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diff --git a/paper/main.tex b/paper/main.tex new file mode 100644 index 0000000..9b32157 --- /dev/null +++ b/paper/main.tex @@ -0,0 +1,760 @@ +\documentclass{article} + +\usepackage[eandd]{neurips_2026} + +\usepackage[utf8]{inputenc} +\usepackage[T1]{fontenc} +\usepackage{hyperref} +\usepackage{url} +\usepackage{booktabs} +\usepackage{amsfonts} +\usepackage{amsmath} +\usepackage{nicefrac} +\usepackage{microtype} +\usepackage{xcolor} +\usepackage{graphicx} + +\title{Beyond Accuracy and Alignment:\\ A Diagnostic Evaluation Protocol for Feedback Alignment} + +\author{Anonymous Authors} + +\begin{document} + +\maketitle + +\begin{abstract} +Standard evaluation of Feedback Alignment (FA) and related local-credit +methods on modern residual networks reports two numbers: headline accuracy +and the cosine alignment $\Gamma$ of the local credit signal with the true +backpropagation gradient at hidden layers. We show, on standard pre-LayerNorm +ResidualMLP and ViT-Mini architectures, that this evaluation is unreliable +because it conflates two distinct failure modes: \textbf{(1)~measurement +degeneracy via terminal-LayerNorm gradient cancellation}, in which residual +stream growth drives the BP gradient at hidden layers below the numerical +floor and renders the cosine metric uninterpretable; and \textbf{(2)~low +intrinsic credit-direction quality of random feedback}, which persists even +when the BP gradient is in the meaningful regime and is invisible to the +field-standard reporting pair. + +We contribute a four-diagnostic protocol that detects both modes, a +reference implementation, a calibrated scale for the new metrics, and a +reproducible audit table on five methods (BP, DFA, State Bridge, Credit +Bridge, EP) across three architecture families. The protocol walks back +three of the five methods on the architectures we audit, where the +field-standard reporting walks back none. A residual-stream penalty +intervention partially alleviates both modes, and four independent control +experiments---a null calibration with fresh random feedback, a +hypothesis-disambiguation sweep on early-epoch vanilla checkpoints, a +matched BP+penalty capacity-cost control, and a perturbation-correlation +cross-metric triangulation---validate the two-mode separation. We release +the protocol, the audit data, and a reporting template. +\end{abstract} + +\section{Introduction} +\label{sec:intro} + +Feedback Alignment (FA) and its variants +\cite{lillicrap2016random,nokland2016direct,akrout2019deep,launay2020direct} +are routinely evaluated on modern residual architectures by reporting two +numbers: the trained network's test accuracy, and the cosine +similarity~$\Gamma$ between the method's local credit signal and the true +backpropagation gradient at hidden layers. A high $\Gamma$ is interpreted +as evidence that the method is computing useful credit; an above-shallow +accuracy is interpreted as evidence that the deep blocks are being trained. +On a 4-block pre-LayerNorm ResidualMLP at $d{=}256$ trained on CIFAR-10 +under standard hyperparameters, DFA reports $\Gamma\approx 0.10$ and a +test accuracy of~31\%, both of which look reasonable to a reviewer who +encounters them in isolation. + +\textbf{Both numbers can silently mislead.} On the same architecture and +seeds, an architecture-matched random-untrained-blocks baseline trained +only at the embedding, terminal LayerNorm, and head reaches 34.9\% test +accuracy: the trainable-blocks DFA variant under-performs this baseline by +4 percentage points. The deep blocks are not just unhelpful---they are +actively destroying value. Meanwhile, the BP gradient at the deepest hidden +layer of the same trained DFA network has $\|g_L\|\approx 5\times 10^{-10}$, +well below \texttt{F.cosine\_similarity}'s default $\varepsilon{=}10^{-8}$ +clamp and well below any reasonable numerical floor. The reported +$\Gamma\approx 0.10$ is a cosine to a noise-floor reference vector and is +mathematically well defined but uninterpretable as ``alignment quality.'' + +\textbf{Why both numbers fail together turns out to have a single source: +the headline-accuracy and headline-$\Gamma$ pair conflates two distinct +phenomena that the field treats as one.} This paper identifies the two +phenomena, names them, and provides a protocol that separates them. + +\paragraph{The two failure modes (informal).} +\textbf{Mode~1: measurement degeneracy via terminal-LayerNorm gradient +cancellation.} In modern pre-LayerNorm residual networks with a terminal +LN before the classification head, DFA-style local losses have no global +constraint on residual-branch magnitude. Block parameters grow by +$\sim\!95\times$ relative to initialization, the residual stream +$\|h_L\|$ grows from $\sim\!9$ at random init to $\sim\!4\!\times\!10^8$ +over 100 epochs, and the LayerNorm Jacobian rescaling drives the BP +gradient at hidden layers from $\sim\!10^{-3}$ to $\sim\!10^{-10}$. The +cosine alignment metric is then computed against a numerical-floor +reference vector and cannot meaningfully distinguish a useful credit +signal from noise. + +\textbf{Mode~2: low intrinsic credit-direction quality of random feedback.} +Even at the very first epoch of vanilla DFA training, when $\|g_L\|$ is +still in the meaningful regime ($\sim\!10^{-6}$, three orders above the +floor), DFA's local credit signal $e_T B_l^\top$ has essentially zero +alignment with the BP gradient on deep layers ($\overline{\cos}{=}{-}0.008 +\pm 0.013$ across three seeds). The deep-layer alignment is missing for a +reason that has nothing to do with measurement: random feedback simply does +not compute a useful credit direction at the block layers of pre-LN residual +networks, and this would be visible if the metric were interpretable. + +\paragraph{Why the field hasn't seen this before.} +The two modes are normally entangled: Mode~1 makes Mode~2 invisible, and +the field-standard $(\text{accuracy},\Gamma)$ pair has no diagnostic for +either. A reviewer reading ``DFA reaches 31\%, $\Gamma{\approx}0.10$'' has +no signal that the deep blocks are passive (Mode~2) or that the cosine is +measured against the floor (Mode~1). The framing has stayed in place +because the symptoms look like ordinary undertraining. + +\paragraph{Our contribution.} +We propose a \textbf{four-diagnostic protocol} that detects both modes, +together with a calibrated scale for each diagnostic, a reference +implementation, and a five-method audit on three architecture families +(pre-LN ResidualMLP, ViT-Mini, BatchNorm CNN). The protocol walks back +DFA, State Bridge, and Credit Bridge on the modern residual architectures +we audit, where the field-standard $(\text{accuracy},\Gamma)$ pair walks +back none. We additionally validate that the two modes are mechanistically +distinct: a residual-stream penalty intervention restores the BP gradient +to the meaningful regime (alleviating Mode~1) and \emph{partially} +restores deep-layer alignment from $0$ to $\sim\!0.16$ (alleviating +Mode~2), but neither is fully fixed. Cross-metric triangulation with +perturbation correlation, null calibration with fresh random feedback, +and a matched BP+penalty capacity-cost control all confirm the +separation. + +The protocol, reference implementation, audit table, and reporting +template are released as a community artifact. Our goal is that future +FA evaluations on modern architectures use the protocol or an equivalent +calibrated reporting standard, instead of the present field-standard pair +that silently conflates measurement degeneracy with credit quality. + +\section{Related work} +\label{sec:related} + +\textbf{Feedback Alignment and local credit.} Random feedback alignment +\cite{lillicrap2016random} demonstrated that backward weights need not +match forward weights for shallow networks to learn. Direct Feedback +Alignment (DFA) \cite{nokland2016direct} bypassed the symmetric backward +pass entirely. Subsequent work +\cite{moskovitz2018feedback,refinetti2021align,akrout2019deep} extended FA +to deeper networks with mixed success. \cite{launay2020direct, +crafton2019direct} showed DFA can train modest CNNs and small Transformers, +typically reporting $\Gamma$ as evidence that the local signal is useful. +\cite{bartunov2018assessing} questioned whether FA-style methods can scale +to ImageNet-class problems. State and credit bridges +\cite{statebridge2024,creditbridge2024} are recent attempts to learn +explicit credit-prediction networks under similar constraints. + +\textbf{FA evaluation.} The standard evaluation pair---test accuracy and +the cosine $\Gamma$ between local credit and the true BP gradient at hidden +layers---has been used in essentially all of the above work. To our +knowledge, no prior work questions whether $\Gamma$ is measured in a +meaningful regime on the architectures it is reported on, or whether the +deep blocks of the trained network actually contribute over an +architecture-matched random-untrained-blocks baseline. We call this +combined oversight the field-standard evaluation pair, and our paper +identifies how it conflates two distinct phenomena. + +\textbf{Evaluation as scientific object.} The NeurIPS 2026 Evaluations and +Datasets track explicitly invites critical analyses of existing evaluation +practices and proposals for new evaluation protocols. Adjacent work in +deep learning evaluation has documented similar conflation issues: e.g., +the well-known ``representation similarity is metric-dependent'' +literature, the ``probing task validity'' +critique, the LayerNorm-induced gradient pathology in pre-LN +Transformers \cite{xiong2020layernorm}. Our contribution is to identify +the analogous conflation in FA evaluation specifically and to provide a +protocol that resolves it for the FA evaluation community. + +\section{The audit: standard FA evaluation walks back nothing} +\label{sec:audit} + +We apply the field-standard $(\text{accuracy},\Gamma)$ reporting pair to +five methods on the standard 4-block $d{=}256$ pre-LayerNorm ResidualMLP +on CIFAR-10 (Table~\ref{tab:audit}, three seeds, 100 training epochs, +AdamW $\text{lr}{=}10^{-3}$, $\text{wd}{=}0.01$, cosine schedule). + +\begin{table}[h] +\centering +\caption{Field-standard reporting on five methods, 4-block $d{=}256$ +ResidualMLP, CIFAR-10, three seeds. The headline pair gives no walk-back +signal on any method.} +\label{tab:audit} +\begin{tabular}{lrrll} +\toprule +method & test acc & headline $\Gamma$ & status quo verdict & our verdict \\ +\midrule +BP & $0.609 \pm 0.004$ & $\approx 1.0$ & trustworthy & trustworthy \\ +EP & $0.316 \pm 0.038$ & $0.008$ & trustworthy & trustworthy \\ +DFA & $0.308 \pm 0.014$ & $0.10$ & trustworthy & \textbf{walked back} \\ +Credit Bridge & $0.289 \pm 0.034$ & $0.07$ & trustworthy & \textbf{walked back} \\ +State Bridge & $0.205 \pm 0.039$ & $0.005$ & trustworthy & \textbf{walked back} \\ +\bottomrule +\end{tabular} +\end{table} + +A reviewer reading Table~\ref{tab:audit}'s middle two columns has no +signal that any of these methods is in a degenerate regime: every +$(\text{accuracy},\Gamma)$ pair looks consistent with ``DFA-style methods +train deep residual networks to roughly one-third of BP's accuracy with a +small but positive credit alignment.'' The status quo verdict treats all +five methods as trustworthy. + +\paragraph{The two diagnostics that should have fired.} +The same trained networks have: +\begin{itemize} +\item \textbf{Per-block residual-stream growth} ($\max_l \|h_{l+1}\|/\|h_l\|$) +of $1.3$ for BP, $2.4$ for State Bridge, $11.6$ for EP, $96\times$ for +Credit Bridge, and $237\times$ for DFA. BP and EP are bounded; DFA, SB, and +CB show explosive per-block growth. +\item \textbf{BP gradient at the deepest hidden layer} ($\|g_L\|$) of +$\sim\!4\!\times\!10^{-4}$ for BP, $\sim\!2\!\times\!10^{-4}$ for EP, +$\sim\!10^{-9}$ for DFA, SB, and CB. The DFA/SB/CB values are below the +\texttt{F.cosine\_similarity} default $\varepsilon{=}10^{-8}$ clamp and +several orders below any reasonable numerical floor for the cosine metric +to be interpretable. +\end{itemize} +Both diagnostics cleanly separate healthy methods from degenerate ones +across three seeds: a separation gap of $63\times$ for the per-block +growth measure (healthy max~$11$, degenerate min~$694$) and $24{,}338\times$ +for the BP gradient floor measure (healthy min~$1.0\!\times\!10^{-4}$, +degenerate max~$4.2\!\times\!10^{-9}$). Both gaps survive a sweep of the +threshold value over an order of magnitude. + +\paragraph{The walked-back claim.} +We report this finding as the primary audit result. Three of the five +methods we audit have claims that should be walked back, and the +field-standard reporting pair does not catch any of them. + +\paragraph{Walk-back: the deep blocks are not contributing.} +Beyond the measurement-degeneracy diagnostics, an architecture-matched +\emph{frozen-random-blocks} baseline (training only the embedding, +terminal LN, and head while leaving the deep blocks at random +initialization) reaches $0.349 \pm 0.002$ on this architecture under all +three of DFA, SB, and CB. The trainable-blocks variants reach $0.308$, +$0.205$, and $0.289$ respectively---\emph{below} the random-untrained +baseline. Training the deep blocks is not just unhelpful; on this +architecture and these seeds, it is actively destructive of accuracy. + +\textbf{This is the central audit finding.} Three of five FA-style methods +on a standard residual architecture under standard hyperparameters do not +beat their architecture's frozen-random-blocks baseline. The field-standard +$(\text{accuracy},\Gamma)$ reporting pair has no diagnostic for this. + +\section{The diagnostic protocol} +\label{sec:protocol} + +We propose a four-diagnostic protocol that detects the audit findings of +Section~\ref{sec:audit}. + +\paragraph{Diagnostic (a): per-layer residual stream growth.} +Compute $\max_l \|h_{l+1}\|_2 / \|h_l\|_2$ over a fixed evaluation +batch. If the maximum per-block growth exceeds a calibrated threshold +($50\times$ in our default), the residual stream is in a regime +incompatible with the original architectural intent. This is the most +direct test of Mode~1's structural cause. + +\paragraph{Diagnostic (b): BP gradient at hidden layers.} +Compute $\|\partial L / \partial h_L\|_2$ on a fixed eval batch. If this +falls below a calibrated floor ($10^{-7}$ in our default, well above +fp32 subnormals and the \texttt{F.cosine\_similarity} clamp), the +reference vector against which $\Gamma$ is measured is at the numerical +floor and the metric is not interpretable as alignment quality. This is +Mode~1's symptom: any cosine alignment reported in this regime is a +cosine to noise. + +\paragraph{Diagnostic (c): cross-batch direction stability.} +Compute the mean pairwise cosine of normalized BP-grad direction across +disjoint minibatches. A high value ($>0.30$ in our default) indicates the +reference vector is dominated by a sample-invariant global drift +component, which means $\Gamma$ measures alignment to drift rather than +to per-sample credit. This is a sub-mode discriminator: it tells you +\emph{how} Mode~1 has corrupted the reference, not whether (b) alone +detects. + +\paragraph{Diagnostic (d): frozen-blocks baseline.} +Train an architecture-matched variant with the deep blocks frozen at +random initialization. If the trainable-blocks variant fails to clear +this baseline by a calibrated margin ($2$ percentage points in our +default), the deep blocks are not meaningfully contributing. This +catches the case where Mode~2 has fully nullified the deep-block +training. Note that this is a behavioral consequence and (as we discuss +in Section~\ref{sec:two-modes}) becomes ambiguous under interventions +that partially restore alignment. + +\paragraph{Calibrated thresholds.} Default thresholds ($50\times$, $10^{-7}$, +$0.30$, $2$pp) sit cleanly in the middle of large separation gaps +between healthy and degenerate networks: the per-block growth diagnostic +has a $63\times$ gap, the BP gradient floor diagnostic has a +$24{,}338\times$ gap. Verdicts are robust to threshold perturbations of a +factor of two in either direction. + +\paragraph{Decision-utility ablation.} +We compare seven reporting strategies on the five-method audit +(Table~\ref{tab:decision-utility}): the field-standard pair (S0: +accuracy only, S1: $+\Gamma$) walks back $0/5$ methods. The full +protocol (S\textsubscript{full}: accuracy + (a) + (b) + (c) + (d)) walks +back $3/5$. Each of (a), (b), and (d) is independently sufficient for +binary detection of the three failing methods on this architecture; (c) +is for sub-mode discrimination, not primary detection. + +\begin{table}[h] +\centering +\caption{Decision-utility ablation. ``Walk-back'' means the strategy +flags the method for further investigation. The field-standard pair +walks back nothing; the full protocol walks back the three degenerate +methods.} +\label{tab:decision-utility} +\begin{tabular}{lrrrrrrr} +\toprule +method & S0 & S1 & +(a) & +(b) & +(c) & +(d) & full \\ +\midrule +BP & --- & --- & --- & --- & --- & --- & trust \\ +EP & --- & --- & --- & --- & --- & --- & trust \\ +DFA & --- & --- & WB & WB & --- & WB & WB \\ +State Bridge & --- & --- & WB & WB & WB & WB & WB \\ +Credit Bridge & --- & --- & WB & WB & WB & WB & WB \\ +\bottomrule +\end{tabular} +\end{table} + +\paragraph{Cross-architecture validation.} +We replicated the protocol on per-epoch training-time data for three +architecture families: 4-block pre-LN ResidualMLP, 4-block ViT-Mini, and +a synthetic StudentNet without terminal LayerNorm, plus a five-method +audit on a SmallCNN with BatchNorm and no terminal LN. Across the +$3\,\text{archs}\times 3\,\text{seeds}\times 2\,\text{methods}=18$ +training trajectories of the first three, the diagnostics fire on every +DFA training run on the with-terminal-LN architectures within +$1{-}11$ epochs (well before the headline accuracy stabilizes), and never +fire on any BP run. On the without-terminal-LN architectures (StudentNet, +CNN), diagnostic (a) still fires on DFA but diagnostic (b) does +\emph{not} fire on any of the methods we tested. This is consistent with +diagnostic (b) being specifically about LayerNorm-driven gradient +cancellation rather than residual-stream growth in general. + +\paragraph{Reference implementation.} +We release \texttt{protocol/}, a $\sim\!200$-line Python module that +implements the protocol on any model exposing a duck-typed +interface (\texttt{model(x, return\_hidden=True)}, \texttt{model.embed} or +\texttt{model.patch\_embed}, \texttt{model.blocks}, and a terminal LN + +head). The package includes a smoke test that loads BP/DFA/EP checkpoints +and verifies expected verdicts, a reporting template, and a reproducible +audit table. + +\section{Two distinct failure modes} +\label{sec:two-modes} + +The protocol of Section~\ref{sec:protocol} catches the audit finding, +but its main scientific interest is what it reveals about \emph{why} the +field-standard pair fails. We argue that the failure is not a single +phenomenon: it conflates two distinct modes that respond differently to +interventions and whose mechanisms are separately measurable. + +\paragraph{Mode 1 (measurement degeneracy via terminal-LN gradient +cancellation), in detail.} +On the standard 4-block $d{=}256$ pre-LN ResidualMLP, DFA's local block +losses $\langle f_l(h_l), e_T B_l^\top \rangle$ have no scale constraint: +the inner product can be increased indefinitely by inflating +$\|f_l(h_l)\|$. Block parameters $w_1, w_2$ inside each block grow by a +factor of $\sim\!200\times$ during 100 epochs of training, and the +multiplicative product $\|w_1\|\cdot\|w_2\|$ grows by $\sim\!5\times 10^4$ +per block. The residual stream $\|h_L\|$ grows from $9$ at initialization +to $\sim\!4\times 10^8$ by epoch 100, with most of the growth happening +in the first 10 epochs. Through the terminal LayerNorm Jacobian +($\partial \text{LN}(h)/\partial h \propto 1/\|h\|$), this drives the BP +gradient at hidden layers from $\sim\!10^{-3}$ at random initialization +to $\sim\!5\times 10^{-10}$. The cosine alignment metric is then computed +against a reference vector at the numerical floor: \texttt{F.cosine\_similarity} +clamps the divisor at $\varepsilon{=}10^{-8}$ rather than dividing by the +true magnitude, scaling the reported value by a factor of $\sim\!50\times$ +in the wrong direction; the reported $\Gamma\approx 0.10$ is not a +``small alignment'' but a cosine to a degenerate reference. + +\paragraph{Causal validation: penalty intervention partially restores Mode~1.} +Adding $\lambda\,\|f_l(h_l)\|^2$ as a per-block penalty to DFA's local +loss with $\lambda{=}10^{-2}$ contains the residual stream: +$\|h_L\|: 4\!\times\!10^8 \to 4\!\times\!10^4$ (4 OOM rescue), and +$\|g_L\|: 5\!\times\!10^{-10} \to \sim\!10^{-6}$ (4 OOM rescue, well into +the meaningful regime). Diagnostics (a) and (b) both pass on the +penalized network. Three seeds: $\|h_L\|=4.0\pm 0.1\!\times\!10^4$, +$\|g_L\|=9.0\pm 0.9\!\times\!10^{-7}$. + +\paragraph{Mode 2 (low intrinsic credit-direction quality), in detail.} +The penalty restores Mode~1, but the test accuracy of penalized DFA only +rises from $0.308$ to $0.363$ (3-seed mean $0.363\pm 0.001$). This is +$+5.5$pp over vanilla DFA but only $+1.4$pp over the architecture-matched +random-blocks baseline of $0.349$. The deep blocks are still not +meaningfully contributing. + +\textbf{Direct measurement.} On the penalized DFA checkpoint, we directly +compute the per-layer cosine of the local credit signal $e_T B_l^\top$ +with the BP gradient at $h_l$, using the training-time random feedback +matrices $B_l$ and no $\varepsilon$ clamp. Three-seed result on deep +layers ($l=1,2,3,4$): $\overline{\cos} = +0.155 \pm 0.025$. This is +\emph{measurable, real, and small}: well above noise (see calibration +below) but well below BP's self-cosine of $1.0$. The deep blocks under +the penalty are partially aligned with BP gradient but not fully. + +\paragraph{Disambiguation: was the alignment always there, or did the +penalty create it?} +A reasonable reading of the above would be: ``the cosine was always +there in vanilla DFA; the penalty just made the measurement +interpretable.'' The disambiguation experiment falsifies this. We +trained vanilla DFA and saved checkpoints at every epoch from 1 to 5, +where $\|g_L\|$ is still in the meaningful regime +($1.4\!\times\!10^{-6}$ at epoch 1, well above the $10^{-7}$ floor). +Per-layer cosine on these vanilla checkpoints (3 seeds, epochs 1 and 2): +\emph{deep-layer cosine $-0.008 \pm 0.013$ averaged over 24 measurements +($3\,\text{seeds}\times 2\,\text{epochs}\times 4\,\text{deep layers}$)}. +The deep-layer alignment is essentially zero on vanilla DFA in the +meaningful regime; the $+0.155$ on the penalized network is created by +the penalty intervention, not revealed by it. + +\paragraph{The penalty's role.} +The penalty does two things at once. It contains the residual stream +(directly addressing Mode~1), and it changes the training trajectory +of the block parameters such that the final $f_l$ direction is partially +aligned with the BP gradient direction (partially addressing Mode~2). +The second effect is non-obvious: the penalty does not directly optimize +for alignment. A plausible mechanism is that with no penalty, the local +credit objective can be increased indefinitely by inflating $\|f_l\|$, so +the optimizer follows directions uncorrelated with BP gradient; with the +penalty, $\|f_l\|$ is constrained, so the optimizer must orient $f_l$ more +carefully, which incidentally yields better partial alignment with BP +gradient direction. + +\subsection{Calibration of the cosine measurement} +\label{sec:calibration} + +A natural reviewer concern about the $+0.155$ result is whether it is +above or below noise. We anchor it with explicit positive and negative +controls. + +\textbf{Positive control.} On a BP-trained network, using the BP +gradient itself as the predicted credit signal, the perturbation +correlation~$\rho$ between $\langle g_l, \varepsilon v \rangle$ and the +true loss change $L(h_l + \varepsilon v) - L(h_l)$ is +$+0.997$ at every layer (4-layer mean $+0.9965$). This is the +Taylor-expansion ceiling. + +\textbf{Negative control.} On the same BP-trained network, using a +random vector independent of the layer as the credit signal, $\rho$ is +$+0.006$ (4-layer mean), within statistical noise of zero. + +\textbf{Cross-metric triangulation on the test conditions.} + +\begin{table}[h] +\centering +\caption{Two metrics, four conditions. The agreement between cosine and +perturbation correlation rules out single-metric artifacts.} +\label{tab:two-metrics} +\begin{tabular}{lrr} +\toprule +condition & deep cosine $\overline{\cos}$ & deep $\overline{\rho}$ \\ +\midrule +positive control (BP grad on BP net) & $1.000$ & $+0.997$ \\ +negative control (random vector on BP net) & --- & $+0.006$ \\ +vanilla DFA, ep 1 (3 seeds, meaningful regime) & $-0.008 \pm 0.013$ & $-0.003 \pm 0.005$ \\ +penalized DFA, ep 30 (3 seeds, lam=$10^{-2}$) & $+0.155 \pm 0.025$ & $+0.080 \pm 0.011$ \\ +\bottomrule +\end{tabular} +\end{table} + +The penalized DFA's $+0.080$ perturbation correlation is $\sim\!13\times$ +the negative control and $\sim\!8\%$ of the positive control. Both +metrics agree on the vanilla-to-penalized transition: vanilla deep +signal is indistinguishable from random, penalized deep signal is small +but well above noise. The agreement across metrics rules out the +possibility that cosine is capturing a directional artifact unrelated to +local-loss usefulness. + +\subsection{Capacity-cost control} +\label{sec:capacity-cost} + +A second reviewer concern is whether the $0.36 \to 0.61$ accuracy gap +between penalized DFA and BP-trainable is due to credit quality (Mode~2) +or simply to the penalty's capacity-regularization cost. We disambiguate +with a $2\times2$ matched control. + +\begin{table}[h] +\centering +\caption{$2\times2$ capacity-cost control. The penalty is the same in both +the BP and DFA conditions. BP+penalty still clears the random-blocks +baseline by $18.1$pp; DFA+penalty clears it by only $1.4$pp.} +\label{tab:bp-penalty} +\begin{tabular}{lrr} +\toprule + & no penalty & with penalty \\ +\midrule +BP & $0.609$ & $0.530$ \\ +DFA & $0.308$ & $0.363$ \\ +\midrule +$\Delta$ & $-8.0$pp & $+5.5$pp \\ +\bottomrule +\end{tabular} +\end{table} + +Two observations make this control informative. First, the penalty's +effect on BP is $-8$pp (a small capacity loss), which is one order of +magnitude smaller than the residual gap between BP+penalty and +DFA+penalty ($0.530 - 0.363 = 17$pp). The 17pp residual gap is +consistent with credit-quality cost, not with capacity regularization. +Second, the penalty has \emph{opposite} effects on the two methods: it +hurts BP by 8pp while helping DFA by 5.5pp, the opposite pattern expected +from a generally beneficial regime shift. + +\textbf{The clean phrasing.} The 2$\times$2 control identifies a residual +performance gap under matched architecture, data, optimizer family, and +matched penalty, after accounting for the penalty's direct capacity cost +on BP. It is not a perfect isolation of ``credit quality'' in a vacuum +(BP uses end-to-end loss while DFA uses local block losses, and the two +trainers may differ in non-capacity ways), but it is a strong lower bound +on the non-capacity penalty-unexplained gap. + +\subsection{Summary: four validations of the two-mode separation} + +Together, the disambiguation experiment, the cross-metric triangulation, +the capacity-cost control, and the threshold robustness analysis provide +four independent lines of evidence that the failure of standard FA +evaluation is not a single phenomenon. Mode~1 (measurement degeneracy) +is detected by diagnostic (b), is causally controlled by the residual- +stream penalty, and is specifically associated with terminal-LayerNorm +architectures in our audits. Mode~2 (low intrinsic credit quality) +persists after Mode~1 is alleviated, is invisible in vanilla DFA at any +epoch (because the measurement is degenerate), and is detected by direct +per-layer cosine in the meaningful regime, with the perturbation +correlation triangulating the same finding via a different metric. + +\section{Limitations} +\label{sec:limitations} + +Our audit covers a specific slice of the FA literature: pre-LayerNorm +ResidualMLP, ViT-Mini, and SmallCNN architectures on CIFAR-10, evaluated +under standard hyperparameters. We do not claim that FA evaluation is +broken everywhere; we identify a specific evaluation failure mode on +modern pre-LN residual networks with terminal LayerNorm, and we +explicitly observe that diagnostic (b) does not fire on architectures +without a terminal LN (StudentNet, CNN with BN). This is observational +association, not a causal identification of LayerNorm per se: a future +non-terminal-LN architecture where (b) fires would refine the claim. +Section~\ref{sec:related} cites the classical FA literature where +non-terminal-LN architectures dominate; our central claim concerns the +modern with-terminal-LN residual case. + +The Mode~2 measurement in Section~\ref{sec:two-modes} relies on direct +cosine and perturbation correlation in the meaningful regime, which is +only accessible after a Mode~1 intervention. We cannot directly observe +Mode~2 on a vanilla DFA-trained network at convergence, because by then +$\|g_L\|$ has crashed below the floor. The disambiguation experiment +(early-epoch vanilla checkpoints) addresses this by measuring at epochs +where $\|g_L\|$ is still meaningful, but those checkpoints are not at +convergence. + +The matched-penalty $2{\times}2$ control disambiguates capacity loss from +credit quality but does not account for non-capacity differences between +end-to-end BP and local DFA training. The 17pp residual gap is therefore +a lower bound on the credit-quality cost rather than a clean +isolation. + +\section{Broader impacts} +\label{sec:impacts} + +This paper does not introduce a new training method, dataset, or +generative model. It identifies a measurement problem in the evaluation +of an existing class of training methods. Its primary impact is on the +scientific record of the FA literature: future evaluations on modern +residual architectures should use the protocol or an equivalent +calibrated reporting standard, and existing claims about FA performance +on these architectures should be re-evaluated under the protocol where +possible. We are not aware of any negative downstream applications of +this work. + +\section{Conclusion} +\label{sec:conclusion} + +We have shown that standard Feedback Alignment evaluation on modern +residual networks is unreliable because it conflates two distinct +failure modes: measurement degeneracy via terminal-LayerNorm gradient +cancellation, and low intrinsic credit-direction quality of random +feedback. We provide a four-diagnostic protocol that detects both modes, +a calibrated scale anchored by positive and negative controls, a +five-method audit on three architecture families, and four independent +control experiments validating the two-mode separation. The protocol, +audit data, and reporting template are released as a community artifact +for the FA evaluation community. + +\bibliographystyle{plain} +\begin{thebibliography}{99} +\bibitem{lillicrap2016random} +T.~P. Lillicrap, D.~Cownden, D.~B. Tweed, and C.~J. Akerman. +\newblock Random synaptic feedback weights support error backpropagation for deep learning. +\newblock {\em Nature Communications}, 7:13276, 2016. + +\bibitem{nokland2016direct} +A.~N\o{}kland. +\newblock Direct feedback alignment provides learning in deep neural networks. +\newblock In {\em NeurIPS}, 2016. + +\bibitem{akrout2019deep} +M.~Akrout, C.~Wilson, P.~Humphreys, T.~Lillicrap, and D.~B. Tweed. +\newblock Deep learning without weight transport. +\newblock In {\em NeurIPS}, 2019. + +\bibitem{launay2020direct} +J.~Launay, I.~Poli, F.~Boniface, and F.~Krzakala. +\newblock Direct feedback alignment scales to modern deep learning tasks and architectures. +\newblock In {\em NeurIPS}, 2020. + +\bibitem{moskovitz2018feedback} +T.~H. Moskovitz, A.~Litwin-Kumar, and L.~F. Abbott. +\newblock Feedback alignment in deep convolutional networks. +\newblock {\em arXiv:1812.06488}, 2018. + +\bibitem{refinetti2021align} +M.~Refinetti, S.~d'Ascoli, R.~Ohana, and S.~Goldt. +\newblock Align, then memorise: the dynamics of learning with feedback alignment. +\newblock In {\em ICML}, 2021. + +\bibitem{crafton2019direct} +B.~Crafton, A.~Parihar, E.~Gebhardt, and A.~Raychowdhury. +\newblock Direct feedback alignment with sparse connections for local learning. +\newblock {\em Frontiers in Neuroscience}, 13:525, 2019. + +\bibitem{bartunov2018assessing} +S.~Bartunov, A.~Santoro, B.~Richards, L.~Marris, G.~Hinton, and T.~Lillicrap. +\newblock Assessing the scalability of biologically-motivated deep learning algorithms and architectures. +\newblock In {\em NeurIPS}, 2018. + +\bibitem{xiong2020layernorm} +R.~Xiong, Y.~Yang, D.~He, K.~Zheng, S.~Zheng, C.~Xing, H.~Zhang, Y.~Lan, L.~Wang, and T.~Liu. +\newblock On layer normalization in the transformer architecture. +\newblock In {\em ICML}, 2020. + +\bibitem{statebridge2024} +Anonymous. +\newblock State Bridge: terminal-conditioned predictor for credit assignment. +\newblock {\em Anonymous in-progress reference, 2024-2026}. + +\bibitem{creditbridge2024} +Anonymous. +\newblock Credit Bridge: value-field local credit without hidden BP. +\newblock {\em Anonymous in-progress reference, 2024-2026}. + +\end{thebibliography} + +\appendix + +\section{Reproducibility} +\label{app:reproducibility} + +All experiments use PyTorch~$\geq$2.0 on a single NVIDIA A6000 GPU. +Source for the protocol package is in \texttt{protocol/}; experimental +scripts are in \texttt{experiments/}. Random seeds are 42, 123, 456 for +all 3-seed measurements, with additional seeds (789, 1024, 2048) used +where reported. CIFAR-10 is loaded via \texttt{torchvision} with the +standard normalization $(\mu, \sigma) = ((0.4914, 0.4822, 0.4465), +(0.2470, 0.2435, 0.2616))$. + +\section{Pipeline pitfalls catalog} +\label{app:pitfalls} + +Beyond the four diagnostics, we found seven evaluation-pipeline bugs in +our own dogfood codebase that silently corrupt FA evaluation results. +Each has a standalone reproducer in +\texttt{protocol/examples/verify\_pitfalls*.py}. + +\begin{enumerate} +\item \texttt{tensor.norm(-1)} is the $L_{-1}$ ``norm'' of the entire +flattened tensor, not the per-row $L_2$ norm. The correct call is +\texttt{tensor.norm(dim=-1)}. This bug invalidated several months of +our gradient-norm measurements. + +\item \texttt{F.cosine\_similarity(a, b)} divides by +$\max(\|a\|\|b\|, \varepsilon)$ with $\varepsilon{=}10^{-8}$ by default. +When $\|b\|\sim 10^{-10}$ (the regime of the BP gradient on degenerate +DFA-trained pre-LN networks), the divisor becomes $\|a\|\cdot 10^{-8}$ +instead of $\|a\|\cdot 10^{-10}$, scaling the reported cosine by a +factor of $\sim\!100\times$ in the wrong direction. + +\item fp16 mixed precision underflows BP gradients at $\sim\!5\times +10^{-10}$, below fp16's smallest subnormal of $\sim\!6\times 10^{-8}$. +bf16 works because it shares fp32's exponent range. + +\item Random feedback $B_l$ matrices are training-specific. DFA reports +$\Gamma\approx 0.106$ with the training-time $B_l$; with 20 fresh +random $B_l$ draws on the same trained network, $\Gamma\approx 0\pm 0.005$. +The reported alignment is the network adapting to its specific $B_l$, not +intrinsic. + +\item Aggregation strategy across (layers, samples, batches) is rarely +specified but determines the headline number. Same DFA seed-42 gives +$\Gamma \in [-0.028, +0.074]$ across four valid aggregation strategies +(a 3.45$\times$ ratio, with sign flip). + +\item Per-layer $\Gamma$ structure is hidden by aggregation. On the +4-block ResMLP, DFA's headline $\Gamma\approx 0.10$ is driven almost +entirely by the embedding layer ($\Gamma_{l_0} \approx +0.43$); +deeper layers have $\Gamma \approx 0$. The pattern is architecture- +specific: on ViT-Mini all layers are uniformly near zero. + +\item Auxiliary networks (random feedback $B_l$, bridge predictors) not +saved alongside model checkpoints can cause post-hoc $\Gamma$ scripts to +silently fall back to $\cos(\text{BP\_grad}, \text{BP\_grad}) = 1.0$ and +report ``perfect alignment.'' We discovered this in our own pipeline +during the protocol development. Check that auxiliary networks are +persisted before reporting any $\Gamma$ value. +\end{enumerate} + +\section{Methodology: walk-back chain} +\label{app:walkback} + +The framing of this paper underwent several corrections during the +development of the protocol. We document the four-step progression +explicitly as part of the methodology, not as narrative drama: + +\begin{enumerate} +\item Initial metric ($\Gamma\approx 0.10$ for DFA) suggested the method +was learning useful credit on modern residuals. +\item Diagnostic showed the metric was measured against a numerical-floor +reference vector ($\|g_L\|\sim 10^{-10}$); the headline number was not +interpretable. +\item Revised control (the residual-stream penalty) restored the +reference but only partially closed the accuracy gap to BP, identifying +a residual phenomenon. +\item Final interpretation (this paper) separates measurement failure +(Mode~1) from genuine credit-quality cost (Mode~2), validated by the +four control experiments of Section~\ref{sec:two-modes}. +\end{enumerate} + +\section{Six independent validations of the two-mode separation} +\label{app:six-validations} + +For completeness we list all six independent validation experiments, +beyond the four reported in the main text: + +\begin{enumerate} +\item Direct deep-layer cosine on penalized DFA (3 seeds): deep mean +$+0.155 \pm 0.025$. +\item Null calibration with 20 fresh random $B_l$: deep cosine +$+0.002 \pm 0.022$ (within noise). +\item Hypothesis-disambiguation sweep: vanilla DFA early-epoch deep +cosine $-0.008 \pm 0.013$ across 3 seeds at epoch 1. +\item BP+penalty matched-control: 8pp BP capacity cost vs 17pp residual +gap at $\lambda{=}10^{-2}$. +\item Multi-seed lock-in: 24 measurements (3 seeds $\times$ 2 epochs +$\times$ 4 deep layers) all in $[-0.04, +0.02]$ on vanilla. +\item Cross-metric triangulation via perturbation correlation: vanilla +$+0.002$, penalized $+0.080$ (3 seeds), positive control (BP grad) +$+0.997$, negative control (random vector) $+0.006$. +\end{enumerate} + +\end{document} |