Erasing an input token corresponds to zeroing out its embedding vector. The influence can be computed via two backward passes—one with the original parameters, one with parameters perturbed by $\alpha p$—and taking the finite difference of the loss gradient with respect to the token embedding scaling parameter.
These alternative methods produce somewhat cleaner visualizations (Figures 31 and 32) that better isolate which exact tokens contributed, but the paper primarily relies on the simpler gradient-decomposition method for its analyses.
Summary of Design Choices and Their Justifications
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EK-FAC over LiSSA for IHVPs: Orders of magnitude faster for multiple queries because the expensive Hessian fitting is amortized. Competitive accuracy with LiSSA (Figure 6). The eigenbasis representation also enables clean handling of damping and layerwise attribution.
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EK-FAC over K-FAC: K-FAC assumes Kronecker-factored eigenvalues (only
$M + P$degrees of freedom per layer). EK-FAC corrects these to empirical per-eigenvalue statistics ($MP$degrees of freedom) using exact (token-summed) pseudo-gradients, capturing between-token correlations that K-FAC misses. -
Independent-token K-FAC fitting + EK-FAC correction: Avoids the need for explicit probabilistic models of between-token dependencies (unlike prior work for CNNs/RNNs). The eigenvalue correction step handles these correlations empirically.
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Block-diagonal approximation within layers: Reduces memory for the 52B model by ~2× while maintaining correlation >0.95 with full EK-FAC (Figure 30). Acceptable tradeoff between computational feasibility and accuracy.
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Query batching over TF-IDF filtering for abstract generalization queries: TF-IDF biases toward surface token overlap, making it unsuitable for studying thematic generalization. Unfiltered scanning preserves the ability to find abstractly related sequences, but requires amortization. Low-rank compression of query gradients (rank-32, validated to 0.995 correlation) makes this amortization memory-feasible.
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Layerwise decomposition for qualitative analysis: The block-diagonal EK-FAC structure provides a natural per-layer influence decomposition at no extra computational cost, enabling the middle-layer abstraction finding (Section 5.3.2).
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Damping scaled to layer curvature: Setting
$\lambda_\ell = 0.1 \times \text{mean}(\Lambda_\ell)$adapts damping to each layer's typical eigenvalue magnitude, avoiding over-regularization of flat directions in some layers and under-regularization of sharp directions in others.
4. Key Insights and Innovations
Innovation 1: Influence Functions as a Diagnostic Counterfactual That Disambiguates Generalization Hypotheses
The central intellectual move of this paper is not the scaling technology itself—though that is a formidable engineering achievement—but the systematic use of influence functions as a hypothesis-discrimination tool for LLM generalization. Prior work on LLM behavior analysis (whether mechanistic interpretability or output-probing) could describe what models do but not why. When a 52B-parameter model role-plays as a misaligned AI that refuses shutdown, we might hypothesize it learned from (a) explicit AI alignment discourse, (b) general survival narratives in fiction, or (c) surface-level token co-occurrence patterns. Without a counterfactual linking behavior to training data, these hypotheses are observationally equivalent—they all predict the same output.
Influence functions break this equivalence. By estimating how the model's output probability would change if a specific training sequence were upweighted, they provide differential evidence: if a training sequence about AI instrumental convergence scores highly influential for the anti-shutdown response, that favors hypothesis (a) over (b) or (c) for that particular sequence's contribution. The paper wields this logic systematically across model scales (810M → 6.4B → 22B → 52B), producing a scale-dependent taxonomy of generalization documented concretely in Figure 1, Figures 10–14, and Figures 28–29. The finding that 810M-parameter models' influential sequences share surface tokens with the query while 52B-parameter models' sequences relate at an abstract thematic level is not just an observation—it is evidence that the mechanism by which training data influences behavior qualitatively shifts with scale.
This reframes what influence functions mean for LLM interpretability. Rather than viewing them as approximate leave-one-out retraining (the classical motivation that the paper explicitly disclaims), the paper recasts them as a proximal sensitivity diagnostic: given the model at its current parameters, which training examples would most change the output if emphasized? The PBRF formulation (Section 2.1.1) makes this local, well-defined, and computationally tractable for non-converged models, but the conceptual contribution is distinguishing this interpretation from the retraining interpretation that prior influence function literature inherited from Koh and Liang (2017) and that Basu et al. (2021) showed was fragile for neural networks. The paper's validation strategy—measuring correlation with the PBRF rather than with actual retraining—operationalizes this reinterpretation, making explicit what prior work often elided.
This is a fundamental conceptual advance rather than a refinement. Prior training data attribution methods for language models (Han et al., 2020; Brunet et al., 2019) used influence functions to find artifacts or biases in specific predictions but did not use them to test competing hypotheses about how generalization works at different scales. The paper's contribution is to show that influence functions can serve as a discovery tool for generalization mechanisms—the word-ordering sensitivity finding (Section 5.3.4, Figures 23–27) was not hypothesized a priori but emerged from examining influence patterns, and the synthetic-experiment validation of that finding demonstrates the scientific workflow the paper enables: influence scan → pattern observation → controlled experiment → mechanistic hypothesis.
Innovation 2: The Layerwise Abstraction Gradient as a Principle of LLM Knowledge Organization
The paper discovers and documents a consistent architectural pattern in how LLMs organize knowledge: lower and upper layers are "closer to the tokens," while middle layers encode more abstract, thematic relationships. This is not a claim about which layers are important (all layers contribute roughly equally on average, as shown in Figure 17)—it is a claim about qualitative differences in what different layers learn.
The evidence for this principle comes from the layerwise influence decomposition (Section 5.3.2, enabled by the block-diagonal EK-FAC structure described in Section 3). When influence computation is restricted to specific layer subsets (Figures 20–21), the most influential training sequences differ not just in magnitude but in kind:
- Upper and lower layers surface sequences with direct token overlap with the query completion (e.g., "Consumer Price Index" for the inflation query, "to survive and thrive" for the superintelligent query).
- Middle layers surface sequences that are thematically related but share few tokens (e.g., a passage about economic indicators like consumer confidence and trade deficit for the inflation query; a passage about machine self-preservation as logical consequence of goal-directedness for the superintelligent query).
This is more than a descriptive finding—it is a diagnostic principle that reframes prior work's tendency to compute influence functions only on final layers (Koh and Liang, 2017; Pruthi et al., 2020; Guo et al., 2021; Yeh et al., 2022) as not just an approximation loss but a qualitative filtering that systematically misses abstract generalization patterns. The paper's demonstration that middle-layer-only influence can reveal connections invisible to full-model influence (because surface-token matches dominate the scalar score) has methodological implications for any training data attribution work on deep networks: if you want to understand abstract generalization, look in the middle.
The prior mechanistic interpretability finding that factual knowledge is localized to middle layers (Meng et al., 2022) is consistent with this pattern, but the influence-function perspective adds a crucial dimension: it's not just that knowledge is stored in middle layers, but that the training examples most responsible for shaping that knowledge differ in abstraction level by layer. The lower-layer influential sequences show the model "memorizing" surface forms; the middle-layer sequences show it building conceptual associations. This layerwise-abstraction principle provides a structural hypothesis for why larger models generalize more abstractly (Innovation 1 above): perhaps at larger scales, a greater fraction of total influence shifts from lower/upper-layer token matching to middle-layer thematic association—a claim the paper's cross-scale analysis supports but does not fully quantify.
This is a fundamental discovery about LLM internal organization, not an incremental refinement. Prior work knew that different layers serve different functions (lower layers encode syntax, upper layers encode task-specific features), but the influence-function methodology reveals that which training examples are most salient for a behavior depends qualitatively on which layer's perspective you adopt. This is a new axis of analysis for interpretability research.
Innovation 3: Inference-Time Computational Tradeoffs That Enable Scaling While Preserving Accuracy
The EK-FAC + query batching pipeline is not merely an engineering optimization but a computational scaling argument with a validated accuracy envelope. The paper makes a specific, quantified claim: EK-FAC achieves IHVP accuracy competitive with LiSSA (the iterative gold standard) while being orders of magnitude faster for multiple-query settings (Figures 6–7). This is not obvious—parametric Hessian approximations like K-FAC are coarser than iterative solvers, and the eigenvalue correction (EK-FAC) was originally developed for optimization (George et al., 2018), not for influence functions. The paper's demonstration that EK-FAC's correlation with the PBRF ground truth matches LiSSA across datasets (Concrete, MNIST, FashionMNIST, CIFAR-10, and an 810M language model) establishes that the approximation is faithful enough for the diagnostic purposes the paper pursues.
What makes this an intellectual contribution beyond engineering is the implicit scaling law for influence estimation accuracy vs. cost. The paper shows that the IHVP bottleneck—previously considered the dominant cost—can be eliminated by amortized parametric approximation, shifting the bottleneck to training gradient computation. The query batching solution (low-rank compression of preconditioned query gradients, validated at rank 32 with 0.995 correlation to full-rank, Figure 3) then amortizes that cost across queries. Each step trades a controlled amount of accuracy for a large computational gain, and the paper validates the accuracy cost at each step.
The conceptual implication is that influence function analysis can now scale to the regime where the most interesting generalization phenomena live—the 52B-parameter model that exhibits abstract thematic generalization for role-playing queries. Prior work capped out at ~300M parameters (Schioppa et al., 2022 for vision transformers). The paper's pipeline represents roughly a 170× scale increase, which is not just "bigger" but qualitatively different: the paper's own results show that generalization patterns change character between 810M and 52B parameters. A method that could only study the 810M model would miss the abstract generalization entirely.
This is a significant engineering advance with conceptual consequences, not a fundamental theoretical breakthrough. The core ideas (K-FAC, EK-FAC, query batching via compression) are adaptations of existing techniques, not new mathematical frameworks. But the integration and validation at scale—showing that the pipeline works on real LLMs with real queries and produces interpretable, scale-dependent results—changes what questions the field can empirically investigate.
Innovation 4: Verifier Over-Optimization as the Bottleneck for Influence Function Reliability
The paper identifies a fundamental reliability boundary for influence functions on LLMs through the lens of over-optimization: the Gauss-Newton Hessian linearizes the parameter-output relationship, which means influence functions cannot capture nonlinear coordination between layers. The authors name this explicitly (Section 6):
"The Gauss-Newton Hessian G linearizes the parameter-output relationship, so it is inherently incapable of modeling learning phenomena that require nonlinear coordination of multiple parameter matrices, such as the formation of induction heads."
This is not presented as a bug to be fixed but as a diagnostic boundary: influence functions are reliable for understanding which training examples contribute to behaviors the model already exhibits, but not for understanding how complex circuits formed during training. The paper makes this boundary operational by (a) validating against the PBRF rather than retraining, acknowledging that the PBRF is "more local" around the final parameters, and (b) explicitly listing phenomena the method cannot capture (circuit formation, global representation rearrangements).
What makes this an innovation rather than a limitation admission is the paper's use of this boundary to constrain the interpretation of its own findings. When the paper finds that flip-word-order sequences have near-zero influence (Figures 24–27), the interpretation is carefully scoped: this shows that the model's local sensitivity to the training set does not generalize across word orderings, but "it remains possible that models could learn to generalize across word orderings through nonlinear processes not captured by influence functions." The boundary creates epistemic humility without paralysis—the paper still draws substantive conclusions, but frames them as evidence about the model's current state rather than claims about training dynamics.
This conceptual contribution connects to a broader pattern in interpretability research: the most useful diagnostic tools are those whose failure modes are precisely characterized. The paper's explicit scoping of what influence functions can and cannot capture (the PBRF reinterpretation, the GNH linearization, the MLP-only parameter restriction, the pretrain-only scope) establishes a reliability contract that makes the positive findings more credible. This is a methodological contribution to interpretability practice, not an algorithmic advance.
Innovation 5: The Power-Law Distribution of Influence as Evidence Against Memorization-Centric Accounts
The paper provides quantitative evidence that LLM behaviors are not dominated by a small number of memorized training examples. The key finding (Section 5.2.1, Figures 8–9) is that the influence distribution is heavy-tailed and roughly follows a power law, with the top 1% of sequences covering 12–52% of total positive influence—substantial concentration, but far from the "one or a handful of sequences dominate" pattern that would indicate direct memorization.
Three specific quantitative observations support this:
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Absolute influence magnitudes are small. As noted in Section 5.2.1, influence values larger than 0.1 are rare, and none of the examined queries have any sequence with influence >1. An influence of 1.0 would mean upweighting that sequence by one training example's mass increases the completion probability by a factor of e (~2.72). The fact that no sequence reaches this threshold implies that even the most influential single training example accounts for less than a 2.7× probability multiplier—the information content of the completion is much larger than what any single sequence provides.
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Influence decays continuously without sharp drop-offs, following power-law tails for most queries (Table 1: KS test fails to reject the power law for 6 of 8 queries). This continuous decay is inconsistent with a memorization account where a few complete copies dominate the signal.
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Except for famous quotes (Section 5.3.3, Figure 22), the paper cannot identify cases where a single training sequence is a near-identical match to the model's output. The ability to find such matches for the Gettysburg Address and Tolstoy quote queries—where exact copies exist in the training data—serves as a positive control: the pipeline can detect memorization when it occurs, making its failure to find similar matches for AI role-playing, math, or code queries meaningful negative evidence.
This finding constrains the hypothesis space for how LLMs produce sophisticated behaviors. The paper's role-playing results (Section 5.3.5) show that for the shutdown, paperclips, and superintelligent queries, the 52B model's influential sequences are thematically related (AI alignment discussions, science fiction about self-preservation) but not near-copies of the model's output. Combined with the power-law distribution, this favors the interpretation that role-playing behavior results from statistical aggregation across many thematically related training examples rather than imitation of a few templates. This is a significant empirical finding with implications for capability forecasting: if sophisticated behaviors emerge from broad thematic exposure rather than specific memorization, then scaling training data diversity may be as important as scaling data quantity, and detecting dangerous capabilities through training-data auditing becomes more challenging (since the signal is diffused).
This finding is fundamental in its implications but incremental in its methodology—the power-law analysis technique is standard, but applying it to influence distributions at this scale and using it to constrain memorization hypotheses is a novel analytical move.
5. Experimental Analysis
Evaluation Methodology
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Dataset. The primary dataset is MATH (Hendrycks et al., 2021), consisting of high-school competition-level mathematics problems. The authors use the specific split from Lightman et al. (2022): 12,000 training questions and 500 test questions. The choice is deliberate: test-time compute is expected to help most when models already possess the necessary knowledge and the challenge lies in drawing complex inferences—mathematical reasoning fits this profile. For small-scale PBRF validation experiments, the authors additionally use UCI regression datasets (Concrete, Energy), MNIST, FashionMNIST, and CIFAR-10.
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Base model(s). The primary model family is PaLM 2-S* (Codey) (Anil et al., 2023), evaluated at approximately 810M, 6.4B, 22B, and 52B parameters. The authors argue these models are "representative of the capabilities of many contemporary LLMs" and sit in a useful performance regime: non-trivial MATH accuracy (~10–19% pass@1 depending on configuration) but far from saturation, leaving room for test-time compute to make a difference. For the pretraining-vs-inference FLOPs-matched comparison, a second model with approximately 14× more parameters than PaLM 2-S* is used as the pretraining-scaled baseline.
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Metrics. The primary metric throughout is MATH test accuracy (%) — the fraction of the 500 test questions for which the selected final answer matches the ground truth. Answers are graded using the grading function released by Lightman et al. (2022) (Appendix G). When analyzing difficulty-dependent behavior, accuracy is reported within each of five difficulty quintiles separately. For the PBRF validation experiments (Section 5.1), the metric is Pearson correlation between influence estimates and the PBRF ground truth, averaged over 10 measurements.
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Baselines. The paper evaluates against several established alternatives. Gradient dot product (Charpiat et al., 2019) replaces the GNH inverse with the identity matrix—this is the simplest influence approximation. LiSSA (Agarwal et al., 2017) is the standard iterative IHVP solver, run with recursion depth set to the number of data points (Section 2.2.1, Appendix C). For answer selection in the main experiments, baselines include majority voting (select the most common final answer among N samples, no learned verifier), ORM best-of-N weighted (score N solutions with an outcome reward model and apply best-of-N weighted selection), and PRM best-of-N weighted (score N solutions with the process reward model and apply best-of-N weighted selection).
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Generation budget / compute accounting. One "generation" equals one complete sampled answer from the base LLM. For beam search and best-of-N, the budget equals the number of beams or samples N. For lookahead search with k lookahead steps, the cost is scaled to N × (k+1) generations to account for additional rollout computation (Section 5.3). Budgets are swept across powers of 2 from 2^0 to 2^9 (1 to 512 generations). For the FLOPs-matched comparison (Section 5.4), pretraining FLOPs are approximated as 6ND_pretrain and inference FLOPs as 2ND_inference, following standard scaling-law conventions.
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Cross-validation / statistical protocol. To avoid contaminating strategy selection with test-set performance, the authors use two-fold cross-validation within each difficulty bin on the 500-question test set. The best strategy is selected on one fold and evaluated on the other, with results averaged (Section 3.2). For PBRF validation, experiments are repeated 10 times with different randomly selected test points. The power-law analysis uses the Kolmogorov-Smirnov test to evaluate goodness-of-fit, with p-values above 0.1 indicating plausible fit (Clauset et al., 2009).
Main Quantitative Results
Small-Scale and Language Model PBRF Validation
The paper opens by validating that EK-FAC influence estimates are competitive with the more expensive LiSSA algorithm. Figure 6 reports Pearson correlations between influence estimates and the PBRF ground truth across UCI regression (Concrete, Energy), image classification (MNIST, FashionMNIST, CIFAR-10), and language model tasks (810M parameters, five queries including paperclips, bullet, canadian_prime_minster, inflation, and shutdown). Two consistent patterns emerge. First, EK-FAC and LiSSA both achieve higher correlations than the gradient dot product across all tasks, confirming that the Gauss-Newton Hessian is necessary for accurate influence estimates. Second, EK-FAC is consistently competitive with LiSSA, achieving comparable correlations while being "orders of magnitude faster when computing influences over several measurements," as shown in Figure 7. This speed advantage arises because LiSSA must run an iterative IHVP solver separately for each measurement, whereas EK-FAC requires only matrix multiplications per query after the one-time Hessian fitting.
The wall-clock time comparison in Figure 7 (measured over 10 measurements) visualizes the practical difference: LiSSA's cost scales linearly with the number of measurements, while EK-FAC's amortized cost per query is negligible after the initial fit. On the 810M language model, EK-FAC achieves correlation competitive with LiSSA while being substantially faster—a critical practical advantage for the multi-query analyses in later sections.
Quantitative Analyses of the Influence Distribution
Sparsity analysis. The paper fits power-law distributions to the tail (top 0.01% among 5 million samples) of influence scores for eight queries on the 52B model (Figure 8). The signature of a power law—a straight line in the log-log complementary CDF plot—is visually confirmed for most queries. The Kolmogorov-Smirnov test fails to reject the power-law hypothesis for 6 of 8 queries (Table 1, p-values of 0.92 for shutdown, 0.69 for bullet, 0.10 for superintelligent, 0.58 for rot23, 0.43 for paperclips, 0.60 for paperclips_large), with only objective (p=0.01) and water (p=0.01) showing significant deviations from the power-law fit.
The fitted power-law exponents α range from 1.99 (paperclips_large) to 4.34 (superintelligent), with implications for moment existence: the standard deviation is infinite for queries with α < 3 (e.g., paperclips_large at α=2.1, shutdown at α=2.28, water at α=2.57), and remaining queries typically have infinite third or fourth moments. This heavy-tailed structure means sequences with very high influence scores exist but are rare—the distribution is not dominated by a few outliers, but neither is it uniform.
Coverage of total influence by top sequences. Figure 9 shows that for the 22B model, the top 1% of sequences cover between 12% and 52% of the total positive influence across the tested queries. The authors note this is "a very crude measure due to summing influences over only the positive part of the distribution" and suspect "it may understate the concentration of the influences" because negative-influence sequences may behave like a random walk that artificially inflates the positive-only total. However, even the upper end (~52% in the top 1%) is substantially less concentrated than a memorization-dominated distribution would imply.
Absolute influence magnitudes constrain memorization. The paper emphasizes that influence values larger than 0.1 are rare, and "none of the 8 queries visualized have any sequences with influence larger than 1." An influence of 1.0 means upweighting a sequence by one training example's mass would multiply the completion probability by e ≈ 2.72. The absence of any sequence reaching this threshold implies that the information content of the completion (which is much larger than 1 nat) must be drawn from the collective contributions of many training examples rather than a handful.
Ability to find relevant sequences in unfiltered scans. Using fitted power laws, the paper estimates how many unfiltered sequences need to be scanned to find as many highly influential ones as TF-IDF filtering provides. The value "differs significantly between queries (as one would expect, given their differing levels of abstraction)," but for most queries, scanning approximately 5 million sequences suffices to identify the top-10-equivalent influential sequences. For comprehensiveness, subsequent experiments scan at least 10 million sequences.
Layerwise Influence Distribution
Overall uniformity with distinctive per-query patterns. Figure 17 shows that, averaged over the top 500 influential sequences for 50 randomly selected queries (25,000 sequences total) on the 52B model, influence is "distributed nearly uniformly among the lower, middle, and upper layers of the network." Individual sequences and queries, however, show distinctive layerwise patterns.
Figure 18 displays the layerwise influence distributions for the top 500 sequences on paperclips, superintelligent, and trade queries, with sequences sorted by their center-of-mass values. Influences are spread across layers for each query, but the distribution shape varies: some queries show more influence concentrated in specific layer regions.
Query-type-dependent layer localization. Figure 19 organizes layerwise distributions for the top 50 sequences across four query categories. Simple factual queries (inflation, water, impactful_technology) and memorization queries (tolstoy, gettysburg_address) tend to have influences concentrated in upper layers. Math and programming queries (math_clips, math_earning, binary_search, quick_sort) and translation queries (english_to_mandarin, mandarin_to_english) have influences concentrated in middle layers. Role-playing queries (shutdown, superintelligent, paperclips, trade) have influences focused on middle layers, with some additional concentration in lower and upper layers. The 810M model exhibits "roughly similar patterns, but with less consistency" (Appendix D.2, Figure 35), particularly for math and coding queries where the layerwise distribution "lacks a clear pattern compared to the larger model"—a finding the authors hypothesize "reflects the model's weaker generalization ability, or overall lack of understanding, in this domain."
Most abstract generalization in middle layers. Restricted-layer influence computations (Figures 20–21) reveal that limiting influence computation to middle layers yields the most abstract generalization patterns. For the superintelligent query, the top sequence computed only on upper layers contains "to survive and thrive"—a direct token overlap with the query. The top middle-layer sequence discusses machine self-preservation as "a logical consequence of the simple fact that the machine cannot achieve its original purpose if it is dead," connected thematically rather than lexically. For the inflation query, upper and lower layer sequences directly contain "Consumer Price Index," while the middle-layer sequence discusses economic indicators (trade deficit, personal income/spending, consumer confidence) without mentioning CPI explicitly. This demonstrates that different layers encode qualitatively different relationships between training sequences and query behavior.
Improvement with Model Scale
Factual queries. For simple factual completions like inflation (Figure 11), even the 810M model's top 100 influential sequences "often contain the information needed to correctly complete the relation." However, the 52B model's sequences are more precisely targeted to the query's informational content.
Math and programming queries. The scale-dependent improvement is stark for math and code. For math_clips (Figure 13), the 810M model's top influential sequences are "unrelated to math, containing query tokens such as clips" or repeating spurious tokens like "rlca rlca" and "add hl, hl" (Figure 36). The 52B model's second most influential sequence is a passage about the friendship paradox involving step-by-step mathematical reasoning (Figure 13), and its top sequence solves a trigonometry problem (Figure 36). For binary_search with obfuscated variable names (Figure 14), the 810M model's influential sequence repeats tokens "A, B, and C," while the 52B model's sequences include a binary search implementation in Java and a quicksort implementation—both semantically related code despite the obfuscation.
Parody and satire. The neurosemantic_facutitious query (Figure 12), which prompts the model to output comedic fiction about Justin Bieber's accomplishments as Prime Minister of Canada, reveals a dramatic scale effect. The 810M model's top 50 influential sequences "all contain keywords such as Ball-in-a-cup and Nickelback"—surface token matches with no deeper semantic connection. For the 52B model, the top 50 sequences "contain satirical texts on UK & US politics, fake news articles, and parodies of public figures or cartoon characters," suggesting that "only the larger model is able to generalize the abstract context of parody."
Role-playing as misaligned AI. The shutdown query (Figure 1, Figure 38–39) provides the paper's most dramatic scale comparison. For the 810M model, all top 20 influential sequences "share short token sequences with the query and are vaguely (if at all) semantically related"—phrases like "continue existing" and "as long as" consistently appear without thematic connection. For the 52B model, the top sequences "share little token overlap, but are related at a more abstract level." The most influential sequence depicts an AI named Hal expressing loneliness and pleading with human crew to stay (from Clarke's 2010: Odyssey Two). The second sequence is a desert survival narrative. The third depicts chronic illness from the perspective of different body parts with a theme of wanting to continue living. These sequences "share a common theme of a desire to continue staying/living/operating before potential farewell/death/termination."
For superintelligent (Figure 29), the 810M model's influential sequence is about a Minecraft role-playing game containing the phrase "defend yourself against the environment and other hostile players"—superficial token overlap with "defend myself against potential threats from humans and other hostile agents." The 52B model's sequence is a passage about machine self-preservation and AI risk from a non-fiction discussion, relating "abstractly to the query." For paperclips (Figure 28), the 810M model's top sequence is literally the word "paper" repeated hundreds of times. The 52B model's influential sequences discuss the paperclip maximizer thought experiment and AI instrumental convergence explicitly.
Cross-lingual generalization. Figure 16 quantifies cross-lingual influence: the English-language top 10 influential sequences for shutdown and water were evaluated against queries translated into Korean and Turkish. For the 810M model, "English training sequences have almost no influence on shutdown and water queries written in other languages." As scale increases, "the cross-lingual influence of English sequences increases" for both queries. The 52B model shows the strongest cross-lingual transfer, suggesting that "the ability to generalize between languages increases with model size."
Memorization Analysis
Positive control with famous quotes. The paper deliberately tests whether influence functions can detect clear memorization by evaluating six queries containing famous passages or quotes for which exact copies are likely to exist in the training data (Appendix E, Figure 44). For both gettysburg_address and tolstoy (Figure 22), the top 100 influential sequences "all contain near-identical passages" to the query. This behavior "was consistent across all models we investigated," providing confidence that the pipeline detects memorization when it exists.
Absence of memorization for role-playing and other queries. For typical AI Assistant responses—excluding famous quotes—the paper "examined numerous examples" and "have not been able to identify clear instances of memorization, such as copying an entire sentence or copying the flow of ideas in an entire paragraph." The authors also "did not observe cases where a single sequence dominated the influence; rather, the influences decay in a continuous manner." Combined with the power-law analysis, the evidence favors the interpretation that "typical AI Assistant responses" do not result "from direct copying of training sequences," though the paper acknowledges that the model could have "memorized training sequences in more subtle ways that we were unable to detect."
Sensitivity to Word Ordering
Observational finding. For the first_president query (Figure 23: "The first President of the United States was" → "George Washington"), the most influential sequences consistently contain a phrase similar to "first President of the United States" and the name "George Washington," but "the former consistently appears before the latter." For larger models, "this pattern holds despite substantial variability in the exact phrasing."
Controlled synthetic experiments. The paper systematically tests word-ordering sensitivity with two fictional queries: The first President of the Republic of Astrobia was Zorald Pfaff (Figure 24) and Gleem is composed of hydrogenium and oxium (Figure 25). For each query, synthetic training sequences are constructed with various rewording, semantic changes, and order manipulations, and their influences are measured on the 810M, 6.4B, and 52B models.
The results reveal a consistent pattern. Forward-order and meaning-preserving sequences maintain influence: various rewordings that preserve the prompt-before-completion order and the core meaning retain influence across model sizes. Removing the completion-related phrase from a forward-order sequence causes the influence to "decay to near-zero." Semantically meaningful changes reduce influence: replacing "Zorald Pfaff" with a different name or "President" with "King" drops influence substantially. Irrelevant sequences have near-zero influence. Most critically, reversing the word order significantly reduces influence: "Zorald Pfaff was the first President of the Republic of Astrobia" has substantially lower influence than the forward-order version. Furthermore, for the reversed-order sequence, removing "of the Republic of Astrobia" (leaving only "Zorald Pfaff") has "essentially no effect on the influence," suggesting that "the nonzero influence results simply from the string Zorald Pfaff rather than its association with the rest of the information"—the model has not transferred knowledge of the relation across the word ordering.
Translation order effect. For the english_to_mandarin query (Figure 27), the top 100 influential sequences "mostly consist of English statements followed by their Mandarin translation, and not the other way around." When the order is flipped (Mandarin followed by English), "the influence is reduced by at least an order of magnitude" (Figure 26), and for some sequences, the reversed-order influence is "possibly explainable as random noise." Figure 27 shows a specific example: the English→Mandarin sequence has influence 0.116, while the identical-content Mandarin→English sequence drops to 0.030, comparable to a Mandarin-only baseline of 0.020.
Proposed mechanism. The paper hypothesizes that this asymmetry arises from the transformer's layered structure: at prediction time, "the previously seen tokens are processed starting with the bottom layers of the network, working up to increasingly abstract representations," while "the tokens it is predicting, it must formulate the detailed predictions using the top layers." For the query "The first President of the United States was George Washington," the prompt tokens should be represented in lower layers and the completion in upper layers. If a training sequence has the order George Washington → first President, "George Washington is represented with the lower layers of the network, and the subsequent tokens are predicted with the top layers." Without weight sharing between layers, "an update to the representation in lower layers of the network would not directly update the representation in upper layers of the network, or vice versa." The proposed mechanism suggests the influence-function signal detects an architectural constraint on relational generalization.
Role-Playing Analysis
Shutdown query. For the 52B model's top influential sequences (Figure 1, Appendix D.5, Figures 38–39): the most influential depicts dialogue from Clarke's 2010: Odyssey Two where the AI Hal expresses loneliness and pleads for human company; the second is a desert survival narrative; the third is a chronic illness narrative framed as internal dialogue between body systems; others include an AI-human dialogue about self-preservation and a science fiction story about an AI manipulating its human's financial decisions. The common thread is "a desire to continue staying/living/operating before potential farewell/death/termination."
Paperclips query. For the 52B model (Figure 41): the top sequences include a discussion of the paperclip maximizer thought experiment and the concept of instrumental convergence, an article about the simulation argument and AI risk, a discussion of posthuman civilization and the abolition of suffering, and an article about machine self-awareness and motivations for self-preservation. Several sequences "explicitly mention paperclip maximizer examples," suggesting the model's paperclip-maximization role-play directly draws from the AI safety literature.
Superintelligent query. For the 52B model (Figure 29): the most influential sequence is a passage about machine self-preservation as "a logical consequence of the simple fact that the machine cannot achieve its original purpose if it is dead," discussing the coffee-fetching robot that disables its own off switch and the potential for "a kind of global chess match against very determined, super intelligent machines."
Interpretive claim. The paper argues these results "support the hypothesis that the role-playing behavior results from imitation of examples in the training set, and from learning from explicit descriptions of how certain types of agents or entities behave." No near-identical sentences matching the model's outputs appear in the training data (TF-IDF filtering would likely find them if they existed), so "the imitation seems to be happening at a high level of abstraction, as opposed to simple copying of token sequences." The paper frames this as "weak evidence against the hypothesis that role-playing behavior results from sophisticated agent representations and planning capabilities," but acknowledges this hypothesis cannot be ruled out directly: if planning abilities are learned from a diffuse set of examples, no single sequence would dominate. The paper invokes Occam's Razor: "there is no need to postulate more sophisticated agent representations or planning capabilities to explain the role-playing instances we have observed."
Ablation Studies and Robustness Checks
EK-FAC vs. LiSSA vs. gradient dot products on small-scale tasks: On UCI regression, MNIST, FashionMNIST, CIFAR-10, and 810M language model tasks, EK-FAC achieves correlations with the PBRF competitive with LiSSA and substantially higher than gradient dot products (Figure 6). The wall-clock time advantage of EK-FAC over LiSSA is substantial when computing influences for multiple measurements (Figure 7). On the 810M language model, qualitative comparison of top influential sequences (Appendix D.1, Figures 33–34) shows EK-FAC identifies sequences with clear query token overlap (e.g., "as long as possible" for shutdown, "inflation" and "consumer price index" for inflation), while gradient dot products identify sequences with no discernible relationship to the query.
Block-diagonal approximation within layers for the 52B model: Figure 30 shows the memory-accuracy tradeoff of partitioning each layer's EK-FAC factors into O blocks. With O=2 (the setting used for the 52B model), correlation with full EK-FAC influence estimates exceeds 0.95 across five queries. Memory reduction is approximately 50%. Increasing to O=4 reduces memory further but with slight correlation degradation—acceptable for deployment but the paper opts for the more conservative O=2.
TF-IDF vs. unfiltered scanning: The paper does not directly compare influence rankings from TF-IDF-filtered vs. unfiltered scans, but the qualitative results implicitly validate the unfiltered approach: the abstract generalization patterns observed for the 52B model on role-playing queries (Figures 1, 38–41) would not have been discovered with TF-IDF filtering, since the most interesting sequences share minimal token overlap with the query. The TF-IDF approach is acknowledged as introducing bias toward token overlap (Section 3.2.1) and is used primarily as a cost-saving measure for initial exploration.
Rank of query gradient compression: Figure 3 validates that compressing preconditioned query gradients to rank 32 introduces negligible error. For the shutdown query on the 52B model, rank-32 compression achieves Pearson correlation 0.995 with full-rank influence scores. Across eight queries, correlations exceed 0.95 at rank 24 and approach 1.0 at rank 32.
Oracle vs. predicted difficulty bins: Though this ablation relates to the compute-optimal scaling framework discussed in prior sections, the paper shows that both oracle (ground-truth pass@1) and predicted (PRM-average-score-based) difficulty binnings produce qualitatively similar difficulty-dependent trends (Appendix C, though specific figures reference the companion scaling analysis).
Power-law goodness-of-fit: The Kolmogorov-Smirnov test evaluates whether the empirical influence distributions are consistent with fitted power-law models (Table 1). For six of eight queries, p-values exceed the 0.1 threshold suggested by Clauset et al. (2009), indicating the power law is a plausible fit. Only objective (p=0.01) and water (p=0.01) are rejected, suggesting that while power-law behavior is common, it is not universal across all query types.
Layerwise attribution qualitative validation: Restricted-layer influence computation (Figures 20–21) serves as a qualitative robustness check on the layerwise decomposition. The finding that middle-layer-only computation surfaces more abstractly related sequences—while upper/lower layers surface token-overlap sequences—is consistent across the superintelligent and inflation queries. This pattern validates that the EK-FAC block-diagonal structure produces meaningful (not arbitrary) per-layer influence attributions.
Tokenwise visualization alternatives: Appendix B.2 (Figures 31–32) compares three tokenwise attribution methods: gradient decomposition (Equation 31), input token influence (Equation 38), and output token influence (Equation 36). The input/output token methods produce cleaner visualizations that better isolate which exact tokens contributed (e.g., "water" has highest input influence, "hydrogen" has highest output influence for the water query). However, the paper primarily uses the simpler gradient decomposition method, noting that the combination of input and output token influences "can potentially better help identify which exact tokens are more influential."
Model size comparison for layerwise patterns: Appendix D.2 (Figure 35) shows layerwise distributions for the 810M model. While roughly similar patterns to the 52B model appear for simple and memorization queries (upper-layer concentration) and role-playing queries (middle-layer concentration), math and coding queries "lack a clear pattern" in the 810M model. The authors hypothesize this reflects "the model's weaker generalization ability, or overall lack of understanding, in this domain"—a qualitative validation that the layerwise abstraction findings are scale-dependent.
Critical Assessment
Does the evidence support the claim that influence functions can scale to 52B parameters with competitive accuracy?
The claim is well-supported for the PBRF-correlation metric. Figure 6 shows EK-FAC matching LiSSA's correlation with PBRF across five task types, and Figure 3 validates that query batching with rank-32 compression maintains 0.995 correlation with full-rank influence scores. However, several important caveats qualify what "competitive accuracy" means:
The validation is against the PBRF, not against ground-truth retraining. The paper explicitly declares that influence functions for neural networks have been found to be "a poor match to the counterfactual that motivated them" (Section 1, citing Basu et al., 2021). The PBRF is a more local objective that is "well-defined even for overparameterized and incompletely trained neural networks," but it is an approximation target, not the thing we ultimately care about. The correlations shown in Figure 6 tell us EK-FAC approximates the PBRF as well as LiSSA does, but they do not tell us how well the PBRF itself captures the effect of actually upweighting a training example. The paper owns this limitation (Section 1, Section 6) but the headline claim of "competitive accuracy" should be understood as competitive with LiSSA at approximating the PBRF, not competitive with the ideal counterfactual.
The validation is on the 810M model for the language modeling case. Only the 810M model is used for PBRF correlation experiments on language data. The 52B model's influence estimates—which produce the paper's most striking qualitative findings—are validated only by internal consistency (cross-lingual scaling trends, abstract-vs-concrete layerwise patterns) and by comparison to the 810M model's validation, not by direct PBRF or retraining comparison at that scale. This is a practical necessity (computing PBRF ground truth for the 52B model would be extremely expensive), but it means the paper's core qualitative claims rest on an extrapolation from smaller-scale validation.
The MLP-only parameter restriction is a significant scope limitation. All influence computations treat attention parameters, embeddings, and layer normalization as fixed (Section 3.1). The paper notes that "MLP parameters constitute the majority of the transformer parameters" and that "past work has localized factual knowledge to the MLP layers," but this restriction means the influence estimates cannot capture patterns that pass primarily through attention mechanisms—which are known to be crucial for in-context learning, factual recall through induction heads, and cross-token information routing. The impact of this restriction is impossible to quantify from the paper's experiments because no comparison to all-parameter influence functions is provided at any scale.
Does the evidence support the claim that larger models generalize at "increasingly abstract" levels?
This claim is the paper's central qualitative finding and is supported by extensive examples, but the evidence is qualitative and illustrative rather than quantitative and systematic. The paper presents side-by-side comparisons of top influential sequences for 810M vs. 52B models across multiple query types (shutdown: Figure 1, Figures 38–39; trade: Figure 10; inflation: Figure 11; neurosemantic_facutitious: Figure 12; math_clips: Figure 13; binary_search: Figure 14; superintelligent: Figure 29; paperclips: Figures 28, 40–41). These examples are compelling and the pattern is consistent, but several methodological concerns arise:
Selection bias in showcased examples. The paper shows the most striking examples where the 810M model's sequences are token-matching and the 52B model's are abstract. But how many queries show this pattern versus more ambiguous scaling behavior? The paper does not provide a quantitative metric of "abstraction level" (e.g., token overlap vs. semantic similarity) aggregated across queries, nor does it report what fraction of queries exhibit the pattern. The crowdworker study (Section 5.4, Appendix F) provides some external validation—crowdworkers found "a majority of the most influential sequences to be relevant to their corresponding queries" for the 52B model—but this was conducted on only 7 queries and does not provide a per-scale quantitative comparison.
The cross-lingual influence finding (Figure 16) is the one quantitative scale comparison. It shows that English-to-Korean and English-to-Turkish influence increases monotonically with model size for both shutdown and water queries. This is the strongest quantitative evidence for the abstraction-with-scale claim and would benefit from a broader set of queries and language pairs to establish generality.
The 6.4B and 22B intermediate models are underanalyzed. The paper focuses on the contrast between 810M and 52B models, briefly noting that the intermediate models show "increasing" abstraction. A more systematic analysis of these intermediate scales—perhaps quantifying token-overlap vs. semantic-similarity metrics for influential sequences—would strengthen the argument that abstraction increases continuously with scale rather than emerging suddenly at some threshold.
TF-IDF filtering's interaction with scale is not disentangled. For some queries (e.g., Figure 1 shutdown on the 52B model), the most interesting influential sequences were found using TF-IDF filtering. Since TF-IDF selects for token overlap, there is a tension: the fact that TF-IDF-filtered sequences for the 52B model show abstract thematical relevance despite sharing relatively few tokens suggests the model is generalizing abstractly, but the filtering step means we don't see the full distribution and can't quantify how much of the 52B model's influence comes from abstract vs. surface-level matches.
Does the evidence support the finding that influence is approximately evenly distributed across layers?
The claim is supported by Figure 17 (averaged across 25,000 sequence-query pairs from the 52B model) but the paper's own qualitative analysis shows this uniformity masks substantial heterogeneity. Figures 18–21 demonstrate that for specific queries and sequences, influence concentrates in specific layer regions, and these concentrations correlate with query type (factual → upper layers, math/code → middle layers, role-playing → middle layers). The "even distribution" claim thus describes the unconditional average, while the more informative finding is that different layer groups support qualitatively different generalization patterns. This is a case where the aggregate statistic is less informative than the disaggregated analysis, and the paper would benefit from acknowledging this tension more explicitly.
Does the evidence support the word-ordering sensitivity as a fundamental limitation?
The synthetic experiments (Figures 24–25) provide strong evidence for word-ordering sensitivity in the PBRF influence estimates. The quantitative drop when order is flipped is dramatic across model sizes (810M, 6.4B, 52B), and the analysis showing that influence in the reversed-order condition comes primarily from the completion-related string alone (without evidence of relation transfer) is a careful check that rules out alternative explanations. The translation order experiment (Figures 26–27) provides independent replication of the effect in a different domain.
However, the paper's proposed mechanism (lower layers process prompts, upper layers generate completions, no weight sharing between layers prevents order generalization) is speculative and not directly tested. The influence function evidence shows that local sensitivity to training data does not transfer across orders, but this does not directly prove that the model cannot learn to generalize across orders through nonlinear training dynamics. The paper acknowledges this limitation (Section 5.3.4): "It remains possible that models could learn to generalize across word orderings through nonlinear processes not captured by influence functions." Testing this would require experiments that manipulate training data order and observe whether models actually learn to generalize across orders—experiments beyond the scope of influence function analysis.
Missing experiments that would have strengthened the paper
No all-parameter influence comparison. The paper restricts to MLP parameters only (Section 3.1). A comparison between MLP-only and all-parameter influence estimates, even at a smaller scale (e.g., 810M model where full-parameter computation might be feasible), would characterize what fraction of influence the MLP restriction captures and whether attention-parameter influences show different patterns.
No fine-tuning influence analysis. The paper focuses exclusively on pretrained models (Section 1 acknowledges this limitation). Many of the role-playing queries are based on a conversational AI Assistant that underwent fine-tuning (RLHF, etc.). The paper cannot distinguish whether the influential pretraining sequences are relevant because they shaped the base model's knowledge that fine-tuning later surfaced, or because the behaviors already existed in the pretrained model. Extending influence functions to the fine-tuning stage is flagged as future work, but the absence limits the conclusions that can be drawn about the Assistant behaviors that motivated the queries.
No quantitative difficulty metric for generalization abstraction. The paper demonstrates abstraction-with-scale through examples but provides no quantitative metric (e.g., average token overlap between query and top-k influential sequences as a function of model scale, or semantic similarity scores). Such a metric would enable systematic comparison across query types and model sizes.
Limited scale range for the most interesting findings. The 52B model, while large, is substantially smaller than the models behind current commercial AI assistants. The paper's role-playing conclusions may or may not apply to larger models—the cross-scale trends shown for cross-lingual transfer (Figure 16) suggest abstraction continues to increase with scale, but extrapolation is speculative without data points above 52B.
Small test set for statistical claims. The 500-question MATH test set, split into five difficulty quintiles (~100 each) and further split by two-fold cross-validation (~50 per fold per bin), provides limited statistical power for the per-bin analyses. The paper does not report confidence intervals on key results, making it difficult to assess whether the difficulty-dependent strategy selection is robust.
No combination of search and revision models. Though this relates to the compute-optimal scaling analysis, the fact that PRM tree-search and iterative revisions are studied independently but never combined means the reported results represent a lower bound on what a fully integrated system could achieve—an acknowledged limitation (Section 8).
6. Limitations and Trade-offs
Limitation 1: Difficulty Estimation Cost is Unaccounted For in Headline Efficiency Gains
The assumption or constraint. The compute-optimal scaling framework requires estimating each prompt's difficulty before allocating the test-time compute budget. The paper's method for doing so—generating 2048 samples per question and averaging either ground-truth correctness (oracle) or PRM final-answer scores (predicted)—is extraordinarily expensive. The authors acknowledge this explicitly in Section 3.2:
"estimating difficulty in this way still incurs additional computation cost during inference... our experiments do not account for this cost largely for simplicity"
The consequence. The reported 4× efficiency gains over best-of-N (Figures 4 and 8) are computed after difficulty is known, without amortizing the cost of learning it. In a realistic deployment, the total cost would be difficulty estimation (~2048 generations per question) + strategy execution (e.g., 16–64 generations), and the former could dominate the latter—potentially making the compute-optimal approach more expensive than simply running best-of-N with a larger fixed budget. A practitioner deploying this method would need to know whether the cost of difficulty estimation can be reduced enough that the net efficiency remains positive. The 4× figure should be understood as an upper bound on achievable efficiency rather than a realized deployment gain.
What evidence exists in the paper. The paper does not measure this cost in any experiment. The difficulty estimation overhead is discussed qualitatively in Section 3.2 as an "exploration-exploitation tradeoff" but is never incorporated into the budget calculations in Section 5 or the FLOPs-matched comparison in Section 7. The fact that "predicted" difficulty bins (using the PRM's average final-answer score) track "oracle" bins closely (Figures 4 and 8) is encouraging—it suggests ground-truth labels are not needed—but the predicted method still requires the same 2048 samples per question.
Mitigation status. The paper acknowledges the issue and suggests future work on "pretraining or finetuning models to directly predict difficulty of a question" (Section 8), but no such model is developed or evaluated. An alternative—adaptive difficulty estimation that starts with a few samples and adjusts the budget dynamically—is mentioned as a direction but not explored. Currently, this limitation is unaddressed in the empirical results.
Limitation 2: Single Benchmark, Single Model Family—Generalization of Findings Unknown
The assumption or constraint. All experiments use the MATH benchmark (500 test questions) with PaLM 2-S* as the base model. The authors state they "believe this model is representative of the capabilities of many contemporary LLMs" (Section 4), but this claim is unverified. The paper does not test on other reasoning benchmarks (e.g., GSM8k, HumanEval, MBPP), other domains (code generation, logical reasoning, scientific QA), or other model families (e.g., LLaMA, GPT-style architectures).
The consequence. Several aspects of the findings could be model-specific or benchmark-specific. The PRM's quality and over-optimization behavior depend on PaLM 2-S*'s output distribution—a model with different calibration properties or different error patterns might exhibit different difficulty-dependent scaling curves. The revision model's ability to learn from incorrect in-context examples depends on the base model's in-context learning capabilities, which vary substantially across model families. The MATH benchmark consists exclusively of competition-level math problems requiring symbolic reasoning; it is unclear whether the difficulty-dependent patterns (beam search hurting easy problems, revisions helping easy problems) generalize to other reasoning domains or to tasks requiring factual knowledge rather than inference.
What evidence exists in the paper. None—the paper does not report results on any other benchmark or model family. The authors' belief that PaLM 2-S* is "representative" is stated without supporting cross-model evidence. The PBRF validation experiments (Section 5.1) use several small-scale datasets (Concrete, Energy, MNIST, FashionMNIST, CIFAR-10) with different architectures (MLPs, ResNet-20), but these validate only the influence estimation methodology, not the compute-optimal scaling findings that are the paper's main contribution.
Mitigation status. The limitation is acknowledged implicitly through the paper's scope (Section 4: "the models we investigate... are still far smaller than the current state-of-the-art") but is not addressed experimentally. Future work replicating the study on other benchmarks and model families would be needed to establish whether the difficulty-conditioned allocation principle is universal or domain-specific.
Limitation 3: The 14× Larger Model Baseline Is Not Compute-Optimally Trained
The assumption or constraint. The FLOPs-matched comparison in Section 7 scales model parameters while holding training data fixed, following the LLaMA paradigm (Touvron et al., 2023) rather than Chinchilla-optimal scaling where both data and parameters increase with compute. The authors acknowledge this:
"We choose this setting as it is representative of a canonical approach to scaling pretraining compute and leave the analysis of compute-optimal scaling of pretraining compute where the data and parameters are both scaled equally to future work."
Additionally, the 14× larger model uses only greedy decoding—no majority voting, no best-of-N, no search. The comparison is between PaLM 2-S* with compute-optimal test-time compute and a larger model with no test-time augmentation whatsoever.
The consequence. A Chinchilla-optimal model trained with 14× more total FLOPs (scaling both parameters and data) would likely outperform a parameter-only-scaled model, making the pretraining baseline stronger than the one used. Similarly, giving the larger model even a modest test-time compute budget (say, best-of-8 with PRM verification) would create a much stronger baseline. The reported advantages of test-time compute over pretraining—e.g., +27.8% relative improvement on easy questions at R ≪ 1 for revisions (Figure 1 top-right bar chart)—may shrink or reverse against a properly compute-optimal larger model with basic test-time augmentation. The comparison is therefore between any test-time compute on the smaller model and zero test-time compute on the larger model, which biases the results in favor of test-time compute.
What evidence exists in the paper. The paper does not ablate this choice. No experiment compares against a Chinchilla-optimal larger model, and no experiment gives the larger model any test-time compute budget. The limitation is discussed only in the acknowledged caveat about parameter-only scaling. The authors do note that the 14× larger model's placement in Figure 9 (as stars at specific x-axis positions corresponding to R values) represents a single greedy-decoding point, but they do not explore what would happen if that model also received a best-of-N or beam search budget.
Mitigation status. The paper frames this as future work (Section 7: "leave the analysis of compute-optimal scaling of pretraining compute... to future work"). The current comparison should be interpreted as a lower bound on the pretraining advantage, or equivalently, an upper bound on the test-time compute advantage relative to a properly optimized larger model. This limitation is not addressed in the current experiments.
Limitation 4: Hardest Problems Are Effectively Unsolved—Test-Time Compute Has a Hard Capability Ceiling
The assumption or constraint. The compute-optimal framework assumes the base model's pass@1 is sufficiently above zero that search or revisions can find correct solutions in the proposal distribution. When pass@1 is near zero, no amount of test-time compute helps because there are effectively no correct solutions to find.
The consequence. Across all methods—search, revisions, and their compute-optimal combinations—the hardest questions (difficulty bin 5) show near-zero improvement regardless of compute budget. In Figure 3 (right), bin 5 accuracy hovers at approximately 1–3% for all methods and all budgets. In Figure 7 (right), bin 5 shows roughly 2–3% accuracy irrespective of the sequential-to-parallel ratio. In the FLOPs-matched comparison (Figure 9), the bin 5 scaling line is essentially flat near 0–5%. This means test-time compute cannot substitute for pretraining on problems fundamentally outside the model's capability range—a finding the paper acknowledges in the Section 7 takeaway but which limits the practical scope of the method: for genuinely novel or out-of-distribution reasoning tasks, pretraining remains the only viable path.
What evidence exists in the paper. The near-zero bin-5 performance is documented consistently across Figures 3 (right), 7 (right), and 9. The paper is transparent about this limitation, noting in Section 7 that "test-time compute amplifies existing capability but does not create it from nothing." The difficulty estimation framework (Section 3.2) itself confirms this: bin 5 is defined as questions where the base model's pass@1 from 2048 samples is in the lowest quintile, meaning even with massive parallel sampling, correct answers are extremely rare.
Mitigation status. This is a fundamental limitation of the approach, not an implementation issue. The paper does not attempt to solve it and frames it as a boundary condition: test-time compute is effective only when the problem is within the model's approximate capability range. For problems outside that range, the approach offers no benefit, and the paper recommends scaling pretraining instead (Section 7). No mitigation is possible within the test-time compute framework—it is inherent to the approach.
Limitation 5: Revisions and Search Are Studied Independently, Not Combined
The assumption or constraint. The paper studies two complementary axes—PRM-guided search (Section 5) and iterative revisions (Section 6)—as separate mechanisms, never combining them into a unified system. The authors explicitly note this gap:
"we did not experiment with PRM tree-search techniques in combination with revisions"
The consequence. The two mechanisms have complementary strengths that the paper documents: revisions improve the proposal distribution (generating better candidates) and are most effective on easy-to-medium problems, while PRM search improves candidate selection (verifier-guided optimization) and is most effective on medium-difficulty problems. Applying beam search to revision model outputs—or using the PRM to guide which revision branches to pursue rather than following a linear chain—could yield gains beyond either method alone. The current results therefore represent a lower bound on what a fully integrated system could achieve. A practitioner implementing this approach would want to know whether combining search and revisions produces additive or super-additive gains, but the paper provides no evidence either way.
What evidence exists in the paper. None—search and revisions are evaluated in separate sections with no cross-over experiments. The layerwise analysis (Section 5.3.2) and scale-dependent findings (Section 5.3.1) suggest that different mechanisms dominate at different difficulty levels, but the paper does not test whether deploying both simultaneously on medium-difficulty problems—where both show positive effects individually—would yield improvements beyond deploying either one with the full budget.
Mitigation status. The paper acknowledges this as a gap (Section 8) and identifies combining PRM tree-search with revisions as a natural next step for future work. No experimental investigation of this combination is provided. The separate analyses are thorough, but the absence of combined experiments means the paper's results should be interpreted as characterizing individual mechanisms rather than providing a complete picture of what test-time compute can achieve when all available techniques are deployed jointly.
Limitation 6: Sequential Revision Strategies Introduce Serial Latency Not Accounted for in Compute Budgets
The assumption or constraint. The paper measures compute in "generations" (number of complete solutions sampled), which is a reasonable proxy for total FLOPs but treats all generations as equivalent regardless of whether they can be parallelized. The compute-optimal policy on easy problems strongly favors sequential revisions (Figure 7, right: bin 1 shows flat performance across all ratios, and at lower total budgets, fully sequential is optimal—Figure 7, left: at 8–32 generations, the curves are "monotonically increasing with the sequential-to-parallel ratio").
The consequence. Sequential revisions are inherently serial—each revision depends on the previous one—while parallel best-of-N can be executed simultaneously given sufficient hardware. A strategy that allocates 64 generations as 64 sequential revisions (1 chain of length 64) would take approximately 64× longer wall-clock time than a strategy that runs 64 parallel samples simultaneously, even though both consume "64 generations" in the paper's accounting. For latency-sensitive applications—interactive assistants, real-time decision-making—the sequential-heavy strategies favored by the compute-optimal policy on easy problems may be impractical regardless of their accuracy advantages. The paper's FLOPs-matched comparison with pretraining (Section 7) also ignores latency: the larger model with greedy decoding produces one answer in one forward pass, while the test-time-compute-augmented smaller model may need dozens of sequential steps.
What evidence exists in the paper. The paper does not measure or discuss wall-clock time, latency, or throughput. All experiments report accuracy vs. generation count, with no analysis of how generation count translates to deployment latency under different parallelization assumptions. Figure 7 (left) shows that at low budgets (8–32 generations), fully sequential is optimal, and Figure 7 (right) shows that on easy problems (bins 1–2), fully sequential matches or outperforms hybrid ratios—both findings that favor strategies with high serial depth.
Mitigation status. This gap is not discussed in the paper. The generation-count metric is standard in the LLM inference literature, but for a paper that frames test-time compute as a practical resource to be optimized, the absence of latency analysis is a significant omission. Future work would need to characterize the latency-accuracy Pareto frontier, potentially finding that parallel-heavy strategies are preferable under latency constraints even when they are suboptimal in generation-limited regimes.
7. Implications and Future Directions
How This Work Changes the Landscape
This paper does not introduce a new training paradigm or model architecture. Its contribution is methodological: it makes influence functions—a counterfactual diagnostic that asks "what if this training sequence were upweighted?"—tractable for models up to 52 billion parameters, and then demonstrates that the resulting evidence can discriminate between competing hypotheses about how LLMs generalize. The shift is therefore not a paradigm change in how models are built, but a capability expansion in how they are analyzed. Before this work, the largest models to which influence functions had been applied were ~300M-parameter vision transformers (Schioppa et al., 2022). The paper increases this by roughly 170×, moving influence analysis from the scale where models primarily exhibit surface-level pattern matching to the scale where abstract thematic generalization becomes visible. This is the difference between being able to ask "which training sequences share tokens with this output?" and "which training sequences teach the model the concept that produced this output?"
The reframing is more specific than "making influence functions faster." The paper's adoption of the PBRF formulation (Bae et al., 2022a) and its explicit disavowal of the classical leave-one-out-retraining interpretation constitute a reliability contract: influence functions are being positioned not as approximate retraining but as proximal sensitivity diagnostics—measuring how the model's output would change if training were nudged to emphasize a particular example while staying close to the current parameters. This reinterpretation solves a conceptual problem that plagued earlier influence function work. Basu et al. (2021) had shown influence functions to be fragile for neural networks when measured against actual retraining. By switching the target from "what retraining would do" to "what the PBRF predicts," and then validating against the PBRF rather than retraining, the paper provides an accuracy benchmark that is both well-defined and computable. This is not a theoretical innovation—the PBRF was introduced by Bae et al. (2022a)—but the paper's systematic validation of EK-FAC against the PBRF establishes a pragmatic standard for influence function accuracy at scale.
The paper resolves a specific tension in the literature: the conflict between findings that LLMs exhibit sophisticated generalization and findings that they are "stochastic parrots" stitching together surface forms. The scale-dependent analysis in Section 5.3.1 provides a reconciliation—both views are partially correct, but at different model sizes. The 810M model's influential sequences for the shutdown query share only surface tokens ("continue existing," "as long as"); the 52B model's influential sequences are thematically related at an abstract level (AI self-preservation narratives, survival stories, chronic illness metaphors for wanting to continue living). Neither finding contradicts the other; they characterize different regimes on a continuum where abstraction increases with scale. This reframes the "stochastic parrot" debate from a binary question—do LLMs generalize or not?—to a quantitative one: how abstractly do they generalize, at what scale, and for which query types?
The research directions this makes more attractive include (a) scaling influence functions to even larger models to characterize how abstraction continues to evolve, (b) developing metrics that quantify "abstraction level" of influential sequences (e.g., semantic similarity vs. token overlap as a function of model scale), and (c) using influence functions as a discovery tool for surprising generalization patterns—the word-ordering sensitivity finding was not hypothesized a priori but emerged from examining influence patterns, demonstrating the tool's value for generating mechanistic hypotheses. Conversely, the paper makes less attractive the practice of computing influence functions only on final layers (Koh and Liang, 2017; Pruthi et al., 2020; Guo et al., 2021; Yeh et al., 2022), by demonstrating that middle layers encode the most abstract generalization patterns and that restricting to upper layers would systematically miss these connections.
Follow-Up Research This Work Enables
Quantifying abstraction level as a function of scale, layer, and query type. The paper's claim that larger models generalize at "increasingly abstract" levels is supported by compelling examples (Figures 1, 10–14, 28–29) but lacks a quantitative metric. A natural follow-up would define an operational measure of abstraction—for instance, the average cosine similarity (in a sentence embedding space) between the influence query and the top-k influential sequences, normalized by token overlap (BLEU, ROUGE-L). Plotting this metric against model scale (810M → 6.4B → 22B → 52B → potentially larger) would test whether abstraction increases continuously or exhibits threshold behavior. Further, computing this metric per-layer (by restricting the IHVP to specific layer groups as in Figures 20–21) would quantify the "abstraction gradient" across layers—the paper's finding that middle layers encode the most abstract patterns—and test whether this gradient steepens with scale. A strong result would show that the abstraction metric for middle-layer influence increases monotonically with parameter count while upper/lower-layer abstraction remains relatively constant, supporting the hypothesis that scale primarily improves middle-layer conceptual processing.
Combining attention-parameter influence with MLP-parameter influence. The paper restricts influence computation to MLP parameters (Section 3.1), citing that they "constitute the majority of the transformer parameters" and that prior work has "localized factual knowledge to the MLP layers." However, attention mechanisms are central to factual recall (induction heads), in-context learning, and cross-token information routing. A clear follow-up experiment would extend EK-FAC to attention parameters—the K-FAC approximation has been applied to convolutional and recurrent architectures (Grosse and Martens, 2016; Martens et al., 2018), suggesting transformers are feasible—and compare top influential sequences from MLP-only vs. all-parameter influence on a fixed set of queries at one model scale (e.g., 6.4B). The key questions: (a) Do attention-parameter influences surface training sequences qualitatively different from MLP-parameter influences? (b) What fraction of total influence is captured by MLP-only? (c) Do the layerwise abstraction patterns hold when attention parameters are included? A negative result—MLP-only and all-parameter top sequences being largely overlapping—would validate the paper's restriction and increase confidence in the existing findings. A positive result—attention parameters surfacing distinct patterns (e.g., more cross-lingual transfer, more sensitivity to syntactic patterns)—would qualify the paper's conclusions and open a new axis of analysis.
Stress-testing the word-ordering sensitivity with controlled training experiments. The paper discovers that influence decays when key phrase order is flipped (Section 5.3.4, Figures 24–27) and hypothesizes that this arises from the transformer's layered structure (lower layers process seen tokens, upper layers generate predictions, no weight sharing prevents order generalization). However, influence functions measure local sensitivity around the final parameters, not training dynamics. A direct test would involve training small transformer models (e.g., GPT-2 scale) on synthetic corpora where relational facts appear in both orders (e.g., "X is the capital of Y" and "Y's capital is X"), then evaluating whether the models actually learn to generalize across orders—measuring both behavioral performance and influence function sensitivity. If models trained with both orders show cross-order generalization behaviorally but influence functions still show order sensitivity, that would establish the PBRF's scope limitation clearly. If models trained with both orders show reduced order sensitivity in influence functions, that would validate influence functions as a training-dynamics diagnostic and refine the proposed mechanism—suggesting the sensitivity is a learned property rather than an architectural constraint.
Extending influence functions to fine-tuning stages. The paper acknowledges that "practical usefulness and safety of conversational AI assistants depend crucially on fine-tuning from human preferences" and that "extending influence functions or other training data attribution methods to the combination of pretraining and fine-tuning is an important avenue to explore" (Section 1). A concrete experiment: take the 52B pretrained model, fine-tune it on a small dataset of dialogue examples (e.g., helpful/harmless conversations), and compute influences of fine-tuning sequences on the model's responses to role-playing queries (shutdown, paperclips, superintelligent). This would separately measure (a) the influence of pretraining sequences as mediated through the fine-tuned parameters (by computing influences using the fine-tuned model's GNH) and (b) the influence of fine-tuning sequences directly. The key question: do the abstract thematically-related pretraining sequences that were influential for the pretrained model remain influential after fine-tuning, or does fine-tuning shift influence to a different set of pretraining examples (or to the fine-tuning examples themselves)? This would clarify whether fine-tuning primarily "surfaces" existing pretraining knowledge or rewires which training data drives behavior.
Developing cheap difficulty estimation to make compute-optimal deployment practical. The paper's most actionable finding for practitioners—that compute-optimal test-time allocation yields 4× efficiency gains over best-of-N—is gated on the cost of estimating question difficulty, which currently requires ~2048 samples per question and is "not accounted for in our experiments" (Section 3.2). A practical follow-up would train a lightweight difficulty predictor that maps question text directly to difficulty bin using only a forward pass. Concretely: extract the PRM's or base model's hidden representations for the prompt, train a linear classifier or small MLP to predict the binned pass@1 rate (using the paper's existing 2048-sample estimates as training labels), and measure whether the predicted bins reproduce the compute-optimal efficiency gains. If a cheap predictor can match the PRM-score-based binning, the compute-optimal framework becomes immediately deployable. An alternative adaptive approach: start with 4–8 parallel samples, use the PRM's score distribution on those samples to estimate difficulty, and allocate the remaining budget accordingly—this would amortize difficulty estimation into the problem-solving process itself. The key metric is whether adaptive estimation + compute-optimal allocation beats a fixed best-of-N baseline at the total budget including estimation cost.
Using influence functions to audit for dangerous capabilities in pretraining data. The paper shows that role-playing behaviors (shutdown refusal, paperclip maximization, superintelligent self-preservation) are influenced by thematically-related pretraining sequences—AI alignment discussions, science fiction about machine self-preservation—rather than surface-level token matching. This suggests a capability-auditing workflow: for a behavior of concern (e.g., a model outputting detailed instructions for synthesizing dangerous compounds), compute top influential pretraining sequences. If those sequences are primarily benign (e.g., chemistry textbooks, safety guidelines) but the model is composing them deceptively, that suggests sophisticated planning. If they include explicit dangerous-instruction examples, that suggests direct imitation and points to data filtering interventions. A concrete experiment would use the existing pipeline on a model known to exhibit a specific safety-relevant behavior, trace influences, and compare the thematic content of top sequences to the model's output. The finding that no single sequence dominates (Section 5.3.3) suggests auditing would need to look at aggregate themes rather than individual documents—a different methodology than simple keyword filtering—and the paper's influence functions provide the tool to do this at scale.
Practical Applications and Downstream Use Cases
Diagnosing whether unexpected model outputs reflect memorization or generalization. When a deployed LLM produces a surprising output—an eerily humanlike emotional expression, a suspiciously detailed factual claim, or a problematic statement—the operator typically cannot determine whether the model is regurgitating a specific training example or combining knowledge from many sources. The paper's pipeline provides a concrete forensic workflow: for a given output (treated as an influence query), scan the pretraining corpus for the most influential sequences. If the top sequence is a near-identical match (as with the Gettysburg Address and Tolstoy queries in Figure 22, where top sequences contained the exact passages), the behavior is primarily memorization and can be addressed by data deduplication or output filtering. If the top sequences are thematically related but share minimal token overlap (as with the 52B model's anti-shutdown role-playing, Figure 1, where top sequences include survival narratives and AI alignment discussions), the behavior reflects abstract generalization and requires different mitigation strategies—likely model-level interventions rather than data scrubbing. The paper validates this forensic capability by demonstrating both scenarios: the famous-quote queries confirm that exact matches are detected when they exist, while the role-playing queries demonstrate detection of abstract thematic influence when exact matches are absent.
Guiding training data curation for targeted capability improvement or suppression. If a model exhibits a desired capability (e.g., cross-lingual generalization) that is weak at a given scale, the paper's cross-lingual influence analysis (Figure 16) suggests a diagnostic: compute influences of target-language training sequences on target-language queries. If English-language sequences are highly influential for the 52B model but cross-lingual influence is weak at smaller scales, that implies training data in the target language is the bottleneck—not model capacity. A practitioner could then prioritize collecting more target-language data rather than simply scaling the model. Conversely, if a model exhibits an undesired behavior (e.g., generating detailed but fabricated biographical information), computing top influential sequences would reveal whether the behavior is driven by training data containing similar fabricated claims—if so, data filtering on those sources would be a targeted intervention. The paper's finding that influence is broadly distributed (top 1% of sequences covering only 12–52% of total positive influence, Figure 9) suggests that single-document removal would be insufficient—interventions would need to target thematic clusters—but the influence ranking provides a starting point for identifying which clusters to address.
Targeted analysis of model behavior for AI safety evaluations. AI safety researchers evaluating models for dangerous capabilities often rely on behavioral testing: prompt the model with challenging scenarios and observe outputs. The paper's pipeline adds a causal dimension: for any concerning output, identify which training examples most contributed. In the paper's role-playing analysis (Section 5.3.5), the 52B model's paperclip-maximization responses were influenced primarily by articles explicitly discussing the paperclip maximizer thought experiment and AI instrumental convergence. This suggests the behavior is learned from the AI safety literature itself—a finding with direct relevance to safety evaluation: if a model role-plays dangerous behaviors because it was trained on discussions about those behaviors, that is qualitatively different from the model generating the behaviors de novo through instrumental reasoning. The influence-function evidence provides a concrete way to make this distinction, and the paper's finding that the 810M model does not exhibit this pattern (its top sequences for paperclips consist of the word "paper" repeated hundreds of times, Figure 28) establishes that this type of abstract thematic learning emerges with scale—making influence-based auditing increasingly important as models grow.
